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      Reply to the reviewers

      We thank both reviewers for their detailed and critical assessment of our work. Below we provide a step-by-step response to your concerns.

      Reviewer #1

      Evidence, reproducibility and clarity

      The manuscript presents data demonstrating the function of BRI1 in removing the H3K27me3 epigenetic marks in genes involved in seed coat development in Arabidopsis. The results support that BRI1 may function here independently of brassinosteroid. The work combines genetics with a large panel of mutant lines, phenotyping by quantitative microscopy and chemical treatment, H3K27me3 profiling by CUT&TAG, and data mining for published gene profiling. The introduction is adequately informative, complete and explaining the state-of-the-art to the readers. The result part may be a bit lengthy (especially the first part) and some parts may be a bit repetitive.

      Thank you for your positive assessment of our work and for the constructive criticism. Below we respond to each of your points.

      Major

      1. Seed size is dependent of multiple factors. And few are explained here, notably the number of seeds per silique, the number of ovule per silique, the position of the silique of the branch (related to the age of the meristem), the total number of produced siliques (fertilised flowers) by the inflorescence meristem and the plant. And maybe if produced by the main and lateral branches. Were the authors consistent in the evaluation of analyzed siliques coming from the same type of branches, same age of the meristem, etc? Especially as some of the analysed mutants are dwarf, which is a sign of different plant fitness compared to WT.

      This is a valid point. We did aim to analyze seeds coming from the main inflorescences of the plants and at similar stages of shoot development. This was harder to achieve in some genotypes, as indeed some BR and JMJ mutants have different plant architectures. However, we did repeat those experiments multiple times and always found consistent differences between the WTs and the mutants. See also our response to your next point and to the first point raised by Reviewer 2, as well as our new Fig. S6.

      1. The seed perimeter measurements in BR mutant seeds (Figure S6) are variable. Are you sue the ovule size does not have any influence? What about presenting the relative size as earlier in the text?

      Yes, this is particularly true for the Col-0 vs dwf5 comparison. The reason for this is that a different growth chamber was used for this experiment (greenhouse vs a climate chamber). We have observed that absolute seed growth phenotypes can change depending on the environmental conditions, which is something we are currently studying. However, importantly, we do not see changes in relative growth of the mutants when compared to the WT, independently of the growth conditions. That is, BR mutants produce consistently smaller seeds than the WT, independently of the conditions in which the plants are grown. To illustrate this point, we now add a new Figure, Fig. S6, where we show four independent biological replicates of assays comparing seed size between WT and det2 or bri1. These replicates were done in different growth chambers.

      Indeed, presenting the data as relative size would solve this issue, but we worried that we would be hiding the "real" values by doing so. However, if the Reviewer and Editor deem it necessary, we could replot the data as relative to WT.

      1. The number of evaluated samples is often {plus minus} n = 30, sometimes less, meaning less than what a silique contains of seeds. Did the authors evaluate the variability and reproductibility of their measurements, e.g, how many siliques per plant, how many plants, how many biological repeats? For example, in Figure S6, the number of measured ovules were as low as 16, which could be the reason why no significant difference in size were observed (low statitical strength). The variation in the Col WT is already visible. Is this variation significant?

      On average we pooled seeds from 6-10 siliques coming from 2-3 different plants of the same genotype. We then took microscopic photos of 60 to 100 random seeds in those pools. Out of those, 30 random photos were used for the measurements. You are right this is an important point. We now added this information to the Methods section.

      Moreover, we did calculate whether the sample size we were using provided enough statistical power. For the differences that we see, of around 50 um in perimeter, 26 samples would have been enough to achieve 80% statistical power, which most studies use as standard. In most of our experiments we used closer to 30 samples, which gives us 95% power.

      Indeed, the left-most panel on Fig S6B is the exception. With that plot we mostly wanted to test if ovules produced by BR mutants were smaller than those of WT plants. That does not seem to be the case, even if the sample size is small. However, if deemed necessary, we can repeat those measurements with a higher sample number.

      1. You indicate (line 149) that REF6 is not expressed in the gametophyte but GFP signal is observed in the cytoplasm for the central cell in Fig 1. The same goes for the expression pattern with the GUS line in Figure S2. (Line 290) One can not exclude expression in the endosperm or embryo with the presented pictures, or in the seed coat in older seeds.

      We interpreted those diffuse signals in the cytoplasm of the gametophyte as background noise, as REF6 should be nuclearly localized. But we could be wrong. We therefore made changes to the text in lines 150-152 to reflect this.

      And you are right that REF6 is expressed in the endosperm and embryo in later stages of development. We mention this in lines 157-159.

      1. Make sure that you do not overstate your result conclusions, or add a reference to some of the statements. For example, line 185, for the choice of 3 DAP time point and the fact that seed coat development is based on cell expansion and interaction with the endosperm. Another example, in line 262, is where it is stated that the jmj mutants are compromised in ovule and pollen development. This was not assessed. You only checked the reduced seed set, not the fitness of the gametophytes. Or in line 337, where you indicate that KLUH is not expressed in all integument layers.

      Thank you for pointing this out. For the claim that seed size at early time points is dictated only by the seed coat and endosperm, and not by the embryo, we added the appropriate reference. For the claim that jmj mutants are compromised in ovule development, this was based on our observations of Fig. S3C. We do see malformed or absent megagametophytes in jmj mutants. For pollen development, you are correct that we did not formally address this. We rephrased the sentence to reflect that. For the statement that KLU is not expressed in all integument cell layers, we added the reference.

      1. Another example of this is in line 289 where you stated "a sporophytic function of JMJs at early stages of seed development, [..] and to a zygotic function at the later stages of seed development". I am not sure on what data do you base this conclusion as in all three categories (endosperm, embryo, seed coat) in Fig 2 and S5, genes are expressed in pre-globular stages. And again in line 475: "seed coat growth genes are expressed independentlyof fertilization". Do you have any evidence, a reference?

      The evidence for a sporophytic JMJ function at early stages of seed development, and zygotic function at later stages, comes from our observations that jmj seed phenotypes are maternal in origin at early stages, but become zygotic later in development. But you are correct that we have to be careful with this interpretation. We now modified that sentence accordingly.

      For the data of Fig 2E and Fig S5, we cannot rule out that some putative REF6 target genes are also expressed even when in the absence of REF6. The expression of those genes is also likely controlled by other factors. The point we wanted to make with those plots is that REF6 may have different target genes in different seed tissues, thus potentially regulating different developmental processes in a tissue-specific manner. We mention this in lines 288-290.

      For your second point, we added the adequate reference.

      1. (around lines 461) I understand that using a 35S promoter is not a good strategy as it would affect many other tissues. Did you consider using a tissue-specific approach as presented in Figure 4?

      We suppose you mean the 35S::ELF6 construct. Yes, this makes sense and we did spend quite some time trying to come up with a good strategy. However, we failed to find a suitable promoter. The issue is that we would need a promoter that is active in all (or most) seed coat layers, but only after fertilization. There are promoters like those of TT genes which are active post-fertilization, but only in one cell layer, and thus likely not useful for our purpose. And there are other promoters, like those of STK or ANT, which are expressed in most integument cell layers, but are also expressed during integument development, and not just after fertilization. So they would have the same issue as the 35S promoter. Unfortunately, so far we have not identified a promoter that would be useful for this kind of experiment, which is why we went with a constitutive promoter, but which is specific to the sporophytic tissues.

      1. You observed that the triple swn clf bri mutant is less dwarf than bri1 mutant and stated in line 483 that it is larger, has more leaves, grow tallerm and flower later and longer. Do you have any qunatitative data? If not, I would state that these observations are qualitative from growing plant aside.

      You are correct that this was based on qualitative assessments, rather than on quantitative data (as it was not the point of the manuscript). We now indicate this in lines 489-490.

      Minor: 1. The title should precise the studies species, here Arabidopsis thaliana. Also the title of one of the part could be rephrased. "in a zygotic manner" sounds strange.

      We modified both title and subtitle, as suggested.

      1. Scale bars are missing in many figures.

      Fixed.

      1. The font size in the graphs is small. The authors may use the empty space of the figures to increase the size of the graphs for clarity. Guidelines could be found here https://tpc.msubmit.net/html/TPC_Detailed_Figure_Guidelines.pdf, as example of good practices.

      You are right. We revised all the figures and increased the font size, especially in the plot labels.

      1. Be consitent in the mutant name, e.g., brz1-D is also presented as brz1-d.

      Fixed.

      1. Figure legend S1: I would not use the word "extremely" while you still have 30% seed set. Extremely would qualifiy for

      We suppose you mean Fig. S3. We corrected the legend.

      1. Figure S8 is missing the WT control for comparison.

      Fixed.

      1. Figure S12, stats are missing

      Fixed.

      1. I would recommend to add a line in the Supplemental tables with the name as this name disappears from the file name during upload. It would help the readers to navigate the data.

      We now made it so the top line is static and is always visible.

      1. Methods: Are all the lines listed used in the study? SR2200 is missing for the method, and please indicate the selection marker for each of the generated lines for open-access of the data if other researchers later use your lines.

      You are right that some references had been left over from a previous document. We now updated the list of lines.

      And indeed, we forgot to mention the use of SR2200. It is now added to the Methods section. We also added the information on the selection markers for the lines we generated.

      1. You have a duplicate for reference Vukašinovíc et al.

      Fixed.

      1. Line 393, remove "s" in embryo and endosperm, in coat (line 674), in size (lines 684, 686

      Fixed.

      1. Line 410, write RPS5A in upper case.

      Fixed throughout the manuscript.

      1. LIne 676, the sentence "...H3K27me3 to be removed from the integuments." I would recomend to be more precise. For example "H3K27mme3 marks to be removed from genes to be expressed in the integuments" or something like that.

      We rephrased this sentence to "We thus hypothesized that BR signaling would be required for JMJ function, allowing for H3K27me3 to be removed from genes necessary for seed coat formation."

      Significance

      The authors provide novel information on the step-wise regulation of seed coat development and its influence on seed size. This is a topic of general interest, beyond the plant model Arabidopsis, especially in the context of reduced seed set caused by (a)biotic stress. The results of this study are valuable to understand seed size regulation in differnet growth context or species. The group previously showed that the auxin phytohormone is necessary after fertilization to initiate seed coat differentiation by inhibiting PRC2. However, as seed coat develops mainly as cell elongation, the epigenetic marks are not diluted by cell division and needs to be actively removed. This study provides insight into this process by identifcation 2 JMJ proteins responsible for removing H3K27me3 marks in the seed coat after fertilization to initiation seed coat development and regulating seed size. BRI1, BES1 and BZR1 are involved in this process, indepently of brassinosteroid, to guide JMJ to their target loci. While the study bring some genetic evidence of this process, molecular insight is still missing. Notably the identification of the target genes and how BRI1 is regulated/activated upon fertilization. Or how auxin and BRI1 co-regulate the process. These questions appear how of scope of this current study.

      Thank you for the assessment. Indeed, the identification of BRI1 downstream genes is out of scope of this work. As you point out earlier in the review, the manuscript is already quite long, and adding such data would make it even more so.

      Reviewer #2

      In this study, Pankaj et al. investigate the role of brassinosteroids and H3K27me3 in seed development, particularly in controlling seed size. They demonstrate that defects in these pathways affect seed size control and suggest that this control occurs in the maternal seed coat. This paper presents novel findings that merit publication and would be of interest to the plant community. However, the data interpretation and presentation could be improved. Additionally, I have a few comments that necessitate further analysis and revision.

      Thank you for the careful and critical assessment of our work. Below we respond to each of the points you raised.

      Major Comments

      1. My main concern is the use of seed size measurement as a proxy for seed coat development. Mature seed size measurements can vary significantly with growth conditions, so it is crucial that the authors present at least three independent experiments (wild type and mutant grown in parallel) in a single box plot to ensure data reliability. Additionally, due to the high number of seeds analyzed, significant changes are often observed, though they are not always reproducible. The authors should standardize their seed measurements, using either seed area or seed perimeter.

      You are right that we do see some variation in seed size between experiments. And, indeed, we suspect this is due to slightly different plant growth conditions, for example when different growth chambers are used. As you suggest, we now show data from four independent biological replicates of seed size comparisons of WT and BR mutants. This is in the new Fig. S6. As you can see, although we do see variations in absolute seed sizes, depending on the growth conditions, there is a consistent difference between WT and mutant seeds across experiments.

      1. It would be beneficial to include data on cell division and cell elongation in the seed coat if the authors aim to extend the seed size phenotype to a seed coat phenotype.

      This is indeed a good point. However, we already showed in a previous publication that seed coat growth is driven by cell elongation and not cell division (https://elifesciences.org/articles/20542). But you are right that this is important to point out. We mention it in lines 66-67.

      1. It is challenging to be fully convinced by the seed coat specificity of the phenotype, as the authors observe variations in total seed set and phenotypic differences in self-crosses and when the mutants are used paternally. Some of the observed phenotypes do not support their hypothesis. In all mutant analyses, the authors should complement their phenotype analysis using seed coat-specific promoters and include heterozygote measurements, as done in some figures.

      We assume you mean the effect of jmj mutations. For BR mutants, we do show data supporting a seed coat effect (Fig. 4). For PRC2 mutants, that has also been previously described (doi.org/10.7554/eLife.20542 and doi.org/10.1073/pnas.1117111108).

      For the JMJ mutants, you are right that we cannot be 100% sure that their effect is purely sporophytic. We now modified the text accordingly to reflect this (see also the response to point 6 of Reviewer 1). We indeed show that REF6 and ELF6 are expressed in the sporophytic tissues of the ovule and that the double mutant has seed coat defects (smaller seed coats and defects in accumulation of proanthocyanidins). And although we can say that those defects are maternal in nature, we can not 100% conclude that they are simply due to the effect of those JMJs in the sporophyte. There may be gametophytic effects that we cannot rule out, even though we do not see either protein expressed in embryo sacs. Thank you for pointing this out.

      Doing a tissue-specific rescue of these phenotypes would be very informative indeed, but also very hard. As we mention in the response to point 7 of Reviewer 1, we do not currently have suitable promoters for this. So we simply cannot run such experiments in a reasonable time frame.

      Overall, we now tried to be more careful in our conclusions and avoid claiming that the effect of JMJs is purely sporophytic. We can make that argument for the BR machinery and for PRC2, but not necessarily for JMJs. You are correct in that assessment.

      1. The authors need to include a fluorescent reporter for ELF6; tissue-specific expression cannot be conclusively determined with the GUS reporter.

      We did obtain an ELF6::GFP line from Caroline Dean's lab (https://www.pnas.org/doi/full/10.1073/pnas.1605733113), but could not see much expression during endosperm or seed coat development. As you can see from that publication, even in embryos and in roots the expression of ELF6:GFP is very blurry. It seems ELF6 is simply expressed at very low levels. We therefore used the GUS reporter, as a more sensitive means to visualize where ELF6 is expressed. You are right that the results are not as precise as that obtained with a fluorescent reporter. However, note that we simply claim that ELF6 is expressed in the integuments and seed coat (line 155). This can be clearly seen in Fig. 1B. The blue product of the β-glucuronidase reaction should be immotile and not travel between tissues (also note that there are no plasmodesmata between endosperm and seed coat). Therefore, we believe that GUS is a suitable reporter to test the seed coat expression of ELF6.

      1. Text editing: In some places, the text is unclear and could benefit from simplification. The authors should replace the term "seed coat formation," as developmentally, integuments are already present before fertilization. The authors are not studying the formation of the seed coat but rather its growth. They should also clarify the term "PRC2 removal." It is unclear whether the authors mean PRC2 lack of expression in the integument, PRC2 eviction from chromatin, or removal of H3K27me3.

      Thank you for noting that. It is very important to us that the text is clear to the reader. If you could indicate where the text is unclear, we are happy to simplify it.

      Regarding the wording, we refer to "seed coat formation" because the seed coat only indeed forms after fertilization. Before fertilization, the sporophytic tissues that cover the megagametophyte are called integuments, and not seed coat. Therefore, we see the seed coat as "forming" from the integuments (i.e., the integuments become seed coat via growth and differentiation).

      With PRC2 removal we indeed mean reduction of expression of PRC2 components. We now make this clear in lines 54-55.

      Minor Comments

      1. L151: Is REF6 expressed in zygotic tissues?

      Reviewer 1 also raised this question. We now added this information to lines 148-150.

      1. Confirm mutant complementation with the different reporter lines.

      All mutant lines that we used have been previously described to be either loss-of-function or hypomorphic mutants. We did not use any mutant line that has not been previously described. We added all references to the corresponding publications in the Methods.

      1. Confirm by qPCR that JMJ13 is indeed not expressed in seeds.

      We tested JMJ13 as a possible factor involved in H3K27me3 removal in the seed coat due to it being described, together with ELF6 and REF6, as one of the three main H3K27 demethylases. But there are, in fact, transcriptomic datasets showing that the expression of JMJ13 is indeed very low or absent in seeds: see RNAseq data in Table S3 in doi.org/10.3389/fpls.2022.998664. Moreover we checked CPMs on published seed scRNAseq datasets (doi.org/10.1038/s41477-021-00922-0) and JMJ13 (AT5G46910) has zero transcript counts in these datasets.

      Because of these two independent instances showing that the expression of JMJ13 is extremely low in seeds (or even totally absent), together with the analysis that we did of the fluorescent reporter line, we believe this is sufficient evidence that this JMJ is specific to the pollen during reproductive development. Note that the reporter that we used is strongly expressed in pollen grains, as had been previously described (doi.org/10.1038/s41556-020-0515-y).

      Even so, if the Reviewer and the Editor deem it necessary that we check JMJ13 expression by qPCR, we can of course do so.

      1. Fig1a and Fig1b: Align the panels in the figure.

      Done.

      1. L183-189: This section is unclear.

      I am sorry that the section is not clear. If you direct us to the points that need to be cleared, we are happy to make changes.

      1. There may be a PDF artifact, but most figures have unattractive misaligned boxes.

      We went through every figure and made slight modifications to avoid such artifacts. We hope they now appear more clear in the new version.

      1. Change the color in Fig 2a.

      Fixed.

      1. The introduction is heavily self-cited. The authors should try to include a broader range of literature.

      It is not clear to us why the Reviewer sees it like that. We only refer to three of our publications in the Introduction. One review manuscript and two research manuscripts. We cite almost 40 manuscripts in the introduction. Therefore, citing three of our works does not seem out of line to us, especially since those manuscripts laid the foundation for this work.

      1. Fig3F: Typo in "microM."

      Fixed.

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

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      Referee #2

      Evidence, reproducibility and clarity

      Review of "BRI1-mediated removal of seed coat H3K27me3 marks is a brassinosteroid-independent process" In this study, Pankaj et al. investigate the role of brassinosteroids and H3K27me3 in seed development, particularly in controlling seed size. They demonstrate that defects in these pathways affect seed size control and suggest that this control occurs in the maternal seed coat. This paper presents novel findings that merit publication and would be of interest to the plant community. However, the data interpretation and presentation could be improved. Additionally, I have a few comments that necessitate further analysis and revision.

      Major Comments

      • My main concern is the use of seed size measurement as a proxy for seed coat development. Mature seed size measurements can vary significantly with growth conditions, so it is crucial that the authors present at least three independent experiments (wild type and mutant grown in parallel) in a single box plot to ensure data reliability. Additionally, due to the high number of seeds analyzed, significant changes are often observed, though they are not always reproducible. The authors should standardize their seed measurements, using either seed area or seed perimeter.

      • It would be beneficial to include data on cell division and cell elongation in the seed coat if the authors aim to extend the seed size phenotype to a seed coat phenotype.

      • It is challenging to be fully convinced by the seed coat specificity of the phenotype, as the authors observe variations in total seed set and phenotypic differences in self-crosses and when the mutants are used paternally. Some of the observed phenotypes do not support their hypothesis. In all mutant analyses, the authors should complement their phenotype analysis using seed coat-specific promoters and include heterozygote measurements, as done in some figures.

      • The authors need to include a fluorescent reporter for ELF6; tissue-specific expression cannot be conclusively determined with the GUS reporter.

      • Text editing: In some places, the text is unclear and could benefit from simplification. The authors should replace the term "seed coat formation," as developmentally, integuments are already present before fertilization. The authors are not studying the formation of the seed coat but rather its growth. They should also clarify the term "PRC2 removal." It is unclear whether the authors mean PRC2 lack of expression in the integument, PRC2 eviction from chromatin, or removal of H3K27me3.

      Minor Comments:

      • L151: Is REF6 expressed in zygotic tissues?

      • Confirm mutant complementation with the different reporter lines.

      • Confirm by qPCR that JMJ13 is indeed not expressed in seeds.

      • Fig1a and Fig1b: Align the panels in the figure.

      • L183-189: This section is unclear.

      • There may be a PDF artifact, but most figures have unattractive misaligned boxes.

      • Change the color in Fig 2a.

      • The introduction is heavily self-cited. The authors should try to include a broader range of literature.

      • Fig3F: Typo in "microM."

      Cross-commenting:

      I think our reviews highlight the same issues. For me, the first point is definitely the most critical.

      Significance

      This paper presents novel findings that merit publication and would be of interest to the plant community. However, the data interpretation and presentation could be improved. Additionally, I have a few comments that necessitate further analysis and revision.

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

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      Referee #1

      Evidence, reproducibility and clarity

      The manuscript presents data demonstrating the function of BRI1 in removing the H3K27me3 epigenetic marks in genes involved in seed coat development in Arabidopsis. The results support that BRI1 may function here independently of brassinosteroid. The work combines genetics with a large panel of mutant lines, phenotyping by quantitative microscopy and chemical treatment, H3K27me3 profiling by CUT&TAG, and data mining for published gene profiling. The introduction is adequately informative, complete and explaining the state-of-the-art to the readers. The result part may be a bit lengthy (especially the first part) and some parts may be a bit repetitive.

      Major comments:

      1. Seed size is dependent of multiple factors. And few are explained here, notably the number of seeds per silique, the number of ovule per silique, the position of the silique of the branch (related to the age of the meristem), the total number of produced siliques (fertilised flowers) by the inflorescence meristem and the plant. And maybe if produced by the main and lateral branches. Were the authors consistent in the evaluation of analyzed siliques coming from the same type of branches, same age of the meristem, etc? Especially as some of the analysed mutants are dwarf, which is a sign of different plant fitness compared to WT.

      2. The seed perimeter measurements in BR mutant seeds (Figure S6) are variable. Are you sue the ovule size does not have any influence? What about presenting the relative size as earlier in the text?

      3. The number of evaluated samples is often {plus minus} n = 30, sometimes less, meaning less than what a silique contains of seeds. Did the authors evaluate the variability and reproductibility of their measurements, e.g, how many siliques per plant, how many plants, how many biological repeats? For example, in Figure S6, the number of measured ovules were as low as 16, which could be the reason why no significant difference in size were observed (low statitical strength). The variation in the Col WT is already visible. Is this variation significant?

      4. You indicate (line 149) that REF6 is not expressed in the gametophyte but GFP signal is observed in the cytoplasm for the central cell in Fig 1. The same goes for the expression pattern with the GUS line in Figure S2. (Line 290) One can not exclude expression in the endosperm or embryo with the presented pictures, or in the seed coat in older seeds.

      5. Make sure that you do not overstate your result conclusions, or add a reference to some of the statements. For example, line 185, for the choice of 3 DAP time point and the fact that seed coat development is based on cell expansion and interaction with the endosperm. Another example, in line 262, is where it is stated that the jmj mutants are compromised in ovule and pollen development. This was not assessed. You only checked the reduced seed set, not the fitness of the gametophytes. Or in line 337, where you indicate that KLUH is not expressed in all integument layers.

      6. Another example of this is in line 289 where you stated "a sporophytic function of JMJs at early stages of seed development, [..] and to a zygotic function at the later stages of seed development". I am not sure on what data do you base this conclusion as in all three categories (endosperm, embryo, seed coat) in Fig 2 and S5, genes are expressed in pre-globular stages. And again in line 475: "seed coat growth genes are expressed independentlyof fertilization". Do you have any evidence, a reference?

      7. (around lines 461) I understand that using a 35S promoter is not a good strategy as it would affect many other tissues. Did you consider using a tissue-specific approach as presented in Figure 4?

      8. You observed that the triple swn clf bri mutant is less dwarf than bri1 mutant and stated in line 483 that it is larger, has more leaves, grow tallerm and flower later and longer. Do you have any qunatitative data? If not, I would state that these observations are qualitative from growing plant aside.

      Minor comments:

      1. The title should precise the studies species, here Arabidopsis thaliana. Also the title of one of the part could be rephrased. "in a zygotic manner" sounds strange.

      2. Scale bars are missing in many figures.

      3. The font size in the graphs is small. The authors may use the empty space of the figures to increase the size of the graphs for clarity. Guidelines could be found here https://tpc.msubmit.net/html/TPC_Detailed_Figure_Guidelines.pdf, as example of good practices.

      4. Be consitent in the mutant name, e.g., brz1-D is also presented as brz1-d.

      5. Figure legend S1: I would not use the word "extremely" while you still have 30% seed set. Extremely would qualifiy for <5%, I guess.

      6. Figure S8 is missing the WT control for comparison.

      7. Figure S12, stats are missing

      8. I would recommend to add a line in the Supplemental tables with the name as this name disappears from the file name during upload. It would help the readers to navigate the data.

      9. Methods: Are all the lines listed used in the study? SR2200 is missing for the method, and please indicate the selection marker for each of the generated lines for open-access of the data if other researchers later use your lines.

      10. You have a duplicate for reference Vukašinovíc et al.

      11. Line 393, remove "s" in embryo and endosperm, in coat (line 674), in size (lines 684, 686

      12. Line 410, write RPS5A in upper case.

      13. LIne 676, the sentence "...H3K27me3 to be removed from the integuments." I would recomend to be more precise. For example "H3K27mme3 marks to be removed from genes to be expressed in the integuments" or something like that.

      Cross-commenting:

      I have been comparing our peer-review reports of the manuscript and found much similarity on our assessment:

      1. The seed size assemment and how this relates to seed coat development

      2. The GUS expression of ELF6 is not sufficient for the provided conclusion of the ELF6 expression

      3. The same would be for REP6

      4. Use of tissue-specific (seed coat specific) promoters to confirm the conclusion.

      Significance

      The authors provide novel information on the step-wise regulation of seed coat development and its influence on seed size. This is a topic of general interest, beyond the plant model Arabidopsis, especially in the context of reduced seed set caused by (a)biotic stress. The results of this study are valuable to understand seed size regulation in differnet growth context or species. The group previously showed that the auxin phytohormone is necessary after fertilization to initiate seed coat differentiation by inhibiting PRC2. However, as seed coat develops mainly as cell elongation, the epigenetic marks are not diluted by cell division and needs to be actively removed. This study provides insight into this process by identifcation 2 JMJ proteins responsible for removing H3K27me3 marks in the seed coat after fertilization to initiation seed coat development and regulating seed size. BRI1, BES1 and BZR1 are involved in this process, indepently of brassinosteroid, to guide JMJ to their target loci. While the study bring some genetic evidence of this process, molecular insight is still missing. Notably the identification of the target genes and how BRI1 is regulated/activated upon fertilization. Or how auxin and BRI1 co-regulate the process. These questions appear how of scope of this current study.

      My filed of expertise: hormones, plant reproduction, Arabidopis, oilseed rape, microscopy, transformation

  2. Sep 2024
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      Reply to the reviewers

      Thank you very much for your editorial handling of our manuscript entitled 'A conserved fungal Knr4/Smi1 protein is vital for maintaining cell wall integrity and host plant pathogenesis'. We have taken on board the reviewers' comments and thank them for their diligence and time in improving our manuscript.

      Please find our responses to each of the comments below.

      Reviewer(s)' comments

      Reviewer #1


      Major comments:


      __1.1. As a more critical comment, I find the presentation of the figures somewhat confusing, especially with the mixing of main figures, supplements to the main figures, and actual supplemental data. On top of that, the figures are not called up in the right order (e.g. Figure 4 follows 2D, while 3 comes after 4; Figure 6 comes before 5...), and some are never called up (I think) (e.g. Figure 1B, Figure 2B). __


      __Response: __The figure order has been revised according to the reviewer's suggestion, while still following eLife's formatting guidelines for naming supplementals. Thank you.

      1.2. I agree that there should be more CWI-related genes in the wheat module linked to the FgKnr4 fungal module, or, vice-versa, CW-manipulating genes in the fungal module. It would at least be good if the authors could comment further on if they find such genes, and if not, how this fits their model.


      Response: Thank you for your insightful suggestion regarding the inclusion of more CWI-related genes in the wheat module linked to the FgKnr4 fungal module F16, or vice versa. We did observe a co-regulated response between the wheat module W05 which is correlated to the FgKnr4 module F16. Namely, we observed an enrichment of oxidative stress genes including respiratory burst oxidases and two catalases (lines 304 - 313) in the correlated wheat module (W05). Early expression of these oxidative stress inducing genes likely induces the CWI pathway in the fungus, which is regulated by FgKnr4. Knr4 functions as both a regulatory protein in the CWI pathway and as a scaffolding protein across multiple pathways in S. cerevisiae (Martin-Yken et al., 2016, https://onlinelibrary.wiley.com/doi/10.1111/cmi.12618 ). Scaffolding protein-encoding genes are typically expressed earlier than the genes they regulate to enable pre-assembly with their interacting partners, ensuring that signaling pathways are ready to activate when needed. In this context, the CWI integrity MAPKs Bck1 and Mkk1 are part of module F05, which includes two chitin synthases and a glucan synthase. This module is highly expressed during the late symptomless phase. The MAPK Mgv1, found in module F13, is expressed consistently throughout the infection process, which aligns with the expectation that MAPKs are mainly post-transcriptionally regulated. Thank you for bringing our attention to this, this is now included in the discussion (lines 427 - 443) along with eigengene expression plots of all modules added to the supplementary (Figure 3 - figure supplement 1).

      To explore potential shared functions of FgKnr4 with other genes in its module, we re-analyzed the high module membership genes within module F16, which includes FgKnr4, using Knetminer (Hassani-Pak et al., 2021; https://onlinelibrary.wiley.com/doi/10.1111/pbi.13583 ). This analysis revealed that 8 out of 15 of these genes are associated with cell division and ATP binding. Four of the candidate genes are also part of a predicted protein-protein interaction subnetwork of genes within module F16, which relate to cell cycle and ATP binding. In S. cerevisiae, the absence of Knr4 results in cell division dysfunction (Martin-Yken et al., 2016, https://onlinelibrary.wiley.com/doi/10.1111/cmi.12618 ). Accordingly, we tested sensitivity of ΔFgknr4 to microtubule inhibitor benomyl (a compound commonly used to identify mutants with cell division defects; Hoyt et al., 1991 https://www.cell.com/cell/pdf/0092-8674(81)90014-3.pdf). We found that the ΔFgknr4 mutant was more susceptible to benomyl, both when grown on solid agar and in liquid culture. This data has now been added Figure 7, and referred to in lines 338-348.

      __Specific issues: __


      1.3. In the case of figure 5, I generally find it hard to follow. In the text (line 262/263), the authors state that 5C shows "eye-shaped lesions" caused by ΔFgknr4 and ΔFgtri5, but I can't see neither (5C appears to be a ΔFgknr4 complementation experiment). The figure legend also states nothing in this regard.

      __Response: __Thank you for your suggestion. We have amended the manuscript to include an additional panel that shows the dissected spikelet without its outer glumes, making the eye shaped diseased regions more visible in Figure 5.

      __1.4. Figure 5D supposedly shows 'visibly reduced fungal burden' in ΔFgknr4-infected plants, but I can't really see the fungal burden in this picture, but the infected section looks a lot thinner and more damaged than the control stem, so in a way more diseased. __


      Response: __Thank you for your insight. We have revised our conclusions based on this image to state that while ΔFgknr4 can colonise host tissue, it does so less effectively compared to the wild-type strain as we are unable to quantitatively evaluate fungal burden using image-colour thresholding due to the overlapping colours of the fungal cells and wheat tissues. Decreased host colonisation is evidenced by (i) reduced fungal hyphae proliferation, particularly in the thicker adaxial cell layer, (ii) collapsed air spaces in wheat cells, and (iii) increased polymer deposition at the wheat cell walls, indicating an enhanced defence response. __Figure 5 has been amended to include these observations in the corresponding figure legend and the resin images now include insets with detailed annotation.

      __1.5. The authors then go on to state (lines 272-273) that they analyzed the amounts of DON mycotoxin in infected tissues, but don't seem to show any data for this experiment. __

      Response: __We have amended this to now include the data in __Figure 5 - figure supplement 2B, thank you.

      Reviewer #2


      __Major issues: __


      2.1 If Knf4 is involved in the CWI pathway, what other genes involved in the CWI pathway are in this fungal module? one of the reasons for developing modules or sub-networks is to assign common function and identify new genes contributing to the function. since FgKnr4 is noted to play a role in the CWI pathways, then genes in that module should have similar functions. If WGCN does not do that, what is the purpose of this exercise?


      Response: __Thank you for raising this point regarding the role of FgKnr4 in the CWI pathway and the expectations for genes of shared function within the FgKnr4 module F16. We did observe that the module containing FgKnr4 (F16) was also correlated to a wheat module (W05) which was significantly enriched for oxidative stress genes. This pathogen-host correlated pattern led us to study module F16, which otherwise lacks significant gene ontology term enrichment, unique gene set enrichments, and contains few characterised genes. This is now highlighted in __lines 233-246. This underscores the strength of the WGCNA. By using high-resolution RNA-seq data to map modules to specific infection stages, we identified an important gene that would have otherwise been overlooked. This approach contrasts with other network analyses that often rely on the guilt-by-association principle to identify novel virulence-related genes within modules containing known virulence factors, potentially overlooking significant pathways outside the scope of prior studies. Therefore, our analysis has already benefited from several advantages of WGCNA, including the identification of key genes with high module membership that may be critical for biological processes, as well as generating a high-resolution, stage-specific co-expression map of the F. graminearum infection process in wheat. This point is now emphasised in lines 233-252. As discussed in response to reviewer 1, Knr4 functions as both a regulatory protein in the CWI pathway and as a scaffolding protein across multiple pathways in S. cerevisiae (Martin-Yken et al., 2016, https://onlinelibrary.wiley.com/doi/10.1111/cmi.12618 ) which would explain its clustering separate from the CWI pathway genes. The high module membership genes within module F16 containing FgKnr4 were re-analysed using Knetminer (Hassani-Pak et al., 2021; https://onlinelibrary.wiley.com/doi/10.1111/pbi.13583 ), which found that 8/15 of these genes were related to cell division and ATP binding. Four of the candidate genes are also part of a predicted protein-protein interaction subnetwork of genes within module F16, which relate to cell cycle and ATP binding. In S. cerevisiae, the absence Knr4 leads to dysfunction in cell division. Accordingly, we tested sensitivity of ΔFgknr4 to the microtubule inhibitor benomyl (a compound commonly used to identify mutants with cell division defects; Hoyt et al., 1991 https://www.cell.com/cell/pdf/0092-8674(81)90014-3.pdf). We found that the ΔFgknr4 mutant was more susceptible to benomyl, both when grown on solid agar and in liquid culture. This data has now been added as Figure 7 and referred to in lines 338-348.


      2.2. Due to development defects in the Fgknr1 mutant, I would not equate to as virulence factor or an effector gene.


      __Response: __We are in complete agreement with the reviewer and are not suggesting that FgKnr4 is an effector or virulence factor, we have been careful with our wording to indicate that FgKnr4 is simply necessary for full virulence and its disruption results in reduced virulence and have outlined how we believe FgKnr4 participates in a fungal signaling pathway required for infection of wheat.


      2.3. What new information is provided with WGCN modules compared with other GCN network in Fusarium (examples of GCN in Fusarium is below) ____https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5069591/ https://doi.org/10.1186/s12864-020-6596-y____ DOI: 10.1371/journal.pone.0013021. The GCN networks from Fusarium have already identified modules necessary/involved in pathogenesis.

      Response: __The 2016 New Phytologist gene regulatory network (GRN) by Guo et al. is large and comprehensive. However, only three of the eleven datasets are in planta, with just one dataset focusing on F. graminearum infection on wheat spikes. The other two in planta datasets involve barley infection and Fusarium crown rot. By combining numerous in planta and in vitro datasets, the previous GRNs lack the fine resolution needed to identify genetic relationships under specific conditions, such as the various stages of symptomatic and symptomless F. graminearum infection of mature flowering wheat plants. This limitation is highlighted in the 2016 paper itself. This network is expanded in the Guo et al., 2020 BMC genomics paper where it includes one additional in planta and nine in vitro datasets. However, the in planta dataset involves juvenile wheat coleoptile infection, which serves as an artificial model for wheat infection but is not on mature flowering wheat plants reminiscent of Fusarium Head Blight of cereals in the field. This model differs significantly in the mode of action of F. graminearum, notably DON mycotoxin is not essential for virulence in this context (Armer et al. 2024, https://pubmed.ncbi.nlm.nih.gov/38877764/ ). The Guo et al., 2020 paper still faces the same issues in terms of resolution and the inability to draw conclusions specific to the different stages of F. graminearum infection. Additionally, these GRNs use Affymetrix data, which miss over 400 genes (~ 3 % of the genome) from newer gene models. In contrast, our study addresses these limitations by analysing a meticulously sampled, stage- and tissue-specific in planta RNA-seq dataset using the latest reference annotation. Our approach provides higher resolution and insights into host transcriptomic responses during the infection process. The importance of our study in the context of these GRNs is now addressed in the introduction (__lines 85-92).


      2.4. Ideally, the WGCN should have been used identify plant targets of Fusarium pathogenicity genes. This would have provided credibility and usefulness of the WGCN. Many bioinformatic tools are available to identify virulence factors and the utility of WGCN in this regard is not viable. However, if the authors had overlapped the known virulence factors in a fungal module to a particular wheat module, the impact of the WGCN would be great. The module W12 has genes from numerous traits represented and WGCN could have been used to show novel links between Fg and wheat. For example, does tri5 mutant affect genes in other traits?

      __Response: __Thank you for your suggestions. In this study we have shown the association between the main fungal virulence factor of F. graminearum, DON mycotoxin, with wheat detoxification responses. Through this we have identified a set of tri5 responsive genes and validated this correlation in two genes belonging to the phenylalanine pathway and one transmembrane detoxification gene. Although we could validate more genes in this tri5 responsive wheat module, our paper aimed to investigate previously unstudied aspects of the F. graminearum infection process and how the fungus responded to changing conditions within the host environment. We accomplished this by characterising a gene within a fungal module that had limited annotation enrichment and few characterised genes. Tri5 on the other hand is the most extensively studied gene in F. graminearum and while the network we generated may offer new insights into tri5 responsive genes, this is beyond the scope of our current study. In addition to the tri5 co-regulated response, we have also demonstrated the coordinated response between the fungal module F16, which contains FgKnr4 that is necessary for tolerance to oxidative stress, and the wheat module W05, which is enriched for oxidative stress genes.


      While our co-expression network approach can be used to explore and validate other early downstream signaling and defense components in wheat cells, several challenges must be considered: (a) the poor quality of wheat gene calls, (b) genetic redundancy due to both homoeologous genes and large gene families, and (c) the presence of DON, which can inhibit translation and prevent many transcriptional changes from being realised within the host responses. Additionally, most plant host receptors are not transcriptionally upregulated in response to pathogen infection (most R gene studies for the NBS-LRR and exLRR-kinase classes), making their discovery through a transcriptomics approach unlikely. These points will be included in our discussion (lines 408-413), thank you.

      Specific issues

      • *

      2.5. Since tri5 mutant was used a proof of concept to link wheat/Fg modules, it would have been useful to show that TRI14, which is not involved DON biosynthesis, but involved in virulence ( https://doi.org/10.3390/applmicrobiol4020058____) impact the wheat module genes.


      Response: __Our goal was to show that wheat genes respond to the whole TRI cluster, not just individual TRI genes. Therefore, the tri5 mutant serves as a solid proof-of-concept, because TRI5 is essential for DON biosynthesis, the primary function of the TRI gene cluster, thereby representing the function of the cluster as a whole. This is now clarified in __lines 217-219. Additionally, the uncertainties surrounding other TRI mutants would complicate the question we were addressing-namely, whether a wheat module enriched in detoxification genes is responding to DON mycotoxin, as implied by shared co-expression patterns with the TRI cluster. For instance, the referenced TRI14 paper indicates that DON is produced in the same amount in vitro in a single media. Although the difference is not significant, the average DON produced is lower for the two Δtri14 transformants tested. Therefore, we cannot definitively rule out that TRI14 is involved in DON biosynthesis and extrapolate this to DON production in planta. Despite this, the suggestion is interesting, and would make a nice experiment but we believe it does not contribute to the overall aim of this study.

      2.6. Moreover, prior RNAseq studies with tri5 mutant strain on wheat would have revealed the expression of PAL and other phenylpropanoid pathway genes?

      __Response: __We agree that this would be an interesting comparison to make but unfortunately no dataset comparing in planta expression of the tri5 mutant within wheat spikes exists.

      2.7. Table S1 lists 15 candidate genes of the F16 module; however, supplementary File 1 indicates 74 genes in the same module. The basis of exclusion should be explained. The author has indicated genes with high MM was used as representative of the module. The 59 remaining genes of this module did not meet this criteria? Give examples.


      Response: __The 15 genes with the highest module membership were selected as initial candidates for further shortlisting from the 74 genes within module F16. In WGCNA, genes with high module membership (MM) (i.e. intramodular connectivity) are predicted to be central to the biological functions of the module (Langfelder and Horvath, 2008; https://bmcbioinformatics.biomedcentral.com/articles/10.1186/1471-2105-9-559 ) and continues to be a metric to identify biologically significant genes within WGCN analyses (https://bmcplantbiol.biomedcentral.com/articles/10.1186/s12870-024-05366-0 Tominello-Ramirez et al., 2024; https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9151341/ ;Zheng et al., 2022; https://www.nature.com/articles/s41598-020-80945-3 Panahi and Hejazi et al 2021). Following methods by Mateus et al. (2019) (https://academic.oup.com/ismej/article/13/5/1226/7475138 ) key genes were defined as those exhibiting elevated MM within the module, which were also strongly correlated (R > |0.70|) with modules of the partner organism (wheat). We have clarified this point in the manuscript. Thank you for the suggestion. (__Lines 253-263).

      2.____8. A list from every module that pass this criteria will be useful resource for functional characterization studies.


      __Response: __A supplementary spreadsheet has been generated which includes full lists of the top 15 genes with the highest module membership within the five fungal modules correlated to wheat modules and a summary of shared attributes among them. Thank you for this suggestion.

      2.9. Figure 3 indicates TRI genes in the module F12; your PHI base in Supp File S2 lists only TRI14. Why other TRI genes such as TRI5 not present in this File?


      Response: For clarity, the TRI genes in module F12 are TRI3, TRI4, TRI11, TRI12, and TRI14 which was stated in Table 1. TRI5 clusters with its neighboring regulatory gene TRI6 in module F11, which exhibits a similar but reduced expression pattern compared to module F12. To improve clarity on this the TRI genes in module F12 are also listed in-text in line 168 and added to Figure 4. The enrichment and correlated relationship of W12 to a cluster's expression still imply a correlated response of the wheat gene to the TRI cluster's biosynthetic product (DON), which is absent in the Δtri5 mutant.

      TRI14 and TRI12 are listed in PHI-base. TRI12 was mistakenly excluded due to an unmapped Uniprot ID, which were added separately in the spreadsheet. We will recheck all unmapped ID lists to ensure all PHI-base entries are included in the final output. Thank you for pointing out this error.


      2.10. What is purpose of listing the same gene multiple times? Example, osp24 (a single gene in Fg) is listed 13 times in F01 module.


      __Response: __This is a consequence of each entry having a separate PHI ID, which represents different interactions including inoculations on different cultivar. Cultivar and various experimental details were omitted from the spreadsheet to reduce information density, however the multiple PHI base ID's will be kept separate to make the data more user friendly when working with the PHI-base database. An explanation for this is now provided in the file's explanatory worksheet, thank you.

      Reviewer #3:


      3.1. Why only use of high confidence transcripts maize to map the reads and not the full genome like Fusarium graminearum? I have never analyzed plant transcriptome.


      __Response: __ In the wheat genome, only high-confidence gene calls are used by the global community (Choulet et al., 2023; https://link.springer.com/chapter/10.1007/978-3-031-38294-9_4 ) until a suitable and stable wheat pan-genome becomes available.

      3.2. The regular output of DESeq are TPMs, how did the authors obtain the FPKM used in the analysis?


      Response: FPKM was calculated using the GenomicFeatures package and included on GitHub to enhance accessibility for other users. However, the input for WGCNA and this study as a whole was normalised counts rather than FPKM. The FPKM analysis was done to improve interoperability of the data for future users and made available on Github. To complement this, the information regarding FPKM calculation is now included in the methods section of the revised manuscript (line 491).

      3.3. Do the authors have a Southern blot to prove the location of the insertion and number of insertions in Zymoseptoria tritici mutant and complemented strains?


      __Response: __No, but the phenotype is attributed to the presence or absence of ZtKnr4, as the mutant was successfully complemented in multiple phenotypic aspects. This satisfies Koch's postulates which is the gold standard for reverse genetics experimentation (Falkow 1988; https://www.jstor.org/stable/4454582 ).

      __3.4. Boxplots and bar graphs should have the same format. In Figures 5 B and F and supplementary figure 6.3 the authors showed the distribution of samples but it is lacking in figure 3 B and all bar graphs. __


      __Response: __Graphs have been modified to display the distribution of all samples, thank you.

      3.5. Line 247 FGRAMPH1_0T23707 should be FGRAMPH1_01T23707


      __Response: __Thank you this has now been amended.

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      Referee #3

      Evidence, reproducibility and clarity

      The authors of the manuscript entitled "A conserved fungal Knr4/Smi1 protein is vital for maintaining cell wall integrity and host plant pathogenesis" used a weighted gene co-expression network to identify Fusarium graminearum genes highly expressed during early symptomless infection of wheat. Based on its sequence and previous studies, authors selected FgKnr4 from the early symptomless Fusarium modules. The characterization of knockout strains revealed a role in morphogenesis, growth, cell wall stress tolerance, and virulence in F. graminearum and the phylogenetically distant fungus Zymoseptoria tritici.

      The methods are properly described and statistical analysis are reasonable so reproducibility is possible. The RNA-seq dataset is already published and the authors provided a repository with the code used to create the co-expression network. However, I have the following questions:

      • Why only use of high confidence transcripts maize to map the reads and not the full genome like Fusarium graminearum? I have never analyzed plant transcriptome.
      • The regular output of DESeq are TPMs, how did the authors obtain the FPKM used in the analysis?
      • Do the authors have a southern blot to prove the location of the insertion and number of insertions in Zymoseptoria tritici mutant and complemented strains?
      • Boxplots and bar graphs should have the same format. In Figures 5 B and F and supplementary figure 6.3 the authors showed the distribution of samples but it is lacking in figure 3 B and all bar graphs.
      • Line 247 FGRAMPH1_0T23707 should be FGRAMPH1_01T23707

      Referees cross-commenting

      I agree with reviewer 1, the order in which the figures are called in the text is confusing. Regardless of figures 5C-D I am no expert in the field therefore I can only say they look like they have not been edited.

      I agree with reviewer 1, data of DON mycotoxin production in infected issues is need it to support statement in line 272-273.

      I agree with Reviewer 2, the criteria to exclude genes from the final selection list should be explained.

      Significance

      The study showed, once again, that a weighted gene co-expression network is a great method to identify new genes of interest regardless of the organism or condition even if not very popular in the fungal pathogen field yet. The study proved that functions identified in a WGCN module from a pathogen have their opposite in the host module. The authors go beyond the theory and demonstrate the effect of the highest expressed gene during the early symptomless stage of infection in maize and wheat fungal pathogens.

      Fungal pathogen, RNA-seq, metabolic models, metabolism, comparative genomics

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      Referee #2

      Evidence, reproducibility and clarity

      Summary: The authors in this manuscript use "dual weighting" to identify clusters or modules of genes from the fungus F. graminearum (Fg) with coordinated expression patterns with genes in wheat modules - potentially uncover key regulators or pathways linking Fg genes with plant traits, including plant pathogenesis. As proof of concept, the authors use one of the fungal genes FgKnr4 identified in a fungal module that has strong link with the wheat module. They were able to show that this gene is likely involved in CWI pathway and affects virulence properties of the fungus

      Major comments:

      Does the WGCN provide useful framework to link fungal genes affecting plant traits? If Knf4 is involved in the CWI pathway, what other genes involved in the CWI pathway are in this fungal module? This is not forthcoming. Due to development defects in the Fgknr1 mutant, I would not equate to as virulence factor or an effector gene.

      Since tri5 mutant was used a proof of concept to link wheat/Fg modules, it would have been useful to show that TRI14, which is not involved DON biosynthesis, but involved in virulence ( https://doi.org/10.3390/applmicrobiol4020058) impact the wheat module genes. Moreover, prior RNAseq studies with tri5 mutant strain on wheat would have revealed the expression of PAL and other phenylpropanoid pathway genes?

      Table S1 lists 15 candidate genes of the F16 module; however, supplementary File 1 indicates 74 genes in the same module.

      The basis of exclusion should be explained. The author has indicated genes with high MM was used as representative of the module. The 59 remaining genes of this module did not meet this criteria? Give examples. Did similar exclusion criteria used for other modules and if so, how many genes in each module pass the criteria? For example, Did TRI5 in module F12 pass this criteria. A list from every module that pass this criteria will be useful resource for functional characterization studies.

      Minor comments:

      Figure 3 indicates TRI genes in the module F12; your PHI base in Supp File S2 lists only TRI14. Why other TRI genes such as TRI5 not present in this File? What is purpose of listing the same gene multiple times? Example, osp24 (a single gene in Fg) is listed 13 times in F01 module.

      Referees cross-commenting

      agree with both reviewers regarding clarification of Figures.

      one of the reasons for developing modules or sub-networks is to assign common function and identify new genes contributing to the function. since FgKnr4 is noted to play a role in the CWI pathways, then genes in that module should have similar functions. If WGCN does not do that, what is the purpose of this exercise?

      Significance

      What new information is provided with WGCN modules compared with other GCN network in Fusarium (examples of GCN in Fusarium is below)

      https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5069591/ https://doi.org/10.1186/s12864-020-6596-y DOI: 10.1371/journal.pone.0013021

      The GCN networks from Fusarium have already identified modules necessary/involved in pathogenesis. Ideally, the WGCN should have been used identify plant targets of Fusarium pathogenicity genes. This would have provided credibility and usefulness of the WGCN.

      Many bioinformatic tools are available to Identify virulence factors and the utility of WGCN in this regard is not viable. However, if the authors had overlapped the known virulence factors in a fungal module to a particular wheat module, the impact of the WGCN would be great. The module W12 has genes from numerous traits represented and WGCN could have been used to show novel links between Fg and wheat. For example, does tri5 mutant affect genes in other traits?

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      A public mRNA-seq dataset from Dilks et al. (2019) for wheat spikelets infected by Fusarium graminearum was used to generate a dual weighted gene co-expression network (WGCN). Since colonization of the spike by F. graminearum progresses from spikelet to spikelet, thereby forming an infection-gradient from early to late stages, quasi spatio-temporal resolution for the transcriptomic dataset can be achieved by cutting the spike into equal pieces along this gradient (in this case cuts were done at rachis internodes 1-2, 3-4, 5-6, and 7-8. The authors created co-expression networks for both, fungal and plant genes, and cross-correlated them. They identify several modules specific for each infection stage. For further analysis, the authors focus on two module pairs. (1) the wheat module 12 (W12), which correlates to Fusarium module 12 (F12), and (2) the Fusarium module 16 (F16) and the correlated wheat modules 1 and 5 (W01/W05). The W12/F12 modules were deemed of interest because they were specific to the transition from symptomless to symptomatic infection stage. Here, the authors find genes related to mycotoxin production to be upregulated in the F12 module, while the W12 is enriched in genes involved in detoxification. F16 and W01/W05 are specific to the earliest stages of infection, and thus most likely involved in fungal virulence. Here, one of the key genes identified is FgKnr4, which the authors show to be important for fungal virulence, as gene knockout leads to a premature stop of disease progression. As the authors show that FgKnr4 is involved in activating cell wall-integrity mechanisms, and may function in oxidative stress-resistance, this reduced virulence may be the result a reduced ability of the fungus to withstand plant defense mechanisms. Interestingly, knocking out an orthologue of FgKnr4 in Zymoseptoria tritici led to similarly reduced virulence of this pathogenic fungus on wheat plant.

      Comments:

      Overall, I find the WGCN analysis to be very interesting and informative, especially because of the different stages of infection. As the dataset is made public (I believe), I think that this will be a really important resource for the community. The exemplary functional analysis of the F16/W01/W05 modules via FgKnr4 is very interesting and demonstrates that novel genes involved in virulence can be identified via this approach. A similar more detailed analysis of the W12/F12 modules with a focus on detoxification mechanisms in the plant (i.e. the W12 module) would be a very interesting bonus, but as much as I would be interested in reading about it, functional gene analyses in wheat are obviously time-consuming, and it is not essential to this manuscript. As a more critical comment, I find the presentation of the figures somewhat confusing, especially with the mixing of main figures, supplements to the main figures, and actual supplemental data. On top of that, the figures are not called up in the right order (e.g. Figure 4 follows 2D, while 3 comes after 4; Figure 6 comes before 5...), and some are never called up (I think) (e.g. Figure 1B, Figure 2B). In the case of figure 5, I generally find it hard to follow. In the text (line 262/263), the authors state that 5C shows "eye-shaped lesions" caused by ΔFgknr4 and ΔFgtri5, but I can't see neither (5C appears to be a ΔFgknr4 complementation experiment). The figure legend also states nothing in this regard. Figure 5D supposedly shows 'visibly reduced fungal burden' in ΔFgknr4-infected plants, but I can't really see the fungal burden in this picture, but the infected section looks a lot thinner and more damaged than the control stem, so in a way more diseased. The authors then go on to state (lines 272-273) that they analyzed the amounts of DON mycotoxin in infected tissues, but don't seem to show any data for this experiment. In contrast to the sometimes confusing data presentation, I find the table of correlated modules (table 1) very helpful, and obviously am happy to see that all data is available in the first author's GitHub account.

      Referees cross-commenting

      just to clarify in regards to my comment on Figures 5C-D, and Reviewer #3's comment "Regardless of figures 5C-D I am no expert in the field therefore I can only say they look like they have not been edited." - I didn't want to insinuate that the images have been edited. Based on the images provided, I just can't see what the authors state is shown. So this is not about editing/manipulation - just about image quality/choice. The phenotypic descriptions by the authors are quite detailed ("eye-shaped lesions", 'visibly reduced fungal burden'...), but at least for me, the images aren't good enough to illustrate and underpin their statements. Maybe better images are needed, maybe magnifications of the exact regions showing the phenotypes? But this is simply a matter of presentation, not of editing/manipulation.

      Second, I agree that there should be more CWI-related genes in the wheat module linked to the FgKnr4 fungal module, or, vice-versa, CW-manipulating genes in the fungal module. It would at least be good if the authors could comment further on if they find such genes, and if not, how this fits their model.

      Significance

      In summary, I think that the presented WGCN analysis of mRNA-seq data with quasi-spatio-temporal resolution is a very helpful approach to identify novel fungal virulence and plant immunity genes, and with the created datasets made public, this will be an interesting and valuable resource for the community. The identification and functional analysis of FgKnr4 works as proof-of-principle. If the data presentation is improved, I believe that this will be an interesting publication.

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      Reply to the reviewers

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

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      Referee #3

      Evidence, reproducibility and clarity

      This study identified Cpn1, a fission yeast ortholog of human Caprin1, to be involved in heterochromatin re-establishment in S. pompe by potentially regulating heterochromatic transcript stability and localization. Moreover, Cpn1 was shown to be important for stress granule formation. Although the role of Cpn1 for heterochromatin establishment and granule formation is strong, the point that there is a crosstalk between the two is weaker and could be explained through multiple independent effects. Overall, the manuscript provides interesting new observations with regards to Cpn1 function that are adequate for publication, however, a few additional validations need to be performed to strengthen the crosstalk conclusion, which could be a new significant connection.

      The following comments could be addressed before publication to improve the manuscript.

      Specific Comments

      1. The point that there is a "Crosstalk between heterochromatin integrity and cytoplasmic RNP granule formation" could be strengthened before publication, or the tone of the manuscript revised to reflect the issues below.

      A) There is no data in this section showing a direct crosstalk between heterochromatin integrity and granules. The results show that certain mutants alter heterochromatin integrity the formation of PABP-containing granules. However, those proteins could have different functions in the nucleus, cytoplasm and upon stress. Thus, granule formation could be independent of heterochromatin perturbation. E.g. Loss of Ago1 could impact cytoplasmic RNA abundance/ stability and this therefore influence granule assembly. Similarly, Cpn1/Caprin could be a multifunctional protein in S. pombe and affect various aspects of RNA metabolism. The possibility, that these proteins have multiple different functions in the cell and heterochromatin integrity and cytoplasmic RNP granule formation could be due to different functions of those proteins and not due to a crosstalk should be discussed as well.

      B) Figure 5 title says that "disruption of heterochromatin alters the formation of PABP-containing RNP granules". There is no data in this figure that shows that "disruption of heterochromatin" directly causes granules. Its rather that heterochromatin mutants show altered PABP-containing RNP granules. While this is fine, it should be pointed out that this is a correlation, with a direct connection being inferred.

      C) The strongest connection of heterochromatin integrity to RNP granules is the accumulation of heterochromatic transcripts in those granules. Therefore, the manuscript could be strengthened by rearranging the sections/figures.

      In addition, Fig. 5A shows PABP containing granules in unstressed conditions for rik1, clr4, ago1 loss. This suggests that those granules contain lots of polyadenylated RNA. Evidence is needed that the mutations studied are not affecting global cytoplasmic translation or mRNA decay (e.g. by puromycin staining and smRNA-FISH staining or qPCR (e.g. GAPDH)). Moreover, it needs to be shown that endogenous expression of Cpn1 is unchanged. If those perturbations affect Cpn1 (or Nxt3) levels, the granule phenotype could be solely due to changes in stress granule promoting proteins. 2. The work would be strengthened by adding some additional experiments. Specifically:

      A) "Previous studies by ourselves and others have provided evidence that accumulation of transcripts on chromatin can impair heterochromatin assembly, possibly through increased formation of RNA-DNA hybrids". Increased RNA-DNA hybrids/ R-loop structures were shown to lead to genomic instability, which could lead to micronuclei formation and nuclei leakage in the cytoplasm during stress. It would be nice to provide close-up view images of those stress induced cytoplasmic granules, that contain cenRNA. Do they contain weaker DAPI signal in those granules, which would be indicative of micronuclei? Moreover, providing an additional stain using either an R-loop antibody, cGAS, or a nuclei membrane marker such as LAMIN B1 could be used to rule out micronuclei/ membranous assemblies.

      B) RNA FISH and quantification for PABP foci in unstressed and stressed clr4Δ dhp1-2 cells is key, which should show the highest changes in foci and RNA accumulation in foci. Are those cells showing an even stronger effect on heterochromatin establishment?

      C) Compared to clr4Δ cpn1Δ, do clr4Δ dhp1-2 cpn1Δ (or cpn1Δ and dhp1-2 cpn1Δ) form more stress induced granules? And do those granules contain more heterochromatic transcripts?

      D) Is heterochromatic transcripts localization in -glucose induced granules also seen with heat shock? 3. Additional tests and quantification is needed to support that conclusion: "...whereas heterochromatin mutants show increased Pabp granule formation in absence of stress, they show a significant reduction in the average number of Pabp foci formed in the presence of stress,...". Different proteins could regulate/loss of proteins impact granule assembly in different manners, for example RNA localization, assembly, disassembly, foci number, foci size, % cells with foci etc. It looks like rik1Δ shows larger foci. Therefore, upon stress, there could be indeed fewer foci because they are larger. A quantification of foci area and total foci area per cell should support or reject that conclusion. Moreover, is the same trend also observed with starvation stress, or only heat shock? 4. The field generally believes G3BP1 is not an endonuclease, and therefore the authors might want to edit the section: " ...these could include, for example, Cpn1 binding partner Nxt3, the human ortholog of which, G3BP1, has been shown to function as an endoribonuclease for degradation of selected RNAs (63)." Although, it was shown that G3BP1 has endoribonuclease activity in that reference, this was never reproduced and is generally now accepted in the field that G3BP1 does not function as a endoribonuclease to regulate RNA homeostasis.

      Minor comment:

      1. Fig. 2 is a bit confusing. Maybe it could help if the controls - to rule out heterochromatin maintenance (B, C,D) - could be better grouped together or put into supplementary.
      2. Fig 4 A, figures for Cpn1R6A-GFP upon glucose starvation is missing.
      3. Fig 4 D, intensity is weaker in mkt1Δ, its difficult to see the granules. It looks like based on the image that there are less granules, but the quantification shows unchanged granules.
      4. Fig 5 D/ Supl S5A, images with stress are missing for rik1 loss (the ones leading to qualifications in 5D)
      5. Fig 5 C, rik1Δ, ago1Δ, co-colocalised with Cpn1-GFP are missing
      6. Fig.6D, one arrow showing cytoplasmic foci is shifted. PABP stain needs to be added to highlight these are cytoplasmic PABP foci.
      7. cen(dg) transcripts show lack of localization in granules in unstressed cells. The explanation why is a bit unclear. "It remained possible that these foci might rather be associated with RNA degradation, ...". Or RNA degradation happens in the nucleoplasm or cytoplasm. Moreover, in the discussion: "Although we were not able to detect stable accumulation of heterochromatic RNAs in these granules by RNA-FISH, we suspect that this may be because these granules are associated with RNA turnover, although it is also possible that they arise as a result of altered RNP homeostasis more broadly." This is confusing. If those granules form due to accumulation of heterochromatic RNAs, then they cannot be the sites for their degradation, because then they would disassemble, if heterochromatic RNAs are degraded.
      8. Clr4Δ and other conditions shows accumulation of cen(dg) RNA-FISH at the centromeres. It would be informative to see if Cpn1-GFP shows colocalization, which could provide additional evidence for the two models in Fig. 7.
      9. Fig. 6D/E: Its difficult to see changes of cen(dg) RNA-FISH intensity at the centromeres in the images. A close-up view should be provided without overexposure to indicate differences.

      Significance

      This manuscript begins to address a possible relationship between stress granule formation and the regulation of heterochromatin. This is an interesting connection, although the mechanism by which such these two processes are connected is unclear at this time.

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      Referee #2

      Evidence, reproducibility and clarity

      In their manuscript titled "Fission yeast Caprin protein is required for efficient heterochromatin establishment", Zhang and colleagues describe the role of Caprin1 (Cpn1), the fission yeast ortholog of mammalian CAPRIN1, in the de novo establishment of heterochromatin. Using reporter assays for heterochromatin formation, they found that deletion of Cpn1 reduces H3K9 methylation, thereby impairing the de novo establishment of silencing, while the maintenance of silencing at centromeric repeats remains unaffected.

      The authors demonstrate that Cpn1 interacts with the fission yeast orthologs of known human CAPRIN1 interaction partners, Nxt3 and Ubp3. These factors are then tested for their influence on the establishment of silencing.

      Using microscopy to observe tagged Cpn1 and known stress granule markers, the authors show that Cpn1 localizes to stress granules. They also quantitatively assess the impact of Cpn1 interactors on stress granule formation. Additionally, the authors note that different RNAi mutants have stress granules even in the absence of envirmental stresses.

      Finally, they investigate the subcellular localization of the cen(dg) transcript using single-molecule RNA FISH. They find that in heterochromatin mutant cells, cen(dg) transcripts localize to the nucleus and exhibit both nuclear and cytoplasmic localization under glucose starvation conditions. The authors also show, through quantification of RNA FISH and RT-qPCR, that cen(dg) transcripts accumulate in Cpn1 mutants.

      Major comments:

      The authors suggest that Cpn1 is requried for efficient degradation of RNA which in-turn helps the establishemnt of heterochromatin potentially by preventing the formation of R-loops. Yet the localization of Cpn1 under non-stressed conditions is cytoplasmic. Additionally the authors show that Cpn1 helps to limit the accumulation of heterochromatic trancripts on chromatin, yet there is no evidence for a nuclear pool of Cpn1 in these condtions.

      In order to strengthen the link between these nuclear processes it is important that the authors follow up on some of the aspects detailed below.

      Is Cpn1 also present in the nucleus in non-stressed conditions? This would be a pre-requesit for a direct mechanisic link for the model that the authors suggest. This could be, for example, adressed by LeptomycinB treatment followed by imaging of Cpn1. Such an experiment could reveal if the protein is shutteling between the nucleus and the cytoplasm.

      In Fig 6 C the authors show co-localization of dh-transcripts with Papb1 under glucose starvation conditions. To strengthen their hypothesis of cen(dg) RNA binding/regulation by Cpn1 show and quantify co-localization of Cpn1 and cen(dg) transcripts.

      The authors observe cytoplasmic cenRNA in Clr4-delta dhp1-2 cells. To substantiate the hypothesis that Cpn1 binds such transcript co-localization of Cpn1-GFP with cen(dg) transcripts should be examined.

      Can the authors rule out that deletion of Cpn1 affects the RNA levels of proteins important for heterochromatin establishment? As Cpn1 could regulate the stability of mRNAs in the cytoplasm it might be worthwhile to consider also an indirect effect of Cpn1 deletion on the process of heterochromatin establishment. The study would benefit from a genomic characterization of Cpn1-delta cells using RNAseq or an extended discussion of this potential caveat.

      Minor comments:

      RNA-FISH images are labeled cen RNA, please provide consistent lables for the transcript throught the manuscript (cen(dg)).

      Please display individual data points for replicate experiments when displaying qPCR results. This would give the reader more opportunities to judge the distribution of the data points. (Fig2 C,D,F,G,H, Fig6 F)

      Fig 2 G: it is not immediately obvious that the two bar plots display different HOOD amplicons. The presentation of the data could be improved.

      Significance

      In the presented manuscript Zhang and colleauges place Cpn1 as a novel factor into the fission yeast RNAi pathway. This study suggests a link between RNAi and stress granule biology which would provide a novel connection of these fields. The manuscript will be of interest to a specialized audience, both in RNAi/heterochromation formation and stress granule biology and additionally would provide a novel function of a CAPRIN ortholog.

      The manuscript is well written and overall the data is presented well. Furthermore the authors provide a solid genetic characterization of Cpn1's effect on heterochromatin establishment. While the manuscript provides several interesting observations their mechanistic link remains unclear and I belive that it would be very important to substaniate their observations with experiments supporting a direct mechanistic link between heterochromatin establishemnt and Cpn1.

      Field of expertise: small RNA mediated heterochromatin formation, RNA biology, chromatin biology

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      In this study, Zhang et al. identified a novel factor named Cpn1 promoting de novo heterochromatin establishment in the fission yeast Schizosaccharomyces pombe. The authors established an elegant genetic approach to identify mutants impaired in the de novo heterochromatin assembly, allowing the quantitative assessment of heterochromatin establishment in a highly reproducible manner. This approach allowed them to revisit potential candidates for heterochromatin establishment from a previous study, leading to the identification of Cpn1. Cells lacking Cpn1 display primarily defects in heterochromatin establishment but not maintenance at constitutive heterochromatin. While the function of Cpn1 was unknown, the authors established a functional link to stress granule formation, demonstrating that Cpn1 is the ortholog of the human RNA-binding protein CAPRIN1, likewise forming a complex with two other factors, Nxt3 and Ubp3. Mutating a putative RNA-binding RRG motif in Cpn1 largely phenocopied the establishment defect seen in the deletion mutant. Moreover, Cpn1 and its complex members co-localize with the stress granule marker poly(A)-binding protein, Pabp. Conversely, deleting Cpn1 or mutating its RRG motif resulted in a reduced number of stress granule formation.

      Providing a further link between heterochromatin and stress granules, the authors showed that heterochromatin-deficient mutants accumulate Papb foci in the absence of stress cells, which was largely dependent on Cpn1. Conversely, the number of stress granules was reduced under stress conditions in these mutants, suggesting that heterochromatic transcripts compete with canonical RNPs that form stress granules. The molecular mechanism by which Cpn1 contributes to heterochromatin establishment remains unclear, though. In contrast to Mkt1, another establishment factor previously studied by the authors, no heterochromatic transcripts were found to be associated with Cpn1 when performing RNA-IP (RIP) experiments. The authors then analyzed pericentromeric transcripts (cen RNA) by smRNA-FISH. Deleting the H3K9 methyltransferase Clr4 resulted in the formation of nuclear foci that co-localized with the centromeric histone variant CENP-A. Glucose starvation increased the number of foci, which were also found in the cytoplasm under this stress condition and partially co-localized with Pabp. Notably, inactivating the exoribonuclease Dph1/Xrn2 also resulted in increased nuclear foci formation and accumulation in the cytosol, which was prevented when Cnp1 was absent. Hence, the authors proposed a model, by which Cpn1 limits accumulation of heterochromatic transcripts on chromatin by facilitating their export and cytoplasmic degradation by Dhp1.

      Major comments

      1. The authors suggest that Cnp1 contributes to heterochromatin establishment by facilitating the removal of excessive heterochromatic transcripts from chromatin. Nevertheless, despite the accumulation of pericentromeric transcripts inside the nucleus in clr4∆, direct evidence for their accumulation on chromatin remains elusive. While the authors cautiously avoid assigning Cnp1 a definite role in heterochromatic transcripts removal, investigating RNA:DNA hybrid accumulation through DNA-RNA immunoprecipitation (DRIP) could strengthen their conclusions. Given the successful application of DRIP by the authors in their Mkt1 study (Taglini et al., 2020) and its prior used by others (PMID: 28404620), this approach appears feasible and judicious when appropriate controls are implemented.
      2. While the data support the hypothesis that Cpn1 binds RNA, the authors could not detect Cpn1 association with heterochromatin transcripts. This could be due to transient interactions and their fast turnover, as the authors suggested. The authors could repeat the RIP experiments in mutants that prevents turnover of transcripts, for instance in dhp1-2 and rrp6∆ mutants.

      Minor comments:

      1. How was the quantification of Pabp and Cpn1 foci performed? Little information is provided ("images were [...] exported to ImageJ analysis"). Given the presence of additional (diffuse) signals even under stress conditions, I'm wondering how foci were distinguished from background? Was there a threshold for signals considered to be 'foci' versus background? The authors should give a more detailed description in the figure legends or Materials & Methods section.
      2. How was the relative sm-FISH intensity in Figure 6D and E determined? Have there been internal controls to ensure that hybridization efficiency was comparable for different strains/samples?

      Significance

      The is an intriguing study that provides several functional links between heterochromatin establishment and stress responses, using a combination of elegant yeast genetics, imaging, biochemical approaches and proteomics. While it was previously shown that heterochromatic transcripts can accumulate on chromatin interfering with heterochromatin assembly (Broenner et al., 2017), this study conceptionally advances our understanding of this process by describing a potential role for Cpn1 in facilitating nuclear export of heterochromatic transcripts. This study further describes the conservation of the human CAPRIN1 complex and its role in cytosolic stress granule assembly in yeast and therefore will be of broad interest for researchers interested in heterochromatin assembly and RNP homeostasis. A limitation of this study is the lack of a distinct molecular mechanism by which Cpn1 promotes heterochromatin establishment. Performing additional experiments could strengthen the authors' arguments and contribute to a better understanding of the underlying mechanism(s).

      I have a longstanding expertise in heterochromatin assembly, transcriptional silencing and yeast genetics using S. pombe and S. cerevisiae as model systems.

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      Reply to the reviewers

      Manuscript number: RC-2024-02546

      Corresponding author: Woo Jae, Kim

      1. General Statements

      The goal of this study is to provide the insights of one specific neuron ‘SIFa’ controls interval timing behavior by its receptor ‘SIFaR’ through neuropeptide relay. Interval timing, or the sense of time in the seconds to hours range, is important in foraging, decision making, and learning in humans via activation of cortico-striatal circuits. Interval timing requires completely distinct brain processes from millisecond or circadian timing. In summary, interval timing allows us to subjectively sense the passage of physical time, allowing us to integrate action sequences, thoughts, and behavior, detect developing trends, and predict future consequences.

      Many researchers have tried to figure out how animals, including humans, can estimate time intervals with such precision. However, most investigations have been conducted in the realm of psychology rather than biology thus far. Because the study of interval timing was limited in its ability to intervene in the human brain, many psychologists concentrated on developing convincing theoretical models to explain the known occurrence of interval timing.

      To overcome the limits of studying interval timing in terms of genetic control, we have reported that the time investment strategy for mating in Drosophila males can be a suitable behavioral platform to genetically dissect the principle of brain circuit mechanism for interval timing. For example, we previously reported that males prolong their mating when they have previously been exposed to rivals (Kim, Jan & Jan, "Contribution of visual and circadian neural circuits to memory for prolonged mating induced by rivals" Nature Neuroscience, 2012) (Kim et al, 2012), and this behavior is regulated by visual stimuli, clock genes, and neuropeptide signaling in a subset of neurons (Kim, Jan & Jan, “A PDF/NPF Neuropeptide Signaling Circuitry of Male Drosophila melanogaster Controls Rival-Induced Prolonged Mating” Neuron, 2013) (Kim et al, 2013). And we also reported that the sensory inputs are required for sexual experienced males to shorten their mating time (Lee, Sun, et al, “Taste and pheromonal inputs govern the regulation of time investment for mating by sexual experience in male Drosophila melanogaster” PLOS genetics, 2023) (Lee et al, 2023).

      Throughout their lives, all animals must make decisions in order to optimize their utility function. Male reproductive success is determined by how many sperms successfully fertilize an egg with a restricted number of investment resources. To optimize male reproductive fitness, a time investment strategy has been devised. As a consequence, we believe that the flexible responses of mating duration to different environmental contexts in Drosophila males might be an excellent model to investigate neural circuits for interval timing.

      The most well-known features of mammalian modulating energy homeostasis between the gut and the brain is one of the most intensively studied neuro-modulatory circuits via the neuronal relay of neuropeptides. In this article, we report that SIFa controls two alternate interval timing behaviors through neuropeptide relay signaling by SIFaR and other important neuropeptides and transmits the internal states of the male brain into decision making. According to our findings, male Drosophila utilize SIFa-SIFaR signaling modulating LMD and SMD behaviors. During our investigation in this regulation, we found a subset of cells that express SIFaR in SOG and AG region are important for the modulation of interval timing behaviors. Furthermore, we discovered a neuropeptide named Corazonin (Crz) which expressed in SIFaR is important for both LMD and SMD behaviors.

      Our discovery of neuropeptide relay of SIFa-SIFaR-Crz-CrzR in male Drosophila in modulating interval timing behaviors will be a huge step forward in our knowledge of interval timing behavior.

      2. Point-by-point description of the revisions

      Reviewer #1

      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 are grateful for the insightful feedback regarding the structure of our data presentation. In response to your valuable suggestion, we have made adjustments in this revised version by downsizing the diagram and ensuring the spacing between the panels.

      Comment 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).

         __Answer:__ We appreciate the reviewer's attention to the details of our experimental design. Indeed, the validation of SIFaR-RNAi efficiency is crucial for interpreting our results accurately. In our initial experiments, we focused on the consistent phenotypic outcomes across the three independent RNAi lines, which collectively suggest the importance of SIFaR in LMD and SMD behaviors. However, we recognize the importance of confirming the effectiveness of our RNAi constructs in reducing SIFaR expression. Initially, we incorporated experiments utilizing *elav-GAL80* to demonstrate that the SIFaR knockdown mediated by the *elavc155* driver is sufficient to eliminate LMD and SMD behaviors. The corresponding results are presented in Figure 1C-D, with a detailed description provided in the manuscript as detailed below.
      

      "The inclusion of elav-GAL80, which suppresses GAL4 activity in a pan-neuronal context, was found to restore both LMD and SMD behaviors when SIFaR was knocked down by a pan-neuronal elavc155 driver (Fig. 1C-D). This observation suggests that the reduction in SIFaR expression mediated by the elavc155 driver is sufficient to significantly impair LMD and SMD behaviors."

         In response to the comments, we have conducted a thorough reevaluation in our revised manuscript. Specifically, we have confirmed the efficiency of the SIFaR-RNAi line HMS00299, which exhibited the most pronounced phenotype when co-expressed with the tub-GAL4 and nSyb-GAL4 drivers, using quantitative real-time PCR (qRT-PCR). It has come to our attention that we omitted mentioning the embryonic lethality induced by the HMS00299 line when combined with either tub-GAL4 or nSyb-GAL4 drivers, which is consistent with the homozygous lethality observed in the *SIFaRB322* mutant. To address this, we have performed qRT-PCR experiments by crossing the HMS00299 line with tub-GAL4; tub-GAL80ts, allowing for the temporary knockdown of SIFaR specifically during the adult stage. We utilized w-/SIFaR-RNAis as a control in these experiments. The outcomes are illustrated in Figure 1E, and we have made the necessary modifications and additions to the manuscript to accurately reflect the efficiency of the SIFaR-RNAi line as detailed below.
      

      "To ensure that RNAi did not have an off-target effect, we tested three independent RNAi strains and found that all three RNAi successfully disrupted LMD/SMD when expressed in neuronal populations. (Fig. S1E-J). We chose to use the HMS00299 line as SIFaR-RNAi for all our experiments because it efficiently disrupts LMD/SMD without UAS-dicer expression. 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. The efficiency of HMS00299 SIFaR-RNAi lines was also validated through quantitative PCR analysis (Fig. 1E). Consequently, we infer that the knockdown of SIFaR using the HMS00299 line nearly completely diminishes the levels of the SIFaR protein."

      We also examined the knockdown efficiency of CrzR in the experiments related to Figure 8 (revised version), following a similar approach (Fig. S7K).

      Comment 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.

      • *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. Consequently, in accordance with the reviewer's recommendation, we conducted genetic validation experiments on novel genetic crosses, including SIFaR-RNAi/+, CrzR-RNAi/+, and GAL4NP5270/+, and incorporated the results in the supplementary figures (Supplementary information 1). We have made the necessary modifications and additions to the manuscript as below.

      "Given those genetic controls, as evidenced by consistent exhibition of normal LMD and SMD behaviors (Supplemental information 1), the observed reduction in SIFaR expression, driven by elavc155, is deemed sufficient to induce significant disruptions in LMD and SMD behaviors."

      However, 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 (Kim et al. 2012; Kim et al. 2013; Lee et al. 2023). 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) (Parks et al. 2004; Yapici et al. 2008). Previous studies have demonstrated that virgin females of this line exhibit increased receptivity to males (Yapici et al. 2008). 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 group reared (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 into 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. 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 (Kim et al. 2012; Kim et al. 2013; Lee et al. 2023; Huang et al. 2024; Zhang et al. 2024). 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."

         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 (Lee *et al*, 2023) 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 (Lee et al, 2023). All mutants and transgenic lines used here have been described previously."

      Comment 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".

      * * 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 (*p* *

      Comment 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 of 24F06-LexA>CD8GFP and SIFa-GAL4>CD8RFP tells us nothing about synapse number, or even whether actual synapses are being formed.*

      • *Answer: We sincerely thank the reviewer for their insightful and constructive feedback regarding the interpretation of our data. We acknowledge the important point raised about the limitations of inferring synapse numbers from the overlap of membrane GFP and RFP signals. We fully concur that more specific techniques, such as the GRASP method, are necessary to accurately quantify synapse numbers, as we have demonstrated in subsequent sections of our manuscript. In the section where we describe the SIFa-SIFaR neuronal architecture labeled with membrane GFP and RFP, we recognize the need for caution in not overstating the implications of these findings as indicative of synapse formation. In light of the reviewer's comments, we have revised our discussion to more accurately reflect the nature of the SIFa-SIFaR neuronal arborizing patterns, as detailed below. This revision aims to provide a more nuanced interpretation of our observations and to align with the current scientific understanding of synaptic quantification.

      "As previously reported, SIFa neurons arborize extensively throughout the CNS, but the neuronal processes of GAL424F06-positive neurons are enriched in the optic lobe (OL), sub-esophageal ganglion (SOG), and abdominal ganglion (AG) (GFP signal in Fig. 2F). Neuronal processes that are positive for SIFa and SIFaR strongly overlap in the prow (PRW), prothoracic and metathoracic neuromere (ProNm and MesoNm), and AG regions (yellow signals in Fig. S3A). We quantified these overlapping neuronal processes between SIFa- and SIFaR-positive neurons and found that approximately 18% of SIFa neurons and 52% of GAL424F06-positive neurons overlap in brain (Fig. S3B, C), whereas approximately 48% of SIFa and 54% of GAL424F06-positive neurons overlap in VNC (Fig. S3D, E). These findings suggest that SIFa neurons and GAL424F06-positive neurons form more neuronal processes in the VNC than in the brain."

      • * 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).*

      • *Answer: We are grateful for the reviewer's critical insights regarding our interpretation of the DenMark and syt.eGFP experiments. We acknowledge the reviewer's point that the overlap of DenMark and syt.eGFP signals does not conclusively indicate synapses and that some of these signals can be expressed outside the expected neuronal compartments, particularly at high levels.

        It is important to note that DenMark and syt.eGFP are markers of synaptic polarity. In the original publication of DenMark, the authors demonstrated that while these two markers are closely apposed, they do not necessarily overlap, as seen in the labeled yellow areas. They concluded that these areas could represent closely apposed regions where "LNv neurons establish presynaptic contacts within the aMe, suggesting that these contacts are on the postsynaptic sites of the LNv neurons themselves. (Nicolaï et al, 2010)" The authors also observed that DenMark-enriched structures appear juxtaposed to, rather than coexpressed with, syt.eGFP, indicating a potential for synapse formation between R neurons within the eb. In contrast, projections to the suboesophageal ganglion, which show strong Syt–GFP expression, are devoid of DenMark, suggesting a different interpretation of the signals (Nicolaï et al, 2010).

        Building on these findings, we have reanalyzed our data with caution (as shown in Figure S3). In the SOG region, where we observed strong yellow signals, these were not limited to cell bodies but also extended to the middle region filled with neural processes. Upon close examination of the DenMark and syt.eGFP signals, we confirmed that these yellow signals are closely juxtaposed, suggesting the possibility of synapse formation between SIFaR24F06 neurons within the SOG. We emphasize that this interpretation is based on the original findings from the DenMark study. To provide clarity for general readers, we have added further explanations regarding the interpretation of these signals, as detailed below. We believe that our revised analysis and the additional explanations will help to clarify the potential implications of our findings, while also acknowledging the limitations and the need for further investigation.

      "DenMark-enriched structures, localized within the SOG, are observed in close apposition to syt.eGFP signals, as indicated by the white-dashed circles (Fig. S3Fa). This spatial relationship suggests that SIFaR-expressing neurons, identified by GAL424F06 labeling, may form synapses with one another within the SOG. The colocalization of yellow signals resulting from the interaction between DenMark and syt.eGFP has been previously interpreted and validated by other researchers, supporting our observation (Nicolaï 2010,Kennedy 2018). In contrast to the yellow signals observed in the SOG, which are indicative of neural processes, the yellow signals detected in the ProNm appear to be associated with cell bodies rather than neural processes, as DenMark signals are often observed to leak out (as shown in Fig. S3Fb) (Nicolaï 2010,Kennedy 2018). Despite the presence of juxtaposed DenMark and syt.GFP signals in the ProNm, the interpretation of the yellow signals as potential synapses between SIFaR neurons remains an open question (indicated by the question mark in Fig. S3K).

        • 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.*

        Answer: We sincerely appreciate the reviewer's critical feedback regarding our initial data interpretation. We acknowledge the important distinction that overlapping membrane markers do not provide a direct measure of synapse formation. In line with the reviewer's suggestion, we have revised the relevant sentence to more accurately reflect this understanding, as detailed below.

      "Neurons expressing Crz were observed in close proximity to SIFaR24F06-expressing neurons within the PRW-SOG of the brain (panels of Brain and SOG in Fig. 6A)."

      • * 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.*

        Answer: We are grateful for the reviewer's insightful comments that highlighted the potential for misleading information in our previous submission. Upon careful reexamination of the virtual fly brain model, we have made the necessary corrections and updated the figures in our revised manuscript (Figure 3B and S4B). This reanalysis has allowed us to further substantiate our findings, confirming that SIFa neurons indeed establish dense synaptic connections with multiple regions of the central brain.

      • * 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).*

      • Answer: We sincerely appreciate the reviewer's valuable suggestion regarding our quantification methods for assessing synaptic changes using GRASP signals. We acknowledge the reviewer's accurate observation that GRASP signals alone cannot provide an exact quantification of synapse number changes. In response to this feedback, we have employed the 'Particle analysis' function of ImageJ to infer the number of synapses from GRASP signals, clearly labeling them as 'number of particles' (as exemplified in Figures S4G and S4J). Additionally, we have compared the average size of each particle to enable a more precise comparison of synapse number changes (as shown in Figures S4H and S4K). While it is true that GRASP signals should not be directly equated with synapse counts, the quantification of GRASP signal intensity can still provide insights into the underlying synaptic connectivity, as described in the original GRASP paper (Feinberg et al, 2008a). Following this approach, previous studies have used signal intensity quantifications to draw conclusions about changes in synaptic specificity in various mutants. Since our methods for measuring GRASP intensity are consistent with the original techniques, we have updated our Y-axis labeling to reflect 'normalized GFP intensity (Norm. GFP Int.)', as exemplified in Figure 4. This change aims to provide a clearer and more accurate representation of our data.

      Comment 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.*

      • Answer: We sincerely appreciate the reviewer's constructive feedback on the section of our manuscript that discusses the role of the SIFa-SIFaR connection in regulating mating duration. We understand that the initial presentation may not have been sufficiently convincing. As we detailed in our previous biorXiv preprint (Wong et al, 2019), we conducted a comprehensive screen of numerous neuropeptides and their receptors that mediate SIFa signals through SIFaR and added those data in Supplementary Table S1 and S2. Among these, Crz was identified as a key neuropeptide in this pathway and is also well-documented for its role in mating duration (Tayler et al, 2012). Our data clearly demonstrate that Crz neurons are responsive to the activity of SIFa neurons, supporting the validity of this connection. Additionally, in another manuscript focusing on the input signals for SIFa (Kim et al*, 2024), we established that CrzR does not function in SIFa neurons, confirming the bidirectional nature of SIFa-to-Crz signaling.

        Inadvertently, we had relegated the Crz knockdown results to supplementary figures, under the assumption that our screening results regarding the relationship between SIFaR and neuropeptides were already well-covered (Wong et al, 2019). In light of the reviewer's comments, we have now relocated the Crz knockdown results, particularly those involving SIFaR-expressing cells, to the main figures (Figure 6F-G). We have also included a more detailed description of our previous screening results within the manuscript, as outlined below, to provide a more comprehensive understanding of our findings.

      "Furthermore, the Crz peptide and Crz-expressing neurons have been characterized as pivotal relay signals in the SIFa-to-SIFaR pathway, which is essential for modulating interval timing behaviors (Wong 2019)."

         We greatly appreciate the reviewer's critical and constructive feedback regarding the detection of SIFa-to-Crz long-distance signaling, particularly their observation that this signaling is detectable from the brain to the VNC but not between brain regions. In response to the reviewer's suggestions, we have made the following adjustments to our manuscript:
      
      1. We have relocated our SIFa-Crz GCaMP data pertaining to the VNC region to the Figures 6L-O) to maintain focus on the primary findings within the main text.
      2. Our deeper analysis has led to the identification of two cells in the Super Intermediate Protocerebrum (SIP) regions that coexpress both Crz and SIFaR24F06, as well as OL cells (Figure 6D-E).
      3. We have included GCaMP data from the brain region in the main figure to provide a comprehensive view of the signaling dynamics (Fig. 6P-R and Fig. S6N-P).
      4. Upon examining the SIFa-to-Crz signaling through GCaMP calcium imaging, we observed that the calcium levels in Crz+/SIFaR+ SIP neurons consistently decreased upon SIFa activation (Figure 6P-R). In contrast, the calcium signals in Crz+/SIFaR+ OL neurons increased upon SIFa activation, similar to the pattern observed in Crz+ AG neurons in the VNC (Figure 6M-O and Figure S6N-P).
      5. We have summarized these findings in Figure 6S and provided a detailed description of the results in the manuscript, as outlined below. "To elucidate the direct response of Crz neurons to the activity of SIFa neurons, we conducted live calcium (Ca2+) imaging in the Super Intermediate Protocererbrum (SIP), OL and AG region of the VNC, where Crz neurons are situated (Fig. 6D, Fig. S6M). Upon optogenetic stimulation of SIFa neurons, we observed a significant increase in the activity of Crz in OL and AG region (Fig. 6L-O, Fig. S6N-P), evidenced by a sustained elevation in intracellular Ca2+ levels that persisted in a high level before gradually declining to baseline levels, where the cells in top region of the SIP exhibit consistently drop down after stimulated the SIFa neurons (Fig. 6P-R). These calcium level changes were in contrast to the control group (without all-trans retinal, ATR) (Fig. 6L-R, Fig. S6N-P). These findings confirm that Crz neurons in OL and AG are activated in response to SIFa neuronal activity, but the activity of Crz neurons in SIP are inhibited by the activition of SIFa neuron, reinforcing their role as postsynaptic effectors in the neural circuitry governed by SIFa neurons. Moreover, these results provide empirical support for the hypothesis that SIFa-SIFaR/Crz-CrzR long-range neuropeptide relay underlies the neuronal activity-based measurement of interval timing."

        We are grateful for the reviewer's opportunity to elaborate on the intriguing findings concerning the expression of CrzR in the heart and its potential link to mating duration. In the context of traditional interval timing models (Meck et al, 2012; Matell, 2014; Buhusi & Meck, 2005), the role of a pacemaker in generating a temporal flow for measuring time is considered essential. The heart, being a well-known pacemaker organ in animals, provides a compelling framework for our discussion. In response to the reviewer's insightful comments, we have expanded upon our hypotheses in the DISCUSSION section, exploring the possible connections between cardiac function and the regulation of mating duration. Our reflections on this topic are detailed as follows:


      "It has been reported that the interaction between the brain and the heart can influence time perception in humans (Khoshnoud et al, 2024). Heart rate is governed by intrinsic mechanisms, such as the muscle pacemaker, as well as extrinsic factors including neural and hormonal inputs (Andersen et al, 2015). 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. Consequently, the CrzR in the fly heart may respond to the Crz signal sent by SIFaR+/Crz+ cells and modulate the heart rate, thereby impacting the perception of time in male flies."

         We appreciate the reviewer's interest in the expression of CrzR in the heart and its potential implications for our study. In response to the reviewer's comments, we have conducted a thorough examination of the fly SCope RNAseq dataset. Our analysis revealed that CrzR is indeed broadly expressed in heart tissue, particularly in areas where the Hand gene is also expressed. This significant finding has been incorporated into our manuscript and is depicted in Figure 8L. As illustrated in Figures 8I-L, which present the SCope tSNE plot for various cell types including neurons, glial cells, muscle systems, and heart, the heart tissue exhibits the most robust expression of CrzR. This observation suggests that the Hand-GAL4 mediated CrzR knockdown experiments may provide insights into the role of CrzR expression in the heart and its influence on the interval timing behavior of male fruit flies. We have expanded upon this interpretation in the relevant sections of our manuscript to ensure a clear and comprehensive understanding of our results.
      
      • *

      Comment 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.

         __Answer:__ We sincerely appreciate the reviewer's insightful suggestions regarding the potential mechanistic underpinnings of how differential calcium activities may modulate LMD and SMD behaviors. In response to this valuable input, we have expanded our discussion to include a hypothesis on how neuropeptide relays could potentially induce context-dependent modulation of synaptic changes and calcium activities within distinct neuronal subsets. This addition aims to provide a more comprehensive understanding of the complex interactions at play, as detailed in the revised manuscript.
      

      "Employing two distinct yet comparable models of interval timing behavior, LMD and SMD, we demonstrated that differential SIFa to SIFaR signaling is capable of modulating context-dependent behavioral responses. Synaptic strengths between SIFa and SIFaR neurons was notably enhanced in group-reared naive males. However, these synaptic strengths specifically diminished in the OL, CB, and AG when males were singly reared, with a particular decrease in the AG region when males were sexually experienced (Fig. 4A-J). Intriguingly, overall calcium signaling within SIFaR24F06 neurons was significantly reduced in group-reared naive males, yet these signals surged dramatically in the OL with social isolation and in the AG with sexual experience (Fig. 4K-T). These calcium signals, as reported by the transcriptional calcium reporter CaLexA, were corroborated by GCaMP live imaging in both the AG and OL regions (Fig. 6L-O and Fig. S6N-P), indicating a close association between elevated calcium levels and LMD and SMD behaviors. The modulation of context-dependent synaptic plasticity and calcium dynamics by the SIFa neuropeptide through a single SIFaR receptor raises the question of how a single receptor can elicit such diverse responses. Recent neuroscientific studies in Drosophila have shown that individual neurons can produce multiple neurotransmitters and that neuropeptides are often colocalized with small molecule neurotransmitters (Nässel 2018,Deng 2019,Croset 2018,Kondo 2020). Consistent with this, we have previously reported that SIFa neurons utilize a variety of neurotransmitters, including glutamate, dopamine, and tyramine (Kim 2024). Therefore, we propose that the SIFa-SIFaR-Crz-CrzR neuropeptidergic relay circuitry may interact with different neurotransmitters in distinct neuronal subpopulations to regulate context-dependent behaviors. Supporting this hypothesis, glutamate, known to function as an inhibitory neurotransmitter in the olfactory pathway of Drosophila (Liu 2013), may be one such candidate. We speculate that neuropeptide cotransmission could underlie the mechanisms facilitating these complex, context-dependent behavioral patterns. Further research is warranted to elucidate how such cotransmission contributes to the intricate behavioral repertoire of the fly."

      Minor Comments: Comment 8. 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.

      • *Answer: We appreciate the reviewer's insightful comments and acknowledge the importance of using intensity measurements in our analysis of CaLexA signals. 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. These have been incorporated as a primary dataset in all our CaLexA results to provide a more accurate representation of our findings. 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, aligning with the reviewer's recommendations and enhancing the overall quality of our manuscript.

      Comment 9. 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?

          __Answer:__ We sincerely thank the reviewer for pointing out the oversight in our initial submission regarding the quantification data. In response to this valuable feedback, we have now included the quantification of neurons co-expressing SIFaR24F06 and Crz in the optic lobe (OL) within Figure 6E. This addition ensures that the figure is complete and provides the necessary numerical support for our observations.
      

      Comment 10. 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?

         __Answer:__ We appreciate the reviewer's attention to the methodology of our study, particularly regarding the use of internal controls in our mating duration assays. As referenced in our cited work by Bretman et al. (2011) (Bretman *et al*, 2011), our internal control strategy involves a comparison of mating durations between males that have been presented with specific sensory cues and those that have not. This approach includes assessing both males that have been exposed to signals and those that have not, which serves as an internal control for each experimental setup. The purpose of this design is to isolate the effects of our manipulations from other potential confounding factors. In response to the reviewer's comments, we have provided a more detailed description of our mating duration assay in the Methods section. We have also expanded our explanation to clarify how this internal control mechanism ensures that any observed differences in mating duration are attributable to the experimental manipulations and not to extraneous variables. This additional information should provide a clearer understanding of our methodology and the rationale behind our experimental design.
      

      Comment 11. 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.

         __Answer: __We appreciate the reviewer’s insight. GRASP and t-GRASP are similar technologies that can clearly show the synaptic connection between neurons. GRASP technology was first generated and performed in *C. elegens* (Feinberg *et al*, 2008b). In 2018, the researchers developed a targeted GFP Reconstitution Across Synaptic Partners method, t-GRASP, which resulted in a strong preferential GRASP signal in synaptic regions.
      
         In our study, we utilized both techniques because of the limitations of the chromosomes where GAL4 and lexA lines located. We also found that during data processing, our method could clearly distinguish the changes in GRASP and t-GRASP signals across three different conditions (naïve, single, and exp.). Therefore, we do not have a particular preference for one technique over the other; both methods are applicable to our experiment.
      
         The genotype we used in Figure 3A is *SIFa2A-lexA, GAL424F06; lexAop-nSyb-spGFP1-10, UAS-CD4-spGFP11*, where the synaptic transmission occurs from *SIFa2A-lexA *to* GAL424F06*. In Figure 4A, the genotype we used is *GAL4SIFa.PT, lexASIFaR-2A; lexAop-2-post-t-GRASP, UAS-pre-t-GRASP*, where the synaptic transmission occurs from SIFa. PT to SIFaR-2A.
      
         In our back-to-back submission paper, “Peptidergic neurons with extensive branching orchestrate the internal states and energy balance of male *Drosophila melanogaster,*” (Kim *et al*, 2024) we identified that *SIFa2A* can label posterior-ventral SIFa neurons (SIFaVP), which can only project to ellipsoid body and fan-shaped body. Combining the GRASP technique, Figure 3A cannot show a strong signal as in Figure 4A. We’ve shown in Figure 1G that *SIFaR-2A *covers almost the whole CNS in *Drosophila*. Thus, the synaptic transmission from SIFa. PT (label 4 SIFa neurons) to SIFaR-2A shows a strong signal under the use of the t-GRASP technique. In this case, the GRASP signals in Figure 3A and Figure 4A are so different because of the usage of different GRASP techniques and different fly lines. We appreciate the reviewer's attention to the clarity of our presentation. In response to the comments, we have taken the opportunity to meticulously revise the figure legends to ensure that the differences are explicitly highlighted and easily understood by the readers.
      

      __ __


      Reviewer #2

      Major concerns: Comment 1.* 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. *

      * * Answer: We are grateful for the opportunity provided by the reviewer to elaborate on our rationale for utilizing the mating duration of male fruit flies as an exemplary genetic model for studying interval timing. At the outset, we would like to acknowledge that mating duration has gained recognition as a valuable genetic model for interval timing, as evidenced by the NIH-NIGMS R01 grant awarded to Michael Crickmore. This grant, which can be reviewed at the provided link (https://grantome.com/grant/NIH/R01-GM134222-01), underscores the significance of this model. Crickmore and colleagues have described in the grant's abstract that "mating duration in Drosophila offers a powerful system for exploring changes in motivation over time as behavioral goals are achieved," and it has the potential to provide "the first mechanistic description of a neuronal interval timing system."

         In light of this, we have incorporated our rationale into the INTRODUCTION section of our manuscript, as detailed below. We believe that our argumentation, supported by the grant's emphasis on the topic, will not only address the reviewer's concerns but also demonstrate to the broader scientific community the significance of the fruit fly's mating duration as a model for interval timing. This concept has been a cornerstone in the historical development of neuroscientific understanding of time perception. We hope that our expanded discussion will effectively convey the potential of the fruit fly mating duration as a genetic model to offer profound insights into the neural mechanisms underlying interval timing, a concept of enduring importance in the field of neuroscience.
      

      "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 (RICHELLE & LEJEUNE, 1980). 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 (Golombek et al, 2014). Interval timing requires entirely different neural mechanisms from millisecond or circadian timing (Meck et al, 2012; Merchant et al, 2012; Buhusi & Meck, 2005). 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 (Buhusi et al, 2009; Tucci et al, 2014). 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 (Thornquist et al, 2020; Gautham et al, 2024; Crickmore & Vosshall, 2013)."

      Comment 2.* 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. *

      * * Answer: We sincerely appreciate the reviewer's thoughtful suggestion to enhance the accessibility of our microscopy images for readers who may be interested. In response to this valuable feedback, we have compiled all of our quantified image files into zip format and included them as Supplementary Information 2 and 3. We believe that this additional material will be beneficial for readers seeking a more in-depth view of our data.

      Comment 3. 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.

         __Answer:__ We sincerely appreciate the reviewer's critical feedback regarding the genetic controls in our study. We acknowledge the importance of this aspect and wish to clarify that we have indeed conducted a substantial number of genetic control experiments for both LMD and SMD behaviors. It is worth noting that much of this data has been previously published in other works. Recognizing the interest from another reviewer on the same topic, we have chosen to reiterate our response here for clarity and convenience. Our comprehensive approach to genetic controls ensures the robustness of our findings, and we believe that the published data further substantiates the reliability of our experimental procedures.
      
         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. However, in accordance with the reviewer's recommendation, we conducted genetic validation experiments on novel genetic crosses, including SIFaR-RNAi/+, CrzR-RNAi/+, and GAL4NP5270/+, and incorporated the results in the supplementary figures (Supplementary information 1). We have made the necessary modifications and additions to the manuscript as below.
      

      "Given those genetic controls, as evidenced by consistent exhibition of normal LMD and SMD behaviors (Supplemental information. 1), the observed reduction in SIFaR expression, driven by elavc155, is deemed sufficient to induce significant disruptions in LMD and SMD behaviors."

      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 (Kim et al. 2012; Kim et al. 2013; Lee et al. 2023). 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) (Parks et al. 2004; Yapici et al. 2008). Previous studies have demonstrated that virgin females of this line exhibit increased receptivity to males (Yapici et al. 2008). 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 group reared (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 into 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. 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 (Kim et al. 2012; Kim et al. 2013; Lee et al. 2023; Huang et al. 2024; Zhang et al. 2024). 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."

      Minor comments: Comment 4.* Line 75: word missing ("...including FEEDING-RELATED BEHAVIOR, courtship, ..."). *

         __Answer:__ We appreciate your vigilance in identifying this error. We have made the necessary correction to ensure the accuracy of our manuscript.*
      

      *

      Comment 5.* Line 120: word missing ("SIFaR expression in adult neurons BUT not glia..."). *

         __Answer:__ We appreciate your careful review and attention to detail. Thank you for bringing this to our notice. We have made the necessary corrections to address the error.*
      

      *

      Comment 6.* I find the figures often to be quite overloaded, and anatomical details often very small (e.g., figure 7A). *

      * * Answer: We appreciate the constructive critique on the layout of our data presentation. Following your insightful recommendation, we have revised the manuscript to enhance clarity. Specifically, we have resized the diagram to be more compact and have also increased the spacing between the panels for better readability.


      __ __


      Reviewer #3

      Major Comments Comment 1.* 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. *

      * * Answer: We are deeply grateful for the insightful and constructive feedback provided by the reviewer on the SIFa-to-SIFaR signaling pathway. We are particularly encouraged by the reviewer's agreement with our findings that support the role of SIFa and SIFaR in regulating mating duration. We concur with the reviewer's suggestion that additional experiments and mechanistic insights are essential to substantiate our conclusions. To this end, we have conducted and included several new experiments, particularly GCaMP data, in the main figures (Figure 6 and S6). Our focus has been intensified on the SIFa-to-Crz signaling, given Crz's established role in controlling mating duration behavior. Below is a summary of the additional experiments we have incorporated:

      1. We have repositioned the SIFa-Crz GCaMP data related to the VNC to Figures 6L-O to ensure that the main text highlights our primary findings.
      2. Our more detailed analysis has identified two cells in the Super Intermediate Protocerebrum (SIP) regions that co-express Crz and SIFaR24F06, along with OL cells (Figure 6D-E).
      3. To provide a complete view of the signaling dynamics, we have included GCaMP data from the brain region in the main figure (Figure 6P-R and Supplementary Figure S6N-P).
      4. Through GCaMP calcium imaging to assess SIFa-to-Crz signaling, we found that calcium levels in Crz+/SIFaR+ SIP neurons consistently decreased with SIFa activation (Figure 6P-R). Conversely, calcium signals in Crz+/SIFaR+ OL neurons increased with SIFa activation, mirroring the pattern seen in Crz+ AG neurons in the VNC (Figure 6M-O and Supplementary Figure S6N-P).
      5. A synthesis of these results is presented in Figure 6S, and we have elaborated on these findings in the manuscript with a detailed description, as detailed below. "To elucidate the direct response of Crz neurons to the activity of SIFa neurons, we conducted live calcium (Ca2+) imaging in the Super Intermediate Protocererbrum (SIP), OL and AG region of the VNC, where Crz neurons are situated (Fig. 6D, Fig. S6M). Upon optogenetic stimulation of SIFa neurons, we observed a significant increase in the activity of Crz in OL and AG region (Fig. 6L-O, Fig. S6N-P), evidenced by a sustained elevation in intracellular Ca2+ levels that persisted in a high level before gradually declining to baseline levels, where the cells in top region of the SIP exhibit consistently drop down after stimulated the SIFa neurons (Fig. 6P-R). These calcium level changes were in contrast to the control group (without all-trans retinal, ATR) (Fig. 6L-R, Fig. S6N-P). These findings confirm that Crz neurons in OL and AG are activated in response to SIFa neuronal activity, but the activity of Crz neurons in SIP are inhibited by the activition of SIFa neuron, reinforcing their role as postsynaptic effectors in the neural circuitry governed by SIFa neurons. Moreover, these results provide empirical support for the hypothesis that SIFa-SIFaR/Crz-CrzR long-range neuropeptide relay underlies the neuronal activity-based measurement of interval timing."

        We are truly grateful for the reviewer's perceptive recommendations concerning the possible mechanisms of LMD and SMD behaviors. In light of this constructive feedback, we have enhanced our discussion to encompass a theoretical framework on the potential role of neuropeptide relays in mediating context-dependent adjustments of synaptic plasticity and calcium signaling within specific neuronal populations. This supplementary perspective is designed to elucidate the intricate dynamics involved, as further elaborated in the updated manuscript.

      "Employing two distinct yet comparable models of interval timing behavior, LMD and SMD, we demonstrated that differential SIFa to SIFaR signaling is capable of modulating context-dependent behavioral responses. Synaptic strengths between SIFa and SIFaR neurons was notably enhanced in group-reared naive males. However, these synaptic strengths specifically diminished in the OL, CB, and AG when males were singly reared, with a particular decrease in the AG region when males were sexually experienced (Fig. 4A-J). Intriguingly, overall calcium signaling within SIFaR24F06 neurons was significantly reduced in group-reared naive males, yet these signals surged dramatically in the OL with social isolation and in the AG with sexual experience (Fig. 4K-T). These calcium signals, as reported by the transcriptional calcium reporter CaLexA, were corroborated by GCaMP live imaging in both the AG and OL regions (Fig. 6L-O and Fig. S6N-P), indicating a close association between elevated calcium levels and LMD and SMD behaviors. The modulation of context-dependent synaptic plasticity and calcium dynamics by the SIFa neuropeptide through a single SIFaR receptor raises the question of how a single receptor can elicit such diverse responses. Recent neuroscientific studies in Drosophila have shown that individual neurons can produce multiple neurotransmitters and that neuropeptides are often colocalized with small molecule neurotransmitters (Nässel 2018,Deng 2019,Croset 2018,Kondo 2020). Consistent with this, we have previously reported that SIFa neurons utilize a variety of neurotransmitters, including glutamate, dopamine, and tyramine (Kim 2024). Therefore, we propose that the SIFa-SIFaR-Crz-CrzR neuropeptidergic relay circuitry may interact with different neurotransmitters in distinct neuronal subpopulations to regulate context-dependent behaviors. Supporting this hypothesis, glutamate, known to function as an inhibitory neurotransmitter in the olfactory pathway of Drosophila (Liu 2013), may be one such candidate. We speculate that neuropeptide cotransmission could underlie the mechanisms facilitating these complex, context-dependent behavioral patterns. Further research is warranted to elucidate how such cotransmission contributes to the intricate behavioral repertoire of the fly."

      • *

      Comment 2. 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.

         __Answer:__ We are grateful for the reviewer's constructive suggestion regarding the need to provide additional behavioral assays using RNAi knockdown to substantiate the SIFa-SIFaR/Crz-CrzR neuropeptide relay. Following the reviewer's advice, we have conducted experiments involving SIFaR24F06/Crz-RNAi and Crz-GAL4/SIFaR-RNAi. The outcomes of these experiments have been detailed and are now presented in a clear and comprehensive manner.
      
         To further aid in the understanding of our results, we have also included a summary diagram in Figure 6S, which illustrates the key findings from these assays. This visual representation is intended to provide a concise overview of the data and to highlight the significance of the SIFa-SIFaR/Crz-CrzR neuropeptide relay in the context of our study.
      

      Comment 3.* 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. *

         __Answer:__ We sincerely appreciate the reviewer's critical feedback regarding the genetic controls in our study. We acknowledge the importance of this aspect and wish to clarify that we have indeed conducted a substantial number of genetic control experiments for both LMD and SMD behaviors. It is worth noting that much of this data has been previously published in other works. Recognizing the interest from another reviewer on the same topic, we have chosen to reiterate our response here for clarity and convenience. Our comprehensive approach to genetic controls ensures the robustness of our findings, and we believe that the published data further substantiates the reliability of our experimental procedures.
      
         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. However, in accordance with the reviewer's recommendation, we conducted genetic validation experiments on novel genetic crosses, including SIFaR-RNAi/+, CrzR-RNAi/+, and GAL4NP5270/+, and incorporated the results in the supplementary figures (Supplementary information 1). We have made the necessary modifications and additions to the manuscript as below.
      

      "Given those genetic controls, as evidenced by consistent exhibition of normal LMD and SMD behaviors (Supplemental information 1), the observed reduction in SIFaR expression, driven by elavc155, is deemed sufficient to induce significant disruptions in LMD and SMD behaviors."

      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 (Kim et al. 2012; Kim et al. 2013; Lee et al. 2023). 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) (Parks et al. 2004; Yapici et al. 2008). Previous studies have demonstrated that virgin females of this line exhibit increased receptivity to males (Yapici et al. 2008). 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 group reared (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 into 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. 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 (Kim et al. 2012; Kim et al. 2013; Lee et al. 2023; Huang et al. 2024; Zhang et al. 2024). 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."

      *○ Using synaptic markers and high-resolution imaging to observe synaptic changes directly. *

         __Answer:__ We sincerely appreciate the reviewer's constructive suggestion to provide high-resolution imaging for a more direct observation of synaptic changes. While we have already included high-resolution imaging data showcasing postsynaptic and presynaptic alterations using Denmark and syt.eGFP (Figure S3), GRASP (Figure 3A-D), and tGRASP (Figure 4A-J), we recognize the value of further elucidation. Consequently, we have conducted additional experiments to examine the presynaptic changes in SIFaR24F06 neurons under varying social contexts, as presented in Figure 5A-G. We are confident that the comprehensive dataset we have now provided, which includes these new findings, will not only address the reviewer's concerns but also effectively convey to the readers the dynamic and critical nature of SIFa-SIFaR synaptic changes in modulating interval timing behaviors.
      

      *○ Electrophysiological recordings from neurons expressing SIFa and SIFaR to analyze their functional connectivity and activity patterns. *

         __Answer:__ We sincerely appreciate the reviewer's constructive suggestions regarding the inclusion of electrophysiological recordings from neurons expressing SIFa and SIFaR to analyze functional connectivity and activity patterns. In response to this valuable feedback, we have conducted *in vivo* calcium imaging using the GCaMP indicator. The results have been incorporated into our manuscript, demonstrating SIFa-SIFaR connectivity and alterations in activity patterns (Figure 5H-L), as well as SIFa-Crz connectivity and changes in activity patterns (Figure 6 and Figure S6). We are confident that these additional data provide compelling evidence supporting the notion that the SIFa-SIFaR/Crz-CrzR neuropeptide relay circuits are robustly interconnected and exhibit activity changes in concert with the observed neuronal modifications.
      
      • *

      Comment 4.* 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. *

      * * Answer: We are grateful for the reviewers' understanding and support for our additional analysis in the revision experiments. While we have already conducted a multitude of experiments pertinent to this manuscript, we are well-positioned to provide a comprehensive revision of the data within a relatively short timeframe.

      Comment 5. 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.

      * * Answer: We sincerely appreciate the reviewer's meticulous comments regarding the omission of certain methodological details in our manuscript. In response, we have now included a detailed description of the temperature control procedures for conditional RNAi induction in the "Fly Stocks and Husbandry" section, as detailed below.

      "For temperature-controlled experiments, including those utilizing the temperature-sensitive tub-GAL80ts driver, the flies were initially crossed and maintained at a constant temperature of 22℃ within an incubator. The temperature shift was initiated post-eclosion. Once the flies had emerged, they were transferred to an incubator set at an elevated temperature of 29℃ for a defined period, after which the experimental protocols were carried out. Wild-type flies were Canton-S (CS)."

         We appreciate the reviewer's guidance on refining our manuscript. In response to the suggestion, we have streamlined the image analysis methods section, removing excessive details to present the information in a more concise and clear manner 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 (Feinberg 2008). The total fluorescent area or region of interest (ROI) was then quantified using ImageJ, as previously reported. For CaLexA signal quantification, we adhered to protocols detailed by Kayser et al. (Kayser et al, 2014), 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 are indicative of alterations in the CaLexA 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. (Kayser et al, 2014). 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 quantification (Feinberg 2008)."

      Comment 6. 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.

         __Answer:__ We appreciate the reviewer's suggestion to refine our figures, and we have indeed reformatted them to provide clearer presentation and improved readability. Regarding the removal of dot blot membranes (DBMs), we have given this considerable thought. While we understand the recommendation, we have chosen to retain the DBMs in our manuscript. 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 (Claridge-Chang & Assam, 2016). The inclusion of DBMs is essential for the accurate interpretation of these estimation statistics, ensuring a comprehensive representation of our findings.
      

      Minor Comments Comment 7. Specific experimental issues that are easily addressable. Clarify the timing of RNAi induction and provide more detailed figure legends for better understanding and reproducibility.

         __Answer:__ We sincerely appreciate the reviewer's suggestion aimed at enhancing our manuscript. As previously addressed in our response to __*Comment 5*__, we have incorporated additional details regarding the timing of RNAi induction within the Methods section. Furthermore, we have expanded upon the figure legends to provide a clearer understanding of our findings, ensuring that the content is accessible to a broader readership.
      

      * Comment 8. Are prior studies referenced appropriately? Yes. *

      __ Answer:__ We are grateful for the reviewer's acknowledgment that our references have been appropriately included and integrated into the manuscript.

      * Comment 9. Are the text and figures clear and accurate? The text is generally clear, but the figures need re-work. See comment above. *

      • *Answer: We appreciate the feedback from the reviewers regarding the clarity of our figures. In response to other reviewers' concerns about the figures appearing too crowded, we have carefully revised the layout of all figures to ensure they are more spacious and aesthetically improved for better readability and visual appeal.

      * Comment 10. 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. *

      * * Answer: We sincerely appreciate the reviewer's constructive suggestion. In response, we have revised the figures by enlarging the images and adjusting the font sizes in the bar plots to enhance readability and clarity.

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      Bretman A, Westmancoat JD, Gage MJG & Chapman T (2011) Males Use Multiple, Redundant Cues to Detect Mating Rivals. Curr Biol 21: 617–622

      Buhusi CV, Aziz D, Winslow D, Carter RE, Swearingen JE & Buhusi MC (2009) Interval Timing Accuracy and Scalar Timing in C57BL/6 Mice. Behav Neurosci 123: 1102–1113

      Buhusi CV & Meck WH (2005) What makes us tick? Functional and neural mechanisms of interval timing. Nat Rev Neurosci 6: 755–765

      Claridge-Chang A & Assam PN (2016) Estimation statistics should replace significance testing. Nat Methods 13: 108–109

      Crickmore MA & Vosshall LB (2013) Opposing Dopaminergic and GABAergic Neurons Control the Duration and Persistence of Copulation in Drosophila. Cell 155: 881–893

      Feinberg EH, VanHoven MK, Bendesky A, Wang G, Fetter RD, Shen K & Bargmann CI (2008a) GFP Reconstitution Across Synaptic Partners (GRASP) Defines Cell Contacts and Synapses in Living Nervous Systems. Neuron 57: 353–363

      Feinberg EH, VanHoven MK, Bendesky A, Wang G, Fetter RD, Shen K & Bargmann CI (2008b) GFP Reconstitution Across Synaptic Partners (GRASP) Defines Cell Contacts and Synapses in Living Nervous Systems. Neuron 57: 353–363

      Gautham AK, Miner LE, Franco MN, Thornquist SC & Crickmore MA (2024) Molecular control of temporal integration matches decision-making to motivational state. bioRxiv: 2024.03.01.582988

      Golombek DA, Bussi IL & Agostino PV (2014) Minutes, days and years: molecular interactions among different scales of biological timing. Philosophical Transactions Royal Soc B Biological Sci 369: 20120465

      Khoshnoud S, Leitritz D, Bozdağ MÇ, Igarzábal FA, Noreika V & Wittmann M (2024) When the heart meets the mind: Exploring the brain-heart interaction during time perception. J Neurosci: e2039232024

      Kim WJ, Jan LY & Jan YN (2012) Contribution of visual and circadian neural circuits to memory for prolonged mating induced by rivals. Nat Neurosci 15: 876–883

      Kim WJ, Jan LY & Jan YN (2013) A PDF/NPF Neuropeptide Signaling Circuitry of Male Drosophila melanogaster Controls Rival-Induced Prolonged Mating. Neuron 80: 1190–1205

      Kim WJ, Song Y, Zhang T, Zhang X, Ryu TH, Wong KC, Wu Z, Wei Y, Schweizer J, Nguyen K-NH, et al (2024) Peptidergic neurons with extensive branching orchestrate the internal states and energy balance of male Drosophila melanogaster. bioRxiv: 2024.06.04.597277

      Lee SG, Sun D, Miao H, Wu Z, Kang C, Saad B, Nguyen K-NH, Guerra-Phalen A, Bui D, Abbas A-H, et al (2023) Taste and pheromonal inputs govern the regulation of time investment for mating by sexual experience in male Drosophila melanogaster. PLOS Genet 19: e1010753

      Matell MS (2014) Neurobiology of Interval Timing. Adv Exp Med Biol: 209–234

      Meck WH, Doyère V & Gruart A (2012) Interval Timing and Time-Based Decision Making. Frontiers Integr Neurosci 6: 13

      Merchant H, Harrington DL & Meck WH (2012) Neural Basis of the Perception and Estimation of Time. Annu Rev Neurosci 36: 313–336

      Nicolaï LJJ, Ramaekers A, Raemaekers T, Drozdzecki A, Mauss AS, Yan J, Landgraf M, Annaert W & Hassan BA (2010) Genetically encoded dendritic marker sheds light on neuronal connectivity in Drosophila. Proc National Acad Sci 107: 20553–20558

      RICHELLE M & LEJEUNE H (1980) Time in Animal Behaviour. Part III: Mech: 188–199

      Tayler TD, Pacheco DA, Hergarden AC, Murthy M & Anderson DJ (2012) A neuropeptide circuit that coordinates sperm transfer and copulation duration in Drosophila. Proc National Acad Sci 109: 20697–20702

      Thornquist SC, Langer K, Zhang SX, Rogulja D & Crickmore MA (2020) CaMKII Measures the Passage of Time to Coordinate Behavior and Motivational State. Neuron 105: 334-345.e9

      Tucci V, Buhusi CV, Gallistel R & Meck WH (2014) Towards an integrated understanding of the biology of timing. Philosophical Transactions Royal Soc B Biological Sci 369: 20120470

      Wong K, Schweizer J, Nguyen K-NH, Atieh S & Kim WJ (2019) Neuropeptide relay between SIFa signaling controls the experience-dependent mating duration of male Drosophila. Biorxiv: 819045

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

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      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.

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      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.

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      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.

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      Reply to the reviewers

      1. Point-by-point description of the revisions

      This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

      Reviewer #1 (Evidence, reproducibility, and clarity (Required)): This is an interesting manuscript from the Jagannathan laboratory, which addresses the interaction proteome of two satellite DNA-binding proteins, D1 and Prod. To prevent a bias by different antibody affinities they use GFP-fusion proteins of D1 and Prod as baits and purified them using anti GFP nanobodies. They performed the purifications in three different tissues: embryo, ovary and GSC enriched testes. Across all experiments, they identified 500 proteins with surprisingly little overlap among tissues and between the two different baits. Based on the observed interaction of prod and D1 with members of the canonical piRNA pathway the authors hypothesized that both proteins might influence the expression of transposable elements. However, neither by specific RNAi alleles or mutants that lead to a down regulation of D1 and Prod in the gonadal soma nor in the germline did they find an effect on the repression of transposable elements. They also did not detect an effect of a removal of piRNA pathway proteins on satellite DNA clustering, which is mediated by Prod and D1. However, they do observe a mis-localisation of the piRNA biogenesis complex to an expanded satellite DNA in absence of D1, which presumably is the cause of a mis-regulation of transposable elements in the F2 generation.This is an interesting finding linking satellite DNA and transposable element regulation in the germline. However, I find the title profoundly misleading as the link between satellite DNA organization and transgenerational transposon repression in Drosophila has not been identified by multi-tissue proteomics but by a finding of the Brennecke lab that the piRNA biogenesis complex has a tendency to localise to satellite DNA when the localisation to the piRNA locus is impaired. Nevertheless, the investigation of the D1 and Prod interactome is interesting and might reveal insights into the pathways that drive the formation of centromeres in a tissue specific manner.

      We thank the reviewer for the overall positive comments on our manuscript. As noted above, we have performed a substantial number of revision experiments and improved our text. We believe that our revised manuscript demonstrates a clear link between our proteomics data and the transposon repression. We would like to make three main points,

      1. Our proteomics data identified that D1 and Prod co-purified transposon repression proteins in embryos. To test the functional significance of this association, we have used Drosophila genetics to generate flies lacking embryonic D1. In adult ovaries from these flies, we observe a striking elevation in transposon expression and Chk2-dependent gonadal atrophy. Along with the results from the control genotypes (F1 D1 mutant, F2 D1 het), our data clearly indicate that embryogenesis (and potentially early larval development) are a period when D1 establishes heritable TE silencing that can persist throughout development.
      2. Based on the newly acquired RNA-seq and small RNA seq data, we have edited our title to more accurately reflect our data. Specifically, we have substituted the word 'transgenerational' with 'heritable', meaning that the presence of D1 during early development alone is sufficient to heritably repress TEs at later stages of development.
      3. In addition, our RNA seq and small RNA seq experiments demonstrate that D1 makes a negligible contribution to piRNA biogenesis and TE repression in adults, despite the significant mislocalization of the RDC complex. In this regard, our results are substantially different from the recent Kipferl study from the Brennecke lab (Baumgartner et al. 2022).

        Major comments Unfortunately, the proteomic data sets are not very convincing. Not even the corresponding baits are detected in all assays. I wonder whether the extraction procedure really allows the authors to analyze all functionally relevant interactions of Prod and D1. It would be good to see a western blot or an MS analysis of the soluble nuclear extract they use for purification compared to the insoluble chromatin. It may well be that a large portion of Prod or D1 is lost in this early step. I also find the description of the proteomic results hard to follow as the authors mostly list which proteins the find as interactors of Prod and D1 without stating in which tissue or with what bait they could purify them (i.e. p7: Importantly, our hits included known chromocenter-associated or pericentromeric heterochromatin-associated proteins, such as Su(var)3-9[52], ADD1[23,24], HP5[23,24],mei-S332[53], Mes-4[23], Hmr[24,39,54], Lhr[24,39], and members of the chromosome passenger complex, such as borr and Incenp[55]). It would be interesting to at least discuss tissue specific interactions.

      Out of six total AP-MS experiments in this manuscript (D1 x 3, Prod x 2 and Piwi), we observe a strong enrichment of the bait in 5/6 attempts (log2FC between 4-12). In the initial submission, the lack of a third high-quality biological replicate for the D1 testis sample meant that only the p-value (0.07) was not meeting the cutoff. To address this, we have repeated this experiment with an additional biological replicate (Fig. S2A), and our data now clearly show that D1 is significantly enriched in the testis sample.

      As suggested by the reviewer, we have also assessed our lysis conditions (450mM NaCl and benzonase) and the solubilization of our baits post-lysis. In Fig. S1D, we have blotted equivalent fractions of the soluble supernatant and insoluble pellet from GFP-Piwi embryos and show that both GFP-Piwi and D1 are largely solubilized following lysis. In Fig. S1E, we also show that our IP protocol works efficiently.

      GFP-Prod pulldown in embryos is the only instance in which we do not detect the bait by mass spectrometry. Here, one reason could be relatively low expression of GFP-Prod in comparison to GFP-D1 (Fig. S1E), which may lead to technical difficulties in detecting peptides corresponding to Prod. However, we note that Prod IP co-purified proteins such as Bocks that were previously suggested as Prod interactors from high-throughput studies (Giot et al. 2003; Guruharsha et al. 2011). In addition, Prod IP from embryos also co-purified proteins known to associate with chromocenters such as Hcs and Saf-B. Finally, the concordance between D1 and Prod co-purified proteins from embryo lysates (Fig. 2A, C) suggest that the Prod IP from embryos is of reasonable quality.

      We also acknowledge the reviewer's comment that the description of the proteomic data was hard to follow. Therefore, we have revised our text to clearly indicate which bait pulled down which protein in which tissue (lines 148-156). We have also highlighted and discussed bait-specific and tissue-specific interactions in the text (lines 162-173).

      Minor comments The authors may also want to provide a bit more information on the quantitation of the proteomic data such as how many values were derive from the match-between runs function and how many were imputed as this can severely distort the quantification.

      Figure 1: Distribution of data after imputation in embryo (left), ovary (middle) and testis (right) datasets. Imputation is performed with random sampling from the 1% least intense values generated by a normal distribution.

      To ensure the robustness of our data analysis, we considered only those proteins that were consistently identified in all replicates for at least one bait (GFP-D1, GFP-Prod or NLS-GFP). This approach resulted in a relative low number of missing values. However, it is also important to bear in mind that in an AP-MS experiment, the number of missing values is higher, as interactors are not identified in the control pulldown. Importantly, the imputation of missing values during the data analysis did not alter the normal distribution of the dataset (Fig. 1, this document). Detailed information regarding the imputed values is also provided (Table 1, this document). The coding script used for the data analysis is available in the PRIDE submission of the dataset (Table 2, this document). This information has been added to our methods section under data availability.

      Table 1: ____Number of match-between-runs and imputations for embryo, ovary and testis datasets

      Dataset

      #match-between-runs

      %match-between-runs

      %imputation

      Embryo

      5541/27543

      20.11%

      8.36%

      Ovary

      1936/9530

      20.30%

      8.18%

      Testis

      1748/7168

      24.39%

      3.12%

      Table 2: ____Access to the PRIDE submission of the datasets

      Name

      ID PRIDE

      UN reviewer

      PW reviewer

      IP-MS of D1 from Testis tissue

      PXD044026

      reviewer_pxd044026@ebi.ac.uk

      ydswDQVW

      IP-MS of Piwi from Embryo tissue

      PXD043237

      reviewer_pxd043237@ebi.ac.uk

      TMCoDsdx

      IP-MS of Prod and D1 proteins from Ovary tissue

      PXD043236

      reviewer_pxd043236@ebi.ac.uk

      VOHqPmaS

      IP-MS of Prod and D1 proteins from Embryo tissue

      PXD043234

      reviewer_pxd043234@ebi.ac.uk

      L77VXdvA

      **Referee Cross-Commenting** I agree with the two other reviewers that the connection between the interactome and the transgenerational phenotype is unclear. This is also what I meant i my comment that the title is somewhat misleading. A systematic analysis of the D1 and Prod knock down effect on mRNAs and small Rnas would indeed be helpful to better understand the interesting effect.

      As suggested by the reviewer, we have performed RNA seq and small RNA seq in control and D1 mutant ovaries (Fig. 4) to fully understand the contribution of D1 in piRNA biogenesis and TE repression. Briefly, the mislocalization of RDC complex in D1 mutant ovaries does not significantly affect TE-mapping piRNA biogenesis (Fig. 4C, E). In addition, loss of D1 does not substantially alter TE expression in the ovaries (Fig. 4B) or alter the expression of genes involved in TE repression (Fig. 4F). Along with the results presented in Fig. 5 and Fig. 6, our data clearly indicate that embryogenesis (and potentially early larval development) is a critical period during which D1 makes an important contribution to TE repression.

      Reviewer #1 (Significance (Required)): Nevertheless, the investigation of the D1 and Prod interactome is interesting and might reveal insights into the pathways that drive the formation of centromeres in a tissue specific manner. It may be mostly interesting for the Drosophila community but could also be exiting for a broader audience interested in the connection of heterochromatin and its indirect effect on the regulation of transposable elements.

      We thank the reviewer again for the helpful and constructive comments, which have enabled us to significantly improve our study. We are excited by the results from our study, which illuminate unappreciated aspects of transcriptional silencing in constitutive heterochromatin.

      Reviewer #2 (Evidence, reproducibility and clarity (Required)): Chavan et al. set out to enrich our compendium of pericentric heterochromatin-associated proteins - and to learn some new biology along the way. An ambitious AP-Mass baited with two DNA satellite-binding proteins (D1 and Prod), conducted across embryos, ovaries, and testes, yielded hundreds of candidate proteins putatively engaged at chromocenters. These proteins are enriched for a restricted number of biological pathways, including DNA repair and transposon regulation. To investigate the latter in greater depth, the authors examine D1 and prod mutants for transposon activity changes using reporter constructs for multiple elements. These reporter constructs revealed no transposon activation in the adult ovary, where many proteins identified in the mass spec experiments restrict transposons. However, the authors suggest that the D1 mutant ovaries do show disrupted localization of a key member of a transposon restriction pathway (Cuff), and infer that this mislocalization triggers a striking, transposon derepression phenotype in the F2 ovaries.

      The dataset produced by the AP-Mass Spec offers chromosome biologists an unprecedented resource. The PCH is long-ignored chromosomal region that has historically received minimal attention; consequently, the pathways that regulate heterochromatin are understudied. Moreover, attempting to connect genome organization to transposon regulation is a new and fascinating area. I can easily envision this manuscript triggering a flurry of discovery; however, there is quite a lot of work to do before the data can fully support the claims.

      We appreciate the reviewer taking the time to provide thoughtful comments and constructive suggestions to improve the manuscript. We believe that we have addressed all the comments raised to the significant advantage of our paper.

      Major comments 1. The introduction requires quite a radical restructure to better highlight the A) importance of the work and B) limit information whose relevance is not clear early in the manuscript. A. Delineating who makes up heterochromatin is a long-standing problem in chromosome biology. This paper has huge potential to contribute to this field; however, it is not the first. Others are working on this problem in other systems, for example PMID:29272703. Moreover, we have some understanding of the distinct pathways that may impact heterochromatin in different tissues (e.g., piRNA biology in ovaries vs the soma). Also, the mutant phenotypes of prod and D1 are different. Fleshing out these three distinct points could help the reader understand what we know and what we don't know about heterochromatin composition and its special biology. Understanding where we are as a field will offer clear predictions about who the interactors might be that we expect to find. For example, given the dramatically different D1 and prod mutant phenotypes (and allele swap phenotypes), how might the interactors with these proteins differ? What do we know about heterochromatin formation differences in different tissues? And how might these differences impact heterochromatin composition?

      The reviewer brings up a fair point and we have significantly reworked our introduction. We share the reviewer's opinion that improved knowledge of the constitutive heterochromatin proteome will reveal novel biology.

      1. The attempt to offer background on the piRNA pathway and hybrid dysgenesis in the Introduction does not work. As a naïve reader, it was not clear why I was reading about these pathways - it is only explicable once the reader gets to the final third of the Results. Moreover, the reader will not retain this information until the TE results are presented many pages later. I strongly urge the authors to shunt the two TE restriction paragraphs to later in the manuscript. They are currently a major impediment to understanding the power of the experiment - which is to identify new proteins, pathways, and ultimately, biology that are currently obscure because we have so little handle on who makes up heterochromatin.

      We agree with this suggestion. We have introduced the piRNA pathway in the results section (lines 205 - 216), right before this information is needed. We've also removed the details on hybrid dysgenesis, since our new data argues against a maternal effect from the D1 mutant.

      The implications of the failure to rescue female fertility by the tagged versions of both D1 and Prod are not discussed. Consequently, the reader is left uneasy about how to interpret the data.

      We understand this point raised by the reviewer. However, in our proteomics experiments, we have used GFP-D1 and GFP-Prod ovaries from ~1 day old females (line 579, methods). These ovaries are morphologically similar to the wild type (Fig. S1C) and their early germ cell development appears to be intact. Moreover, chromocenter formation in female GSCs is comparable to the wildtype (Fig. 1C-D). These data, along with the rescue of the viability of the Prod mutant (Fig. S1A-B), suggest that the presence of a GFP tag is not compromising D1 or Prod function in the early stages of germline development and is consistent with published and unpublished data from our lab. In addition, D1 and Prod from ovaries co-purify proteins such as Rfc38 (D1), Smn (D1), CG15107 (Prod), which have been identified in previous high-throughput screens (Guruharsha et al. 2011; Tang et al. 2023). For these reasons, we believe that GFP-D1 and GFP-Prod ovaries are a good starting point for the AP-MS experiment. We speculate that the failure to completely rescue female fertility may be due to improper expression levels of GFP-D1 or GFP-Prod flies at later stages of oogenesis, which are not present in ovaries from newly eclosed females and therefore unlikely to affect our proteomic data.

      1. How were the significance cut-offs determined? Is the p-value reported the adjusted p-value? As a non-expert in AP-MS, I was surprised to find that the p-value, at least according to the Methods, was not adjusted based on the number of tests. This is particularly relevant given the large/unwieldy(?) number of proteins that were identified as signficant in this study. Moreover, the D1 hit in Piwi pull down is actually not significant according to their criteria of p We used a standard cutoff of log2FC>1 and p2FC and low p-value) since these are more likely to be bona fide interactors. Third, we have used string-DB for functional analyses where we can place our hits in existing protein-protein interaction networks. Using this approach, we detect that Prod (but not D1) pulls down multiple members of the RPA complex in the embryo (RPA2 and RpA-70, Fig. S2B) while embryonic D1 (but not Prod) pulls down multiple components of the origin recognition complex (Orc1, lat, Orc5, Orc6, Fig. S2C) and the condensin I complex (Cap-G, Cap-D2, barr, Fig. S2D). Altogether, these filtering strategies allow us to eliminate as many false positives as possible while making sure to minimize the loss of true hits through multiple testing correction.

      How do we know if the lack of overlap across tissues is indeed germline- or soma-specialization rather than noise?

      To address this part of the comment, we have amended our text (lines 162-173) as follows,

      'We also observed a substantial overlap between D1- and Prod-associated proteins (yellow points in Fig. 2A, B, Table S1-3), with 61 hits pulled down by both baits (blue arrowheads, Fig. 2C) in embryos and ovaries. This observation is consistent with the fact that both D1 and Prod occupy sub-domains within the larger constitutive heterochromatin domain in nuclei. Surprisingly, only 12 proteins were co-purified by the same bait (D1 or Prod) across different tissues (magenta arrowheads, Fig. 2C, Table S1-3). In addition, only a few proteins such as an uncharacterized DnaJ-like chaperone, CG5504, were associated with both D1 and Prod in embryos and ovaries (Fig. 2D). One interpretation of these results is that the protein composition of chromocenters may be tailored to cell- and tissue-specific functions in Drosophila. However, we also note that the large number of unidentified peptides in AP-MS experiments means that more targeted experiments are required to validate whether certain proteins are indeed tissue-specific interactors of D1 and Prod.'

      To make this inference, conducting some validation would be required. More generally, I was surprised to see no single interactor validated by reciprocal IP-Westerns to validate the Mass-Spec results, though I am admittedly only adjacent to this technique. Note that colocalization, to my mind, does not validate the AP-MS data - in fact, we would a priori predict that piRNA pathway members would co-localize with PCH given the enrichment of piRNA clusters there.

      Here, we would point out that we have conducted multiple validation experiments with a specific focus on the functional significance of the associations between D1/Prod and TE repression proteins in embryos. While the reviewer suggests that piRNA pathway proteins may be expected to enrich at the pericentromeric heterochromatin, this is not always the case. For example, Piwi and Mael are present across the nucleus (pulled down by D1/Prod in embryos) while Cutoff, which is present adjacent to chromocenters in nurse cells, was not observed to interact with either D1 or Prod in the ovary samples.

      Therefore, for Piwi, we performed a reciprocal AP-MS experiment in embryos due to the higher sensitivity of this method (GFP-Piwi AP-MS, Fig. 3B). Excitingly, this experiment revealed that four largely uncharacterized proteins (CG14715, CG10208, Ugt35D1 and Fit) were highly enriched in the D1, Prod and Piwi pulldowns and these proteins will be an interesting cohort for future studies on transposon repression in Drosophila (Fig. 3C).

      Furthermore, we believe that determining the localization of proteins co-purified by D1/Prod is an important and orthogonal validation approach. For Sov, which is implicated in piRNA-dependent heterochromatin formation, we observe foci that are in close proximity to D1- and Prod-containing chromocenters (Fig. 3A).

      As for suggestion to validate by IP-WBs, we would point out that chromocenters exhibit properties associated with phase separated biomolecular condensates. Based on the literature, these condensates tend to associate with other proteins/condensates through low affinity or transient interactions that are rarely preserved in IP-WBs, even if there are strong functional relationships. One example is the association between D1 and Prod, which do not pull each other down in an IP-WB (Jagannathan et al. 2019), even though D1 and Prod foci dynamically associate in the nucleus and mutually regulate each other's ability to cluster satellite DNA repeats (Jagannathan et al. 2019). Similarly, IP-WB using GFP-Piwi embryos did not reveal an interaction with D1 (Fig. S4B). However, our extensive functional validations (Figures 4-6) have revealed a critical role for D1 in heritable TE repression.

      The AlphaFold2 data are very interesting but seem to lack of negative control. Is it possible to incorporate a dataset of proteins that are not predicted to interact physically to elevate the impact of the ones that you have focused on? Moreover, the structural modeling might suggest a competitive interaction between D1 and piRNAs for Piwi. Is this true? And even if not, how does the structural model contribute to your understanding for how D1 engages with the piRNA pathway? The Cuff mislocalization?

      In the revised manuscript, we have generated more structural models using AlphaFold Multimer (AFM) for proteins (log2FC>2, p0.5 and ipTM>0.8), now elaborated in lines 175-177. Despite the extensive disorder in D1 and Prod, we identified 22 proteins, including Piwi, that yield interfaces with ipTM scores >0.5 (Table S4, Table S8). These hits are promising candidates to further understand D1 and Prod function in the future.

      For the predicted model between Prod/D1 and Piwi (Fig. S4A), one conclusion could indeed be competition between D1/Prod and piRNAs for Piwi. Another possibility is that a transient interaction mediated by disordered regions on D1/Prod could recruit Piwi to satellite DNA-embedded TE loci in the pericentromeric heterochromatin. These types of interactions may be especially important in the early embryonic cycles, where repressive histone modifications such as H3K9me2/3 must be deposited at the correct loci for the first time. We suggest that mutating the disordered regions on D1 and Prod to potentially abrogate the interaction with Piwi will be important for future studies.

      The absence of a TE signal in D1 and Prod mutant ovaries would be much more compelling if investigated more agnostically. The observation that not all TE reporter constructs show a striking signal in the F2 embryos makes me wonder if Burdock and gypsy are not regulated by these two proteins but possibly other TEs are. Alternatively, small RNA-seq would more directly address the question of whether D1 and Prod regulate TEs through the piRNA pathway.

      We completely agree with this comment from the reviewer. We have performed RNA seq on D1 heterozygous (control) and D1 mutant ovaries in a chk26006 background. Since Chk2 arrests germ cell development in response to TE de-repression and DNA damage(Ghabrial and Schüpbach 1999; Moon et al. 2018), we reasoned that the chk2 mutant background would prevent developmental arrest of potential TE-expressing germ cells and we observed that both genotypes exhibited similar gonad morphology (Fig. 4A). From our analysis, we do not observe a significant effect on TE expression in the absence of D1, except for the LTR retrotransposon tirant (Fig. 4B). We also do not observe differential expression of TE repression genes (Fig. 4F).

      We have complemented our RNA seq experiment with small RNA profiling from D1 heterozygous (control) and D1 mutant ovaries. Here, overall piRNA production and antisense piRNAs mapping to TEs were largely unperturbed (Fig. 4C-E).

      Overall, our data is consistent with the TE reporter data (Fig. S7) and suggests that zygotic depletion of D1 does not have a prominent role in TE repression. However, we have uncovered that the presence of D1 during embryogenesis is critical for TE repression in adult gonads (Fig. 6, Fig. S9).

      I had trouble understanding the significance of the Cuff mis-localization when D1 is depleted. Given Cuff's role in the piRNA pathway and close association with chromatin, what would the null hypothesis be for Cuff localization when a chromocenter is disrupted? What is the null expectation of % Cuff at chromocenter given that the chromocenter itself expands massively in size (Figure 4D). The relationship between these two factors seems rather indirect and indeed, the absence of Cuff in the AP would suggest this. The biggest surprise is the absence of TE phenotype in the ovary, given the Cuff mutant phenotype - but we can't rule out given the absence of a genome-wide analysis. I think that these data leave the reader unconvinced that the F2 phenotype is causally linked to Cuff mislocalization.

      We apologize that this data was not more clearly represented. In a wild-type context, Cuff is distributed in a punctate manner across the nurse cell nuclei, with the puncta likely representing piRNA clusters (Fig. 5A-B). We find that a small fraction of Cuff (~5%) is present adjacent to the nurse cell chromocenter (inset, Fig. 5A and Fig. 5D). In the absence of D1, the nurse cell chromocenters increase ~3-4 fold in size. However, the null expectation is still that ~5% of total Cuff would be adjacent to the chromocenter, since the piRNA clusters are not expected to expand in size. In reality, we observe ~27% of total Cuff is mislocalized to chromocenters. Our data indicate that the satellite DNA repeats at the larger chromocenters must be more accessible to Cuff in the D1 mutant nurse cells. This observation is corroborated by the significant increase in piRNAs corresponding to the 1.688 satellite DNA repeat family (Fig. 4E).

      The lack of TE expression in the F1 D1 mutant was indeed surprising based on the Cuff mislocalization but as the reviewers pointed out, we only analyzed two TE reporter constructs in the initial submission. In the revised manuscript, we have performed both RNA seq and small RNA seq. Surprisingly, our data reveal that the Cuff mislocalization does not significantly affect piRNA biogenesis (Fig. 4C, D) and piRNAs mapping to TEs. As a result, both TE repression (Fig. 4B) and fertility (Fig. 6D) are largely preserved in the absence of D1 in adult ovaries.

      Finally, we thank the reviewer for their excellent suggestion to incorporate the F2 D1 heterozygote (Fig. S9) in our analysis! This important control has revealed that the maternal effect of the D1 mutant is negligible for gonad development and fertility (Fig. 6B-D). Rather, our data clearly emphasize embryogenesis (or early larval development) as a key period during which D1 can promote heritable TE repression. Essentially, D1 is not required during adulthood for TE repression if it was present in the early stages of development.

      Apologies if I missed this, but Figure 5 shows the F2 D1 mutant ovaries only. Did you look at the TM6 ovaries as well? These ovaries should lack the maternally provisioned D1 (assuming that females are on the right side) but have the zygotic transcription.

      As mentioned above, this was a great suggestion and we've now characterized this important control in the context of germline development and fertility, to the significant advantage of our paper.

      Minor comments 9. Add line numbers for ease of reference

      We apologize for this. Line numbers have been added in the full revision.

      1. The function of satellite DNA itself is still quite controversial - I would recommend being a bit more careful here - the authors could refer instead to genomic regions enriched for satellite DNA are linked to xyz function (see Abstract line 2 and 7, for example.)

      The abstract has been rewritten and does not directly implicate satellite DNA in a specific cellular function. However, we have taken the reviewer's suggestion in the introduction (line 57-58).

      "Genetic conflicts" in the introduction needs more explanation.

      This sentence has been removed from the introduction in the revised manuscript.

      "In contrast" is not quite the right word. Maybe "However" instead (1st line second paragraph of Intro)

      Done. Line 57 of the revised manuscript.

      Results: what is the motivation for using GSC-enriched testis?

      We use GSC-enriched testes for practical reasons. First, they contain a relatively uniform population of mitotically dividing germ cells unlike regular testes which contain a multitude of post-mitotic germ cells such as spermatocytes, spermatids and sperm. Second, GSC-enriched testes are much larger than normal testes and reduced the number of dissections that were needed for each replicate.

      1. Clarify sentence about the 500 proteins in the Results section - it's not clear from context that this is the union of all experiments.

      Done. Lines 145-149 in the revised manuscript.

      The data reported are not the first to suggest that satellite DNA may have special DNA repair requirements. e.g., PMID: 25340780

      We apologize if we gave the impression that we were making a novel claim. Specialized DNA repair requirements at repetitive sequences have indeed been previously hypothesized(Charlesworth et al. 1994) and studied and we have altered the text to better reflect this (lines 193-195). We have cited the study suggested by the reviewer as well as studies from the Chiolo(Chiolo et al. 2011; Ryu et al. 2015; Caridi et al. 2018) and Soutoglou(Mitrentsi et al. 2022) labs, which have also addressed this fascinating question.

      Page 10: indicate-> indicates.

      Done.

      1. Page 14: revise for clarity: "investigate a context whether these interactions could not take place"

      We've incorporated this suggestion in the revised text (lines 383-386).

      1. Might be important to highlight the 500 interactions are both direct and indirect. "Interacting proteins" alone suggests direct interactions only.

      Done. Lines 145-149.

      The effect of the aub mutant on chromocenter foci did not seem modest to me - however, the bar graphs obscure the raw data - consider plotting all the data not just the mean and error?

      Done. This data is now represented by a box-and-whisker plot (Fig. S5), which shows the distribution of the data.

      Reviewer #2 (Significance (Required)):

      The dataset produced by the AP-Mass Spec offers chromosome biologists an unprecedented resource. The PCH is long-ignored chromosomal region that has historically received minimal attention; consequently, the pathways that regulate heterochromatin are understudied. Moreover, attempting to connect genome organization to transposon regulation is a new and fascinating area. I can easily envision this manuscript triggering a flurry of discovery; however, there is quite a lot of work to do before the data can fully support the claims.

      This manuscript represents a significant contribution to the field of chromosome biology.

      We thank the reviewer for the positive evaluation of our manuscript, and we really appreciate the great suggestion for the F2 D1 heterozygote control! Overall, we believe that our manuscript is substantially improved with the addition of RNA seq, small RNA seq and important genetic controls. Moreover, we are excited by the potential of our study to open new doors in the study of pericentromeric heterochromatin.

      Reviewer #3 (Evidence, reproducibility and clarity (Required)): In the manuscript entitled "Multi-tissue proteomics identifies a link between satellite DNA organization and transgenerational transposon repression", the authors used two satellite DNA-binding proteins, D1 and Prod, as baits to identify chromocenter-associated proteins through quantitative mass spectrometry. The proteomic analysis identified ~500 proteins across embryos, ovaries, and testes, including several piRNA pathways proteins. Depletion of D1 or Prod did not directly contribute to transposon repression in ovary. However, in the absence of maternal and zygotic D1, there was a dramatic increase of agametic ovaries and transgenerational transposon de-repression. Although the study provides a wealth of proteomic data, it lacks mechanistic insights into how satellite DNA organization influence the interactions with other proteins and their functional consequences.

      We thank the reviewer for highlighting that this study will be a valuable resource for future studies on the composition and function of pericentromeric heterochromatin. Based on the reviewer's request for more mechanistic knowledge into how satellite DNA organization affects transposon repression, we have performed RNA seq and small RNA seq, added important genetic controls and significantly improved our text. In the revised manuscript, our data clearly demonstrate that embryogenesis (and potentially early larval development) is a critical time period when D1 contributes to heritable TE repression. Flies lacking D1 during embryogenesis exhibit TE expression in germ cells as adults, which is associated with Chk2-dependent gonadal atrophy. We are particularly excited by these data since TE loci are embedded in the satellite DNA-rich pericentromeric heterochromatin and our study demonstrates an important role for a satellite DNA-binding protein in TE repression.

      Major____ comments 1. While the identification of numerous interactions is significant, it would be helpful to acknowledge that lots of these proteins were known to bind DNA or heterochromatin regions. To strengthen the study, I recommend conducting functional validation of the identified interactions, in addition to the predictions made by Alphfold 2.

      We are happy to take this comment on board. In fact, we believe that the large number of DNA-binding and heterochromatin-associated proteins identified in this study are a sign of quality for the proteomic datasets. In the revised manuscript, we have highlighted known heterochromatin proteins co-purified by D1/Prod in lines 148-151 as well as proteins previously suggested to interact with D1/Prod from high-throughput studies in lines 153-156 (Guruharsha et al. 2011; Tang et al. 2023). In this study, we have focused on the previously unknown associations between D1/Prod and TE repression proteins and functionally validated these interactions as presented in Figures 3-6.

      The observation of transgenerational de-repression is intriguing. However, to better support this finding, it would be better to provide a mechanistic explanation based on the data presented.

      We appreciate this comment from the reviewer, which is similar to major comment #6 raised by reviewer #2. To generate mechanistic insight into the underlying cause of gonad atrophy in the F2 D1 mutant, we have performed RNA seq, small RNA seq and analyzed germline development and fertility in the F2 D1 heterozygous control (Fig. S9).

      For the RNA seq, we used D1 heterozygous (control) and D1 mutant ovaries in a chk26006 background. Since Chk2 arrests germ cell development in response to TE de-repression and DNA damage(Ghabrial and Schüpbach 1999; Moon et al. 2018), we reasoned that the chk2 mutant background would prevent developmental arrest of potential TE-expressing germ cells and we observed that both genotypes exhibited similar gonad morphology (Fig. 4A). From our analysis, we do not observe a significant effect on TE expression in the absence of D1, except for the LTR retrotransposon tirant (Fig. 4B). We also do not observe differential expression of TE repression genes (Fig. 4F).

      We have complemented our RNA seq experiment with small RNA profiling from D1 heterozygous (control) and D1 mutant ovaries. Here, overall piRNA production and antisense piRNAs mapping to TEs were largely unperturbed (Fig. 4C-E). Together, these data are consistent with the TE reporter data (Fig. S7) and suggests that zygotic depletion of D1 does not have a prominent role in TE repression.

      However, we have uncovered that the presence of D1 during embryogenesis is critical for TE repression in adult gonads (Fig. 6, Fig. S9). Essentially, either only maternal deposited D1 (F1 D1 mutant) or only zygotically expressed D1 (F2 D1 het) were sufficient to ensure TE repression and fertility. In contrast, a lack of D1 during embryogenesis (F2 D1 mutant) led to elevated TE expression and Chk2-mediated gonadal atrophy.

      Our results also explain why previous studies have not implicated either D1 or Prod in TE repression, since D1 likely persists during embryogenesis when using depletion approaches such as RNAi-mediated knockdown or F1 generation mutants.

      Minor____ comments 3. Given the maternal effect of the D1 mutant, in Figure 4, I suggest analyzing not only nurse cells but also oocytes to gain a more comprehensive understanding.

      We agree with the reviewer that this experiment can be informative. In the F2 D1 mutant ovaries, germ cell development does not proceed to a stage where oocytes are specified, thus limiting microscopy-based approaches. Nevertheless, we have gauged oocyte quality in all the genotypes using a fertility assay (Fig. 6D) since even ovaries that have a wild-type appearance can produce dysfunctional gametes. In this experiment, we observe that fertility is largely intact in the F1 D1 mutant and F2 D1 heterozygote strains, suggesting that it is the presence of D1 during embryogenesis (or early larval development) that is critical for heritable TE repression and proper oocyte development.

      The conclusion that D1 and Prod do not directly contribute to the repression of transposons needs further analysis from RNA-seq data. Alternatively, the wording could be adjusted to indicate that D1 and Prod are not required for specific transposon silencing, such as Burdock and gypsy.

      Agreed. We have performed RNA-seq in D1 heterozygous (control) and D1 mutant ovaries in a chk26006 background (Fig. 4A, B) as described above.

      As D1 mutation affects Cuff nuclear localization, it would be insightful to sequence the piRNA in the ovaries.

      Agreed. We have performed small RNA profiling from D1 heterozygous (control) and D1 mutant ovaries. Despite the significant mislocalization of the RDC complex, overall piRNA production and antisense piRNAs mapping to TEs were largely unaffected (Fig. 4C-E). However, we observed significant changes in piRNAs mapping to complex satellite DNA repeats (Fig. 4D), but these changes were not associated with a maternal effect on germline development or fertility (F2 D1 heterozygote, Fig. 6B-D).

      **Referee Cross-Commenting**

      I appreciate the valuable insights provided by the other two reviewers regarding this manuscript. I concur with their assessment that substantial improvements are needed before considering this manuscript for publication.

      1. The proteomics data has the potential to be a valuable resource for other scientific community. However, I share the concerns raised by reviewer 1 about the current quality of the data sets. Addressing this, it will augment the manuscript with additional data to show the success of the precipitation. Moreover, as reviewer 2 and I suggested, additional co-IP validations of the IP-MS results are needed to enhance the reliability.

      In the revised manuscript, we have performed multiple experiments to address the quality of the MS datasets based on comments raised by reviewer #1. They are as follows,

      Out of six total AP-MS experiments in this manuscript (D1 x 3, Prod x 2 and Piwi), we observe a strong enrichment of the bait in 5/6 attempts (log2FC between 4-12, Fig. 2A, B, Fig. S2A, Table S1-S3, Table S7). In the D1 testis sample from the initial submission, the lack of a third biological replicate meant that only the p-value (0.07) was not meeting the cutoff. To address this, we have repeated this experiment with an additional biological replicate (Fig. S2A), and our data now clearly show that D1 is also significantly enriched in the testis sample.

      As suggested by the reviewer #1, we have assessed our lysis conditions (450mM NaCl and benzonase) and the solubilization of our baits post-lysis. In Fig. S1D, we have blotted equivalent fractions of the soluble supernatant and insoluble pellet from GFP-Piwi embryos and show that both GFP-Piwi and D1 are largely solubilized following lysis. In Fig. S1E, we also show that our IP protocol works efficiently.

      The only instance in which we do not detect the bait by mass spectrometry is for GFP-Prod pulldown in embryos. Here, one reason could be relatively low expression of GFP-Prod in comparison to GFP-D1 (Fig. S1E), which may lead to technical difficulties in detecting peptides corresponding to Prod. However, we note that Prod IP from embryos co-purified proteins such as Bocks that were previously suggested as Prod interactors from high-throughput studies (Giot et al. 2003; Guruharsha et al. 2011). In addition, Prod IP from embryos also co-purified proteins known to associate with chromocenters such as Hcs(Reyes-Carmona et al. 2011) and Saf-B(Huo et al. 2020). Finally, the concordance between D1 and Prod co-purified proteins from embryo lysates (Fig. 2A, C) suggest that the Prod IP from embryos is of reasonable quality.

      As for the IP-WB validations, we would point out that chromocenters exhibit properties associated with phase separated biomolecular condensates. In our experience, these condensates tend to associate with other proteins/condensates through low affinity or transient interactions that are rarely preserved in IP-WBs, even if there are strong functional relationships. One example is the association between D1 and Prod, which do not pull each other down in an IP-WB (Jagannathan et al. 2019), even though D1 and Prod foci dynamically associate in the nucleus and mutually regulate each other's ability to cluster satellite DNA repeats (Jagannathan et al. 2019). Similarly, IP-WB using GFP-Piwi embryos did not reveal an interaction with D1 (Fig. S4B). However, our extensive functional validations (Figures 4-6) have revealed a critical role for D1 in heritable TE repression.

      I agree with reviewer 2 that the present conclusion is not appropriate regarding D1 and Prod do not contribute to transposon silencing. As reviewer 2 and I suggested, the systematical analysis by using both mRNA-seq and small RNA-seq is required to draw the conclusion.

      Agreed. We have performed RNA seq and small RNA seq as elaborated above. Our conclusions on the role of D1 in TE repression are now much stronger.

      1. The transgenerational phenotype is an intriguing aspect of the study. I agree with reviewer 2 that the inclusion of TM6 ovaries would be a nice control. Further, it is hard to connect this phenotype with the interactions identified in this manuscript. It would be appreciated if the author could provide a mechanistic explanation.

      We have significantly improved these aspects of our study in the revised manuscript. Through the analysis of germline development in the F2 D1 heterozygotes as suggested by reviewer #2, in addition to the recommended RNA seq and small RNA seq, we have now identified embryogenesis (and potentially early larval development) as a time period when D1 makes an important contribution to TE repression. Loss of D1 during embryogenesis leads to TE expression in adult germline cells, which is associated with Chk2-dependent gonadal atrophy. Taken together, we have pinpointed the specific contribution of a satellite DNA-binding protein to transposon repression.

      Reviewer #3 (Significance (Required)):

      Although this study successfully identified several interactions, the authors did not fully elucidate how these interactions contribute to the transgenerational silencing of transposons or ovary development.

      We thank the reviewer for the thoughtful comments and overall positive evaluation of our study, especially the proteomic dataset. We are confident that the revised manuscript has improved our mechanistic understanding of the contribution made by a satellite DNA-binding protein in TE repression.

      References

      Baumgartner L, Handler D, Platzer SW, Yu C, Duchek P, Brennecke J. 2022. The Drosophila ZAD zinc finger protein Kipferl guides Rhino to piRNA clusters eds. D. Bourc'his, K. Struhl, and Z. Zhang. eLife 11: e80067.

      Caridi CP, D'Agostino C, Ryu T, Zapotoczny G, Delabaere L, Li X, Khodaverdian VY, Amaral N, Lin E, Rau AR, et al. 2018. Nuclear F-actin and myosins drive relocalization of heterochromatic breaks. Nature 559: 54-60.

      Charlesworth B, Sniegowski P, Stephan W. 1994. The evolutionary dynamics of repetitive DNA in eukaryotes. Nature 371: 215-220.

      Chiolo I, Minoda A, Colmenares SU, Polyzos A, Costes SV, Karpen GH. 2011. Double-strand breaks in heterochromatin move outside of a dynamic HP1a domain to complete recombinational repair. Cell 144: 732-744.

      Ghabrial A, Schüpbach T. 1999. Activation of a meiotic checkpoint regulates translation of Gurken during Drosophila oogenesis. Nat Cell Biol 1: 354-357.

      Giot L, Bader JS, Brouwer C, Chaudhuri A, Kuang B, Li Y, Hao YL, Ooi CE, Godwin B, Vitols E, et al. 2003. A protein interaction map of Drosophila melanogaster. Science 302: 1727-1736.

      Guruharsha KG, Rual JF, Zhai B, Mintseris J, Vaidya P, Vaidya N, Beekman C, Wong C, Rhee DY, Cenaj O, et al. 2011. A protein complex network of Drosophila melanogaster. Cell 147: 690-703.

      Huo X, Ji L, Zhang Y, Lv P, Cao X, Wang Q, Yan Z, Dong S, Du D, Zhang F, et al. 2020. The Nuclear Matrix Protein SAFB Cooperates with Major Satellite RNAs to Stabilize Heterochromatin Architecture Partially through Phase Separation. Molecular Cell 77: 368-383.e7.

      Jagannathan M, Cummings R, Yamashita YM. 2019. The modular mechanism of chromocenter formation in Drosophila eds. K. VijayRaghavan and S.A. Gerbi. eLife 8: e43938.

      Mitrentsi I, Lou J, Kerjouan A, Verigos J, Reina-San-Martin B, Hinde E, Soutoglou E. 2022. Heterochromatic repeat clustering imposes a physical barrier on homologous recombination to prevent chromosomal translocations. Molecular Cell 82: 2132-2147.e6.

      Moon S, Cassani M, Lin YA, Wang L, Dou K, Zhang ZZ. 2018. A Robust Transposon-Endogenizing Response from Germline Stem Cells. Dev Cell 47: 660-671 e3.

      Pascovici D, Handler DCL, Wu JX, Haynes PA. 2016. Multiple testing corrections in quantitative proteomics: A useful but blunt tool. PROTEOMICS 16: 2448-2453.

      Reyes-Carmona S, Valadéz-Graham V, Aguilar-Fuentes J, Zurita M, León-Del-Río A. 2011. Trafficking and chromatin dynamics of holocarboxylase synthetase during development of Drosophila melanogaster. Molecular Genetics and Metabolism 103: 240-248.

      Ryu T, Spatola B, Delabaere L, Bowlin K, Hopp H, Kunitake R, Karpen GH, Chiolo I. 2015. Heterochromatic breaks move to the nuclear periphery to continue recombinational repair. Nat Cell Biol 17: 1401-1411.

      Tang H-W, Spirohn K, Hu Y, Hao T, Kovács IA, Gao Y, Binari R, Yang-Zhou D, Wan KH, Bader JS, et al. 2023. Next-generation large-scale binary protein interaction network for Drosophila melanogaster. Nat Commun 14: 2162.

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      Referee #3

      Evidence, reproducibility and clarity

      In the manuscript entitled "Multi-tissue proteomics identifies a link between satellite DNA organization and transgenerational transposon repression", the authors used two satellite DNA-binding proteins, D1 and Prod, as baits to identify chromocenter-associated proteins through quantitative mass spectrometry. The proteomic analysis identified ~500 proteins across embryos, ovaries, and testes, including several piRNA pathways proteins. Depletion of D1 or Prod did not directly contribute to transposon repression in ovary. However, in the absence of maternal and zygotic D1, there was a dramatic increase of agametic ovaries and transgenerational transposon de-repression. Although the study provides a wealth of proteomic data, it lacks mechanistic insights into how satellite DNA organization influence the interactions with other proteins and their functional consequences.

      Major

      1. While the identification of numerous interactions is significant, it would be helpful to acknowledge that lots of these proteins were known to bind DNA or heterochromatin regions. To strengthen the study, I recommend conducting functional validation of the identified interactions, in addition to the predictions made by Alphfold 2.
      2. The observation of transgenerational de-repression is intriguing. However, to better support this finding, it would be better to provide a mechanistic explanation based on the data presented. Minor
      3. Given the maternal effect of the D1 mutant, in Figure 4, I suggest analyzing not only nurse cells but also oocytes to gain a more comprehensive understanding.
      4. The conclusion that D1 and Prod do not directly contribute to the repression of transposons needs further analysis from RNA-seq data. Alternatively, the wording could be adjusted to indicate that D1 and Prod are not required for specific transposon silencing, such as Burdock and gypsy.
      5. As D1 mutation affects Cuff nuclear localization, it would be insightful to sequence the piRNA in the ovaries.

      Referee Cross-Commenting

      I appreciate the valuable insights provided by the other two reviewers regarding this manuscript. I concur with their assessment that substantial improvements are needed before considering this manuscript for publication.

      1. The proteomics data has the potential to be a valuable resource for other scientific community. However, I share the concerns raised by reviewer 1 about the current quality of the data sets. Addressing this, it will augment the manuscript with additional data to show the success of the precipitation. Moreover, as reviewer 2 and I suggested, additional co-IP validations of the IP-MS results are needed to enhance the reliability.
      2. I agree with reviewer 2 that the present conclusion is not appropriate regarding D1 and Prod do not contribute to transposon silencing. As reviewer 2 and I suggested, the systematical analysis by using both mRNA-seq and small RNA-seq is required to draw the conclusion.
      3. The transgenerational phenotype is an intriguing aspect of the study. I agree with reviewer 2 that the inclusion of TM6 ovaries would be a nice control. Further, it is hard to connect this phenotype with the interactions identified in this manuscript. It would be appreciated if the author could provide a mechanistic explanation.

      Significance

      Although this study successfully identified several interactions, the authors did not fully elucidate how these interactions contribute to the transgenerational silencing of transposons or ovary development.

    3. 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

      Chavan et al. set out to enrich our compendium of pericentric heterochromatin-associated proteins - and to learn some new biology along the way. An ambitious AP-Mass baited with two DNA satellite-binding proteins (D1 and Prod), conducted across embryos, ovaries, and testes, yielded hundreds of candidate proteins putatively engaged at chromocenters. These proteins are enriched for a restricted number of biological pathways, including DNA repair and transposon regulation. To investigate the latter in greater depth, the authors examine D1 and prod mutants for transposon activity changes using reporter constructs for multiple elements. These reporter constructs revealed no transposon activation in the adult ovary, where many proteins identified in the mass spec experiments restrict transposons. However, the authors suggest that the D1 mutant ovaries do show disrupted localization of a key member of a transposon restriction pathway (Cuff), and infer that this mislocalization triggers a striking, transposon derepression phenotype in the F2 ovaries.

      The dataset produced by the AP-Mass Spec offers chromosome biologists an unprecedented resource. The PCH is long-ignored chromosomal region that has historically received minimal attention; consequently, the pathways that regulate heterochromatin are understudied. Moreover, attempting to connect genome organization to transposon regulation is a new and fascinating area. I can easily envision this manuscript triggering a flurry of discovery; however, there is quite a lot of work to do before the data can fully support the claims.

      Major

      1. The introduction requires quite a radical restructure to better highlight the A) importance of the work and B) limit information whose relevance is not clear early in the manuscript. A. Delineating who makes up heterochromatin is a long-standing problem in chromosome biology. This paper has huge potential to contribute to this field; however, it is not the first. Others are working on this problem in other systems, for example PMID:29272703. Moreover, we have some understanding of the distinct pathways that may impact heterochromatin in different tissues (e.g., piRNA biology in ovaries vs the soma). Also, the mutant phenotypes of prod and D1 are different. Fleshing out these three distinct points could help the reader understand what we know and what we don't know about heterochromatin composition and its special biology. Understanding where we are as a field will offer clear predictions about who the interactors might be that we expect to find. For example, given the dramatically different D1 and prod mutant phenotypes (and allele swap phenotypes), how might the interactors with these proteins differ? What do we know about heterochromatin formation differences in different tissues? And how might these differences impact heterochromatin composition? B. The attempt to offer background on the piRNA pathway and hybrid dysgenesis in the Introduction does not work. As a naïve reader, it was not clear why I was reading about these pathways - it is only explicable once the reader gets to the final third of the Results. Moreover, the reader will not retain this information until the TE results are presented many pages later. I strongly urge the authors to shunt the two TE restriction paragraphs to later in the manuscript. They are currently a major impediment to understanding the power of the experiment - which is to identify new proteins, pathways, and ultimately, biology that are currently obscure because we have so little handle on who makes up heterochromatin.
      2. The implications of the failure to rescue female fertility by the tagged versions of both D1 and Prod are not discussed. Consequently, the reader is left uneasy about how to interpret the data.
      3. How were the significance cut-offs determined? Is the p-value reported the adjusted p-value? As a non-expert in AP-MS, I was surprised to find that the p-value, at least according to the Methods, was not adjusted based on the number of tests. This is particularly relevant given the large/unwieldy(?) number of proteins that were identified as signficant in this study. Moreover, the D1 hit in Piwi pull down is actually not significant according to their criteria of p <0.05 (D1 is p=0.05).
      4. How do we know if the lack of overlap across tissues is indeed germline- or soma-specialization rather than noise? To make this inference, conducting some validation would be required. More generally, I was surprised to see no single interactor validated by reciprocal IP-Westerns to validate the Mass-Spec results, though I am admittedly only adjacent to this technique. Note that colocalization, to my mind, does not validate the AP-MS data - in fact, we would a priori predict that piRNA pathway members would co-localize with PCH given the enrichment of piRNA clusters there.
      5. The AlphaFold2 data are very interesting but seem to lack of negative control. Is it possible to incorporate a dataset of proteins that are not predicted to interact physically to elevate the impact of the ones that you have focused on? Moreover, the structural modeling might suggest a competitive interaction between D1 and piRNAs for Piwi. Is this true? And even if not, how does the structural model contribute to your understanding for how D1 engages with the piRNA pathway? The Cuff mislocalization?
      6. The absence of a TE signal in D1 and Prod mutant ovaries would be much more compelling if investigated more agnostically. The observation that not all TE reporter constructs show a striking signal in the F2 embryos makes me wonder if Burdock and gypsy are not regulated by these two proteins but possibly other TEs are. Alternatively, small RNA-seq would more directly address the question of whether D1 and Prod regulate TEs through the piRNA pathway.
      7. I had trouble understanding the significance of the Cuff mis-localization when D1 is depleted. Given Cuff's role in the piRNA pathway and close association with chromatin, what would the null hypothesis be for Cuff localization when a chromocenter is disrupted? What is the null expectation of % Cuff at chromocenter given that the chromocenter itself expands massively in size (Figure 4D). The relationship between these two factors seems rather indirect and indeed, the absence of Cuff in the AP would suggest this. The biggest surprise is the absence of TE phenotype in the ovary, given the Cuff mutant phenotype - but we can't rule out given the absence of a genome-wide analysis. I think that these data leave the reader unconvinced that the F2 phenotype is causally linked to Cuff mislocalization.
      8. Apologies if I missed this, but Figure 5 shows the F2 D1 mutant ovaries only. Did you look at the TM6 ovaries as well? These ovaries should lack the maternally provisioned D1 (assuming that females are on the right side) but have the zygotic transcription.

      Minor

      1. Add line numbers for ease of reference
      2. The function of satellite DNA itself is still quite controversial - I would recommend being a bit more careful here - the authors could refer instead to genomic regions enriched for satellite DNA are linked to xyz function (see Abstract line 2 and 7, for example.)
      3. "Genetic conflicts" in the introduction needs more explanation.
      4. "In contrast" is not quite the right word. Maybe "However" instead (1st line second paragraph of Intro)
      5. Results: what is the motivation for using GSC-enriched testis?
      6. Clarify sentence about the 500 proteins in the Results section - it's not clear from context that this is the union of all experiments.
      7. The data reported are not the first to suggest that satellite DNA may have special DNA repair requirements. e.g., PMID: 25340780
      8. Page 10: indicate-> indicates.
      9. Page 14: revise for clarity: "investigate a context whether these interactions could not take place"
      10. Might be important to highlight the 500 interactions are both direct and indirect. "Interacting proteins" alone suggests direct interactions only.
      11. The effect of the aub mutant on chromocenter foci did not seem modest to me - however, the bar graphs obscure the raw data - consider plotting all the data not just the mean and error?

      Significance

      The dataset produced by the AP-Mass Spec offers chromosome biologists an unprecedented resource. The PCH is long-ignored chromosomal region that has historically received minimal attention; consequently, the pathways that regulate heterochromatin are understudied. Moreover, attempting to connect genome organization to transposon regulation is a new and fascinating area. I can easily envision this manuscript triggering a flurry of discovery; however, there is quite a lot of work to do before the data can fully support the claims.

      This manuscript represents a significant contribution to the field of chromosome biology.

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      Referee #1

      Evidence, reproducibility and clarity

      This is an interesting manuscript from the Jagannathan laboratory, which addresses the interaction proteome of two satellite DNA-binding proteins, D1 and Prod. To prevent a bias by different antibody affinities they use GFP-fusion proteins of D1 and Prod as baits and purified them using anti GFP nanobodies. They performed the purifications in three different tissues: embryo, ovary and GSC enriched testes. Across all experiments, they identified 500 proteins with surprisingly little overlap among tissues and between the two different baits. Based on the observed interaction of prod and D1 with members of the canonical piRNA pathway the authors hypothesized that both proteins might influence the expression of transposable elements. However, neither by specific RNAi alleles or mutants that lead to a down regulation of D1 and Prod in the gonadal soma nor in the germline did they find an effect on the repression of transposable elements. They also did not detect an effect of a removal of piRNA pathway proteins on satellite DNA clustering, which is mediated by Prod and D1. However, they do observe a mis-localisation of the piRNA biogenesis complex to an expanded satellite DNA in absence of D1, which presumably is the cause of a mis-regulation of transposable elements in the F2 generation.

      This is an interesting finding linking satellite DNA and transposable element regulation in the germline. However, I find the title profoundly misleading as the link between satellite DNA organization and transgenerational transposon repression in Drosophila has not been identified by multi-tissue proteomics but by a finding of the Brennecke lab that the piRNA biogenesis complex has a tendency to localise to satellite DNA when the localisation to the piRNA locus is impaired.

      Nevertheless, the investigation of the D1 and Prod interactome is interesting and might reveal insights into the pathways that drive the formation of centromeres in a tissue specific manner.

      Major comments

      Unfortunately, the proteomic data sets are not very convincing. Not even the corresponding baits are detected in all assays. I wonder whether the extraction procedure really allows the authors to analyze all functionally relevant interactions of Prod and D1. It would be good to see a western blot or an MS analysis of the soluble nuclear extract they use for purification compared to the insoluble chromatin. It may well be that a large portion of Prod or D1 is lost in this early step. I also find the description of the proteomic results hard to follow as the authors mostly list which proteins the find as interactors of Prod and D1 without stating in which tissue or with what bait they could purify them (i.e. p7: Importantly, our hits included known chromocenter-associated or pericentromeric heterochromatin-associated proteins, such as Su(var)3-9[52], ADD1[23,24], HP5[23,24],mei-S332[53], Mes-4[23], Hmr[24,39,54], Lhr[24,39], and members of the chromosome passenger complex, such as borr and Incenp[55]). It would be interesting to at least discuss tissue specific interactions.

      Minor comments

      The authors may also want to provide a bit more information on the quantitation of the proteomic data such as how many values were derive from the match-between runs function and how many were imputed as this can severely distort the quantification.

      Referee Cross-Commenting

      I agree with the two other reviewers that the connection between the interactome and the transgenerational phenotype is unclear. This is also what I meant i my comment that the title is somewhat misleading. A systematic analysis of the D1 and Prod knock down effect on mRNAs and small Rnas would indeed be helpful to better understand the interesting effect.

      Significance

      Nevertheless, the investigation of the D1 and Prod interactome is interesting and might reveal insights into the pathways that drive the formation of centromeres in a tissue specific manner. It may be mostly interesting for the Drosophila community but could also be exiting for a broader audience interested in the connection of heterochromatin and its indirect effect on the regulation of transposable elements.

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      Reply to the reviewers

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

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      Referee #2

      Evidence, reproducibility and clarity

      In this manuscript by Kehrer et al., use an elegant Apex2 BioID method to identify novel putative microneme proteins by mass-spectrometry and pick one candidate for further characterization. They identify a novel putative microneme protein they name Akratin which they characterize through targeted gene deletion and a series of complementation experiments. This reveals first that akratin appears to be functioning in male gamete egress, and though complementation using a putative trafficking mutant, also in midgut traversal.

      Overall the study is thoroughly performed but some of the conclusions are not fully supported.

      1)The newly identified microneme protein is still putative in my mind as the authors have not co-localized it with another marker. This is crucial for conclusions about its putative function and crucial for the trafficking experiment as explained below. It is also important given the high number of putative false positives in the BioID experiment.

      2)I would consider it essential to also localise the Apex2 tagged SOAP protein as the authors cannot be sure that there is a partial mislocalisation of the protein leading to false positives.

      3)I am not convinced by the trafficking defect. This could be because the localsation in the images are not easy to distinguish and it may be much clearer looking down the microscope. I think co-localisation with another microneme marker would go a long way and demonstrating that akratin upon mutation actually localises elsewhere is important. It is even more important since there is no phenotype in male egress, but then later in ookinetes, which is a bit surprising if this is a proper conserved trafficking motif.

      4)The candidate selection section is poorly described. A flow chart or clearer inclusion/ exclusion criteria would be useful.

      5)I understand the approach to focus on more abundant biotinylated proteins, however, I think it may not be the best approach to use peptide counting. Apex2 labelling as the authors rightfully say, is mainly based on tyrosine labelling of surface exposed areas, so the abundance of proteins in the IP will depend on accessible tyrosines, protein abundance, distance from the bait, size of the protein and how many tryptic peptides can be generated. Reproducible results between 2 conditions are more likely to show true positives and may be the best way to prioritize, or assign confidence. Also: cOuld the authors use mean intensity values for the peptides covering proteins as a metric for abundance using label free quantification? This is not a requirement but may allow quantification in a slightly better way. I am not sure about the Table S1 colour scheme (the legend does not explain green, purple and blue shading). Are all green ones confirmed microneme proteins? Please add a proper descripton of the table and columns.

      6)Figure 2C and D are from PlasmoDB and should ideally not be included as figure panels. This is misleading and could either be mentioned in the text, or put into supplementary data with a clear note that the authors have not aquired these data. I would also suggest to move figures 3A-C into figure 2 and present the KO with the complementation data for a direct comparison.

      Minor:

      1)When the authors say "numbers of peptides identified": is this unique peptides or does it include non-unique peptides?

      2)Figures 1 I-K could move into supplementary as they are somewhat non-informative given the nature of BioID described in the main points.

      3)Line 253: Whether akratin is involved in membrane lysis directly, or important for microneme secretion so this is a knock-on effect is not known. This could be added to the discussion, but there is no evidence for this statement in the results section.

      4)Line 274: Refers to Figure 3F, which does not exist.

      5)Line 333: Overall I think this is a bit of an overstatement. The use of Apex2 in these conditions is definitely nice to see but for now the authors have validated none of the microneme proteins by co-localization. So we are still a bit in the dark how well the method works in terms of false positives. The targeting motif in my mind is not yet confirmed in the absence of co-localisations with other markers. An alternative explanation could be that the c-terminus of the protein is important for its function in one stage, but not another but that trafficking is not- or only marginally affected.

      Significance

      The significance of the manuscript in my mind lies in the application of Apex2 in Plasmodium parasites, which will be an advance for the field. However, we do not learn about labeling times, how short it can be so its potential is not fully looked at.

      The list of the putative micronemes will of course be of high interest for the community, but because of the limited validation in this study will require further validation by others.

      The identification of the dual function of this protein in transmission in egress and ookinete traversal is interesting and surely leads to further studies. The identification of a putative differential trafficking motif is intruiging, if, as stated in the major concerns, this can be validated.

      My expertise lies in Plasmodium biology with good knowledge of mass-spectrometry approaches.

      Referees Cross-commenting

      I agree with the assessment of the other reviewer, a slightly more detailed discussion of the hits would be desireable (exported proteins, why are they there). This could be a drawback of the system used, and mentioned.

      Western blot of the GFP is a very good idea to clarify whether the localization is maybe, in parts, GFP that is not fused to the full lenght protein, either by cleavage, or a breakdown product.

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      Referee #1

      Evidence, reproducibility and clarity

      Proximity labelling using BirA has emerged as a highly successful approach to identify interaction partners and proteins in compartments of a protein of interest in the living cell. A number of recent studies applied this approach with malaria parasites and demonstrated its usefulness. However, a drawback of using BirA is the time required to obtain good yields of biotinylated proteins (usually many hours). APEX is a much faster alternative to BirA that however has so far not been used in apicomplexan parasites. Here Kehrer and colleagues use APEX2 to identify proteins of the micronemes of mature Ookinetes, a task that due to the short time available for labelling, would have been difficult with BirA. From the obtained hits the authors chose a protein they named akratin and carried out a detailed functional analysis. They found that akratin is needed for microgametogenesis and for ookinete migration. Complementation with either the Pb or Pf GFP-tagged version of akratin rescued all defects of the mutant, despite the low sequence similarity and differing number of predicted transmembrane segments in the P. falciparum protein. Interestingly a mutant form of this protein with an ablated putative trafficking motif in its C-terminus also caused an ookinete migration phenotype but microgametogenesis was unaffected, hinting at intricacies in its function.

      This is a clearly written and interesting paper reporting the first use of APEX-based BioID in malaria parasites and demonstrates that it is possible to take advantage of BioID in short lived stages. The ookinete microneme proteome reported here compares favourably with that derived from organelle purifications and will provide a resource to identify the proteins and understand their involvement in migration and adhesion of this and possibly other parasite stages. The example protein chosen for functional analysis in this work nicely illustrates this. A validation of some more of the unknown hits to be true microneme proteins would have been beneficial, but given the high number of known true positives in the hit list this is not absolutely essential for the paper. Overall this manuscript therefore provides a nice piece of work adding a list of proteins for future study and a new player important for mosquito infection.

      Minor points:

      1.several proteins taken as true hits in TableS1 are not obvious to me, such as plasmepsin V and several exported proteins. Are they expected to be trafficked via the micronemes in ookinetes?

      2.Fig. 1C: '+ Streptavidin', this should be '+ streptavidin beads'

      3please insert a referral to Figure S2 (similarity of the Plasmodium akratin homologs) somewhere around line 180, the only reference to this figure I could find in the text was in line 214. Figure S3 (line 184) is mentioned in a context to support the absence of homologues outside Plasmodium spp but shows the generation of the akratin KO. Maybe this should have been a citation to Figure S2, but then something is missing from that figure.

      4.line 192, it might be useful to clarify in the text what 10 and 7 blood stage growth means (multiplication rate?).

      5.the observation that akratin as a multi TM protein with signal peptide seems to be soluble in the parasite is rather unlikely. Is there a precedent for this? My best guess would be that this is GFP alone due to degradation or processing of the akratin-GFP fusion. A Western blot, if sufficient material is available, would clarify this. In regards to the localisation of akratin in the different stages it should also be taken into account that calling anything 'vesicular' based on fluorescent microscopy is rather speculative.

      6.line 199, how can the low number of ookinetes affect their speed? Could this remark have been intended for the next sentence (199-201/Fig. 2I) as the lack of transmission to mosquitoes may have been due to the reduced number of ookinetes rather than a deficiency of individual ookinetes? To exclude the latter, were parasite number used matched to exclude that this was the case in Fig. 2I?

      7.line 272-4, is there a way to quantify the phenotype in ookinetes, e.g. using intensity profile plots showing the distribution across the cell? Many cells still seem to show peripheral staining in the trafficking mutant. Could it again be that some of the protein is processed and the increased cytoplasmic staining represents GFP alone (see also comment 5)? In that case the level of processing rather than trafficking (alone) might be affected in the mutant.

      8.lines 396 and 397, there is a minuscule -1 before the chemicals in my pdf.

      9.line 58. remove 'not' and 'or': neither been identified nor been characterised

      10.lines 88 to 94: English could be polished some more in this part. Line 91, replace 'ones', e.g. with 'proteins'

      11.lines 245 and 253: add commas after (Figure 4B) and (Figure 4D), respectively

      12.line 254; change possibly into possible

      13.line 296-71: it might be helpful to mention in the text that this was again the complementation strategy (used for the Pb and Pf akratin)

      14.while going beyond the scope of this manuscript, would it be possible to use the APEX introduced here to label structures in EM? A comment on this might be useful for readers interested in using this domain.

      Significance

      This is the first use of APEX2 in apicomplexans and this will be very useful for the field. The ookinete microneme proteome will provide a resource to study key aspects of this stage. The unknown proteins in the hit list still have to be confirmed to be true positives, but given the high number of true positives among the known proteins, the success rate should be acceptable. Akratin is a new protein among several known to be important for transmission to the mosquito host. As illustrated by this and other studies, many important questions remain how microgametes egress from the cell and how in vitro gliding and mosquito gut wall penetration relate. Akratin, together with the previously known proteins, will be instrumental in solving these questions.

      My expertise (to put this assessment into perspective): I am a cell biologist working with P. falciparum blood stages and have no or limited experience with mosquito stages and P. berghei. My grasp of the technical difficulties to work with ookinetes and other mosquito stages as presented in this manuscript are therefore limited. Nevertheless, it appears to me that the work is well done and that the overall outcome from this paper is significant and will be of great interest to the field.

      Referees Cross-Commenting

      I think the other reviewer's request to carry out a co-loc experiment with a microneme marker to show that akratin and SOAP-APEX are in the correct location is very reasonable and should be done. I also share the view about the trafficking domain. This is reflected in my comment (points 5 and 7) on quantifying the phenotype of the 'trafficking mutant' and the possbility of not looking at the full length protein as it may be a processed/degraded version of the protein that still contains GFP. Western blots, if possible with these parasite stages, might clear this up.

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      Reply to the reviewers

      Manuscript number: RC-2024-02378

      Corresponding author(s): Angelika Böttger

      [Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

      • *

      If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

      1. General Statements [optional]

      After we have carefully studied the four reviews we have received, we made some major revisions to the manuscript. These included the following main points:

      • Concerns regarding clarity of the manuscript: we have substantially edited the abstract, introduction and discussion part of the manuscript and added many more references to previous work by other authors, especially Cazet 2021, Tursch 2022 and Gahan 2017. We focused our introduction and discussion on organizer function and on the Gierer-Meinhardt-Model for pattern formation. We think that the conclusions are of great general interest because they suggest a function of the Hydra head organizer according to the original definition by Hans Spemann, that is “harmonious interlocking of separate processes which makes up development”. Notch signaling, in our interpretation, is an instrument for this function of the organizer. Comparison with Craspedacusta compellingly illustrates this idea.
      • Concerns regarding Craspedacusta experiments: we have isolated four Craspedacusta transcripts (CsSp5, CsWnt3, CsAlx and CsNOWA) and analyzed their response to DAPT during head regeneration in Craspedacusta. This revealed that DAPT did not inhibit CsWnt3 expression, in accordance with it not having an effect on head regeneration in Craspedacusta However, DAPT inhibited expression of the other potential CsNotch target genes, confirming that DAPT generally works in Craspedacusta polyps as Notch-inhibitor.
      • Concerns regarding HyKayak function: we have conducted a rescue experiment to show the function of Hykayak as a target for Notch-regulated repressor genes and a local inhibitor of Wnt-3 expression, which revealed that the expected up-regulation of HyWnt3 in DAPT-treated animals was very weak and did not rescue the DAPT-regeneration phenotype-this was discussed, but data were not included.

      2. Point-by-point description of the revisions

      This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *


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

      Major: • The introduction is lacking a full description of what is known about transcriptional changes during Hydra regeneration and in particular the role of Wnt signalling in this process. Of note the authors do not cite several important studies from recent years including (but not limited to):

      *https://doi.org/10.1073/pnas.2204122119 *

      *https://doi.org/10.1186/s13072-020-00364-6 *

      *https://doi.org/10.1101/587147 *

      *https://doi.org/10.7554/eLife.60562 This problem is further compounded later when the authors do not cite/discuss work which has performed the same or similar analyses to their own. The authors should endeavor to give a more comprehensive background knowledge. *

      Answer:

      Our work focuses on the role of Notch-signalling during Hydra head regeneration, specifically when the head is removed at an apical position. We therefore now have included additional information about transcriptional changes during this process in the introduction. In addition, we have included the suggested citations in the introduction to give a more general background knowledge.

      e.g. .Following decapitation, the expression of Hyβ-catenin and HyTcf was upregulated earliest, followed by local activation of Wnt genes. Among these, HyWnt3 and HyWnt11 appeared within 1.5 h of head removal, followed by HyWnt1, HyWnt9/10c, HyWnt16, and HyWnt7, indicating their role in the formation of the Hydra head organizer (Hobmayer et al., 2001; Lengfeld et al., 2009; Philipp et al., 2009; Tursch et al., 2022).

      • The authors do not cite or reference at all the study by Cazet et al. which used iCRT14 along with RNAseq and ATACseq to probe the role of Wnt signaling during early regeneration. This is a major issue. Although I appreciate that the authors have done much longer time courses and that their data therefore add something to our understanding it will still be important to discuss here. For example, the authors show that Wnt3 is activated normally in iCRT14 animals. Is this also seen in the RNAseq from Cazet et al.*
      • *

      Answer:

      iCRT14 was used in Hydra regeneration experiments by Gufler et al (which we did cite) and Cazet et al, but the specific aspects of hypostome and tentacle regeneration were not addressed. Cazet et al. have analyzed HyWnt3expression after iCRT treatment during the first 12 hrs of regeneration. Our data show, in addition that HyWnt3 is not controlled by TCF-dependent transcription during Hydra head regeneration after apical cuts throughout the whole regeneration process including the morphogenesis state. Nevertheless, the other Wnt-genes, which are indicated in canonical Wnt-signalling are affected by iCRT14 also in our study.

      We have now included comparison of Cazet- and our data, we wrote:

      HyWnt3 and Wnt9/10c expression are swiftly induced by injuries. When HyWnt3 and HyWnt9/10 activities are sustained, organizers can be formed, which induce ectopic heads when the original organizer tissue (the head) is removed (Cazet et al., 2021; Tursch et al., 2022).”

      The effect of iCRT14 had been analyzed in previous studies (Cazet et al., 2021; Gufler et al., 2018; Tursch et al., 2022). All showed b-catenin-dependency for down-regulation of head specific genes in foot regenerates at time points up to 12 hrs after head removal, including HyWnt3. They also stated a failure of head regeneration in the presence of iCRT14 but, in accordance with our study, did not reveal that HyWnt3 expression at future heads depended on b-catenin. None of these studies analyzed the regeneration of tentacles and hypostomes separately and they did not report whether* the regeneration of hypostomes 48 hrs after head removal occurred normally upon iCRT14 treatment. *

      • The visualizations used in Figure 3 are quite difficult to interpret and do to in all cases match descriptions in the text. The way the same type data is displayed in figure 5 so much nicer. It is also better to treat the same types of data in the same manner consistently throughout the paper. For Hes, for example, the authors state that there is a reduction although the data shows that this is very small and taking into account the 95% confidence interval does not seem to be significant. If this is the case then the positive control is not working in this experiment. This would be much clear if individual time points were compared like in figure 5 and statistical tests shown. The authors then state that Alx is not affected but there is actually a larger effect than what they deemed significant for Hes (the axes are notably different between these two and I think a more consistent axis would make the genes more comparable). Similarly, Gsc is described as being not affected at 8 hours but it appears again to change more that the positive control Hes. Given this I would call into question the validity of this dataset and/or the interpretation by the authors. A more thorough analysis including taking better into account statistical significance would go a long way to increasing confidence in this data. • The same issues in interpretation described for Figure 3 also apply to figure 4. The authors state that Wnt7 is affected less than Wnt1 and 3 but this is not evident in the figure and no comparative analysis is performed to confirm this. The same for Wnt 11 and 9/10c where what the authors description is very difficult to see in the figure. Sp5 is apparently upregulated, but this is not discussed. Again the axes are notably different making it even more difficult to compare between samples. __Answer*____:__

      We have now presented the data by simple scatter blots with significance information for every data point. This allows comparison between samples as requested by the reviewer. The GAMs were moved to the supplement. We believe that some readers may appreciate GAM-representation of the data because of the accessibility of the confidence interval over time.

      Concerning DAPT:

      “We now performed RT-qPCR analysis to compare gene expression dynamics of these genes during head regeneration 0, 8, 24, 36 and 48 hrs after head removal. Animals were either treated with 30 µM DAPT in 1% DMSO, or 1% DMSO as control for the respective time frames. Timepoint 0 was measured immediately after head removal. The results of these analyses revealed that HyHes expression was clearly inhibited by DAPT during the first 36 hrs after head removal (Fig. 3B), confirming previously published data which had indicated HyHes as a direct target for NICD (Münder et al., 2010). HyAlx expression levels were slightly up-regulated after 24 hrs, but later partially inhibited by DAPT (Fig. 3C). CnGsc expression under DAPT treatment initially (8hrs) was comparable to control levels, but then it was strongly inhibited (Fig. 3D). This goes along with the observed absence of organizer activity in regenerating Hydra tips (Münder et al., 2013). Interestingly, a similar result was seen for HySp5 expression, which was also normal at 8 hrs but was then inhibited by DAPT at later time points (Fig. 3E). HyKayak, while expression is normal after 8 hrs, was strongly overexpressed between 24 and 36 hrs of regeneration in DAPT-treated polyps in comparison to control regenerates (Fig. 3F).

      Concerning iCRT14

      Next, following the same procedure as described for DAPT, we compared the gene expression dynamics of iCRT14-treated regenerates with control regenerates. We found that the expression of HyWnt3 was not inhibited by iCRT14. In fact, it even appeared slightly up-regulated at the 8 hrs time point (Fig. 4A). Normal HyWnt3-expression at the end of the regeneration period was confirmed by in-situ hybridization for HyWnt3 as shown in Fig. 1D, indicating that HyWnt3 expression patterns and expression levels in ecto- and endodermal cells of the hypostome were faithfully regenerated (Fig. 4A). In contrast, HyAlx expression was completely abolished by iCRT14 (Fig. 4B), consistent with the observation that iCRT14-treated head regenerates did not regenerate any tentacles (Fig. 1A). HySp5 expression was not significantly affected by iCRT14 treatment at any time point (Fig. 4C).

      Furthermore, we found that CnGsc levels in iCRT14 remained similar to control regenerates up to 24 hrs, but were attenuated at later time points (Fig. 4D), very similar to the expression dynamics of the Notch-target gene HyHes (Fig. 4E). The expression of HyKayak was decreased at 8 hrs after head removal in the presence of iCRT14, but then increased above control levels after 48 hrs (Fig. 4F). There were no significant changes in the expression dynamics of HyBMP2/4 and HyBMP5/8b between iCRT14-treated regenerates and controls (Fig. 4G, H).”

      The precise number of biological replicates can be seen in the individual diagrams, they included for most genes three biological replicates, with always three technical replicates for each data point. Biological replicates were obtained over several years by different researchers. For some genes, we obtained very consistent data with high confidence in every experiment (e.g. HyWnt3, HyBMP4). We illustrate this in table 1, where three arrows indicate all such cases. With some genes we observed greater variation, which we interpret as no effect or a minor effect in table 1. Some of these variations may be explained by our observation of wave-like patterns in the expression dynamics. Therefore, we have included the following statement:

      “In addition, the gene expression dynamics for many of the analyzed genes appears in wave-like patterns in some experiments (see Figs S3 and S4). As we have only four time points measured, we cannot draw strong conclusions from these observations, except that some of the deviations in our data points (e.g. 48 hrs HyHes)”

      • In their description of figure 4 the authors completely omit to discuss the Cazet et al dataset which has the exact same early timepoints for iCRT14 treatment. This must be discussed and compared and any difference noted. * Answer:

      We included the iCRT14 results from Cazet et al., in our revised manuscript (see above).

      • End of page 11: The authors propose a model thereby the role of Notch in Wnt3 expression may be due to the presence of a repressor. However, I don't see any putative evidence at that stage. The authors also do not cite relevant work from both Cazet et al. and Tursch et al which show that Wnt3 is likely upregulated by bZIP TFs. In both these cases the authors show evidence of bZIP TF binding sites in the Wnt3 promoter along with other analyses. This is very relevantto the model presented by the authors here and must be discussed and compared. - * In particular the authors put forward HyKayak as an inhibitor of Wnt3 and this should be discussed along with the previous work.

      Answer:

      Tursch et al. 2022 did not claim that HyWnt3 is upregulated by bZiP TFs. They showed that HyWnt3 was strongly upregulated in a position-independent manner upon inhibition of the p38 or JNK (c-Jun N-terminal kinase) pathways (i.e., stress-induced MAPK pathways). This would rather support our hypothesis that HyKayak (AP-1 protein) might be a repressor of Wnt3-expression.

      Cazet et al have indicated that injury-responsive bZIP TFs are the most plausible regulators of canonical Wnt-signalling components during the early generic wound response. They identified CRE-elements, which can be bound by bZIP TFs, in the putative regulatory sequences of HyWnt3. However, they focused on the early stage of regeneration (0-12hpa), and showed that bZIP TFs, including jun, fos and creb are transiently upregulated at 3hpa and hypothesise that they could induce the upregulation of HyWnt3 at this stage as an injury response. We have to point out that the Hydra fos-homolog Hykayak, which our work is concerned with, is not identical with the fos-gene described in Cazet’s paper. In addition, the Hykayak gene was downregulated by Notch signalling during the morphogenesis state of regeneration (24-36 hrs), which is not the same stage investigated by Cazet et al. To avoid confusion, we have now included the Cazet-fos-sequence in our sequence comparison in Fig. S1 (fos_Cazet_HYDVU). Moreover, we have included more information about fos_Cazet in the context of a comparison with HyKayak.

      • *

      Different bZiP transcriptional factors (TFs) may have different effects on the expression of Wnt genes, and these effects are context-dependent. In previous research, Cazet et al. identified another Hydra fos gene (referred to as fos_cazet) and bZiP TF binding sites in the putative regulatory sequences of HyWnt3 and HyWnt9/10c. They showed that bZiP TF-genes, including Jun and fos, were transiently upregulated 3 hrs after amputation, therefore they hypothesized that bZiP TFs could induce TCF-independent upregulation of HyWnt3 during the early generic wound response (Cazet et al., 2021). However, in our study HyKayak expression continuously increased throughout the entire head regeneration process (Fig. 3E and 4E) including the morphogenesis stages (24-48 hrs post-amputation). Another study reported that inhibition of the JNK pathway (which disrupts formation of the AP-1 complex) resulted in upregulation of HyWnt3 expression in both, head and foot regenerates (Tursch et al., 2022). This result might support our hypothesis, but it only included the first 6 hours after amputation, similar to Cazet’s research. Therefore, it appears that HyKayak and fos_Cazet may have opposing roles in the regulation of Wnt-gene expression and are possibly activated by different signaling pathways depending on the stages of regeneration.

      • On page 12 the authors conclude based on gene expression in inhibitor treatment that there is a “change in complex composition of the two transcription factors.” This is something which would require biochemical evidence and I therefore suggest they remove this entirely. * Answer:

      we have removed this sentence

      • The authors use experiments in Craspedacusta to test their hypothesis of the role of Wnt and Notch signaling in Hydra. There is, in my opinion, an incorrect logic here. Regardless of the outcome, the roles of Wnt and Notch could conceivably be different in the two species and therefore testing hypothesis from one is not possible in the other. The authors should reframe their discussion of this to be more of a comparative framework. Moreover, the results do not necessarily indicate what the authors say. In Hydra Notch signaling is required to form the hypostome/mouth and this is not the case in Craspedacusta while Wnt signaling is required. The authors do not cite an important study from another Hydrozoan Hydractinia (Gahan at al.,2017). In that study the authors show that DAPT inhibits tentacles during regeneration but that the hypostome (or at least the arrangement of neurons and cnidocytes around the mouth) forms normally. This would indicate that in Hydractinia the process of head formation is different to in Hydra and would be congruent with what is shown here in Craspedacusta. This should be more thoroughly discussed, and all relevant literature cited.* Answer:

      We have concentrated our Craspedacusta work on Notch-signalling now. We only show that DAPT does not inhibit the regeneration of Craspedacusta heads. We have included new data showing that nevertheless it has an effect on the expression of hypothetical Notch target genes, but not on CsWnt3 (new Fig. 7). We have re-written our discussion accordingly and included the Hydractinia-work about Notch (Gahan2017). Although the Hydractinia paper lacks gene expression studies making it difficult to directly compare with the Hydra data, it supports our claim that Notch is required for regeneration of polyps with head and tentacles. We indeed do not know anything about Wnt-signalling in Craspedacusta. Our new results show that it is probably expressed in the head, because we observe very low levels of expression in the polyps after head removal, which increases considerably during regeneration of the head. This was included in the results:

      Results:

      “Finally, we investigated the expression of the Craspedacusta Wnt3-gene and its response to DAPT treatment during head regeneration. We observed low expression level of CsWnt3 after head removal (t=0), which dramatically increased as the head regenerated, suggesting that Wnt3 is expressed in the head of Craspedacusta polyps as it is in the head of other cnidarians including Hydra, Hydractinia and Nematostella (Hobmayer et al., 2000; Kusserow et al., 2005; Plickert et al., 2006). In accordance with having no effect on head regeneration, DAPT also did not inhibit CsWnt3 expression during this process in Craspedacusta. This is opposite to the situation in Hydra. If CsWnt3 would be involved in the Craspedacusta head regeneration, this could explain the failure of DAPT to interfere with this process”.

      Discussion part

      “Head regeneration also occurs in the colonial sea water hydrozoan Hydractinia. Colonies consist of stolons covering the substrate and connecting polyps, including feeding polyps, which have hypostomes and tentacles, and are capable of head regeneration, similar to Hydra polyps. Wnt3 is expressed at the tip of the head and by RNAi mediated knockdown it was shown that this gene is required for head regeneration (Duffy et al., 2010). In the presence of DAPT, Gahan et al observed that proper heads did not regenerate, similar to Hydra. However, they observed regeneration of the nerve ring around the hypostome indicating the possibility that hypostomes had been regenerated. Unfortunately, this study did not include gene expression data and therefore it is not clear whether Wnt3 expression was affected or not (Gahan et al., 2017).

      …..

      An interesting question was whether regeneration of cnidarian body parts, which are only composed of one module, also requires Notch-signalling. This is certainly true for the Hydra foot, which regenerates fine in the presence of DAPT (Käsbauer et al. 2007). Moreover, we tested head regeneration in Craspedacusta polyps, which do not have tentacles, and show that DAPT does not have an effect on this regeneration process. This corroborates our idea that Notch is required for regeneration in cnidarians, when this process involves two pattern forming processes to produce two independent structures, which are controlled by different signalling modules. This would be the case for the Hydra and for the Hydractinia heads, but not for Craspedacusta. ”

      Moreover, we indicate at the end of our discussion that further studies about head regeneration in Craspedacusta and the genes involved would be desirable. We believe this would be beyond the scope of the current paper and we are working on a new Craspedacusta study.

      “Future studies on expression patterns of the genes that control formation of the Hydra head, including Sp5 and Alx in Craspedacusta could provide insights into the evolution of cnidarian body patterns. Sp5 and Alx appear to be conserved targets of Notch-signalling in the two cnidarians we have investigated. Wnt-3, while being inhibited by Notch-inhibition in Hydra head regenerates, is not a general target of Notch signalling. It was not affected by DAPT in our comparative transcriptome analysis (Moneer et al. 2021b) on uncut Hydra polyps, and it was also not affected by DAPT in regenerating heads of Craspedacusta.”

      • From reading the manuscript I do not fully understand the model the authors put forward. It is unclear what "coordinating two independent pattern forming systems" really means. It might be beneficial to make a schematic illustration of the model and how it goes wrong in both sets of inhibitor treatments. * Answer:

      We have edited the manuscript considerably and explained what we mean with the two pattern forming systems. It starts with the abstract:

      Hydra head regeneration consists of two parts, hypostome/organizer and tentacle development.”

      Thus, in accordance with regeneration of two head structures we find two signaling and gene expression modules with HyWnt3 and HyBMP4 part of a hypostome/organizer module, and BMP5/8, HyAlx and b-catenin part of a tentacle module. We conclude that Notch functions as an inhibitor of tentacle production in order to allow regeneration of hypostome/head organizer.

      “Polyps of Craspedacusta do not have tentacles and thus, after head removal only regenerate a hypostome with a crescent of nematocytes around the mouth opening. This corroborates the idea that Notch-signaling mediates between two pattern forming processes during Hydra head regeneration”

      We have included the description of the organizer concept in the introduction, because we consider this relevant for our model:

      “The “organizer effect” entails a “harmonious interlocking of separate processes which makes up development”, or a side-by-side development of structures independently of each other (Spemann, 1935). In addition to inducing the formation of such structures, the organizer must ensure their patterning (Anderson and Stern, 2016). With reference to Hydra’s hydranth formation after head removal or transplantation, this involves the side-by side induction of hypostome tissue and tentacle tissue. Moreover, it includes the establishment of a regularly organized ring of tentacles with the hypostome doming up in the middle. The function of the Hydra“center of organization” would then be to pattern hypostome and tentacles and to allow for their harmonious re-formation after head removal”.

      In the discussion we integrate the organizer concept with the Gierer-Meinhardt reaction-diffusion models which still explain many aspects of Hydra development.

      Is Notch part of the organizer? The organizer is defined as a piece of tissue with inductive and structuring capacity. Notch is expressed in all cells of Hydra polyps (Prexl et al., 2011) and overexpression of NICD does not induce second axes all over the Hydra body column (Pan et al., 2024), as seen with overexpression of stabilized b-catenin (Gee et al., 2010). Moreover, Notch functions differently during regeneration after apical and basal cuts. Phenotypically during head regeneration in DAPT, we clearly recognize a missing inhibition of tentacle tissue after apical cuts and missing inhibition of head induction after basal cuts (Pan et al., 2024). We would thus rather suggest that the organizer activity of Hydra tissue utilizes Notch-signaling as a mediator of inhibition. As our study of transgenic NICD overexpressing and knockdown polyps had suggested, the localization of Notch signaling cells depends on relative concentrations of Notch- and Notch-ligand proteins, which are established by gradients of signaling molecules that define the Hydra body axis (Pan et al., 2024; Sprinzak et al., 2010) . This is in very good agreement with a ”reaction-diffusion-model” provided by Alfred Gierer and Hans Meinhardt (Gierer and Meinhardt, 1972; Meinhardt and Gierer, 1974) suggesting a gradient of positional values across the Hydra body column. This gradient may determine the activities of two activation/inhibition systems, one for tentacles and one for the head. When the polyps regenerate new heads, Notch could provide inhibition for either system, depending on the position of the cut.

      We provide a new Fig. 8., which clearly illustrates the effects of DAPT and iCRT14 on hypostome and tentacle regeneration.

      Minor: • The abstract could be rewritten to have more of an introduction to the problem rather than jumping directly into results. It would also be beneficial if the abstract followed the logic of the paper.

      Answer: We agree and have re-written the abstract.

      • In Figure 3 and 4 it is not clear why they are divided into A and B. It appears that the categorization of genes into different groups lacks a clear rationale. This seems totally unnecessary. In addition, the order in which the genes are described in the text does not match what is seen in the figure making it confusing to follow. • In Figure 5 the authors use two different types of charts and I would stick with one. B is much better as it shows the individual data points as well as other information. I would use this throughout including in Figure 3 and 4. *

      __Answer: __

      We changed Fig. 3, 4 and 5 according to these comments and now present the data in one format over all three figures, in scatterplots (more detailed answer above).

      We are now describing the results in the order of the figures, with A and B omitted.

      Figure S3 is missing a description of panel C.

      In figure S3 it is not clear why the inhibitor was removed and not kept on throughout the experiment. Please discuss. __Answer: __

      Fig. S3 was removed.

      Figure S4 has no A or B in the figure, only in the legend. __Answer: __

      We have included A and B…

      *Reviewer #1 (Significance (Required)):

      Although some of the authors data appear to be novel I find the study makes only minor progress on the questions. In particular the authors do not properly cite the relevant literature and to put their manuscript into the correct context. The new model proposed by the authors is based entirely on qPCR data which is not thoroughly analyzed and are not strong enough in the absence of information about the spatial expression the genes they discuss. The proposal of HyKayak as a negative regulator of Wnt3 is interesting but the authors do not provide any solid direct evidence for this (ChIP, EMSA etc) and it is somewhat in disagreement with other models of bZIP function in the literature (which again are not discussed).*

      The manuscript is of limited general interest. It has a number of interesting observations which would be of interest to the Hydra community and the broader cnidarian community. The study lacks contextualization within a broader framework, whether it be in the context of regeneration or Wnt/Notch signaling. This limitation may narrow the overall interest in it.

      Answer:

      Our previous analysis of the effect of Notch on head regeneration in Hydra (Münder 2013) had suggested the inhibition model, which is part of Fig. 8. We show now that during head regeneration in Hydra formation of two structures is guided by different signaling/transcription modules, one using Wnt3 and BMP4, but not b-catenin; and one using BMP5/8 and b-catenin. We suggest that Notch functions as an inhibitor “of use” to the organizer when the “two-part” head structure is regenerated.

      We agree that our original manuscript was not well enough written to clearly put it into developmental context. We now focus the discussion of our work sharply on the organizer problem and think that the conclusions are of great general interest. In a simple view they suggest that the function of the Hydra head organizer is to allow harmonious development of head and tentacles, which we consider separate, and on a molecular basis independently regulated parts of the Hydra head. Notch signaling, in our interpretation, is an instrument of the organizer. Our comparison with Craspedacusta illustrates this idea. Craspedacusta only regenerates one head structure, which is possible in the absence of this instrument (also see reviewers 3 and 4).

      Concerning HyKayak, there is no disagreement with other authors as we analyze a fos-gene different from the one discussed by Cazet et al (see above). We have conducted a rescue experiments as suggested by reviewer 3 with the Kayak-inhibitor and with HyKayak shRNAi knockdown, however, rescue of the phenotype was not achieved although HyWnt3 was upregulated after DAPT treatment in the knockdown group. We attribute this to the very strong effect of DAPT. We have adjusted our hypothesis and only suggest that HyKayak could be a target for the Notch-induced repressor genes (e.g.HyHes). We mentioned this failed rescue in the manuscript (answer for see reviewer 3). Further experiments, e.g Chip/EMSA constitute a new project on the basis of these ideas and should be reserved for further studies of the Kayak-function in Hydra.

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

      *The study investigates the role of Notch and beta-catenin signaling in coordinating head regeneration in Hydra. It combines gene expression dynamics, inhibitor treatments, and comparisons with Craspedacusta polyps to propose a lateral inhibition model for Notch function during Hydra head regeneration, mediating between two pattern-forming systems.

      Three main concerns arise from this work:*

      • Lack of spatial expression data: The study proposes a model based on pattern-forming systems but falls short of providing direct spatial expression data for the genes under consideration in both control and treated scenarios. This gap weakens the empirical support for the proposed model. __Answer:*__

      The expression patterns for most of the presented genes including HyAlx and HyWnt3 in the presence and absence of DAPT have been published before (Münder 2013). Expression patterns for all other genes during regeneration (except Hykayak) are already known from literature. For Hykayak we have included expression data from Siebert et al (single cell transcriptome analysis) in the supplementary material. For iCRT14 treatment, we carried out a FISH-experiment and showed that HyWnt3 is expressed in the normal pattern at the hypostome. For further genes after DAPT and iCRT-treatment in situ hybridisation data are indeed lacking (e.g. BMP5/8). However, we have analyzed some very strongly downregulated regulated genes (e.g. HyAlx completely downregulated by iCRT14, all HyWnts and BMP2-4completely downregulated by DAPT) and for those in situ hybridisation could (1) be difficult due to low expression in treated samples and (2) may not be informative.

      • Clarity and relevance of Craspedacusta comparisons: The section discussing the regeneration in Craspedacusta polyps appears somewhat disjointed from the main narrative, with its contribution to the overarching story of Hydra regeneration remaining unclear. *

      Answer:

      We had not intended to explain gene expression during Craspedacusta head regeneration but wanted to prove our hypothesis that Notch is needed to allow side-by-side development of two newly arising structures, which use different signalling modules during head regeneration. That Notch is __not __needed for the regeneration of Craspedacusta, a polyp without tentacles, appears to strengthen our main hypothesis. In order to connect this point more clearly to the narrative we have included new data. We show that CsWnt3 expression lowers after head removal and rises when the head regenerates, indicating CsWnt3-expression in the head of Craspedacusta polyps. Moreover, we show now that Notch in Craspedacusta may have similar target genes as in Hydra (e.g. Sp5 and Alx), might also affect nematocyte differentiation as in Hydra, but does not inhibit Wnt3 expression. We also acknowledge that a precise understanding of the molecular pathways for head regeneration in Craspedacusta requires further work and have removed the results of iCRT14 treatment because of our lack of knowledge about the role of b-catenin in Craspedacusta patterning. Citations from our changed text are found in the answer to reviewer 1.

      • Accessibility of the text: The study's presentation, including its title, abstract, and main text, presents challenges in terms of clarity and accessibility, making it difficult for readers to follow and understand the research's scope, methodologies, and conclusions.*

      • *

      Answer:

      We agree and have completely re-written the abstract, and large parts of the introduction and discussion (also see above answer for reviewer 1).

      Reviewer #2 (Significance (Required)):

      In conclusion, while the study aims to advance our understanding of the complex signaling pathways governing Hydra head regeneration, it necessitates significant revisions. Enhancing the empirical evidence through detailed spatial patterning data, clarifying the comparative analysis with Craspedacusta polyps, and __refining the narrative __to improve accessibility are critical steps needed to solidify the study's contributions to the field.

      Answer:

      By including Kayak-expression data from Siebert et al and indicating the places of major expression of all analysed genes schematically in the Figs describing the qPCR data we revised our manuscript. We have added new data about Craspedacusta and believe that our re-written manuscript refines the narrative by focusing on the organizer (see answer to reviewer 1).



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

      Major comments:

      - In the abstract, the authors assert that their findings "indicate competing pathways for hypostome and regeneration." However, the nature of this competition and its resolution is not adequately elucidated within the manuscript. The term "competition" lacks context and clarity, leaving the reader without a clear understanding of what pathways are competing, for what, and how this competition is resolved during regeneration. Furthermore, this concept is not further explored or referenced throughout the remainder of the manuscript, leaving it somewhat disconnected from the main body of the research. It is recommended that the authors either revise the statement in the abstract to provide more clarity on the competing pathways and their implications for regeneration, or alternatively, if the authors believe there is sufficient evidence to support the claim of competing pathways, they should expand upon this point within the main body of the manuscript. Additional argumentation and evidence would be necessary to substantiate such a claim and provide a deeper understanding of the mechanisms underlying regeneration in Hydra.

      Answer:

      We agree and have removed any reference to “competing” pathways from the abstract and the main text.

      - The abstract makes a significant assertion regarding the mechanism by which Notch signaling impacts the expression of HyWnt3, suggesting that it operates by inhibiting HyKayak-mediated repression of HyWnt3 rather than directly activating transcription at the HyWnt3 promoter. This claim is central to the goals outlined in the study, which aim to elucidate the functioning of Notch signaling in HyWnt3 expression. To bolster this assertion, it would be prudent for the authors to conduct experiments demonstrating the mediating role of Kayak. Specifically, demonstrating that downregulation of Kayak through RNAi can rescue the DAPT-mediated downregulation of Wnt3 would provide strong support for the authors' claim. Additionally, while not strictly necessary, it would be beneficial to investigate whether chemical inhibition of Wnt can rescue the phenotype resulting from Kayak RNAi. Conducting and analyzing such experiments within a 2-3-month revision period should be feasible given that the authors already possess all necessary materials and have developed the required methods. These additional experiments would not only strengthen the evidence supporting the authors' claim but also provide further insights into the regulatory mechanisms at play in Notch signaling and HyWnt3 expression.

      • *

      Answer:

      We have conducted the suggested rescue experiments with the kayak-inhibitor, however, rescue was not achieved. We also tried rescue experiments by combining DAPT treatment and Kayak shRNA knockdown. HyWnt3 was slightly upregulated after DAPT treatment in the Kayak knockdown group but the phenotype could not be rescued. We are therefore now only state that HyKayak could be a target for the Notch-induced repressor genes (e.g.HyHes). We mentioned the failed rescue experiments in the manuscript:

      Results:

      *The up-regulation of HyKayak by DAPT suggests that HyKayak may serve as a potential target gene for Notch-regulated repressors including HyHes and CnGsc, potentially acting as a repressor of HyWnt3 gene transcription. *

      Discussion:

      We therefore suggest that the Hydra Fos-homolog HyKayak inhibits HyWnt3 expression and can be a target for a Notch-induced transcriptional repressor (like HyHes) in the regenerating Hydra head. Nevertheless, we were not able to rescue the DAPT-phenotype by inhibiting HyKayak, neither by using the inhibitor nor by shRNA-treatment, probably due to the strength of the DAPT effect. Therefore, we cannot exclude that Notch activates HyWnt3 directly, or that it represses unidentified Wnt-inhibitors through HyHes or CnGsc.

      - The usage of the term "lateral inhibition" in the title and abstract of the manuscript carries specific implications, as it is commonly associated with distinct mechanisms in the context of Notch signaling and reaction-diffusion systems. Notably, in the Notch signaling context, lateral inhibition typically refers to the amplification of small differences between neighboring cells through direct interactions, facilitated by the limitations of Notch signaling to immediate neighbors. Conversely, in reaction-diffusion systems, such as the Gierer-Meinhardt model, lateral inhibition describes long-range inhibition associated with pattern formation.

      Given this discrepancy, it is crucial for the authors to clarify their interpretation of "lateral inhibition" to avoid ambiguity and ensure accurate understanding. If they are referring to Notch-specific lateral inhibition, they should provide evidence of adjacent localization of Notch and Delta cells to support their argument. Alternatively, if they are invoking the concept of long-range inhibition described by the Gierer-Meinhardt model, they must explain how a membrane-tethered ligand like Notch can exert effects beyond one cell diameter from the signaling center.

      * Regardless of the interpretation chosen by the authors, addressing this clarification will have significant implications for the subsequent treatment of their arguments. Depending on their chosen interpretation, experimental demonstrations may be necessary to substantiate their claims, which could be laborious and time-consuming. However, such demonstrations are essential for establishing the validity of the term "lateral inhibition" as used in the title and abstract of the manuscript.*

      Answer:

      We agree with the reviewer concerning the term “lateral inhibition” and have now removed it. Instead, we have emphasized that our data clearly show during apical regeneration a Notch-mediated inhibition of tentacle tissue formation. We also discuss data from our most recent publication (Pan 2024) showing that this is the opposite at basal cuts, where the loss of Notch function leads to the regeneration of two heads. We then discuss this in the context of the Gierer-Meinhardt Model and in the context of the organizer (also see above in answer to reviewer 1):

      It is true that it is difficult to reconcile the long-range signaling processes, on which the Gierer-Meinhardt model is based with the cell-cell interactions mediated by Notch-signaling. We have now published a mathematical model to explain our understanding of this for the role of Notch during budding and in steady state animals (Pan2024), which is based on work by Sprinzak et al 2010. For head regeneration, we do not have such a model yet. Here we are looking at expression patterns changing over time. Therefore, we assume waves of gene expression, relying on the autoinhibitory function of the HyHes-repressor. This is included in the discussion:

      In addition, the gene expression dynamics for many of the analyzed genes appears in wave-like patterns in some experiments (see Figs S3 and S4). As we have only four time points measured, we cannot draw strong conclusions from these observations, except that some of the deviations in our data points (e.g. 48 hrs HyHes) might be caused by oscillations. Nevertheless, we propose that the dynamic development of gene expression patterns over the time course of regeneration hint at a wave like expression of Notch-target genes (e.g. HyAlx, (Münder et al., 2013; Smith et al., 2000)). Hes-genes have been implicated in mediating waves of gene expression, e.g. during segmentation and as part of the circadian clock (Kageyama et al., 2007). This property is due to the capability of Hes-proteins to inhibit their own promoter. Future models for head regeneration in Hydra should consider the function of Notch to inhibit either module of the regeneration process and the potential for the Notch/Hes system to cause waves of gene expression. Such waves intuitively seem necessary to change the gene expression patterns underlying morphogenesis during the time course of head regeneration.

      - The utilization of Craspedacusta as a comparative model in the argumentation of the manuscript appears somewhat unclear. The authors posit that Notch is essential for organizer emergence in Hydra, while Wnt is not necessary, as indicated by the observed effects of iCRT14 beta-catenin/TCF inhibition. However, in Craspedacusta, which lacks tentacles but possesses an organizer, one might anticipate a conserved requirement for organizer formation but not tentacle development. Therefore, it would be reasonable to expect that Craspedacusta would still form an organizer under iCRT14 treatment but would not depend on Notch signaling, as the necessity to separate tentacle formation from organizer formation is absent. The authors' observation that Craspedacusta fails to form an organizer under iCRT14 treatment partially aligns with these expectations. However, the complexity of the results suggests a need for a deeper understanding of the involvement of different pathways in Craspedacusta. Before applying inhibitors, it would be crucial to elucidate the spatiotemporal differences in the expression of relevant Wnt and Notch pathway components between Hydra and Craspedacusta. This knowledge would provide valuable insights into the specific roles of these pathways in organizer formation and tentacle development in both species, helping to clarify the observed differences in response to iCRT14 treatment. Additionally, considering the possibility of differential sensitivity to iCRT14 (see comment below) between Hydra and Craspedacusta would be essential for accurately interpreting the results and drawing meaningful conclusions regarding the involvement of Notch and Wnt signaling pathways in these processes.

      Answer:

      We have clarified in our re-written manuscript that the organizer functions in Hydra heads and head regeneration to harmonize the development of two independent structures (see answer for reviewer 1) and that Notch-signalling is an instrument to achieve this. Craspedacusta polyps do not have tentacles, thus we do not see two independent structures. Correspondingly, we see that they do not need Notch-signaling. We do not know whether they have organizer tissue, because they are too small to perform transplantation experiments. Similarly, in situ hybridisation experiments to look for CsWnt expression are hard to envisage. What we have now done during the revision of this paper are RT-qPCR experiments to follow the expression of CsWnt3 after head removal until a new head is formed. This indicated the localization of CsWnt3 expression in the head (citations in response to reviewer 1).

      We agree that the role of Wnt/b-catenin for Craspedacusta cannot be sufficiently described with our iCRT14 experiment and therefore removed it. To strengthen the DAPT data, we also examined Craspedacusta homologs of the Hydra Notch-target genes that we had previously identified (Moneer2021). We found that expression of CsSp5 and CsAlx were inhibited by DAPT. This was also true for the nematocyte gene NOWA (see new Fig. 7). In Hydra, DAPT blocks one important differentiation step of nematocytes and therefore the expression of all genes expressed in differentiating capsule precursors, including NOWA is inhibited, while the number of mature capsules does not change. To see the same DAPT effect on NOWA-expression in Craspedacusta reassured us that DAPT had entered the animals and might also have a similar effect on nematocytes as in Hydra.

      Minor comments - The concentration-dependent effects of iCRT14 on beta-catenin signaling, as demonstrated by Gufler et al. 2018, suggest that the efficacy of inhibition may vary depending on the concentration used. Specifically, Gufler et al. found that a concentration of 10µM was sufficient for efficient inhibition of beta-catenin signaling. However, in the current study, the authors utilized a concentration of 5µM of iCRT14. Given the central role of the observed effects, particularly the persistence of Wnt3 expression, in the argumentation of the manuscript, it is plausible that these effects could be attributed to partial inhibition resulting from the lower concentration of iCRT14 used in the study. To address this potential limitation, the authors could consider conducting a quick examination of the effects of 10µM iCRT14 or utilizing other inhibitors of beta-catenin/TCF interaction, such as iCRT3. By comparing the effects of different concentrations or alternative inhibitors, the authors could ascertain whether the observed effects are indeed attributable to partial inhibition from 5µM iCRT14, or if they persist despite higher concentrations or alternative inhibitors. This additional experimentation would provide valuable insights into the specificity and efficacy of the inhibition and strengthen the validity of the conclusions drawn regarding the role of beta-catenin signaling in the observed phenomena.

      Answer:

      The iCRT14 concentration was adjusted to 5 µM because the initial 10µM proved to be too toxic. 5µM also produced the same phenotypes and results as seen before. Cazet et al. also used 5 µM iCRT14 in their study.

      - The use of Generalized Additive Models (GAMs) in Figures 3 and 4 to present the time series qPCR results may introduce some challenges in interpretation due to the potential for distortion of values at specific time points based on neighboring ones. Given the relatively low time resolution of the data, this approach could lead to a distorted depiction of the temporal dynamics. For instance, in Figure 3B, where Wnt3 peaks at 10 hours, the absence of measurements between 8 and 24 hours introduces uncertainty regarding the accuracy and reliability of this peak at 10 hours.

      * To address these concerns and enhance clarity, it may be advisable for the authors to consider presenting the data using simple boxplots instead of GAMs. Boxplots provide a more straightforward visualization of the distribution of data at each time point, allowing for a clearer interpretation of trends and fluctuations over time. This approach would mitigate the potential for distortion introduced by GAMs and provide a more accurate representation of the temporal dynamics observed in the qPCR results*

      • *

      Answer:

      We agree and have changed the data representation to simple scatterplots (see answers for reviewer 1).

      - The comparison of the effects of iCRT14 versus DAPT treatments would benefit from having consistent gene expression data across both treatments. However, in Figure 4A, there are fewer genes tested compared to Figure 3A, with Hes and Kayak omitted. While the authors interpretation suggests that these genes may not change after iCRT14 treatment due to their upstream position in the signaling pathways, it is essential to empirically demonstrate this relationship, as it is central to the conclusions drawn. To address this gap in the analysis, it would be valuable for the authors to provide a time series of differential expression for Hes and Kayak following iCRT14 treatment.

      Answer:

      We have provided a time series for expression of HyHes and HyKayak in responses to iCRT14 treatment during regeneration (see Fig.4).

      “We found that the expression the Notch-target gene HyHes remained similar to control regenerates up to 24 hrs, but then was attenuated (Fig. 4A), possibly due to failure of tentacle boundary formation, the tissue where HyHes is strongly expressed…The expression of HyKayak was decreased at 8 hrs after head removal in the presence of iCRT14, came back to normal up to 36 hrs and was suddenly increased after 48 hrs (Fig. 4E), correlating with inhibition of the HyHes repressor. There were no significant changes in the expression dynamics of HyBMP2/4 and HyBMP5/8b between iCRT14-treated regenerates and controls (Fig. 4F, G).”

      - The analysis of the impact of chemical inhibition of Notch and Wnt signaling in Figure 7 schematic highlights changes in spatial expression patterns of the target genes. However, the interpretation of their impact primarily relies on qPCR data. As evident from Figure 7, when Notch is inhibited, it is anticipated that Kayak expression will shift from the area of the tentacles to the tip. This spatial shift in expression patterns is a critical aspect of the authors' arguments, especially considering the centrality of Kayak in their findings. Notably, similar spatial expression patterns have been demonstrated for Alx using FISH in Pan et al., available on BioRxiv. Given the importance of Kayak in the presented arguments, it is advisable to also investigate its spatial expression patterns using techniques such as FISH.

      • *

      Answer:

      We have, instead of FISH-experiments, included expression data for HyKayak from Siebert et al 2019 (single cell transcriptome data) in Fig. S1D, which show its expression in head- and battery cells (tentacle cells). This is similar to HyAlx. Therefore, Kayak-FISH would be expected to reveal expression of the gene at the tip of the regenerate the whole time, similar to HyAlx, because tentacle gene inhibition or patterning does not occur (see Münder 2013). Due to the failure of our rescue experiment to demonstrate the function of kayak we have omitted kayak from Fig. 8 and only mention in the discussion that it could be a target for Notch activated transcriptional repressors, like HyHes or CnGsc.

      Reviewer #3 (Significance (Required)):

      *The paper introduces novelties to the field of regeneration and developmental biology by leveraging Craspedacusta polyp as a novel model system for investigating the evolutionary and developmental dynamics of tentacles. In doing so, it sheds new light on the intricate mechanisms underlying tentacle formation and patterning. Furthermore, the study implicates Kayak in the regulation of Wnt3, adding a fresh perspective to our understanding of the molecular pathways governing Hydra regeneration. Notably, the results of the research challenge the prevailing notion of autoregulation of Wnt3, which has long been considered fundamental to organizer formation in Hydra. While these findings offer intriguing insights, further investigation will be crucial to conclusively ascertain the validity of this assertion. *

      • *

      Despite the clarity of the data presented, the interpretation and integration of these findings in the manuscript are lacking. The narrative at times feels disjointed, with different storylines loosely connected. While the findings are intriguing and merit publication, a substantial revision of the manuscript is necessary to provide a more coherent and illuminating interpretation of the results. *The implications of this research extend beyond the specific confines of Craspedacusta polyp and Hydra biology. It holds significant relevance for both the Hydra biology community and the broader field of Notch signaling research. *

      By highlighting the pivotal role of Notch signaling in regeneration and patterning within Hydra, the study enriches our comprehension of this model organism and its evolutionary adaptations. Moreover, it provides a valuable lens through which the evolution of Notch signalling cascades can be examined. This interdisciplinary approach underscores the interconnectedness of diverse biological systems and underscores the importance of exploring novel model organisms to unravel the complexities of evolution and development.

      • *

      Answer:

      We have edited the manuscript considerably and re-written the introduction and the discussion parts. We are focusing on integrating this work with the organizer concept in developmental biology, and on the Gierer-Meinhardt-model, and point out that Notch-signaling is required for the development of two head structures by inhibiting the development of either one during head regeneration, which is necessary to enable the development of the other one. Which one is inhibited depends on the positional value of the tissue where the cut occurs. Craspedacusta polyps do only have one structure. We suggest that this is why head regeneration does not require Notch-signalling in Craspedacusta. In contrast, as we have included in our discussion now, Hydractinia polyps, again with head/mouth and tentacles, require Notch-signaling for head regeneration (according to Gahan 2019), see also answers for reviewers 1 and 2.



      Reviewer #4 (Evidence, reproducibility and clarity (Required)):

      Major comments:

      The conclusions from the experiments are drawn accurately, not overstating the results. The main conclusion, that in Hydra Notch pathway mediates between two patterning modules, hypostome and tentacle forming modules, is supported by in situ hybridization and qPCR analyses of hypostome and tentacle specific genes.

      OPTIONAL. Authors hypothesize, that Notch maintains expression of Wnt3 vie its targets, transcriptional repressors Goosecoid or Hes, which halt the expression of Wnt3 repressor HyKayak. Epistatic relationships between Notch, Goosecoid or Hes and HyKayak could be tested, first, by combining pharmacological inhibition of Notch by DAPT with shRNA-mediated knockdown and second, in double knockdowns generated by electroporating shRNAs for two genes simultaneously. If the proposed in the pathway relationships are correct the repressive effect of DAPT treatment on an organizer regeneration should be rescued in HyKayak shRNA-mediated knockdown. Regeneration of an organizer also should occur in Notch/HyKayak and Goosecoid (Hes)/HyKayak shRNA-mediated double knockdowns. Electroporation of shRNAs for multiple genes is an effective and quick way to generate double and triple knockdowns. The proposed experiments will much strengthen the conclusions drawn from this study. Given that the authors have successfully used shRNA-mediated technique to generate HyKayak knockdown animals, they should be able to complete the proposed experiments within in a couple of months. Answer:

      We very much like the suggested strategy to probe the regeneration pathways by shRNA-mediated knockdown experiments- this will be a basis for future investigations.

      We conducted the suggested rescue experiment by combining the DAPT treatment and Kayak shRNA knockdown. HyWnt3 was slightly upregulation after DAPT treatment in the Kayak knockdown group. However, this upregulation did not rescue the organizer’s regeneration. We think that the effect of DAPT is too strong. We have included this in the discussion of our results (see answer for reviewer 2).

      • The data are presented in a logical and clear manner. The paper is easy to read, and the conclusions are explicit for each experimental section. The methodology is described in detail and should be easy to reproduce.*

      • All experiments are done with multiple biological and technical replicates. However, the description of statistical analysis used in each case is missing, p values and error bars are missing in Fig. 2B and Fig. S4. Author should add this information in the main text or in the figure legends.*

      Answer:

      The statistical information was now added in the methods section.

      Minor comments:

      • Fig. 1E. It would be more convincing to present tentacle and hypostome regeneration data separately, comparing hypostome regeneration in treated animals with DMSO control, and in a separate analysis comparing tentacle regeneration with control. Provide the description of statistical method, p values and error bars. If authors prefer to stick to the current way of presenting they should also provide description of statistical analysis used and statistical data.*
      • *

      Answer:

      We changed the representation in Fig. 1E. We now use scatter plots in the main text with p-values added, and explained the statistics of the GAM representation in the supplementary material.

      • Results, section 4 Kayak. Authors use T5424 inhibitor to block the potential interactions between HyKayak with HyJun. The resulted increase in Wnt3 expression measured by qPCR clearly supports the idea of HyKayak being a repressor of Wnt3. However, authors are going further and present the phenotype of T5424 treatment, shortening of the tentacles. Many factors can influence the length of the tentacles. For example, shortening of tentacles is a strong indication of poisoning or animal being in general unwell. At a concentration double of the one used in the experiment T5424 causes a disintegration of the animals (Fig. 3S). It would be more convincing if the authors could provide an in situ hybridization image showing an expansion of Wnt3 expression domain down the hypostome. This is the result one would expect from the inhibition of HyKayak which, according to the proposed mechanism, restricts Wnt3 spatial expression to the most apical portion of the regenerating tip. Alternatively, authors could try to see if T5424 rescues the inhibition of an organizer formation resulted by DAPT treatment. The latter experiment might be difficult to perform due to a possible toxic effect of multidrug treatment. I suggest that authors either include the proposed experiments or leave the results of the Fig S3 out.*

      Answer:

      According to this suggestion we have removed the phenotypes of polyps after treatment with T5424.

      • Results, section 3.2, paragraph 4. 'This also applies for the suggested Hydra organizer gene CnGsc, and BMP2/4 (Broun, Sokol et al. 1999). Please, insert the citation for BMP2/4.*

      • *

      Answer:

      We inserted the citation for BMP2-4 (Watanabe 2014).


      Reviewer #4 (Significance (Required)):

      *Significance:

      The current study is a continuation of the author's previous work where they have characterized Notch pathway in Hydra and showed its role in the regeneration of an organizer and patterning of Hydra head. Here, they present the study of Notch pathway in the context of b-catenin pathway, a pathway that has been shown to be essential for the axis induction and patterning in Hydra. The authors challenge this dogma and show, that during head regeneration b-catenin transcriptional activity is not required either to maintain the expression of wnt3 nor to acquire an inductive activity of the regenerating organizer. Second, they show, that transcriptional fos-related factor Kayak is negatively regulated by Notch-signaling and, in turn, represses transcription of Wnt3. Based on those findings authors propose a function of the Notch pathway in Hydra head regeneration, particularly in spatial separation of the hypostome/organizer module from the tentacle module. The role of Notch pathway in lateral inhibition is well documented in bilaterians. However, in Cnidaria, a sister group to Bilateria, the function of Notch was so far restricted to neurogenesis. This study is very important for our understanding of the evolution of morphogenesis as it shows the ancient role that the Notch pathway is playing in axial patterning, possibly, through lateral inhibition.

      This study can be of a great interest to both researchers specializing in cnidarian development and to a broader audience interested in the evolution of morphogenesis.*

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      Referee #4

      Evidence, reproducibility and clarity

      This is a very nice study exploring the function of Notch pathway in Hydra, a member of early Metazoa Cnidaria. The main conclusions of the study are:

      1. -catenin pathway is required not for regeneration of Hydra hypostome/ the organizer, as previously thought, but rather for regeneration of tentacles and correct patterning of Hydra head.
      2. During head regeneration Notch pathway, possibly, through lateral inhibition, blocks tentacle fate at the most apical region of the regenerating tip, allowing a hypostome/an organizer to develop. This might occur via the targets of Notch pathway, transcriptional repressors Goosecoid and Hes.
      3. During head regeneration Notch pathway is required to maintain the expression of Hydra organizer gene Wnt3 as well as other canonical wnt genes. This occurs, possibly, through repression of HyKayak, Hydra homologue of a transcriptional fos-related factor Kayak, that, in turn, represses Wnt3.

      Major comments:

      1. The conclusions from the experiments are drawn accurately, not overstating the results. The main conclusion, that in Hydra Notch pathway mediates between two patterning modules, hypostome and tentacle forming modules, is supported by in situ hybridization and qPCR analyses of hypostome and tentacle specific genes.
      2. OPTIONAL. Authors hypothesize, that Notch maintains expression of Wnt3 vie its targets, transcriptional repressors Goosecoid or Hes, which halt the expression of Wnt3 repressor HyKayak. Epistatic relationships between Notch, Goosecoid or Hes and HyKayak could be tested, first, by combining pharmacological inhibition of Notch by DAPT with shRNA-mediated knockdown and, second, in double knockdowns generated by electroporating shRNAs for two genes simultaneously. If the proposed in the pathway relationships are correct the repressive effect of DAPT treatment on an organizer regeneration should be rescued in HyKayak shRNA-mediated knockdown. Regeneration of an organizer also should occur in Notch/HyKayak and Goosecoid(Hes)/HyKayak shRNA-mediated double knockdowns. Electroporation of shRNAs for multiple genes is an effective and quick way to generate double and triple knockdowns. The proposed experiments will much strengthen the conclusions drawn from this study. Given that the authors have successfully used shRNA-mediated technique to generate HyKayak knockdown animals, they should be able to complete the proposed experiments within in a couple of months.
      3. The data are presented in a logical and clear manner. The paper is easy to read, and the conclusions are explicit for each experimental section. The methodology is described in detail and should be easy to reproduce.
      4. All experiments are done with multiple biological and technical replicates. However, the description of statistical analysis used in each case is missing, p values and error bars are missing in Fig. 2B and Fig. S4. Author should add this information in the main text or in the figure legends.

      Minor comments:

      1. Fig. 1E. It would be more convincing to present tentacle and hypostome regeneration data separately, comparing hypostome regeneration in treated animals with DMSO control, and in a separate analysis comparing tentacle regeneration with control. Provide the description of statistical method, p values and error bars. If authors prefer to stick to the current way of presenting they should also provide description of statistical analysis used and statistical data.
      2. Results, section 4 Kayak. Authors use T5424 inhibitor to block the potential interactions between HyKayak with HyJun. The resulted increase in Wnt3 expression measured by qPCR clearly supports the idea of HyKayak being a repressor of Wnt3. However, authors are going further and present the phenotype of T5424 treatment, shortening of the tentacles. Many factors can influence the length of the tentacles. For example, shortening of tentacles is a strong indication of poisoning or animal being in general unwell. At a concentration double of the one used in the experiment T5424 causes a disintegration of the animals (Fig. 3S). It would be more convincing if the authors could provide an in situ hybridization image showing an expansion of Wnt3 expression domain down the hypostome. This is the result one would expect from the inhibition of HyKayak which, according to the proposed mechanism, restricts Wnt3 spatial expression to the most apical portion of the regenerating tip. Alternatively, authors could try to see if T5424 rescues the inhibition of an organizer formation resulted by DAPT treatment. The latter experiment might be difficult to perform due to a possible toxic effect of multidrug treatment. I suggest that authors either include the proposed experiments or leave the results of the Fig S3 out.
      3. Results, section 3.2, paragraph 4. 'This also applies for the suggested Hydra organizer gene CnGsc, and BMP2/4 (Broun, Sokol et al. 1999). Please, insert the citation for BMP2/4.

      Significance

      The current study is a continuation of the author's previous work where they have characterized Notch pathway in Hydra and showed its role in the regeneration of an organizer and patterning of Hydra head. Here, they present the study of Notch pathway in the context of -catenin pathway, a pathway that has been shown to be essential for the axis induction and patterning in Hydra. The authors challenge this dogma and show, that during head regeneration -catenin transcriptional activity is not required either to maintain the expression of wnt3 nor to acquire an inductive activity of the regenerating organizer. Second, they show, that transcriptional fos-related factor Kayak is negatively regulated by Notch signaling and, in turn, represses transcription of Wnt3. Based on those findings authors propose a function of the Notch pathway in Hydra head regeneration, particularly in spatial separation of the hypostome/organizer module from the tentacle module. The role of Notch pathway in lateral inhibition is well documented in bilaterians. However, in Cnidaria, a sister group to Bilateria, the function of Notch was so far restricted to neurogenesis. This study is very important for our understanding of the evolution of morphogenesis as it shows the ancient role that the Notch pathway is playing in axial patterning, possibly, through lateral inhibition.

      This study can be of a great interest to both researchers specializing in cnidarian development and to a broader audience interested in the evolution of morphogenesis.

      The reviewer's field of expertise includes cnidarian development, axial patterning and morphogenesis in Hydra, biochemical pathways in Hydra axial patterning, Hippo pathway regulation and tissue patterning in multiple organisms

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      Referee #3

      Evidence, reproducibility and clarity

      Summary:

      In the reviewed study by Steichele et al., the authors investigate the roles of Notch and Wnt signaling pathways in the regeneration process of Hydra hypostome and tentacles. They observe that treatment with DAPT prevents the emergence of an organizer and hypostome, whereas inhibition of beta-catenin/TCF interaction does not affect organizer formation but hinders tentacle development. The authors delve into the molecular mechanisms underlying these observations, examining the impact of different treatments on the expression of genes crucial for organizer and tentacle emergence. Notably, they identify Kayak as a target of Notch signaling, which is upregulated following DAPT treatment. Furthermore, RNAi against Kayak results in the overexpression of Wnt3, suggesting an inhibitory role of Kayak on Wnt3 expression. This inhibitory effect is corroborated using the Fos/Jun inhibitor T5224. In their investigation, the authors compare the effects of Notch and Wnt signaling inhibition using a polyp species, Craspedacusta, which possesses an organizer but lacks tentacles. They find that while Notch inhibition does not affect this polyp, inhibition of canonical Wnt signaling does.

      Major comments:

      • In the abstract, the authors assert that their findings "indicate competing pathways for hypostome and regeneration." However, the nature of this competition and its resolution is not adequately elucidated within the manuscript. The term "competition" lacks context and clarity, leaving the reader without a clear understanding of what pathways are competing, for what, and how this competition is resolved during regeneration. Furthermore, this concept is not further explored or referenced throughout the remainder of the manuscript, leaving it somewhat disconnected from the main body of the research.

      It is recommended that the authors either revise the statement in the abstract to provide more clarity on the competing pathways and their implications for regeneration, or alternatively, if the authors believe there is sufficient evidence to support the claim of competing pathways, they should expand upon this point within the main body of the manuscript. Additional argumentation and evidence would be necessary to substantiate such a claim and provide a deeper understanding of the mechanisms underlying regeneration in Hydra.<br /> - The abstract makes a significant assertion regarding the mechanism by which Notch signaling impacts the expression of HyWnt3, suggesting that it operates by inhibiting HyKayak-mediated repression of HyWnt3 rather than directly activating transcription at the HyWnt3 promoter. This claim is central to the goals outlined in the study, which aim to elucidate the functioning of Notch signaling in HyWnt3 expression. To bolster this assertion, it would be prudent for the authors to conduct experiments demonstrating the mediating role of Kayak. Specifically, demonstrating that downregulation of Kayak through RNAi can rescue the DAPT-mediated downregulation of Wnt3 would provide strong support for the authors' claim. Additionally, while not strictly necessary, it would be beneficial to investigate whether chemical inhibition of Wnt can rescue the phenotype resulting from Kayak RNAi. Conducting and analyzing such experiments within a 2-3-month revision period should be feasible given that the authors already possess all necessary materials and have developed the required methods. These additional experiments would not only strengthen the evidence supporting the authors' claim but also provide further insights into the regulatory mechanisms at play in Notch signaling and HyWnt3 expression. - The usage of the term "lateral inhibition" in the title and abstract of the manuscript carries specific implications, as it is commonly associated with distinct mechanisms in the context of Notch signaling and reaction-diffusion systems. Notably, in the Notch signaling context, lateral inhibition typically refers to the amplification of small differences between neighboring cells through direct interactions, facilitated by the limitations of Notch signaling to immediate neighbors. Conversely, in reaction-diffusion systems, such as the Gierer-Meinhardt model, lateral inhibition describes long-range inhibition associated with pattern formation.

      Given this discrepancy, it is crucial for the authors to clarify their interpretation of "lateral inhibition" to avoid ambiguity and ensure accurate understanding. If they are referring to Notch-specific lateral inhibition, they should provide evidence of adjacent localization of Notch and Delta cells to support their argument. Alternatively, if they are invoking the concept of long-range inhibition described by the Gierer-Meinhardt model, they must explain how a membrane-tethered ligand like Notch can exert effects beyond one cell diameter from the signaling center.

      Regardless of the interpretation chosen by the authors, addressing this clarification will have significant implications for the subsequent treatment of their arguments. Depending on their chosen interpretation, experimental demonstrations may be necessary to substantiate their claims, which could be laborious and time-consuming. However, such demonstrations are essential for establishing the validity of the term "lateral inhibition" as used in the title and abstract of the manuscript. - The utilization of Craspedacusta as a comparative model in the argumentation of the manuscript appears somewhat unclear. The authors posit that Notch is essential for organizer emergence in Hydra, while Wnt is not necessary, as indicated by the observed effects of iCRT14 beta-catenin/TCF inhibition. However, in Craspedacusta, which lacks tentacles but possesses an organizer, one might anticipate a conserved requirement for organizer formation but not tentacle development. Therefore, it would be reasonable to expect that Craspedacusta would still form an organizer under iCRT14 treatment but would not depend on Notch signaling, as the necessity to separate tentacle formation from organizer formation is absent.

      The authors' observation that Craspedacusta fails to form an organizer under iCRT14 treatment partially aligns with these expectations. However, the complexity of the results suggests a need for a deeper understanding of the involvement of different pathways in Craspedacusta. Before applying inhibitors, it would be crucial to elucidate the spatiotemporal differences in the expression of relevant Wnt and Notch pathway components between Hydra and Craspedacusta. This knowledge would provide valuable insights into the specific roles of these pathways in organizer formation and tentacle development in both species, helping to clarify the observed differences in response to iCRT14 treatment. Additionally, considering the possibility of differential sensitivity to iCRT14 (see comment below) between Hydra and Craspedacusta would be essential for accurately interpreting the results and drawing meaningful conclusions regarding the involvement of Notch and Wnt signaling pathways in these processes.

      Minor comments

      • The concentration-dependent effects of iCRT14 on beta-catenin signaling, as demonstrated by Gufler et al. 2018, suggest that the efficacy of inhibition may vary depending on the concentration used. Specifically, Gufler et al. found that a concentration of 10µM was sufficient for efficient inhibition of beta-catenin signaling. However, in the current study, the authors utilized a concentration of 5µM of iCRT14. Given the central role of the observed effects, particularly the persistence of Wnt3 expression, in the argumentation of the manuscript, it is plausible that these effects could be attributed to partial inhibition resulting from the lower concentration of iCRT14 used in the study. To address this potential limitation, the authors could consider conducting a quick examination of the effects of 10µM iCRT14 or utilizing other inhibitors of beta-catenin/TCF interaction, such as iCRT3. By comparing the effects of different concentrations or alternative inhibitors, the authors could ascertain whether the observed effects are indeed attributable to partial inhibition from 5µM iCRT14, or if they persist despite higher concentrations or alternative inhibitors. This additional experimentation would provide valuable insights into the specificity and efficacy of the inhibition and strengthen the validity of the conclusions drawn regarding the role of beta-catenin signaling in the observed phenomena.
      • The use of Generalized Additive Models (GAMs) in Figures 3 and 4 to present the time series qPCR results may introduce some challenges in interpretation due to the potential for distortion of values at specific time points based on neighboring ones. Given the relatively low time resolution of the data, this approach could lead to a distorted depiction of the temporal dynamics. For instance, in Figure 3B, where Wnt3 peaks at 10 hours, the absence of measurements between 8 and 24 hours introduces uncertainty regarding the accuracy and reliability of this peak at 10 hours.

      To address these concerns and enhance clarity, it may be advisable for the authors to consider presenting the data using simple boxplots instead of GAMs. Boxplots provide a more straightforward visualization of the distribution of data at each time point, allowing for a clearer interpretation of trends and fluctuations over time. This approach would mitigate the potential for distortion introduced by GAMs and provide a more accurate representation of the temporal dynamics observed in the qPCR results - The comparison of the effects of iCRT14 versus DAPT treatments would benefit from having consistent gene expression data across both treatments. However, in Figure 4A, there are fewer genes tested compared to Figure 3A, with Hes and Kayak omitted. While the authors interpretation suggests that these genes may not change after iCRT14 treatment due to their upstream position in the signaling pathways, it is essential to empirically demonstrate this relationship, as it is central to the conclusions drawn. To address this gap in the analysis, it would be valuable for the authors to provide a time series of differential expression for Hes and Kayak following iCRT14 treatment. - The analysis of the impact of chemical inhibition of Notch and Wnt signaling in Figure 7 schematic highlights changes in spatial expression patterns of the target genes. However, the interpretation of their impact primarily relies on qPCR data. As evident from Figure 7, when Notch is inhibited, it is anticipated that Kayak expression will shift from the area of the tentacles to the tip. This spatial shift in expression patterns is a critical aspect of the authors' arguments, especially considering the centrality of Kayak in their findings. Notably, similar spatial expression patterns have been demonstrated for Alx using FISH in Pan et al., available on BioRxiv. Given the importance of Kayak in the presented arguments, it is advisable to also investigate its spatial expression patterns using techniques such as FISH.

      Significance

      The paper introduces novelties to the field of regeneration and developmental biology by leveraging Craspedacusta polyp as a novel model system for investigating the evolutionary and developmental dynamics of tentacles. In doing so, it sheds new light on the intricate mechanisms underlying tentacle formation and patterning. Furthermore, the study implicates Kayak in the regulation of Wnt3, adding a fresh perspective to our understanding of the molecular pathways governing Hydra regeneration. Notably, the results of the research challenge the prevailing notion of autoregulation of Wnt3, which has long been considered fundamental to organizer formation in Hydra. While these findings offer intriguing insights, further investigation will be crucial to conclusively ascertain the validity of this assertion.

      Despite the clarity of the data presented, the interpretation and integration of these findings in the manuscript are lacking. The narrative at times feels disjointed, with different storylines loosely connected. While the findings are intriguing and merit publication, a substantial revision of the manuscript is necessary to provide a more coherent and illuminating interpretation of the results.

      The implications of this research extend beyond the specific confines of Craspedacusta polyp and Hydra biology. It holds significant relevance for both the Hydra biology community and the broader field of Notch signaling research. By highlighting the pivotal role of Notch signaling in regeneration and patterning within Hydra, the study enriches our comprehension of this model organism and its evolutionary adaptations. Moreover, it provides a valuable lens through which the evolution of Notch signaling cascades can be examined. This interdisciplinary approach underscores the interconnectedness of diverse biological systems and underscores the importance of exploring novel model organisms to unravel the complexities of evolution and development.

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      Referee #2

      Evidence, reproducibility and clarity

      The study investigates the role of Notch and beta-catenin signaling in coordinating head regeneration in Hydra. It combines gene expression dynamics, inhibitor treatments, and comparisons with Craspedacusta polyps to propose a lateral inhibition model for Notch function during Hydra head regeneration, mediating between two pattern-forming systems.

      Three main concerns arise from this work:

      1. Lack of spatial expression data: The study proposes a model based on pattern-forming systems but falls short of providing direct spatial expression data for the genes under consideration in both control and treated scenarios. This gap weakens the empirical support for the proposed model.
      2. Clarity and relevance of Craspedacusta comparisons: The section discussing the regeneration in Craspedacusta polyps appears somewhat disjointed from the main narrative, with its contribution to the overarching story of Hydra regeneration remaining unclear.
      3. Accessibility of the text: The study's presentation, including its title, abstract, and main text, presents challenges in terms of clarity and accessibility, making it difficult for readers to follow and understand the research's scope, methodologies, and conclusions.

      Significance

      In conclusion, while the study aims to advance our understanding of the complex signaling pathways governing Hydra head regeneration, it necessitates significant revisions. Enhancing the empirical evidence through detailed spatial patterning data, clarifying the comparative analysis with Craspedacusta polyps, and refining the narrative to improve accessibility are critical steps needed to solidify the study's contributions to the field.

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      Referee #1

      Evidence, reproducibility and clarity

      Steichele et al tackle a long standing question about the precise role of Notch signalling during Hydra head regeneration. They compare the inhibition of Wnt signalling and Notch signalling by pharmacological inhibition. The authors show that inhibition of Wnt signalling blocks tentacle formation but not formation of the hypostome, wnt3 expression or organizer activity. The authors further attempt to understand this in a comparative sense using Craspedacusta. In addition, the authors propose HyKayak as a potential repressor of Wnt3 expression downstream of Notch signalling. there are howerver a number of major and minor problems with the study which must be addressed before it is suitable for publication as outlined below:

      Major:

      • The introduction is lacking a full description of what is known about transcriptional changes during Hydra regeneration and in particular the role of Wnt signalling in this process. Of note the authors do not cite several important studies from recent years including (but not limited to):

      https://doi.org/10.1073/pnas.2204122119

      https://doi.org/10.1186/s13072-020-00364-6

      https://doi.org/10.1101/587147

      https://doi.org/10.7554/eLife.60562

      This problem is further compounded later when the authors do not cite/discuss work which has performed the same or similar analyses to their own. The authors should endeavor to give a more comprehensive background knowledge. - The authors do not cite or reference at all the study by Cazet et al. which used iCRT14 along with RNAseq and ATACseq to probe the role of Wnt signaling during early regeneration. This is a major issue. Although I appreciate that the authors have done much longer time courses and that their data therefore add something to our understanding it will still be important to discuss here. For example, the authors show that Wnt3 is activated normally in iCRT14 animals. Is this also seen in the RNAseq from Cazet et al., - The visualizations used in Figure 3 are quite difficult to interpret and do to in all cases match descriptions in the text. The way the same type data is displayed in figure 5 si much nices.It is also better to treat the same types of data in the same manner consistently throught the paper. For Hes, for example, the authors state that there is a reduction although the data shows that this is very small and taking into account the 95% confidence interval does not seem to be significant. If this is the case then the positive control is not working in this experiment. This would be much clear if individual time points were compared like in figure 5 and statistical tests shown. The authors then state that Alx is not affected but there is actually a larger effect than what they deemed significant for Hes ( the axes are notably different between these two and I think a more consistent axis would make the genes more comparable). Similarly, Gsc is described as being not affected at 8 hours but it appears again to change more that the positive control Hes. Given this I would call into question the validity of this dataset and/or the interpretation by the authors. A more thorough analysis including taking better into account statistical significance would go along way to increasing confidence in this data. - The same issues in interpretation described for Figure 3 also apply to figure 4. The authors state that Wnt7 is affected less than Wnt1 and 3 but this is not evident in the figure and no comparative analysis is performed to confirm this. The same for Wnt 11 and 9/10c where what the authors description is very difficult to see in the figure. Spt5 is apparently upregulated, but this is not discussed. Again the axes are ntably different making it even more difficult to compare between samples. - In their description of figure 4 the authors completely omit to discuss the Cazet et al dataset which has the exact same early timepoints for iCRT14 treatment. This must be discussed and compared and any difference noted. - End of page 11: The authors propose a model thereby the role of Notch in Wnt3 expression may be due to the presence of a repressor. However, I don't see any putative evidence at that stage. The authors also do not cite relevant work from both Cazet et al. and Tursch et al which show that Wnt3 is likely upregulated by bZIP TFs. In both these cases the authors show evidence of bZIP TF binding sites in the Wnt3 promoter along with other analyses. This is very relevant to the model presented by the authors here and must be discussed and compared. In particular the authors put forward HyKayak as an inhibitor of Wnt3 and this should be discussed along with the previous work. - On page 12 the authors conclude based on gene expression in inhibitor treatment that there is a change in complex composition of the two transcription factors. This is something which would require biochemical evidence and I therefore suggest they remove this entirely. - The authors use experiments in Craspedacusta to test their hypothesis of the role of Wnt and Notch signaling in Hydra. There is, in my opinion, an incorrect logic here. Regardless of the outcome, the roles of Wnt and Notch could conceivably be different in the two species and therefore testing hypothesis from one is not possible in the other. The authors should reframe their discussion of this to be more of a comparative framework. Moreover, the results do not necessarily indicate what the authors say. In Hydra Notch signaling is required to form the hypostome/mouth and this is not the case in Craspedacusta while Wnt signaling is required. The authors do not cite an important study from another Hydrozoan Hydractinia (Gahan at al.,2017). In that study the authors show that DAPT inhibits tentacles during regeneration but that the hypostome (or at least the arrangement of neurons and cnidocytes around the mouth) forms normally. This would indicate that in Hydractinia the process of head formation is different to in Hydra and would be congruent with what is shown here in Craspedacusta. This should be more thoroughly discussed, and all relevant literature cited. - From reading the manuscript I do not fully understand the model the authors put forward. It is unclear what "coordinating two independent pattern forming systems" really means. It might be beneficial to make a schematic illustration of the model and how it goes wrong in both sets of inhibitor treatments.

      Minor:

      • The abstract could be rewritten to have more of an introduction to the problem rather than jumping directly into results. It would also be beneficial if the abstract followed the logic of the paper.
      • In Figure 3 and 4 it is not clear why they are divided into A and B. It appears that the categorization of genes into different groups lacks a clear rationale .This seems totally unnecessary. In addition, the order in which the genes are described in the text does not match what is seen in the figure making it confusing to follow.
      • In Figure 5 the authors use two different types of charts and I would stick with one. B is much better as it shows the individual data points as well as other information. I would use this throughout including in Figure 3 and 4.
      • Figure S3 is missing a description of panel C.
      • In figure S3 it is not clear why the inhibitor was removed and not kept on throughout the experiment. Please discuss.
      • Figure S4 has no A or B in the figure, only in the legend.

      Significance

      Although some of the authors data appear to be novel I find the study makes only minor progress on the questions. In particular the authors do not properly cite the relevant literature and to put their manuscript into the correct context. The new model proposed by the authors is based entirely on qPCR data which is not thoroughly analyzed and are not strong enough in the absence of information about the spatial expression the genes they discuss. The proposal of HyKayak as a negative regulator of Wnt3 is interesting but the authors do not provide any solid direct evidence for this (ChIP, EMSA etc) and it is somewhat in disagreement with other models of bZIP function in the literature (which again are not discussed).

      The manuscript is of limited general interest. It has a number of interesting observations which would be of interest to the Hydra community and the broader cnidarian community. The study lacks contextualization within a broader framework, whether it be in the context of regeneration or Wnt/Notch signaling. This limitation may narrow the overall interest in it.

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

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      Reply to the reviewers

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

      I have mixed feelings regarding this manuscript. On the one hand, the authors did an impressive amount of work. On the other hand, the manuscript seems overly descriptive (writing should be more concise) without a clear message or hypothesis that is cohesive to all the presented evidence. Below, I will outline my concerns.

      We appreciate the comment about missing a cohesive presentation. We worked extensively to improve that in the revised manuscript.

      Reviewer #1- first part

      1. I am not an expert in the field of viral biology and immunology. I wonder how well the IFN treatment mimics the cellular response to infection (yet without the virus). Also, how good is ruxolitinib at blocking the IFN response ? I would appreciate it if you could explain both with one or two sentences and provide the necessary references.

      The reviewer is correct that we cannot claim that interferon treatment mimics exactly the cellular response. However, the expression of interferon-stimulated genes (ISGs) is a major arm of the antiviral response to HCMV (c.f. doi:10.3390/v10090447, doi:10.2217/fvl-2018-0189). In addition, Ruxolitinib is a potent and selective Janus kinase 1 and 2 inhibitor (doi:10.1021/ol900350k), and we have shown in the past that it very effectively reduces the expression of many ISGs (doi: 10.1038/s41590-018-0275-z). Since ISGs constitute a major part of the host response to HCMV infection, the fact that their expression leads to minor changes in the tRNA pool strongly suggests that it is mainly the virus (as opposed to the host cell) that mediates the changes seen in the tRNA pools during HCMV infection. In the revised version, these claims were amended, and relevant references were added (pages 5, lines 132-136).

      (MAJOR) Can these two treatments really allow the effects of host response and viral infection to be separated? OR in other words, are these two effects really orthogonal? In my opinion, they are NOT. Fig. 1E seems to support my opinion, as the changes seen for the "IFN" sample relative to the "uninfected" sample (referred to as "changes-A" below), are parallel to the changes seen for the "24hpi + ruxo" sample relative to the "24hpi" sample ("changes-B"). More specifically, changes-A represent the host response, as argued by the author, whereas changes-B represent the elimination of the host response (due to ruxo, conditioned on the virus-driven effect). If the virus-driven effect and the host response could really be separated, one would expect changes-A and changes-B are more or less opposite. However, they appeared to be parallel, suggesting that uninfected versus infected conditions can have totally different (even opposite) host responses. More importantly, if one cannot separate the host response from virus-driven effects, the conclusion of "tRNA changes are driven by virus, not host response" is then unfounded.

      This is an important point to clarify. Changes-A indeed represent the effect of the host antiviral response on the tRNA pool. Changes-B, however, represent a mix of two effects. 1: counteracting the effect of the host antiviral response on the tRNA pool, which we show is a minor effect, and 2: The enhanced effect of the virus, since ruxolitinib, by inhibiting the host antiviral response, enhances the viral infection. It may indeed be that both the virus and the host antiviral effects are in the same direction. However, it is clear that the antiviral effect is minor. Thus, it is likely that the second effect of ruxolitinib (i.e., allowing enhanced viral infection) is the more substantial one. Therefore, it seems as though the viral effect and the elimination of the host effect are in the same direction. This point was clarified in the revised version (page 6, lines 145-146).

      Even if we let go of this previous point and accept that these results indeed offer some support for the notion that the virus-driven effect are the main contributor to the shifts in tRNA pool, the support is at best moderate. A big gap here is "how?" I suggest the authors should at least give some insight on how virus can do that in Discussion (and mention it with one sentence in Results).

      We certainly welcome the challenge, which we now meet in the revision. In short, here, transcription regulation of tRNAs, mainly upon viral infection, is poorly studied. Unlike other herpesviruses, HCMV does not cause a host shut-off of the host transcripts. Upon HCMV infection, the tRNA transcription machinery is upregulated significantly, which probably contributes to the upregulation in pre-tRNA (doi.org/10.1016/j.semcdb.2023.01.011). However, it is still unknown what the viral factors are that promote upregulation in the tRNA transcription machinery. We now relate to this point in the results (page 6, lines 147-148) and discuss the known effects of viral infection of tRNA expression in the discussion section (page 15, lines 447-451).

      The authors compared the HCMV codon usage to the proliferation and differentiation signatures of human cells. But these two signatures are not compared with measured tRNA expression. It might shed some light on the general characteristics of tRNA pool shifts due to infection (towards a proliferation-like or differentiation-like signature). This fits in the general topic of virus-host interaction and might give more evidence for the point that HMCV is adapted to a differentiation signature (as it drives the host into that state).

      We performed the analysis suggested by the reviewer. We found that the tRNA pool of uninfected HFF cells correlated to the same extent with proliferation codon usage (r=0.29, p-value=0.029) and differentiation codon usage (r=0.26, p-value=0.05). Similar correlations to the proliferation and differentiation signature were found when analyzing the tRNA pool 72h post-infection (proliferation r=0.33, p-value=0.011, differentiation r=0.28, p-value=0.034). This result suggests no general shift in the tRNA pool towards a specific codon usage signature.

      How is the dashed box in Fig3A/B chosen?

      We determined the dashed lines based on the most prominent groups of transcripts best adapted to proliferation or differentiation codon usage signatures. Figure S3A clearly shows the two groups without viral genes. We emphasize this point in the legend of Figure S3A (page 36, lines 1157).

      The tAI values shown in Fig3C-E are extremely low (compared to other reports I am aware of). Does this mean that the adaptation of viral codon usage to human cell supply is actually very weak? This is in opposition to the major claims made in this section.

      We acknowledge that the tAI values presented here are lower than typically presented. However, this is due to how tAI was calculated rather than the potential weak adaptation between viral genes and tRNA supply. Specifically, unlike previous works that estimate tRNA availability based on tRNA gene copy number, here we calculated tAI using tRNA sequencing (in order to capture the dynamics in the tRNA pool during infection). Indeed, the value of tAI calculated by tRNA read counts is lower than tAI calculated by tRNA copy number. This is due to the skewed distribution of tRNA read counts (some tRNAs are highly expressed, and others are lowly expressed), while tRNA copy number is distributed more evenly. Thus, due to the mathematical nature of the tAI (computing geometric rather than arithmetic average of tRNA availability), the skewed distribution observed in the data results in lower tAI values. When computing tAI based on gene copy number, we get higher tAI values (0.3 on average). Nevertheless, as all tAI calculations here were done similarly, the comparisons between gene groups or genes are valid.

      I believe that the part about SARS-CoV-2 could be made more concise. It is sufficient to mention that results may differ from those obtained with HCMV in one paragraph.

      The section on SARS-Cov-2 is now made rather succinct. This virus is mainly given as a comparison to the primary virus studied in this paper - HCMV.

      Line 299 on page 11 - I do not believe codon usage between different viruses can be directly compared, let alone reaching such a conclusion. Some viruses have low CAI or tAI to humans, but they have co-evolved with humans for a long time. Furthermore, there are viruses that infect multiple hosts, but their CAI for a host with which they have long co-evolved is higher while their CAI for a host that is relatively new is lower.

      We agree with the reviewer that a direct link between co-evolution time and tAI may not always exist. Indeed, other factors might explain the observation that SARS-CoV-2 genes are less adapted than HCMV genes. These may include effective population sizes and mutation rates that vary substantially. We, therefore, removed this conclusion from the manuscript.

      (MAJOR) A more general comment is that there is a difference between tRNA expression and the abundance of translation-ready tRNA. The process of charging tRNA with amino acids may take a long time. It is the abundance of the charged-tRNA (the ternary complex of aminoacylated tRNA and EF-Tu-GTP) that is of biological importance. In this regard, the use of tRNA expression falls short.

      The reviewer raises a valid point. Indeed, our tRNA sequencing protocol measures both charged and uncharged tRNAs that constitute the cell's mature tRNA pool. Compared to previous studies that focus on the transcription process of tRNAs in viral-infection models by sequencing the pre-tRNAs, here we look at the mature tRNA pool that accounts for both transcription and post-transcription processes. Therefore, we changed the use of "tRNA expression" to "mature-tRNA levels" and "highly" or "lowly-abundant tRNAs" rather than “highly” or “lowly expressed tRNAs” in the manuscript. We note, however, that although limited in the ability to differentiate between charged and uncharged tRNAs, the tRNA sequencing protocol used here is commonly used and validated as a state-of-the-art protocol in tRNA sequencing (10.1016/j.molcel.2021.01.028, 10.1038/s41467-020-17879-x, etc.), mainly because it addresses the level of "ready-to-use" tRNA.

      Reviewer #1- second part

      1. (MAJOR) Prior to the actual competition assay in the first high-throughput screen (cell competition assay), the authors applied two days of antibiotic selection and two days of recovery. This could result in a serious problem of false negatives or drop outs. Specifically, an sgRNA targeting an essential gene with high efficiency would kill the cells, leaving no (or a small number of) cells in the ancestor population at the beginning of the competition process. A sgRNA's enrichment in competing populations cannot be reliably estimated in such situations. I am not certain that the FDR used in Figure 5B is sufficient to address this issue. Please clarify whether it could. Providing raw counts for competing and ancestor populations would also be helpful.

      As customary in CRISPR screens, the step of lentiviral transduction and antibiotic selection is necessary to ensure that only CRISPR-edited cells are left in the population. Indeed, essential genes like housekeeping genes are probably removed from the competing population relatively quickly, which might result in their dropouts. We could have lost some tRNA hits in the cell growth CRISPR screen (Figure 5B-C) because of their overall essentiality for cell growth. The MAGcK tool we used, the state-of-the-art in the field, filters out sgRNAs with low read counts to be able to calculate false discovery rates. Indeed, we identified 15 tRNAs that were depleted from the competing cells. We believe that our procedure minimizes the concern of dropouts. tRNA dropout in the HCMV infection CRISPR screen (Figure 6B-C) can also happen, which means our screen underestimates the essentiality of tRNAs to HCMV infection. However, this concern does not affect the significance of the hits we did find. We acknowledge this inherent difficulty in CRISPR screens and will provide the raw read counts of all samples upon full submission. We emphasize, though, that while valid, this concern applies to essentially any CRISPR screen that is commonplace in genomics these days.

      It is also highly questionable to me the nearly negligible effects of tRNA modification enzymes. This may be explained by the point above. Indeed, the dots of tRNA modification enzymes in general appear to have higher FDR (lower y values) when compared to red dots with similar enrichment levels.

      This is a valid point. We found a lack of essentiality of tRNA modification enzymes in both screens. We analyzed additional CRISPR screens and compared the effect of tRNA modification enzyme knockouts relative to the restriction and dependency factors we used in the library. The tested screens included 34 knockout CRISPR screens we downloaded from the BioGRID ORCS database that have similar parameters to our screen. Namely, they all test cell proliferation in a time-course manner, using a pooled sgRNA library and using the MAGeCK tool for data analysis. Overall, the screens use different human cell lines and diverse sgRNA libraries. Although potentially surprising, we found that the lack of essentiality of tRNA modification enzymes was also observed in the analyzed CRISPR screens (Figure S5B and on page 11, lines 322-330, and on page 18, lines 539-541). One potential reason is if some of these enzymes were "backed up" by others, which we mentioned. Another explanation is that most tRNA modification enzymes are indeed not essential for growth and for viral infection (now described in the Discussion, page 18, lines 544-545). Alternatively, dropouts can explain this result, as suggested by the reviewer. To examine the likelihood of the dropout option, we examined the average raw read count of the tRNA modification enzyme in the ancestor samples. We compared it to that of other sub-groups. We found that raw read counts of the tRNA modification enzymes are not different than other sub-groups in the CRISPR library. Thus, the dropout issue cannot explain our screens' lack of essentiality of tRNA modification enzymes.

      The screen based on IE2-GFP labeled HCMV measures a phenotype that is very difficult to interpret. Particularly, I am not sure if GFP2 and GFP3 are good controls for comparing GFP4 (GFP1 might be better). Various factors can affect GFP levels, including, but not limited to, dilution caused by a rapidly dividing host cell, unhealthy translational machinery resulting from infection or microenvironment. My point is supported by some observations in Fig6B. For example, SEC61B, a restriction factor for HCMV infection, is enriched in the GFP2 group, contrary to expectations. It is necessary for the authors to prove with firm evidence that their choice of GFP signal thresholds is appropriate.

      We acknowledge the concern. Specifically, the translation of the GFP gene itself could be affected by the tRNA manipulation done. To account for this potential concern, we tested the codon usage of the eGFP gene (which is the GFP version we used in the system) and compared it with tRNA essentiality, as determined by the cell growth CRISPR screen. We report this in the revised manuscript (page 13, lines 390-392, and added Figure S6D). We found that GFP does not tend to significantly use codons that correspond to essential or less essential tRNAs. The same lack of correlation was also found for the tRNA essentiality upon HCMV infection (not shown).

      More generally, we show that GFP intensity does correlate with viral genome copies (Figure S6A). Also, from mRNA-seq data of temporal HCMV infection (10.1016/j.celrep.2022.110653), IE2 (UL122) shows a dynamic expression- high expression pick in early infection, then a decline in expression level followed by a gradual increase.

      Altogether, we believe that the IE2-GFP level provides a good estimation for viral load.

      Regarding SEC61B, which served as a control in our screen – the referee is rightly asking why it behaves oppositely from what's expected, given that this was supposed to be a restriction factor of HCMV infection. We returned to the literature on the essentiality of this gene upon HCMV infection. In Weissman's paper (10.1038/384432a0), which was the reference for choosing control genes in our system, this gene was targeted through two different CRISPR technologies, once with CRISPR knockout and once with CRISPRi. Interestingly, only upon CRISPRi did this gene prove to be a restriction factor (i.e., improved infection upon reduction of the gene). We comment on this peculiar fact in the revised manuscript (page 13, lines 370-374). However, we note that the rest of our positive and negative controls deliver the expected results – increasing or reducing infection as expected from their role, thus lending considerable support to our experimental system. It is possible, especially in light of our screen, and since other positive and negative controls behave as expected, that the status of the SEC61B gene as a "restriction factor" of viral infection needs to be reconsidered, as we now suggest.

      I would appreciate more information regarding why restriction factors of cell growth have a high GFP2/GFP4. Intuitively, a KO of restriction factors of cell growth should result in better growth and higher GFP, thus leading to enrichment in GFP4, not GFP2.

      The reviewer raises an interesting question (although not at the heart of this work, as sgRNAs for the cell growth restriction factor mainly aim to serve as controls for the CRISPR screen). HCMV has a complex interaction with the cellular cell cycle. Specifically, it establishes a unique G1/S arrest that is both stimulatory and inhibitory since, on the one hand, it serves the virus to arrest the cell cycle, a critical step for viral genome replication. On the other hand, the virus needs many of the resources that serve cell growth. Both p53 and CDKN1A are important regulators at this stage; therefore, their interaction with the virus may indeed be complex. For example, p53 is upregulated by a viral infection. However, it is sequestered in the viral replication compartments, and its transcriptional are down-regulated, but its absence harms viral propagation (doi: 10.1128/mBio.02934-21, doi: 10.1128/jvi.72.3.2033-2039.1998, doi: 10.1128/jvi.00505-06). Therefore, it is not surprising that genes related to cell growth and cell cycle have complex effects on HCMV infection. We mention the essentiality of p53 for HCMV infection in the results (page 14, line 404).

      Line 404 "nonetheless"

      We appreciate the reviewer for noticing the typo. We corrected it.

      Reviewer #1 (Significance (Required)):

      The relation between human tRNA supply and viral translation is a topic of profound biological and biomedical importance. In this study, the authors used HCMV infection as the primary model to investigate this question. Results fall into two major parts: (i) changes in the tRNA pool during viral infection, and (ii) the impact of tRNA-related gene KO on viral infection.

      We appreciate the detailed report. We addressed the major points raised in the revised manuscript.

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

      In this study by Aharon-Hefetz et al., the researchers examined changes in tRNA pools during virus infections. The translation machinery plays a crucial role in virus replication. Consequently, host cells have developed sensors and effectors within this compartment to counteract viral mechanisms. The translation apparatus serves as a pivotal point in the virus-host conflict. Therefore, investigating alterations in the translation machinery during infections is vital for gaining a comprehensive understanding of the infection process. This study offers a thorough and high-quality analysis of data in a relevant cell culture system involving two different viruses. By conducting tRNA sequencing, the researchers studied the human tRNA pool following infections with human Cytomegalovirus (HCMV) and SARS-CoV-2. Changes in tRNA expression induced by HCMV were mainly driven by the virus infection itself, with minimal impact from the cellular immune response. Interestingly, specific tRNA post-transcriptional modifications seemed to influence stability and were subject to manipulation by HCMV. Conversely, SARS-CoV-2 did not lead to significant alterations in tRNA expression or post-transcriptional modifications. Moreover, a systematic CRISPR screen targeting human tRNA genes and modification enzymes allowed the identification of specific tRNAs and enzymes that either enhanced or reduced HCMV infectivity and cellular growth. This information enabled them to control the development of HCMV-specific tRNA modifications, highlighting the importance of these tRNA epitranscriptome modifications in virus replication. The authors concluded that the observed differences between the viruses are consistent with HCMV genes aligning with differentiation codon usage and SARS-CoV-2 genes reflecting proliferation codon usage. This observation's connection to the biology of HCMV and SARS-CoV-2 lies in the codon usage of structural and gene expression-related viral genes, showing a significant adaptation to host cell tRNA pools. Notably, these genes from both viruses demonstrated the highest adaptation to the tRNA pool of infected cells. The reason behind this phenomenon remains unclear. One hypothesis suggests that a high level of structural gene expression is necessary during activation. Testing this hypothesis could involve examining if hindering tRNA modifications affects virus morphogenesis. In summary, this study presents an interesting and innovative perspective on how viruses modify the translation machinery. The meticulous analysis sheds light on a central interaction point between viruses and their host cells.

      Reviewer #2 (Significance (Required)):

      In summary, this study presents an interesting and innovative perspective on how viruses modify the translation machinery. The meticulous analysis sheds light on a central interaction point between viruses and their host cells.

      We thank the reviewer for finding our work interesting, innovative, and well analyzed

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

      Summary

      Aharon-Hefetz et al. present the expression dynamics and modification signatures of tRNAs using DM-tRNA-seq in human foreskin fibroblasts or Calu3 cells during infections with two diverse viruses, HCMV and SARS-CoV2, respectively. They also use a newly designed tRNA-centric CRISPR library to screen the essentiality of tRNA and tRNA factors during HCMV-GFP infection. They find several tRNAs that are differentially expressed during HCMV infection, and most closely resemble the set of tRNAs shown to be used during cellular differentiation. Additionally, tRNA differential expression does not resemble that following interferon treatment, implying that virus modulation of tRNAs is unique to the general interferon response. They compare codon usage signatures during infection to their prior-defined sets of proliferation/differentiation tRNA genes. In their CRISPR screen, they find that different tRNAs can promote or restrict HCMV infection levels, as measured by the intensity of GFP fluorescence marker in their virus. Surprisingly, there were few tRNA modification factor hits that contributed to growth or infection.

      Reviewer #3- major comments

      1. The topic of this work is important, and the analysis performed here is assumed to be top quality, based on the previous work by the last author. The weakness with this body of work is a lack of rigor, specifically regarding validation and follow-up studies. Without these experiments, the reader lacks confidence in stated conclusions. For example: There is no validation or clue to how penetrant CRISPR is against tRNA genes. Given how duplicated some tRNA families are, it is possible that CRISPR is more effective against certain families compared to others. While this is likely an inherent caveat in all CRISPR screens, it would lend confidence in this approach to see some validation of tRNA KO by northern blot or RT-qPCR or sequencing.

      We thank the reviewer for raising this important issue. Indeed, many tRNA genes appear in multiple copies in the human genome. Yet, based on our previous work, we expect parallel editing of multiple copies using the same sgRNA. In our previous work (doi.org/10.7554/eLife.58461), we validated, based on several tRNA families, the ability of our tRNA CRISPR system to successfully target and affect tRNA expression levels. This included sequencing of the edited tRNA genes (i.e., DNA sequencing), in which we observed diverse INDEL mutations that predicted full disruption of the tRNA structure. Furthermore, we sequenced the tRNA pool of CRISPR-edited cells and found the downregulation of the targeted tRNAs to be up to 2-4-fold. This previous work provides foundations and confidence in this tRNA-CRISPR approach.

      Nevertheless, to further mitigate the reviewer's concern, we also plan to perform additional experiments in the current settings. We will choose individual tRNAs from our CRISPR screen as representatives to validate CRISPR editing. We will target each tRNA independently and test expression reduction by sequencing. We shall share the results in the full revision if granted.

      1. There is no validation that tRNA modification factor knockouts alter tRNA modification levels. Without this knowledge, the lack of essentiality cannot be confidently and fully interpreted. If the group does not validate whether individual tRNA modification factor knockouts alter modification profiles, then all possible explanations should be posited. For example, it is possible that 1) there could be major redundancy among tRNA modification enzymes, as the authors posit in the Discussion 2) tRNA modification enzymes are not essential for growth bc their activity/the modification they place is non-essential for growth, OR 3) the knockouts are not fully penetrant. I think this Discussion should be expanded to make caveats clearer. Perhaps referencing whether tRNA modification factors have been shown to be essential in other CRISPR screens would be helpful.

      Regarding the possible explanations for the lack of essentiality of tRNA modification enzymes, we agree with all three possibilities the reviewer raised. Reviewer #1 raised an additional option, in which tRNA modification enzymes are essential for HCMV infection and cell growth; thus, we cannot detect them in the screens because they drop out early in the process (before collecting the ancestor samples). We checked this possibility and found comparable read counts of sgRNAs targeting tRNA modification enzymes to that of other sub-libraries. This result suggests the drop-outs of sgRNA targeting are unlikely to happen on our screens.

      Furthermore, as the reviewer asked, we analyzed additional CRISPR screens and compared the effect of tRNA modification enzyme knockouts relative to the restriction and dependency factors we used in the library. The tested screens included 34 knockout CRISPR screens we downloaded from the BioGRID ORCS database that have similar parameters to our screen. Namely, they all test cell proliferation in a time-course manner, using a pooled sgRNA library and using the MAGeCK tool for data analysis. Overall, the screens use different human cell lines and diverse sgRNA libraries. Although potentially surprising, we found that the lack of essentiality of tRNA modification enzymes was also observed in the analyzed CRISPR screens (Figure S5B and on page 11, lines 322-330, and on page 18, lines 539-541).

      1. There is no validation that factors modulating GFP intensity in the HCMV screen actually impact virus replication. This is the point most important to this body of work. While GFP intensity does correlate to genome copies as shown by the authors, GFP read-out on a case-by-case basis could be simply due to factors required for expression/translation of GFP. Are any of the tRNA hits enriched or not represented in GFP reporter sequence? Either way, this information is informative.

      We acknowledge the concern. Specifically, the translation of the GFP gene itself could be affected by the tRNA manipulation done. To account for this potential concern, we tested the codon usage of the eGFP gene (which is the GFP version we used in the system) and compared it with tRNA essentiality, as determined by the cell growth CRISPR screen. We report this in the revised manuscript (page 13, lines 390-392, and added Figure S6D). We found that GFP does not tend to significantly use codons that correspond to essential or less essential tRNAs. The same lack of correlation was also found for the tRNA essentiality upon HCMV infection (not shown).

      Additionally, given that the hits are cross-compared ONLY to other infected (low intensitiy "GFP+") cells, and not to an uninfected population, there is no guarantee that these primarily drive HCMV infection. The top hits should be validated in HFFs, infected with HCMV, with resulting titers/viral gene expression/genome copies measured. Additionally, the reasons for not using a GFP- population as a control should be clarified.

      We agree that additional experiments on some hits may be warranted. We plan to examine for such an effect on infection using an individual gene version of the assay. In particular, we will target individually candidate tRNA genes following validation (as described previously in point 1). We will then infect the tRNA-targeted cells with HCMV and measure the effectiveness of HCMV infection using a standard titer assay.

      The reviewer also suggest comparing GFP1/2/3 to an ancestor in addition to comparing them to GFP4. Towards that we now show a GFP2 vs ancestor comparison (shown below). The results look very similar and are now added to the supplemental material of the revised manuscript (page 13, lines 385-387, Figure S6B).

      Though careful codon usage analysis for HCMV versus the human host was analyzed, it seems pertinent to analyze whether the differentially expressed tRNAs during infection correlate to either codon usage profiles. Figure 3C and S3C intend to address this point for viral gene groups; however, I would encourage the authors to expand the description of these results to make them easier to interpret, especially for those not in the tRNA field. For example, "tRNA adaptation index (tAI)" is not defined in the text, but simply referenced. For clarity, you should include a brief explanation of what this measure describes. Following, when reporting results from Figure 3, the results can then be delivered with more specific and interpretable language. These steps will ensure maximal scientific communication to the audience.

      We appreciate the reviewer's comment regarding the importance of scientific communication and making this manuscript easier to interpret, especially for readers unfamiliar with the world of tRNAs and translation efficiency. We added a description of our motivation to use tAI and the meaning of the measurement (page 9, lines 241-243). We also elaborated on the results part and made the results more interpretable (page 9, lines 245 and 249-250).

      Finally, given that changes are most visible at 72 hpi, the analysis should include expression based on this time point for comparison.

      Regarding the time point used for tAI calculation (Figure 3), we tested the tAI measured by the tRNA pool at 72hpi and got very similar results to that obtained using the tRNA pool measured at 24hpi. As 24hpi represents the pick of HCMV infection, we decided to present this analysis. In the current revised version, we also added the analysis done using the tRNA pool measured 72hpi as suggested by the reviewer (Figure S3D).

      Reviewer #3- minor comments

      1. I would recommend more care in terminology used for the CRISPR screen (Figures 5 and 6) to make the manuscript easier to digest. Labeling sgRNAs-containing cells as " Reduced Growth/Infection" or "Increased Growth/Infection" is not immediately easy to understand. For example, saying this sgRNA "increased growth" could refer to the knockdown increasing growth OR could mean that this sgRNA was enriched in cells with increased growth, which are opposing. It might be more clear to state to use depleted/enriched terminology in these figure labels. This also applies to the text, be sure to plainly describe the terminology and what it means each time you refer to the CRISPR results.

      This is a good point. Indeed, focusing on the significant enrichment of the sgRNAs, rather than their effect on growth or infection, is more straightforward. We changed the terminology in Figures 5C and 6C and the text in the current version.

      Is there actual evidence that the new tRNA sgRNA library is more effective than that used previously? State if so.

      We assume the referee refers to our previous paper on the smaller-scale library (doi.org/10.7554/eLife.58461). The addition here is that the library is much more comprehensive (the previous one targeted only 20 tRNAs). We point it out in the revised manuscript (page 17, lines 499-501).

      Fig 1A-C: The cutoff for "red" symbol distinction is not stringent enough. 1.05 would be red, but that is not convincingly upregulated. The cutoff should be at least FC>1.2.

      We thank the reviewer for bringing our intention to this point. In the current version, we changed the cutoff of absolute fold change higher than 1.2 in Figures 1A-C and S1A (also in legend).

      Need thorough description of tRNA bioinformatics and modification analysis (citing past work is not appropriate here-need to make accessible to your audience).

      Further thorough descriptions of tRNA bioinformatics and modification analysis are added in the revised version (page 6, lines 149-151, page 7, lines 178-183).

      Line 182- Result headings could be more informative, even with small adjustments. For example "Specific tRNA modifications are modulated in response to HCMV infection" is more clear and accurate, as there are only a few measurable changes in tRNA modification. Limitations of using sequencing techniques to analyze modifications (versus MS) should also be discussed.

      We changed that heading accordingly.

      We also mentioned the advantages and disadvantages of using sequencing to assess tRNA modification levels (page 7, lines 184-187).

      It is not immediately clear why the viral plot looks different in Fig S3B compared to Fig 3B.

      We thank the referee for spotting this. We employed different length cutoffs on the genes in each panel and have now fixed that in the revised manuscript.

      Line 254-255. This point is not immediately clear-please include more specific language detailing the logic leading to this conclusion.

      Indeed, the logic here was missing. The idea was that longer genes are associated with gene conservation, hence functionality. Thus, non-canonical HCMV genes that are both long and codon-optimized might have a function during HCMV infection. We added this explanation to the text (pages 8-9, lines 235-238).

      Line 408- "may be essential"-I would modify the language here. Especially given there is no true comparison with uninfected cells.

      We improved the language throughout the revised manuscript.

      There are a number of recent publications profiling tRNA expression in herpesviruses. These should be mentioned and discussed in the context of this work. I know some were included in the reference list, but the body of work as a whole, and how this work fits in and pushes the horizon, could be further emphasized. It is quite impressive that this is a conserved feature of herpesvirus infection. a. PMID: 36752632 b. PMID: 35110532 c. PMID: 34535641 d. PMID: 33986151 e. PMID: 33323507 f. PMID: 35458509

      We thank the reviewer for highlighting these works. We added a discussion item regarding tRNA expression in HCMV and other herpesviruses with the references (pages 15-16, lines 447-458)

      CoV2 Discussion point-The lack of tRNA expression regulation might have more to do with the length of the infection (6 hpi cov2- also didn't see much a change at 5hpi with hcmv). This should be proposed as a possibility.

      It is a possibility that due to the high stability of tRNAs, expression regulation of tRNAs will not affect the tRNA pool in short infection such as of SARS-CoV-2. We added this explanation in the discussion part, page 15, lines 441-442.

      Line 582. Misspelled schlafen in Discussion. (SLFN, not SFLN)

      The point is fixed in the revised manuscript.

      Reviewer #3 (Significance (Required)):

      General assessment: I found this paper exciting to read, given the dearth of knowledge regarding viral modulation of tRNA expression.

      We appreciate the reviewer's comment

      However, the work is highly descriptive, with a complete absence of follow-up or validation studies. At the very least, I would have hoped that the authors validated that viral titer (and not just GFP intensity) was impacted by some of the hits. The lack of confirmation and quality control overall diminishes confidence in the stated conclusions.

      However, I think the topic is timely, important, and that this manuscript offers tools to the community at large to learn more about viral manipulation or other drivers of tRNA regulation. Once follow-up/validation experiments are added to the work, as detailed below, this manuscript will be of broad importance and highly impactful.

      As mentioned above, we plan to add such validations to the fully revised manuscript.

      Advance: While there have been many studies suggesting tRNA regulation occurs during viral infection (these pubs should be referenced as mentioned above), this is an advance due to the fact that it begins to address whether tRNA expression changes functionally impact viral replication. This will be much more solid with follow-up experiments confirming that hits alter HCMV replication (rather than GFP intensity).

      Audience: This will be of broad interest to those with interest in virology and gene expression. The new sub-libraries of tRNA-related factors might be useful to be tested in other cell types and settings. Again, as the work stands, it is descriptive and hypothesis-stimulating, but the conclusions need validation and further support.

      We thank the referee for the encouraging words and the suggested analyses. We already implemented most of the suggestions in the current revised version and hope to add further experiments in a fully revised manuscript.

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      Referee #3

      Evidence, reproducibility and clarity

      Summary

      Aharon-Hefetz et al. present the expression dynamics and modification signatures of tRNAs using DM-tRNA-seq in human foreskin fibroblasts or Calu3 cells during infections with two diverse viruses, HCMV and SARS-CoV2, respectively. They also use a newly designed tRNA-centric CRISPR library to screen the essentiality of tRNA and tRNA factors during HCMV-GFP infection. They find several tRNAs that are differentially expressed during HCMV infection, and most closely resemble the set of tRNAs shown to be used during cellular differentiation. Additionally, tRNA differential expression does not resemble that following interferon treatment, implying that virus modulation of tRNAs is unique to the general interferon response. They compare codon usage signatures during infection to their prior-defined sets of proliferation/differentiation tRNA genes. In their CRISPR screen, they find that different tRNAs can promote or restrict HCMV infection levels, as measured by the intensity of GFP fluorescence marker in their virus. Surprisingly, there were few tRNA modification factor hits that contributed to growth or infection.

      Major Comments

      1. The topic of this work is important, and the analysis performed here is assumed to be top quality, based on the previous work by the last author. The weakness with this body of work is a lack of rigor, specifically regarding validation and follow-up studies. Without these experiments, the reader lacks confidence in stated conclusions. For example:
        • a. There is no validation or clue to how penetrant CRISPR is against tRNA genes. Given how duplicated some tRNA families are, it is possible that CRISPR is more effective against certain families compared to others. While this is likely an inherent caveat in all CRISPR screens, it would lend confidence in this approach to see some validation of tRNA KO by northern blot or RT-qPCR or sequencing.
        • b. There is no validation that tRNA modification factor knockouts alter tRNA modification levels. Without this knowledge, the lack of essentiality cannot be confidently and fully interpreted. If the group does not validate whether individual tRNA modification factor knockouts alter modification profiles, then all possible explanations should be posited. For example, it is possible that 1) there could be major redundancy among tRNA modification enzymes, as the authors posit in the discussion 2) tRNA modification enzymes are not essential for growth bc their activity/the modification they place is non-essential for growth, OR 3) the knockouts are not fully penetrant. I think this discussion should be expanded to make caveats clearer. Perhaps referencing whether tRNA modification factors have been shown to be essential in other CRISPR screens would be helpful.
        • c. There is no validation that factors modulating GFP intensity in the HCMV screen actually impact virus replication. This is the point most important to this body of work. While GFP intensity does correlate to genome copies as shown by the authors, GFP read-out on a case-by-case basis could be simply due to factors required for expression/translation of GFP. Are any of the tRNA hits enriched or not represented in GFP reporter sequence? Either way, this information is informative. Additionally, given that the hits are cross-compared ONLY to other infected (low intensitiy "GFP+") cells, and not to an uninfected population, there is no guarantee that these primarily drive HCMV infection. The top hits should be validated in HFFs, infected with HCMV, with resulting titers/viral gene expression/genome copies measured. Additionally, the reasons for not using a GFP- population as a control should be clarified.
      2. Though careful codon usage analysis for HCMV versus the human host was analyzed, it seems pertinent to analyze whether the differentially expressed tRNAs during infection correlate to either codon usage profiles. Figure 3C and S3C intend to address this point for viral gene groups; however, I would encourage the authors to expand the description of these results to make them easier to interpret, especially for those not in the tRNA field. For example, "tRNA adaptation index (tAI)" is not defined in the text, but simply referenced. For clarity, you should include a brief explanation of what this measure describes. Following, when reporting results from Figure 3, the results can then be delivered with more specific and interpretable language. These steps will ensure maximal scientific communication to the audience. Finally, given that changes are most visible at 72 hpi, the analysis should include expression based on this time point for comparison.

      Minor Comments

      1. I would recommend more care in terminology used for the CRISPR screen (Figures 5 and 6) to make the manuscript easier to digest. Labeling sgRNAs-containing cells as " Reduced Growth/Infection" or "Increased Growth/Infection" is not immediately easy to understand. For example, saying this sgRNA "increased growth" could refer to the knockdown increasing growth OR could mean that this sgRNA was enriched in cells with increased growth, which are opposing. It might be more clear to state to use depleted/enriched terminology in these figure labels. This also applies to the text, be sure to plainly describe the terminology and what it means each time you refer to the CRISPR results.
      2. Is there actual evidence that the new tRNA sgRNA library is more effective than that used previously? State if so.
      3. Fig 1A-C: The cutoff for "red" symbol distinction is not stringent enough. 1.05 would be red, but that is not convincingly upregulated. The cutoff should be at least FC>1.2.
      4. Need thorough description of tRNA bioinformatics and modification analysis (citing past work is not appropriate here-need to make accessible to your audience)
      5. Line 182- Result headings could be more informative, even with small adjustments. For example "Specific tRNA modifications are modulated in response to HCMV infection" is more clear and accurate, as there are only a few measurable changes in tRNA modification. Limitations of using sequencing techniques to analyze modifications (versus MS) should also be discussed.
      6. It is not immediately clear why the viral plot looks different in Fig S3B compared to Fig 3B.
      7. Line 254-255. This point is not immediately clear-please include more specific language detailing the logic leading to this conclusion.
      8. Line 408- "may be essential"-I would modify the language here. Especially given there is no true comparison with uninfected cells.
      9. There are a number of recent publications profiling tRNA expression in herpesviruses. These should be mentioned and discussed in the context of this work. I know some were included in the reference list, but the body of work as a whole, and how this work fits in and pushes the horizon, could be further emphasized. It is quite impressive that this is a conserved feature of herpesvirus infection.
        • a. PMID: 36752632
        • b. PMID: 35110532
        • c. PMID: 34535641
        • d. PMID: 33986151
        • e. PMID: 33323507
        • f. PMID: 35458509
      10. CoV2 discussion point-The lack of tRNA expression regulation might have more to do with the length of the infection (6 hpi cov2- also didn't see much a change at 5hpi with hcmv). This should be proposed as a possibility.
      11. Line 582. Misspelled schlafen in discussion. (SLFN, not SFLN)

      Significance

      General assessment: I found this paper exciting to read, given the dearth of knowledge regarding viral modulation of tRNA expression. However, the work is highly descriptive, with a complete absence of follow-up or validation studies. At the very least, I would have hoped that the authors validated that viral titer (and not just GFP intensity) was impacted by some of the hits. The lack of confirmation and quality control overall diminishes confidence in the stated conclusions. However, I think the topic is timely, important, and that this manuscript offers tools to the community at large to learn more about viral manipulation or other drivers of tRNA regulation. Once follow-up/validation experiments are added to the work, as detailed below, this manuscript will be of broad importance and highly impactful.

      Advance: While there have been many studies suggesting tRNA regulation occurs during viral infection (these pubs should be referenced as mentioned above), this is an advance due to the fact that it begins to address whether tRNA expression changes functionally impact viral replication. This will be much more solid with follow-up experiments confirming that hits alter HCMV replication (rather than GFP intensity).

      Audience: This will be of broad interest to those with interest in virology and gene expression. The new sub-libraries of tRNA-related factors might be useful to be tested in other cell types and settings. Again, as the work stands, it is descriptive and hypothesis-stimulating, but the conclusions need validation and further support.

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      Referee #2

      Evidence, reproducibility and clarity

      In this study by Aharon-Hefetz et al., the researchers examined changes in tRNA pools during virus infections. The translation machinery plays a crucial role in virus replication. Consequently, host cells have developed sensors and effectors within this compartment to counteract viral mechanisms. The translation apparatus serves as a pivotal point in the virus-host conflict. Therefore, investigating alterations in the translation machinery during infections is vital for gaining a comprehensive understanding of the infection process.

      This study offers a thorough and high-quality analysis of data in a relevant cell culture system involving two different viruses. By conducting tRNA sequencing, the researchers studied the human tRNA pool following infections with human Cytomegalovirus (HCMV) and SARS-CoV-2. Changes in tRNA expression induced by HCMV were mainly driven by the virus infection itself, with minimal impact from the cellular immune response. Interestingly, specific tRNA post-transcriptional modifications seemed to influence stability and were subject to manipulation by HCMV. Conversely, SARS-CoV-2 did not lead to significant alterations in tRNA expression or post-transcriptional modifications.

      Moreover, a systematic CRISPR screen targeting human tRNA genes and modification enzymes allowed the identification of specific tRNAs and enzymes that either enhanced or reduced HCMV infectivity and cellular growth. This information enabled them to control the development of HCMV-specific tRNA modifications, highlighting the importance of these tRNA epitranscriptome modifications in virus replication. The authors concluded that the observed differences between the viruses are consistent with HCMV genes aligning with differentiation codon usage and SARS-CoV-2 genes reflecting proliferation codon usage. This observation's connection to the biology of HCMV and SARS-CoV-2 lies in the codon usage of structural and gene expression-related viral genes, showing a significant adaptation to host cell tRNA pools. Notably, these genes from both viruses demonstrated the highest adaptation to the tRNA pool of infected cells. The reason behind this phenomenon remains unclear. One hypothesis suggests that a high level of structural gene expression is necessary during activation. Testing this hypothesis could involve examining if hindering tRNA modifications affects virus morphogenesis. In summary, this study presents an interesting and innovative perspective on how viruses modify the translation machinery. The meticulous analysis sheds light on a central interaction point between viruses and their host cells.

      Significance

      In summary, this study presents an interesting and innovative perspective on how viruses modify the translation machinery. The meticulous analysis sheds light on a central interaction point between viruses and their host cells.

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      Referee #1

      Evidence, reproducibility and clarity

      I have mixed feelings regarding this manuscript. On the one hand, the authors did an impressive amount of work. On the other hand, the manuscript seems overly descriptive (writing should be more concise) without a clear message or hypothesis that is cohesive to all the presented evidence. Below, I will outline my concerns.

      Regarding the first part.

      1. I am not an expert in the field of viral biology and immunology. I wonder how well the IFN treatment mimics the cellular response to infection (yet without the virus). Also, how good is ruxolitinib at blocking the IFN response ? I would appreciate it if you could explain both with one or two sentences and provide the necessary references.
      2. (MAJOR) Can these two treatments really allow the effects of host response and viral infection to be separated? OR in other words, are these two effects really orthogonal? In my opinion, they are NOT. Fig. 1E seems to support my opinion, as the changes seen for the "IFN" sample relative to the "uninfected" sample (referred to as "changes-A" below), are parallel to the changes seen for the "24hpi + ruxo" sample relative to the "24hpi" sample ("changes-B"). More specifically, changes-A represent the host response, as argued by the author, whereas changes-B represent the elimination of the host response (due to ruxo, conditioned on the virus-driven effect). If the virus-driven effect and the host response could really be separated, one would expect changes-A and changes-B are more or less opposite. However, they appeared to be parallel, suggesting that uninfected versus infected conditions can have totally different (even opposite) host responses. More importantly, if one cannot separate the host response from virus-driven effects, the conclusion of "tRNA changes are driven by virus, not host response" is then unfounded.3. Even if we let go of this previous point and accept that these results indeed offer some support for the notion that the virus-driven effect are the main contributor to the shifts in tRNA pool, the support is at best moderate. A big gap here is "how?" I suggest the authors should at least give some insight on how virus can do that in Discussion (and mention it with one sentence in Results).
      3. The authors compared the HCMV codon usage to the proliferation and differentiation signatures of human cells. But these two signatures are not compared with measured tRNA expression. It might shed some light on the general characteristics of tRNA pool shifts due to infection (towards a proliferation-like or differentiation-like signature). This fits in the general topic of virus-host interaction and might give more evidence for the point that HMCV is adapted to a differentiation signature (as it drives the host into that state).
      4. How is the dashed box in Fig3A/B chosen?
      5. The tAI values shown in Fig3C-E are extremely low (compared to other reports I am aware of). Does this mean that the adaptation of viral codon usage to human cell supply is actually very weak? This is in opposition to the major claims made in this section.
      6. I believe that the part about SARS-CoV-2 could be made more concise. It is sufficient to mention that results may differ from those obtained with HCMV in one paragraph.
      7. Line 299 on page 11 - I do not believe codon usage between different viruses can be directly compared, let alone reaching such a conclusion. Some viruses have low CAI or tAI to humans, but they have co-evolved with humans for a long time. Furthermore, there are viruses that infect multiple hosts, but their CAI for a host with which they have long co-evolved is higher while their CAI for a host that is relatively new is lower.
      8. (MAJOR) A more general comment is that there is a difference between tRNA expression and the abundance of translation-ready tRNA. The process of charging tRNA with amino acids may take a long time. It is the abundance of the charged-tRNA (the ternary complex of aminoacylated tRNA and EF-Tu-GTP) that is of biological importance. In this regard, the use of tRNA expression falls short.

      Regarding the second part,

      1. (MAJOR) Prior to the actual competition assay in the first high-throughput screen (cell competition assay), the authors applied two days of antibiotic selection and two days of recovery. This could result in a serious problem of false negatives or drop outs. Specifically, an sgRNA targeting an essential gene with high efficiency would kill the cells, leaving no (or a small number of) cells in the ancestor population at the beginning of the competition process. A sgRNA's enrichment in competing populations cannot be reliably estimated in such situations. I am not certain that the FDR used in Figure 5B is sufficient to address this issue. Please clarify whether it could. Providing raw counts for competing and ancestor populations would also be helpful.
      2. It is also highly questionable to me the nearly negligible effects of tRNA modification enzymes. This may be explained by the point above. Indeed, the dots of tRNA modification enzymes in general appear to have higher FDR (lower y values) when compared to red dots with similar enrichment levels.
      3. The screen based on IE2-GFP labeled HCMV measures a phenotype that is very difficult to interpret. Particularly, I am not sure if GFP2 and GFP3 are good controls for comparing GFP4 (GFP1 might be better). Various factors can affect GFP levels, including, but not limited to, dilution caused by a rapidly dividing host cell, unhealthy translational machinery resulting from infection or microenvironment. My point is supported by some observations in Fig6B. For example, SEC61B, a restriction factor for HCMV infection, is enriched in the GFP2 group, contrary to expectations. It is necessary for the authors to prove with firm evidence that their choice of GFP signal thresholds is appropriate.
      4. I would appreciate more information regarding why restriction factors of cell growth have a high GFP2/GFP4. Intuitively, a KO of restriction factors of cell growth should result in better growth and higher GFP, thus leading to enrichment in GFP4, not GFP2.
      5. Line 404 "nonetheless"

      Significance

      The relation between human tRNA supply and viral translation is a topic of profound biological and biomedical importance. In this study, the authors used HCMV infection as the primary model to investigate this question. Results fall into two major parts: (i) changes in the tRNA pool during viral infection, and (ii) the impact of tRNA-related gene KO on viral infection.

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      Reply to the reviewers

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

      The manuscript by Jeong et al. describes effects of neuronal signalling on collective behavior by measuring social distance (SD) which is used as a measure for social network behavior. Authors screened for a panel of inbred DGRP lines and compared the SD due to prior experience of group or single culturing when flies are recorded in a 55 mm diameter petri-dish. The screen uncovered 3 short Sd and three long-SD lines, and subsequent experiments showed differences in various behaviors such as recovery from injury, search for food and SD. Using RNA-seq from heads of flies they implicate Dsk signalling and show neuronal architecture and activity differences between grouped and isolated male flies. They implicate Dsk signalling in recovery from injury affecting SD but it was dispensable for grouped vs. isolated flies. I have suggestions to support the claims made, analysis and interpretation of the data and improve the clarity of writing. See my specific comments below.

      Major comments:

      1. For recording social behaviour in flies, arenas with sloped walls have been extensively used called 'fly bowl' (Simon et al. 2010 doi:10.1371/journal.pone.0008793; Robie et al., 2017, doi: 10.1016/j.cell.2017.06.032), or 'flyworld' (Liu et al., 2018 doi:10.1371/journal.pcbi.1006410). Such geometry ensures that flies don't walk on the side of the arena, and don't occlude each other. However, in the screen carried out in this manuscript, a petri-dish of 5.5 cm diameter filled with agar was used to record social network formation. Given the propensity of flies to walk on the walls of such circular arena, it will be difficult to know if the long and short SD behavior resulting from propensity to form clusters is an artefact of the assay condition used. It would be important to test the SNB and SD of at least the 6 selected short and long SD lines in arena with sloped walls to rule out this possibility.

      To minimize complications from side-wall walking or z-stacking of individual flies, the circular arena used in our study was filled with agar, making a space of 5.5 cm in diameter x ~0.15 cm in height (see below). In fact, the surface tension of the agar solution led to a rounded interface between the agar bed and the side wall that could prevent side-wall walking and partially mimic the sloped wall effects. We included representative video clips for SNB recording in the revised manuscript to further justify our experimental conditions. We also revised our method text accordingly and cited the relevant reference.

      Methods section would require additional details about the SNB assay for instance, the height of the agar bed and the effective height in which interactions was recorded is not mentioned.

      As described in our response to reviewer #1, major comment #1 above, we revised our method text accordingly.

      Figure 2C and 2D results in larvae seems to contradict previous studies that have shown that isolated flies eat more as adults (Li et al. Nature, 2021) and Dsk-RNAi increases feeding in larvae and adults (Soderberg et al., 2012). It might be due to unique characteristic of DGRP lines used and would be helpful to discuss this.

      We reason that high-digging activity in a group of individual larvae can increase the accessibility to "solid" food, thereby promoting their food intake over 12-h during development. However, food consumption rates and their regulation can vary depending on developmental stages or feeding conditions (e.g., larvae vs. adults; liquid vs. solid food; long-term vs. short-term) (https://pubmed.ncbi.nlm.nih.gov/30914005/; https://pubmed.ncbi.nlm.nih.gov/24937262/). It is thus not fair to align our results directly to those observed under very different biological/experimental contexts. For instance, Li et al. measured the amount of liquid food consumption in individually isolated adults from group culture vs. transient social isolation (i.e., 1-week isolation after eclosion). Soderberg et al. assessed the 15-minute feeding activities of larvae or adults on solid food but did not compare the feeding activity between grouped vs. isolated individuals. Therefore, it is not conclusive whether the DSK-depletion phenotypes are relevant to social experience or whether DSK signaling controls short-term feeding per se. Accordingly, we believe our observations do not necessarily contradict previous studies or indicate characteristics unique to the DGRP lines used in our study.

      Rutabaga mutants for Fig S3 are directly compared with CS flies in the maze assay and it appears from methods that these lines were not isogenized, this can significantly impact the results. Similarly for some of the subsequent Dsk experiments it appears that lines were not isogenized (see below). These experiments would either need to be repeated of this caveat needs to be explicitly mentioned to avoid misinterpretation of the data.

      Since genetic backgrounds could substantially contribute to mutant phenotypes, we mentioned the caveat in our revised manuscript. As the reviewer suggested above, testing isogenized lines could be one option to confirm the genetic effects. Our study took an alternative approach where the observed phenotypes were validated by independent genetic models. For instance, the importance of DSK signaling in injury-induced SNB plasticity was validated by genomic deletions of DSK and DSK receptor genes, as well as by transgenic RNAi (Fig. 7B and 7C). In the revised manuscript, we examined additional mutant alleles of rutabaga (Fig. S6, rut[1] and rut[2080]), CCKLR-17D1 (Fig. S15, CCKLR-17D1[delta1] and CCKLR-17D1[delta2]), and CCKLR-17D3 genes (Fig. S15, CCKLR-17D3[delta1] and CCKLR-17D3[delta2]) to substantiate our original findings.

      For Figure 3 describing RNA-seq data additional analysis would be helpful. Gene expression from isolated and grouped flies have been studied earlier by microarray and RNA-seq methods (Wang et al., PNAS 2008; Agrawal et al., JEB 2020; Li et al. Nature, 2021). Data from these studies should be compared with to see if there are common patterns of gene expression between long and short SD flies vs. group and isolated flies.

      According to the reviewer's suggestion, we compared our DEG analysis with those reported in the previous studies. Genes upregulated in socially deprived flies overlapped substantially between our data and the published ones. However, the number of genes commonly upregulated in grouped cultures was very limited in the pairwise comparisons, and Dsk was the only gene upregulated across DEG analyses. Also, DEGs between the short vs. long SD lines barely overlapped with those between grouped vs. isolated flies across independent studies. We speculate that Drosophila has evolved a genetic reprogram where social isolation robustly induces the expression of select genes regardless of genetic backgrounds (i.e., DGRP lines in our study vs. Canton-S in the previous studies), whereas diverse genetic pathways shape the baseline SD traits. We revised our text accordingly and included these new analyses in the revised manuscript (Fig. S10 and Dataset S3).

      GEO accession number and the analyzed list of DEGs should be provided as supplementary information.

      As described in our original manuscript, we submitted our raw data to the European Nucleotide Archive (ENA accession number PRJEB61423). Since ENA and GEO share their data, uploading our data redundantly onto the GEO should not be necessary. Our original manuscript also included all the DEG lists as supplementary tables (Datasets S1-S3).

      Figure 3E & F are not referred to in the main text, also there is no description of how the data was generated. Is this based on published data from Mackay lab about DGRP lines, if so, aggression experiments were not convincing in those studies and have been shown to not recapitulate 'real' aggression by other labs for several of the DGRP lines tested (Chowdhury et al., 2021, doi: 10.1038/s42003-020-01617-6).

      The main text of our original manuscript actually referred to Fig. 3E and 3F. We revised our figure legend to indicate the resources of raw DGRP data and clarified the method for the correlation comparisons. Since we employed the published aggression data from the Mackay lab study (https://pubmed.ncbi.nlm.nih.gov/26100892), we experimentally validated that the long-SD lines indeed show more lunges (i.e., a well-established indicator of aggression behaviors) than the short-SD lines in our revised manuscript (Fig. S11).

      Dsk was shown to be reduced in isolated flies by RNA-seq and play a role in aggression by an earlier study (Agrawal et al., 2020) and should be cited appropriately (line 180-181) and elsewhere.

      The paper was appropriately cited in our original/revised manuscript.

      For Fig. 4A-B, source images for other two DGRP lines should be included at least in supplementary information, if not as main figure.

      Representative confocal images for the other DGRP lines were included in the revised manuscript (Fig. 6A).

      For Fig. 5, what is the reason that uninjured flies don't show any SD phenotype? Are there any changes in their velocity? This is mentioned in passing on line 228-29 but should be properly discussed.

      Genomic deletions or transgenic manipulations of the DSK-CCKLR-17D1 pathway gave consistent effects on the injury-induced clustering but not on baseline SD or walking speed. We reason that the DSK-CCKLR-17D1 pathway is dedicated to encoding early-life social experience by enforcing DSK neuron activity and their male-specific postsynaptic signaling. We clarified our text including the genetic background issue in the revised manuscript. Please also see our response to reviewer #1, major comment #4 above.

      Trans-Tango and UAS-Denmark, SytGFP experiments were performed previously by Wu et al., 2020 and Wang et al., 2021 for Dsk, these two studies observed that P1 neurons are presynaptic and Dsk neurons are post synaptic but in Figure 4 it's not clear what are the presynaptic and post synaptic neurons. Also these studies are not cited appropriately in this section.

      The two studies expressed trans-Tango in P1 neurons (P1>trans-Tango) to demonstrate that DSK-expressing neurons are postsynaptic to P1 neurons. They further visualized some overlaps between axon terminals of P1 neurons (P1>sytGFP) and dendrites of DSK neurons (Dsk>DenMark). On the other hand, we expressed the trans-Tango in DSK neurons (Dsk>trans-Tango) to visualize their male-specific/social experience-dependent postsynaptic targets. We also visualized brain regions positive for both synaptic signals from Dsk>sytGFP and the postsynaptic signals from Dsk>trans-Tango. The two studies were cited in our original manuscript to discuss presynaptic partners of DSK neurons and their distinct roles in animal behaviors. We further cited the two studies in this result section of our revised manuscript.

      Minor comments:

      1. Line no. 286: please mention about the relative humidity and light & dark cycle conditions and when experiments were conducted (ZT).

      Flies were reared at 40-50% humidity under 12-h light: 12-h dark cycles. Behavioral experiments were primarily conducted between ZT4 and ZT8. We revised the method text accordingly.

      Line no. 311: How many days old flies were used (isolated and group housed) for the behavior and transcriptomic studies?

      We revised the method text to better describe our experimental conditions.

      Line no. 349: for RNA extraction please mention how many fly heads were used and ZT for collection.

      Flies were harvested at ZT4-6, and total RNAs were extracted from 35 fly heads. We revised the method text accordingly.

      Line no. 358: Italicize "Drosophila melanogaster".

      Corrected.

      Reviewer #1 (Significance (Required)):

      This manuscript will be of interest to neuroscientists studying Drosophila social behaviors. The manuscript asks interesting questions and authors have done extensive set of experiments but the progress appears incremental given the current state of the field, especially for the later part of the manuscript. Some of the interpretation would also require additional data to bolster the claims made. Finally, the findings from this study could be better discussed in the context of what it is already known.

      We believe our revised text and additional data in the revised manuscript clarify the reviewer concerns and better support our original findings.

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

      The article explores the social network behavior (SNB) of Drosophila, focusing on individual social distance (SD) within groups over time. A systemic analysis revealed that short SD is associated with long developmental time, low food intake, and hypoactivity. Group culturing compensates for developmental inferiority in short social distance individuals. Social interactions during early development positively impact adult physiology and adaptive social plasticity. Transcriptome analyses show genetic diversity for SD traits. The neuropeptide Drosulfakinin (DSK) signaling mediates social network behavior plasticity via receptor CCKLR-17D1, particularly in males, suggesting a dedicated neural mechanism encoding early-life experiences to adaptively transform group properties. The research suggests that animals have developed neural mechanisms to encode early-life experiences. It offers insights into the genetic foundation and adaptability of social behavior in Drosophila, shedding light on the neural processes involved in social memory and the adaptive behaviors of groups. These findings have broader implications for understanding similar neural mechanisms governing social memory and group behaviors in other species.

      Major concerns:

      Major 1. In Figure 2H, the latency to 75% arrival of short-SD isolated fruit flies (no matter with or without pioneers) is close to that of group fruit flies with pioneers while the latency to 75% arrival of long-SD isolated fruit flies (no matter with or without pioneers) is close to that of group fruit flies without pioneers; How to explain the difference in latency to 75% array between long-SD and short-SD isolated fruit flies? It seems that only in the long-SD fruit flies from the grouped experience, the absence of pioneers will increase the time it takes to reach the target food in the maze.

      Social deprivation effects on pioneer-free group foraging somewhat varied across the long SD lines (Fig. 4B and S5, blue). We reason that the hyperactivity of individual long-SD flies facilitates their food-seeking behaviors in the maze, weakening the pioneer effects or even overriding the group property. Nonetheless, our statistical analyses validated that 1) prior social experience did not significantly affect the group performance of 16 naive flies in the maze assay (the only exception was DGRP707, a long-SD line that showed longer latency in group-cultured naive flies than in socially isolated ones), 2) the presence of pioneers significantly shortened the latency in both short- and long-SD lines, and 3) the pioneer effects were evident only in group-cultured flies. We accordingly revised our result text to better elucidate our conclusion.

      Major 2. In Figure 3C, there are two up-regulated genes in the Drosophila group that overlap in short-SD and long-SD strains. Apart from Dsk, what is the other gene? In addition, for isolated fruit flies, both short-SD and long-SD lines have more gene expression upregulated. How to explain this phenomenon? Can you briefly explore the reasons for their upregulation and instead of involvement in SNB plasticity, what kind of physiological functions may they have?

      The other gene commonly upregulated in group-cultured DGRP flies was Arc1 (Activity-regulated cytoskeleton-associated protein), implicated in synaptic plasticity and fat metabolism (https://flybase.org/reports/FBgn0033926.htm). Arc1 downregulation upon social isolation could be relevant to the weak postsynaptic signaling of DSK neurons (Fig. 6D and 6E) or be a part of the metabolic reprogramming (Fig. 5D; also see below). Nonetheless, we focused on the neuropeptide DSK, given its unique expression in the brain and relevance to other social behaviors (e.g., mating, aggression). In fact, Dsk was the only overlapping gene that was downregulated upon social isolation across independent studies (Fig. S10A).

      As the reviewer pointed out, social isolation upregulated many genes, including those involved in metabolism. Our revised manuscript additionally showed that upregulated but not downregulated genes upon social isolation were substantially conserved across genetic backgrounds or independent DEG studies (Fig. 5C and S10A). We speculate that Drosophila has evolved a genetic reprogram where social isolation elevates metabolic gene expression to adaptively induce a metabolic shift for energy storage and fitness. We revised our text accordingly.

      Major 3. In lines 219-223, the genomic deletion by mutant or depletion by RNA interference emphasizes the role of neuropeptides DSK and its receptor CCKLR-17D1 in injury-induced clustering behaviors. How about the effect of neuropeptides overexpression? Do they confer injury-induced social interactions to isolated male flies. Meanwhile, in line 238, the transgenic excitation of CCKLR-17D1 neurons emphasizes the function of neuronal synaptic transmission in the pathway. Indeed, both neuropeptide expression and neuronal synaptic connections may be involved in the regulation of injury-induced clustering behaviors. It is recommended to separate the discussion of protein expression and the respective regulatory modes at the neuronal circuit level.

      We could not test DSK overexpression effects on injury-induced clustering in socially isolated males since we failed to validate DSK overexpression from a relevant transgenic line (https://flybase.org/reports/FBal0184043.htm). Instead, we provided additional data in the revised manuscript that independent genomic deletions of the CCKLR-17D1 locus (Fig. S15) or transgenic silencing of the synaptic transmission in CCKLR-17D1 neurons (Fig. S16) suppressed the injury-induced clustering in group-cultured male flies. According to the reviewer's suggestion, we modified our text to better distinguish between the effects of gene/protein expression vs. relevant neuron activities on social behavior plasticity.

      Major 4. Since a significant portion of the work in the first half of this paper is focused on elucidating two types of social distance in SNB, is there any difference in the regulation of social network plasticity by Dsk signaling pathway in the short-SD and long-SD lines?

      As the reviewer suggested, it will be informative to determine if Dsk signaling for social behavior plasticity is differentially regulated in short- vs. long-SD lines. One technical issue is that genetic factors shaping their SD traits still need to be defined. So, we are limited to performing standard genetic/transgenic experiments using the DGRP lines while retaining their SD phenotypes. Accordingly, our current approach was to compare DSK expression in short- vs. long-SD lines under grouped- vs. isolated-culture conditions. Future studies should address the review comment above.

      Minor ones:

      Minor 1. There is a color difference between the data spots and the figure legends in Figure 2H.

      Corrected.

      Minor 2. The anatomical sample images in Figure 4 and Figure 5 require scale bars.

      We added scale bars to Fig. 6 and 7 in the revised manuscript.

      Minor 3. The "grouped" and "grp" in Figures 3B-3F can be unified as "grp", while the "isolated" and "iso" can be unified as "iso". So that the male and female symbols in Figure 3F will not have any deviation in the mark.

      We unified the labels throughout the revised manuscript according to the reviewer's suggestion.

      Minor 4. The difference in Denmark signals of each group of neurons under the condition of injury should also be compared in Figure 4C.

      The DenMark signals were also compared between control and injury conditions (Fig. S12).

      Minor 5. What is the effect of inactivating CCKLR-17D1 or CCKLR-17D3 by shibire on injury-induced clustering in group-cultured adults in Figure 5E? (This relates to major comment 3)

      We actually employed a tetanus toxin light chain (TNT) to block synaptic transmission in CCKLR-17D1 neurons and found that the transgenic manipulation of CCKLR-17D1 neuron activity suppressed injury-induced clustering in group-cultured males (Fig. S16). Since 1) our additional data using independent deletion alleles further excluded the possible implication of CCKLR-17D3 in the SNB plasticity (Fig. S15) and 2) a transgenic Gal4 knock-in for the CCKLR-17D-3 locus is not available, we focused on the CCKLR-17D1 experiments in our current study and wished to leave more detailed circuit analyses for future studies.

      Reviewer #2 (Significance (Required)):

      General assessment:

      The strengths of this work is that the authors have identified specific lines with short social distance or long social distance by conducting extensive screening experiments. By transcriptome analyses and gene ontology (GO) analyses they revealed genes up or down regulation in the social experience. They have also narrowed down to the DSK signaling involved in the social experience encoding process. However, the study's limitation lies in the lack of clarity regarding the DSK signaling pathway. The mechanisms through which social experiences affect neuronal activity and synaptic connections remain unclear. Further research on upstream and downstream pathways could enhance understanding. Although the article proposes injury-induced clustering behaviors, the key sensory pathways involved in social network behavior plasticity during early social experiences are not well-defined. Conducting sensory deprivation experiments could elucidate sensory involvement. Overall, the study's strengths lie in its comprehensive approach, large sample size, and translational potential. To enhance future research, investigating the complexity of neural mechanisms and expanding the exploration of regulating pathways could be beneficial. Additionally, exploring the ecological relevance of the findings could deepen our understanding of social behavior in natural environments.

      Our current work provides a neuroanatomical basis for early-life social memory and experience-dependent plasticity of social-interaction behaviors. We believe future studies will build up the mechanical details for social experience-dependent DSK expression, DSK neuron activity, and behavioral outputs. Regarding the key sensory pathways, we examined injury-induced SNB plasticity of distinct sensory mutants (e.g., olfactory, visual, auditory, etc.) and our revised manuscript provided additional data that norpA-dependent visual sensing might play a crucial role in this process (Fig. S9), consistent with the previous finding that vision is required for larval clustering behaviors in Drosophila (https://pubmed.ncbi.nlm.nih.gov/28918946/).

      Advance:

      Compared to previous studies such as Heiko Dankert et al.'s publication in 2009 in Nature Methods and Assa Bentzur et al.'s publication in 2020 in Current Biology, which also investigated the impact of early life experiences on male social behavior and examined various aspects of social network construction, this study employs a systematic analysis of social network behavior (SNB) in Drosophila, integrating genetic, physiological, and behavioral assessments. The authors conducted detailed and systematic analyses through transcriptome and gene ontology (GO) analyses, including the visualization of gene expression heatmaps, volcano plots, and overlapping analysis of differentially expressed genes (DEGs) between grouped and isolated conditions. Additionally, this research delved into the regulatory pathway of DSK signaling in male-specific SNB plasticity, with a particular focus on the DSK to CCKLR-17D1 signaling, which encodes early social experiences. The research provides valuable insights into the genetic basis and adaptability of social behavior in Drosophila. Moreover, it illuminates the neural mechanisms that underlie social memory and the ability of groups to adapt across different species.

      Audience:

      Researchers conducting basic research in genetics, neuroscience, behavioral biology, and evolutionary biology, particularly those focused on understanding social behavior and its underlying genetic and neural mechanisms, will find this study highly relevant. Additionally, researchers studying social cognition, social memory, and group dynamics in various species may also be interested in these findings.

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

      Jeong et al. investigate the influence of genetic factors and early-life social experience on social network behaviors in adult Drosophila. Utilizing isogenic DGRP lines, the study correlates social distances with key developmental and physiological traits-developmental time, digging activity, and food intake. The findings suggest that adult flies with shorter social distance -indicating closer proximity to each other-face developmental disadvantages that are offset by the benefits of social grouping. The authors argue for an evolutionary advantage in such social behaviors, suggesting they help compensate for individual developmental deficits. The study further identifies the Dsk signaling pathway as a key mediator of social network behavior plasticity in male flies, particularly under challenging conditions like mechanical injury.

      The study undertakes a broad range of behavioral and neurogenetic approaches, demonstrating an extensive scope of research efforts. Despite its ambitious scope, the manuscript lacks a clear rationale and cohesive flow among its sections. The numerous experiments do not merge into a unified narrative, leaving the reader questioning the reasoning and progression behind the experimental choices. The manuscript needs a clearer structure, well-defined hypotheses, and more detailed methodological descriptions. Greater emphasis on novelty and better integration with existing literature are also needed. The lack of control experiments and adequate statistical analysis weakens some conclusions.

      Major comments

      1. The authors show that flies in short SD lines reduce their activity over time, leading to the formation of social clusters (Fig. 1B). This clustering could potentially be attributed to reduced activity rather than active social preferences. It would be informative to test whether these SD flies exhibit similar social behaviors when placed in a larger arena, to test if the clustering persists under varied environmental conditions.

      Short-SD flies did not reduce their moving speed over time when we placed a single fly in the original arena and assessed its locomotor behavior individually (Fig. S2). Thus, it is likely that the reduced activity in a group of short-SD flies is an effect of clustering over time but not necessarily the cause. We also confirmed that short and long SD lines retain their clustering property even in a larger arena (8.5 cm in diameter) (Fig. S3). We included these new data in our revised manuscript to better demonstrate active social preferences in the DGRP lines.

      In lines 78-79, the authors claim that "short-SD flies gradually reduced SD over time and stayed in the cluster." However, the study established SD clustering by only analyzing behavior during the last quarter of a 10-minute window, assigning a single data point to each fly and taking the average for group SD. Yet, a single value cannot demonstrate whether initially formed clusters remained stable-unchanged-over time. To strengthen this point, the authors could investigate dynamic changes in SD over a longer period to demonstrate stability, or alternatively, adjust the language to better convey the findings. Additionally, including a time scale in Fig. 1B would enhance the clarity of these findings.

      We traced dynamic changes in SD and walking speed of representative DGRP lines over the 10-minute window (Fig. 2A and 2B) and modified our text accordingly in the revised manuscript. We also included a time scale in Fig. 1B and relevant figures.

      The statistical analysis presented in Figure 2C-D raises concerns. It appears that feeding and digging efficiency in both SD type lines benefit from socialization, suggesting that the effects attributed to SD might stem from the overall digging and feeding activity of each line. Therefore, it is crucial to integrate both social distance (short vs. long) and socialization (grouped vs. isolated) into the analysis using methods that allow for the assessment of confounding effects (interaction), such as two-way ANOVA or regression, depending on the data. This would help authors to clarify whether isolation reduces feeding overall (both line types) and determine if this reduction is more pronounced in short-SD lines. Additionally, it is counterintuitive that lines with more larvae per cluster show worse digging efficiency when previous studies, such as Dombrovski et al. (2017), have shown that larger groups of larvae typically exhibit better digging efficiency. This discrepancy highlights the need for a thorough re-evaluation of the data and assumptions regarding group dynamics and their impact on resource access.

      As the reviewer suggested, we employed ordinary or aligned ranks transformation 2-way ANOVA (depending on the normality and equal variance of a given dataset) to determine if social distance and socialization cooperatively contribute to developmental phenotypes. Our new analyses confirmed significant interaction effects of social distance and socialization on most developmental phenotypes tested (i.e., larval digging activity, developmental time, %male progeny, and %eclosion success). These results convincingly support that short-SD larvae benefit more from socialization than long-SD larvae to compensate for the inferior phenotypes in isolated individuals. We speculate that the feeding amount of isolated long-SD individuals may be saturating for normal development (i.e., developmental time, %male progeny), possibly explaining the lack of interaction effects on food intake while displaying developmental inferiorities only in isolated short-SD individuals. We reason that grouped long-SD flies should not necessarily display poorer digging activity than grouped short-SD flies since isolated long-SD individuals displayed much higher digging activity than isolated short-SD individuals. Consistent with the previous finding, both SD lines showed better digging efficiency when grouped than isolated. We included these new analyses in the revised manuscript and modified our text accordingly. To clarify any statistical issues, we included a summary of all our statistical analyses performed in the revised manuscript (Dataset S5).

      The choice to use the percentage of male progeny as a measure of developmental success is confusing, especially without an explanation for why it is favored over measures like overall progeny survival rates. As with digging and feeding, the statistical analysis should include an examination of potential interaction effects to fully assess how social conditions impact developmental outcomes.

      The percentage of male progeny was one of the most evident developmental phenotypes on which social distance and socialization showed significant interaction effects. In the revised manuscript, we further included the percentage of eclosed flies as a measure for the overall progeny survival rate (Fig. 3F) and performed 2-way analyses to validate the significant interaction effects of social distance and socialization on various larval/developmental phenotypes. Please see our response to reviewer #3, major comment #3 above.

      The rationale for using physical injury to induce SNB in the study is not clearly explained, raising concerns about the potential impact of injury on overall locomotion. Before employing such a method in sociality experiments, it is crucial to demonstrate that the injury does not affect locomotion. Additionally, the study's methodologies for transitioning between grouped and isolated cultures (present only in Fig. 2I and not in the methods section), as well as the specific methods used to measure social distance (SD) in isolated flies, are not sufficiently detailed. This lack of clarity complicates the evaluation of the study's conclusions.

      To determine if the long-SD lines express their social behaviors selectively (e.g., upon physiological challenges), we introduced physical injury to the SNB analysis. There was a positive correlation between locomotion activity and SD trait among DGRP lines (i.e., DGRP lines with low walking speed and centroid velocity exhibited short-SD phenotypes in general) (Fig. 1D). This observation thus prompted us to hypothesize that modest injury may reduce locomotor activity in individuals, facilitate their interactions in a group, and shorten the overall SD. The mechanical injury actually shortened SD in both the short- and long-SD lines (Fig. 4D and S7A). Under the same experimental condition, mechanical injury reduced walking speed and centroid velocity only in the long-SD lines (Fig. S8), whereas social isolation blunted the injury effects (Fig. 4D, S7A, and S8). We reason that our injury condition does not severely impair general locomotion per se to abolish or overestimate SNB, but low activity in grouped long-SD flies is likely a consequence of their injury-induced clustering. We clarified our original text for the rationale and included the new data in the revised manuscript (Fig. S8). We also revised the method text for the transitions between grouped and isolated cultures, as well as for measuring SD in isolated flies.

      Lines 104-106 "The clustering property of short-SD lines may have evolved as a compensation mechanism for their developmental inferiority in individuals". To support this claim, the authors should assess the significance of interactions terms as stated earlier.

      Please see our responses to the reviewer's relevant comments above (reviewer #3, major comments #3 and #4).

      In Fig. 4, the authors conclude that Drosulfakinin (DSK) signaling encodes early-life experiences for SNB plasticity. It is crucial for the authors to differentiate whether changes in feeding behavior are directly due to DSK or if they are secondary effects resulting from altered social interactions mediated by DSK.

      Previous studies demonstrated that DSK is a satiety-signaling molecule whose expression is elevated upon feeding to suppress food intake (https://pubmed.ncbi.nlm.nih.gov/34398892/; https://pubmed.ncbi.nlm.nih.gov/32314736/; https://pubmed.ncbi.nlm.nih.gov/25187989/; https://pubmed.ncbi.nlm.nih.gov/22969751/). Under our experimental context, social isolation downregulated DSK expression and DSK neuron activity, whereas isolated larvae rather reduced their food intake. It is thus unlikely that changes in the feeding behavior of isolated larvae directly implicate DSK-dependent satiety signaling. We discussed this issue in our revised manuscript.

      In Fig 4, the data show that DSK peptide is significantly increased in cell bodies in grouped long DS lines when compared with grouped short DS lines (Fig. 4B). However, no changes are reported at the level of DSK projection levels when comparing these groups. Can the authors clarify this?

      The SD-trait effects on DSK levels were evident in cell bodies but not in DSK neuron projections. We reason that axonal transport or processing of the neuropeptide was limiting under the group-culture condition. These observations might also be relevant to our conclusion that Dsk is not crucial for shaping the SD traits per se. We revised our text accordingly.

      Additionally, the data show that DSK activity is reduced by isolation in both types of SD. To clarify if this effect is driven by isolation only, and not type of line (short vs long SD line), the interaction term should be tested. Furthermore, it is not clear what lines are used in live imaging (e.g., Fig 4C-F).

      We detected no significant interaction effects of SD type and social isolation on DSK expression (Fig. 6B). Live-brain imaging of the GCaMP-expressing DSK neurons was performed using a transgenic line (i.e., Dsk-Gal4>UAS-GCaMP) in a wild-type background. Since genetic factors shaping the SD traits were not defined in each DGRP line, we could not combine the transgenes with DGRP backgrounds while retaining their respective SD phenotypes (please also see our response to reviewer #2 major comment #4 above). Nonetheless, the GCaMP imaging demonstrates that 1) either injury or social isolation alone significantly affects DSK neuron activity, but 2) the two conditions act independently on the GCaMP signals (i.e., no significant interaction effects). We clarified it in our revised manuscript and displayed each genotype used in our imaging experiments.

      In the 'Male-specific DSK-CCKLR-17D1 signalling mediates SNB plasticity' section (line 217), the analysis should include an interaction term to account for the possible confounding effects of isolation and injury on SD. This would aid in determining whether the impacts of social isolation and injury on DSK signalling and SNB plasticity are independent of each other or if they interact in significant ways, as stated by the authors.

      Throughout our revised manuscript, we performed 2-way analyses to validate the interaction effects of isolation and injury on SD and support our conclusion. We also included a summary of all our statistical analyses performed in the revised manuscript (Dataset S5).

      Minor comments

      1. The introduction section would also benefit from major rewriting to clearly indicate the research gap and hypothesis tested. The introduction section would also benefit from major rewriting to clearly indicate the research gap and hypothesis tested. The manuscript would benefit from a more thorough integration of previous studies related to Drosophila social behavior (e.g., Blumstein, D. T. et al., 2010; Schneider, J., Dickinson, M. H., & Levine, J. D., 2012; Simon, A. F. et al., 2012; Ramdya, P. et al., 2015). While the current references are adequate, a more detailed discussion of how this study builds upon and diverges from existing literature would be beneficial.

      The introduction of our original manuscript starts from previous findings on Drosophila social behaviors and clearly indicates what remains elusive, thereby defining our biological questions. We further explain why we focus on SD among other social network measures published previously and outline our approaches for new findings in this study (i.e., the principles of social network behavior and its plasticity). Since our original text was written in a concise manner, we revised the introduction to give a more detailed description of what earlier studies have discovered according to the reviewer suggestion.

      A better description of methods, especially behavioral approaches, could vastly help in understanding the results. Clarifying the methodologiy, particularly the behavioral approaches, would greatly enhance the understanding of the results. Also, the method for quantifying the total number of larvae per vial is unclear, particularly whether variations in larval density were considered. This is crucial, as different densities could affect the available sensory cues necessary for larval aggregation, such as vision (e.g. Dombrovski et al. Curr Biol. 2019). Better descriptions of the results and inclusion of exact statistical analyses used in support of the claims are also needed.

      We revised our method text to better describe our experimental conditions. We further described how we controlled larval density to prepare group-cultured larvae and adults for analyzing larval behaviors and developmental phenotypes. Finally, we included a summary of all our statistical analyses performed in the revised manuscript (Dataset S5).

      Some terms and descriptions in the manuscript are somewhat ambiguous, such as "social memory" and "adaptive social plasticity" and should be better defined.

      We better defined the two key short terms in the introduction of our revised manuscript.

      Line 86-89: "Social interactions compensate for developmental inferiority in short-SD larvae Why do flies display SNB? One clue comes from the previous observation that Drosophila larvae collectively dig culture media and improve food accessibility, possibly facilitating their constitutive feeding during early development..." - This paragraph could be moved to the introduction section.

      As we reorganized the introduction in our revised manuscript, we feel it should be fine to leave the paragraph above in the original context.

      In lines 77-78, the manuscript mentions that the locomotion trajectories of individual flies confirm certain characteristics but fails to provide an analysis of individual locomotion metrics, e.g., tortuosity, distance walked, etc. The authors should add quantitative analysis to support claims about trajectories or alternatively rephrase the sentence to remove any claims about the trajectories of flies.

      As the reviewer suggested, we added quantitative analyses of cumulative walking distances over time and total walking distances in individual flies to our revised manuscript (Fig. 2D and S1C).

      After screening 175 strains, three short and long SD lines were selected. It would be good if justification for the authors' choice were included, as the selected lines were not the ones with the longest or shortest SD as seen in Fig. 1C.

      We ranked individual DGRP lines for each of the two group properties (i.e., SD and centroid velocity) and then selected the top and bottom three lines based on their average ranking. We included this rationale in our revised manuscript.

      Other comments:

      • Line 72-73: What correlation was performed? This should be included in the results/methods section.

      As described in the figure legend of our original manuscript, the significance of the correlation was determined by Spearman correlation analysis. We further included the method description in the results and methods section of our revised manuscript.

      • Line 113: Change "pre-trained colleagues" to "pre-trained flies".

      Changed.

      • Lines 321 and 325: Use "3D" instead of "2D" as three dimensions are given?

      Corrected.

      • Ensure all figures are correctly scaled and aligned.

      We revised our figures to avoid any of these issues.

      • Video: Including short videos for each behavioral test (e.g., feeding) would help in understanding it.

      We included representative video files for SNB and aggression assays in the revised manuscript (Video S1-S12).

      • Fig. 4 should include control neurons that do not change with social grouping; authors should also show ROI.

      We included new data for control neurons (Fig. S13, Pdf-Gal4>UAS-GCaMP7f) and also showed ROI for quantification in our revised manuscript (Fig. 6C and S13).

      • Line 27, 86: Change "inferiority" to "disadvantage".

      We feel inferiority fits better in the context of our overall study.

      Reviewer #3 (Significance (Required)):

      This study extends existing knowledge by linking specific genetic pathways to behavioral outcomes in a well-established model system, providing new insights into the genetic and neural basis of social behavior. The use of DGRP lines to dissect the impact of genetic variation on behavior is particularly valuable. The identification of the Dsk signaling pathway as a mediator of these behaviors under stress is interesting. However, the study would benefit from more in-depth statistical analysis and expanded experimental designs to solidify the conclusions. It should also more clearly highlight the novelty of its findings and better integrate them with the current literature on Dsk signaling and social behaviors.

      My expertise is in behavioral neuroscience. The insights from this study promise to deepen our understanding of the genetic and neural mechanisms behind social behaviors. The potential implications of this research are likely to extend well beyond Drosophila, influencing studies across various species.

      Reviewer #4 (Evidence, reproducibility and clarity (Required)):

      Summary:

      The manuscript investigates the role of Drosulfakinin (Dsk) signaling in Drosophila social network behavior (SNB) and its plasticity based on early-life experiences. The study employs a systematic analysis using 175 inbred strains to link short social distance (SD) with developmental time, food intake, and activity levels. Key findings suggest that social interactions during development compensate for individual developmental inferiority and that early-life social experience is necessary for adaptive social behaviors in adults. The genetic basis of SNB is further explored through transcriptome analyses, implicating Dsk and one of its receptors in mediating these behaviors.

      Major comments:

      Are the key conclusions convincing?

      The key conclusions are well-supported by the data presented. The association between early-life social interactions and adult social behaviors is convincingly demonstrated through multiple experimental setups.

      We appreciate the reviewer's positive feedback on our rigorous approaches and key conclusions.

      Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

      Some claims, particularly those regarding the evolutionary implications of Dsk signaling and its conservation across species, might benefit from being presented as hypotheses or speculations rather than definitive conclusions. This would align with the current evidence while acknowledging the need for further investigation.

      As the reviewer suggested, we toned down our claims on the evolutionary implications of Dsk signaling.

      Would additional experiments be essential to support the claims of the paper?

      Measure aggression and male-male courtship behavior in the 6 DGRP lines to examine whether SD correlates with these behaviors.

      Aggression but not male-male courtship behaviors correlated with SD phenotypes in the 6 DGRP lines. We included the new data in our revised manuscript (Fig. S4 and S11). Please also see our response to a relevant reviewer comment above (reviewer #1, major comment #7).

      Include behavior results of flies tested in Figures 4C and D.

      We included the behavior data in our revised manuscript (Fig. S12A).

      Repeat the CCKLR-17D1 experiments shown in Figures 5 F and G for CCKLR-17D3 to provide extra evidence that CCKLR-17D1 mediates DSK's effects on SNB.

      We employed a transgenic Gal4 knock-in for the CCKLR-17D1 locus to specifically manipulate the activity of CCKLR-17D1-expressing neurons. However, a Gal4 knock-in line for the CCKLR-17D3 locus was not available for pairwise comparison. We instead provide extra evidence for CCKLR-17D1 function in SNB plasticity by showing that 1) independent genomic deletions of CCKLR-17D1 but not CCKLR-17D3 suppressed injury-induced clustering in group-cultured males (Fig. S15) and 2) blocking of synaptic transmission in CCKLR-17D1 neurons phenocopied CCKLR-17D1 deletion (Fig. S16). Please also see our response to a relevant reviewer comment above (reviewer #2, minor comment #5)

      Are the suggested experiments realistic in terms of time and resources?

      These experiments are realistic and feasible within typical research timelines. These might require a few months and moderate funding.

      According to the reviewer suggestions, we included new pieces of data in our revised manuscript to address the reviewer concerns and further support our conclusions.

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

      The methods section is detailed, providing sufficient information for replication.

      We appreciate the reviewer's positive feedback on our method description.

      Are the experiments adequately replicated and statistical analysis adequate?

      The experiments appear to be adequately replicated, and the statistical analyses are generally appropriate. However, ensuring consistent selection of statistical methods can further support the evidence presented (Figures 2C and D).

      We performed more appropriate statistical analyses in the revised manuscript (e.g., 2-way ANOVA of the data presented in our original Fig. 2C and 2D) and included a summary of all the statistical analyses in the revised manuscript (Dataset S5). Please also see our responses to the reviewer comments above (reviewer #3, major comments #3 and #10; reviewer #3, minor comment #2).

      Minor comments:

      Specific experimental issues that are easily addressable:

      Ensure clarity in the presentation of figures and legends. Some figures could benefit from more detailed legends explaining all aspects of the data shown.

      We revised our figures and figure legends to address this issue and improve clarity.

      Are prior studies referenced appropriately?

      The manuscript references prior studies appropriately, providing a solid context for the current research.

      We appreciate the reviewer comment.

      Are the text and figures clear and accurate?

      The text is clear, but some figures, particularly those with complex data, could be more informative with additional annotations.

      We revised our figures and figure legends to address this issue.

      The larvae pictures in Figure 2A should be replaced with ones with higher resolution with drawn larval contours.

      We replaced the larval pictures with higher resolution and indicated individual larvae with arrows in the revised manuscript (Fig. 3A).

      Scale bars are missing in most of the images shown.

      We added scale bars to our revised figures.

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

      Consider providing a graphical abstract summarizing the key findings. This would aid readers in quickly grasping the main conclusions. Additionally, breaking down complex figures into simpler, more focused panels might improve readability.

      As the reviewer suggested, we split complex figures into simpler ones to improve the readability of our revised manuscript and data. We also provided a graphical abstract summarizing our findings (Fig. 8).

      Reviewer #4 (Significance (Required)):

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

      This study provides significant conceptual advances in understanding the genetic and neurobiological basis of social behavior in Drosophila. By linking early-life social experiences to adult social behaviors, it highlights the importance of developmental context in shaping adult phenotypes.

      Place the work in the context of the existing literature (provide references, where appropriate).

      The work builds on previous studies on Drosophila social behavior and neurogenetics. It extends the current understanding by integrating developmental and adult behaviors with genetic and molecular analyses. References to foundational works in Drosophila social behavior and recent studies on neuropeptide signaling are well-placed.

      State what audience might be interested in and influenced by the reported findings.

      Researchers in the fields of neurogenetics, behavioral ecology, developmental biology, and evolutionary biology will find this work particularly relevant. It also has implications for those studying social behavior across species, including mammals.

      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.

      Expertise: Neurogenetics, Behavioral Neuroscience, Drosophila Genetics, Social Behavior, Bioinformatics. I have sufficient expertise to evaluate the genetic, behavioral, and transcriptomics aspects of the study. Specific details on the imaging studies might require additional expert evaluation.

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      Referee #4

      Evidence, reproducibility and clarity

      Summary:

      The manuscript investigates the role of Drosulfakinin (Dsk) signaling in Drosophila social network behavior (SNB) and its plasticity based on early-life experiences. The study employs a systematic analysis using 175 inbred strains to link short social distance (SD) with developmental time, food intake, and activity levels. Key findings suggest that social interactions during development compensate for individual developmental inferiority and that early-life social experience is necessary for adaptive social behaviors in adults. The genetic basis of SNB is further explored through transcriptome analyses, implicating Dsk and one of its receptorS in mediating these behaviors.

      Major comments:

      Are the key conclusions convincing?

      The key conclusions are well-supported by the data presented. The association between early-life social interactions and adult social behaviors is convincingly demonstrated through multiple experimental setups. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Some claims, particularly those regarding the evolutionary implications of Dsk signaling and its conservation across species, might benefit from being presented as hypotheses or speculations rather than definitive conclusions. This would align with the current evidence while acknowledging the need for further investigation.

      Would additional experiments be essential to support the claims of the paper?

      Measure aggression and male-male courtship behavior in the 6 DGRP lines to examine whether SD correlates with these behaviors. Include behavior results of flies tested in Figures 4C and D. Repeat the CCKLR-17D1 experiments shown in Figures 5 F and G for CCKLR-17D3 to provide extra evidence that CCKLR-17D1 mediates DSK's effects on SNB.

      Are the suggested experiments realistic in terms of time and resources?

      These experiments are realistic and feasible within typical research timelines. These might require a few months and moderate funding.

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

      The methods section is detailed, providing sufficient information for replication.

      Are the experiments adequately replicated and statistical analysis adequate?

      The experiments appear to be adequately replicated, and the statistical analyses are generally appropriate. However, ensuring consistent selection of statistical methods can further support the evidence presented (Figures 2C and D).

      Minor comments:

      Specific experimental issues that are easily addressable:

      Ensure clarity in the presentation of figures and legends. Some figures could benefit from more detailed legends explaining all aspects of the data shown.

      Are prior studies referenced appropriately?

      The manuscript references prior studies appropriately, providing a solid context for the current research.

      Are the text and figures clear and accurate?

      The text is clear, but some figures, particularly those with complex data, could be more informative with additional annotations. The larvae pictures in Figure 2A should be replaced with ones with higher resolution with drawn larval contours. Scale bars are missing in most of the images shown.

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

      Consider providing a graphical abstract summarizing the key findings. This would aid readers in quickly grasping the main conclusions. Additionally, breaking down complex figures into simpler, more focused panels might improve readability.

      Significance

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

      This study provides significant conceptual advances in understanding the genetic and neurobiological basis of social behavior in Drosophila. By linking early-life social experiences to adult social behaviors, it highlights the importance of developmental context in shaping adult phenotypes.

      Place the work in the context of the existing literature (provide references, where appropriate).

      The work builds on previous studies on Drosophila social behavior and neurogenetics. It extends the current understanding by integrating developmental and adult behaviors with genetic and molecular analyses. References to foundational works in Drosophila social behavior and recent studies on neuropeptide signaling are well-placed.

      State what audience might be interested in and influenced by the reported findings.

      Researchers in the fields of neurogenetics, behavioral ecology, developmental biology, and evolutionary biology will find this work particularly relevant. It also has implications for those studying social behavior across species, including mammals.

      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.

      Expertise: Neurogenetics, Behavioral Neuroscience, Drosophila Genetics, Social Behavior, Bioinformatics. I have sufficient expertise to evaluate the genetic, behavioral, and transcriptomics aspects of the study. Specific details on the imaging studies might require additional expert evaluation.

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      Referee #3

      Evidence, reproducibility and clarity

      Jeong et al. investigate the influence of genetic factors and early-life social experience on social network behaviors in adult Drosophila. Utilizing isogenic DGRP lines, the study correlates social distances with key developmental and physiological traits-developmental time, digging activity, and food intake. The findings suggest that adult flies with shorter social distance -indicating closer proximity to each other-face developmental disadvantages that are offset by the benefits of social grouping. The authors argue for an evolutionary advantage in such social behaviors, suggesting they help compensate for individual developmental deficits. The study further identifies the Dsk signaling pathway as a key mediator of social network behavior plasticity in male flies, particularly under challenging conditions like mechanical injury.

      The study undertakes a broad range of behavioral and neurogenetic approaches, demonstrating an extensive scope of research efforts. Despite its ambitious scope, the manuscript lacks a clear rationale and cohesive flow among its sections. The numerous experiments do not merge into a unified narrative, leaving the reader questioning the reasoning and progression behind the experimental choices. The manuscript needs a clearer structure, well-defined hypotheses, and more detailed methodological descriptions. Greater emphasis on novelty and better integration with existing literature are also needed. The lack of control experiments and adequate statistical analysis weakens some conclusions.

      Major comments

      1. The authors show that flies in short SD lines reduce their activity over time, leading to the formation of social clusters (Fig. 1B). This clustering could potentially be attributed to reduced activity rather than active social preferences. It would be informative to test whether these SD flies exhibit similar social behaviors when placed in a larger arena, to test if the clustering persists under varied environmental conditions.
      2. In lines 78-79, the authors claim that "short-SD flies gradually reduced SD over time and stayed in the cluster." However, the study established SD clustering by only analyzing behavior during the last quarter of a 10-minute window, assigning a single data point to each fly and taking the average for group SD. Yet, a single value cannot demonstrate whether initially formed clusters remained stable-unchanged-over time. To strengthen this point, the authors could investigate dynamic changes in SD over a longer period to demonstrate stability, or alternatively, adjust the language to better convey the findings. Additionally, including a time scale in Fig. 1B would enhance the clarity of these findings.
      3. The statistical analysis presented in Figure 2C-D raises concerns. It appears that feeding and digging efficiency in both SD type lines benefit from socialization, suggesting that the effects attributed to SD might stem from the overall digging and feeding activity of each line. Therefore, it is crucial to integrate both social distance (short vs. long) and socialization (grouped vs. isolated) into the analysis using methods that allow for the assessment of confounding effects (interaction), such as two-way ANOVA or regression, depending on the data. This would help authors to clarify whether isolation reduces feeding overall (both line types) and determine if this reduction is more pronounced in short-SD lines. Additionally, it is counterintuitive that lines with more larvae per cluster show worse digging efficiency when previous studies, such as Dombrovski et al. (2017), have shown that larger groups of larvae typically exhibit better digging efficiency. This discrepancy highlights the need for a thorough re-evaluation of the data and assumptions regarding group dynamics and their impact on resource access.
      4. The choice to use the percentage of male progeny as a measure of developmental success is confusing, especially without an explanation for why it is favored over measures like overall progeny survival rates. As with digging and feeding, the statistical analysis should include an examination of potential interaction effects to fully assess how social conditions impact developmental outcomes.
      5. The rationale for using physical injury to induce SNB in the study is not clearly explained, raising concerns about the potential impact of injury on overall locomotion. Before employing such a method in sociality experiments, it is crucial to demonstrate that the injury does not affect locomotion. Additionally, the study's methodologies for transitioning between grouped and isolated cultures (present only in Fig. 2I and not in the methods section), as well as the specific methods used to measure social distance (SD) in isolated flies, are not sufficiently detailed. This lack of clarity complicates the evaluation of the study's conclusions.
      6. Lines 104-106 "The clustering property of short-SD lines may have evolved as a compensation mechanism for their developmental inferiority in individuals". To support this claim, the authors should assess the significance of interactions terms as stated earlier.
      7. In Fig. 4, the authors conclude that Drosulfakinin (DSK) signaling encodes early-life experiences for SNB plasticity. It is crucial for the authors to differentiate whether changes in feeding behavior are directly due to DSK or if they are secondary effects resulting from altered social interactions mediated by DSK.
      8. In Fig 4, the data show that DSK peptide is significantly increased in cell bodies in grouped long DS lines when compared with grouped short DS lines (Fig. 4B). However, no changes are reported at the level of DSK projection levels when comparing these groups. Can the authors clarify this?
      9. Additionally, the data show that DSK activity is reduced by isolation in both types of SD. To clarify if this effect is driven by isolation only, and not type of line (short vs long SD line), the interaction term should be tested. Furthermore, it is not clear what lines are used in live imaging (e.g., Fig 4C-F).
      10. In the 'Male-specific DSK-CCKLR-17D1 signalling mediates SNB plasticity' section (line 217), the analysis should include an interaction term to account for the possible confounding effects of isolation and injury on SD. This would aid in determining whether the impacts of social isolation and injury on DSK signalling and SNB plasticity are independent of each other or if they interact in significant ways, as stated by the authors.

      Minor comments

      1. The introduction section would also benefit from major rewriting to clearly indicate the research gap and hypothesis tested. The introduction section would also benefit from major rewriting to clearly indicate the research gap and hypothesis tested. The manuscript would benefit from a more thorough integration of previous studies related to Drosophila social behavior (e.g., Blumstein, D. T. et al., 2010; Schneider, J., Dickinson, M. H., & Levine, J. D., 2012; Simon, A. F. et al., 2012; Ramdya, P. et al., 2015). While the current references are adequate, a more detailed discussion of how this study builds upon and diverges from existing literature would be beneficial.
      2. A better description of methods, especially behavioral approaches, could vastly help in understanding the results. Clarifying the methodologiy, particularly the behavioral approaches, would greatly enhance the understanding of the results. Also, the method for quantifying the total number of larvae per vial is unclear, particularly whether variations in larval density were considered. This is crucial, as different densities could affect the available sensory cues necessary for larval aggregation, such as vision (e.g. Dombrovski et al. Curr Biol. 2019). Better descriptions of the results and inclusion of exact statistical analyses used in support of the claims are also needed.
      3. Some terms and descriptions in the manuscript are somewhat ambiguous, such as "social memory" and "adaptive social plasticity" and should be better defined.
      4. Line 86-89: "Social interactions compensate for developmental inferiority in short-SD larvae Why do flies display SNB? One clue comes from the previous observation that Drosophila larvae collectively dig culture media and improve food accessibility, possibly facilitating their constitutive feeding during early development..." - This paragraph could be moved to the introduction section.
      5. In lines 77-78, the manuscript mentions that the locomotion trajectories of individual flies confirm certain characteristics but fails to provide an analysis of individual locomotion metrics, e.g., tortuosity, distance walked, etc. The authors should add quantitative analysis to support claims about trajectories or alternatively rephrase the sentence to remove any claims about the trajectories of flies.
      6. After screening 175 strains, three short and long SD lines were selected. It would be good if justification for the authors' choice were included, as the selected lines were not the ones with the longest or shortest SD as seen in Fig. 1C.

      Other comments:

      • Line 72-73: What correlation was performed? This should be included in the results/methods section.
      • Line 113: Change "pre-trained colleagues" to "pre-trained flies".
      • Lines 321 and 325: Use "3D" instead of "2D" as three dimensions are given?
      • Ensure all figures are correctly scaled and aligned.
      • Video: Including short videos for each behavioral test (e.g., feeding) would help in understanding it.
      • Fig. 4 should include control neurons that do not change with social grouping; authors should also show ROI.
      • Line 27, 86: Change "inferiority" to "disadvantage".

      Significance

      This study extends existing knowledge by linking specific genetic pathways to behavioral outcomes in a well-established model system, providing new insights into the genetic and neural basis of social behavior. The use of DGRP lines to dissect the impact of genetic variation on behavior is particularly valuable. The identification of the Dsk signaling pathway as a mediator of these behaviors under stress is interesting. However, the study would benefit from more in-depth statistical analysis and expanded experimental designs to solidify the conclusions. It should also more clearly highlight the novelty of its findings and better integrate them with the current literature on Dsk signaling and social behaviors.

      My expertise is in behavioral neuroscience. The insights from this study promise to deepen our understanding of the genetic and neural mechanisms behind social behaviors. The potential implications of this research are likely to extend well beyond Drosophila, influencing studies across various species.

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      Referee #2

      Evidence, reproducibility and clarity

      The article explores the social network behavior (SNB) of Drosophila, focusing on individual social distance (SD) within groups over time. A systemic analysis revealed that short SD is associated with long developmental time, low food intake, and hypoactivity. Group culturing compensates for developmental inferiority in short social distance individuals. Social interactions during early development positively impact adult physiology and adaptive social plasticity. Transcriptome analyses show genetic diversity for SD traits. The neuropeptide Drosulfakinin (DSK) signaling mediates social network behavior plasticity via receptor CCKLR-17D1, particularly in males, suggesting a dedicated neural mechanism encoding early-life experiences to adaptively transform group properties. The research suggests that animals have developed neural mechanisms to encode early-life experiences. It offers insights into the genetic foundation and adaptability of social behavior in Drosophila, shedding light on the neural processes involved in social memory and the adaptive behaviors of groups. These findings have broader implications for understanding similar neural mechanisms governing social memory and group behaviors in other species.

      Major concerns:

      Major 1. In Figure 2H, the latency to 75% arrival of short-SD isolated fruit flies (no matter with or without pioneers) is close to that of group fruit flies with pioneers while the latency to 75% arrival of long-SD isolated fruit flies (no matter with or without pioneers) is close to that of group fruit flies without pioneers; How to explain the difference in latency to 75% array between long-SD and short-SD isolated fruit flies? It seems that only in the long-SD fruit flies from the grouped experience, the absence of pioneers will increase the time it takes to reach the target food in the maze.

      Major 2. In Figure 3C, there are two up-regulated genes in the Drosophila group that overlap in short-SD and long-SD strains. Apart from Dsk, what is the other gene? In addition, for isolated fruit flies, both short-SD and long-SD lines have more gene expression upregulated. How to explain this phenomenon? Can you briefly explore the reasons for their upregulation and instead of involvement in SNB plasticity, what kind of physiological functions may they have?

      Major 3. In lines 219-223, the genomic deletion by mutant or depletion by RNA interference emphasizes the role of neuropeptides DSK and its receptor CCKLR-17D1 in injury-induced clustering behaviors. How about the effect of neuropeptides overexpression? Do they confer injury-induced social interactions to isolated male flies. Meanwhile, in line 238, the transgenic excitation of CCKLR-17D1 neurons emphasizes the function of neuronal synaptic transmission in the pathway. Indeed, both neuropeptide expression and neuronal synaptic connections may be involved in the regulation of injury-induced clustering behaviors. It is recommended to separate the discussion of protein expression and the respective regulatory modes at the neuronal circuit level.

      Major 4. Since a significant portion of the work in the first half of this paper is focused on elucidating two types of social distance in SNB, is there any difference in the regulation of social network plasticity by Dsk signaling pathway in the short-SD and long-SD lines?

      Minor ones:

      Minor 1. There is a color difference between the data spots and the figure legends in Figure 2H.

      Minor 2. The anatomical sample images in Figure 4 and Figure 5 require scale bars.

      Minor 3. The "grouped" and "grp" in Figures 3B-3F can be unified as "grp", while the "isolated" and "iso" can be unified as "iso". So that the male and female symbols in Figure 3F will not have any deviation in the mark.

      Minor 4. The difference in Denmark signals of each group of neurons under the condition of injury should also be compared in Figure 4C.

      Minor 5. What is the effect of inactivating CCKLR-17D1 or CCKLR-17D3 by shibire on injury-induced clustering in group-cultured adults in Figure 5E? (This relates to major comment 3)

      Significance

      General assessment:

      The strengths of this work is that the authors have identified specific lines with short social distance or long social distance by conducting extensive screening experiments. By transcriptome analyses and gene ontology (GO) analyses they revealed genes up or down regulation in the social experience. They have also narrowed down to the DSK signaling involved in the social experience encoding process. However, the study's limitation lies in the lack of clarity regarding the DSK signaling pathway. The mechanisms through which social experiences affect neuronal activity and synaptic connections remain unclear. Further research on upstream and downstream pathways could enhance understanding. Although the article proposes injury-induced clustering behaviors, the key sensory pathways involved in social network behavior plasticity during early social experiences are not well-defined. Conducting sensory deprivation experiments could elucidate sensory involvement. Overall, the study's strengths lie in its comprehensive approach, large sample size, and translational potential. To enhance future research, investigating the complexity of neural mechanisms and expanding the exploration of regulating pathways could be beneficial. Additionally, exploring the ecological relevance of the findings could deepen our understanding of social behavior in natural environments.

      Advance:

      Compared to previous studies such as Heiko Dankert et al.'s publication in 2009 in Nature Methods and Assa Bentzur et al.'s publication in 2020 in Current Biology, which also investigated the impact of early life experiences on male social behavior and examined various aspects of social network construction, this study employs a systematic analysis of social network behavior (SNB) in Drosophila, integrating genetic, physiological, and behavioral assessments. The authors conducted detailed and systematic analyses through transcriptome and gene ontology (GO) analyses, including the visualization of gene expression heatmaps, volcano plots, and overlapping analysis of differentially expressed genes (DEGs) between grouped and isolated conditions. Additionally, this research delved into the regulatory pathway of DSK signaling in male-specific SNB plasticity, with a particular focus on the DSK to CCKLR-17D1 signaling, which encodes early social experiences. The research provides valuable insights into the genetic basis and adaptability of social behavior in Drosophila. Moreover, it illuminates the neural mechanisms that underlie social memory and the ability of groups to adapt across different species.

      Audience:

      Researchers conducting basic research in genetics, neuroscience, behavioral biology, and evolutionary biology, particularly those focused on understanding social behavior and its underlying genetic and neural mechanisms, will find this study highly relevant. Additionally, researchers studying social cognition, social memory, and group dynamics in various species may also be interested in these findings.

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      Referee #1

      Evidence, reproducibility and clarity

      The manuscript by Jeong et al. describes effects of neuronal signalling on collective behavior by measuring social distance (SD) which is used as a measure for social network behavior. Authors screened for a panel of inbred DGRP lines and compared the SD due to prior experience of group or single culturing when flies are recorded in a 55 mm diameter petri-dish. The screen uncovered 3 short Sd and three long-SD lines, and subsequent experiments showed differences in various behaviors such as recovery from injury, search for food and SD. Using RNA-seq from heads of flies they implicate Dsk signalling and show neuronal architecture and activity differences between grouped and isolated male flies. They implicate Dsk signalling in recovery from injury affecting SD but it was dispensable for grouped vs. isolated flies. I have suggestions to support the claims made, analysis and interpretation of the data and improve the clarity of writing. See my specific comments below.

      Major comments:

      1. For recording social behaviour in flies, arenas with sloped walls have been extensively used called 'fly bowl' (Simon et al. 2010 doi:10.1371/journal.pone.0008793; Robie et al., 2017, doi: 10.1016/j.cell.2017.06.032), or 'flyworld' (Liu et al., 2018 doi:10.1371/journal.pcbi.1006410). Such geometry ensures that flies don't walk on the side of the arena, and don't occlude each other. However, in the screen carried out in this manuscript, a petri-dish of 5.5 cm diameter filled with agar was used to record social network formation. Given the propensity of flies to walk on the walls of such circular arena, it will be difficult to know if the long and short SD behavior resulting from propensity to form clusters is an artefact of the assay condition used. It would be important to test the SNB and SD of at least the 6 selected short and long SD lines in arena with sloped walls to rule out this possibility.
      2. Methods section would require additional details about the SNB assay for instance, the height of the agar bed and the effective height in which interactions was recorded is not mentioned.
      3. Figure 2C and 2D results in larvae seems to contradict previous studies that have shown that isolated flies eat more as adults (Li et al. Nature, 2021) and Dsk-RNAi increases feeding in larvae and adults (Soderberg et al., 2012). It might be due to unique characteristic of DGRP lines used and would be helpful to discuss this.
      4. Rutabaga mutants for Fig S3 are directly compared with CS flies in the maze assay and it appears from methods that these lines were not isogenized, this can significantly impact the results. Similarly for some of the subsequent Dsk experiments it appears that lines were not isogenized (see below). These experiments would either need to be repeated of this caveat needs to be explicitly mentioned to avoid misinterpretation of the data.
      5. For Figure 3 describing RNA-seq data additional analysis would be helpful. Gene expression from isolated and grouped flies have been studied earlier by microarray and RNA-seq methods (Wang et al., PNAS 2008; Agrawal et al., JEB 2020; Li et al. Nature, 2021). Data from these studies should be compared with to see if there are common patterns of gene expression between long and short SD flies vs. group and isolated flies.
      6. GEO accession number and the analyzed list of DEGs should be provided as supplementary information.
      7. Figure 3E & F are not referred to in the main text, also there is no description of how the data was generated. Is this based on published data from Mackay lab about DGRP lines, if so, aggression experiments were not convincing in those studies and have been shown to not recapitulate 'real' aggression by other labs for several of the DGRP lines tested (Chowdhury et al., 2021, doi: 10.1038/s42003-020-01617-6).
      8. Dsk was shown to be reduced in isolated flies by RNA-seq and play a role in aggression by an earlier study (Agrawal et al., 2020) and should be cited appropriately (line 180-181) and elsewhere.
      9. For Fig. 4A-B, source images for other two DGRP lines should be included at least in supplementary information, if not as main figure.
      10. For Fig. 5, what is the reason that uninjured flies don't show any SD phenotype? Are there any changes in their velocity? This is mentioned in passing on line 228-29 but should be properly discussed.
      11. Trans-Tango and UAS-Denmark, SytGFP experiments were performed previously by Wu et al., 2020 and Wang et al., 2021 for Dsk, these two studies observed that P1 neurons are presynaptic and Dsk neurons are post synaptic but in Figure 4 it's not clear what are the presynaptic and post synaptic neurons. Also these studies are not cited appropriately in this section.

      Minor comments:

      1. Line no. 286: please mention about the relative humidity and light & dark cycle conditions and when experiments were conducted (ZT).
      2. Line no. 311: How many days old flies were used (isolated and group housed) for the behavior and transcriptomic studies?
      3. Line no. 349: for RNA extraction please mention how many fly heads were used and ZT for collection.
      4. Line no. 358: Italicize "Drosophila melanogaster".

      Significance

      This manuscript will be of interest to neuroscientists studying Drosophila social behaviors. The manuscript asks interesting questions and authors have done extensive set of experiments but the progress appears incremental given the current state of the field, especially for the later part of the manuscript. Some of the interpretation would also require additional data to bolster the claims made. Finally, the findings from this study could be better discussed in the context of what it is already known.

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      Reply to the reviewers

      We thank all reviewers for their constructive criticism and suggestions. We have addressed all the points as detailed below. We also added an experiment that strengthens the connection between replication stress and GSF2 and suggests a role of GSF2 in recovery from the DNA replication checkpoint arrest (Fig. 4g).

      Reviewer #1 (Evidence, reproducibility and clarity)

      Summary

      The manuscript by the Khmelinskii group reports that they have successfully constructed two conditional degron libraries of budding yeast for almost all proteins. For this purpose, the authors employed an improved auxin-inducible degron (AID2). Initially, they constructed yeast libraries by fusing HaloTag to the N- or C-terminus of proteins and found that C-terminal tagging is less likely to affect the location and function of proteins (Fig. 1). Based on this finding, the authors fused mNG-AID*-3Myc or AID*-3Myc (AID-v1 or AID-v2 library, respectively) to more than 5600 proteins and found that 4079 proteins were significantly depleted when cells were treated with 5-Ph-IAA (Fig. 2). A fitness defect was observed for over 60% of essential proteins, indicating the target depletion showed the expected phenotype in many cases (Fig. 3). Finally, the authors screened proteins required for maintaining viability in the presence of MMS, CPT and HU, and identified common proteins involved in DNA repair (such as RAD52 epistasis proteins) and other proteins specific for MMS, CPT or HU resistance (Fig. 4). Furthermore, the authors revealed that an ER membrane protein, Gsf2, is required for HU resistance, which was not found in previous studies with the YKO library because gsf2∆ cells in the YKP library had acquired a suppressor mutation (Fig. 4e).

      Major comments

      1 - In Figure S2a, the authors initially checked the growth of yeast cells expressing OsTIR1(F74G) under the GAL1 promoter, saying that "expression of OsTir1(F74G) from the strong galactose-inducible GAL1 promoter had a negligible impact on yeast fitness (page 3)". To me, the OsTIR1(G74G) expressing cells showed slightly slower growth compared to the control cells. Moreover, the cells expressing it under the very strong GPD promoter showed apparent slow growth, suggesting that OsTIR1(F74G) overexpression caused a side effect. The authors should carefully evaluate the cells with GAL1-OsTIR1(F74G).

      Indeed high levels of OsTir1(F74G) impaired growth, at least in the strain background used in our experiments. Expression from the strongest promoter we tested (GPD) resulted in an obvious fitness defect, whereas conditional expression from the strong GAL1 promoter had a small impact on fitness and expression from the weaker CYC1 and ADH1 promoters did not affect fitness (Fig. S2a). Despite the small fitness impairment, we decided to use the GAL1-OsTIR1(F74G) construct for the AID libraries for two reasons: the conditional nature of this promoter is likely to limit adaptation to expression of OsTir1(F74G) and the high expression levels of OsTir1(F74G) are less likely to limit degradation of AID-tagged proteins. We added this explanation to the Results section.

      As suggested by the reviewer, we quantitatively evaluated the fitness impact of the GAL1-OsTIR1(F74G) construct. Using the colony size data of the AID-v1 library (grown on galactose medium with 1 µM 5-Ph-IAA, Fig. 2c), we compared colony sizes of OsTIR1– and OsTIR1+ strains for non-essential ORFs. As degradation of non-essential proteins is not expected to affect fitness, the difference in colony size between OsTIR1– and OsTIR1+ strains can be attributed to OsTir1 expression. On average, the presence of the OsTIR1 construct reduced colony size by 7% (median fitness of OsTIR1+ strains relative to OsTIR1– strains of 0.93 ± 0.06, n = 4698 non-essential ORFs). We performed the same comparison for strains that did not exhibited OsTIR1-dependent protein degradation. In this set of strains, the presence of the OsTIR1 construct also reduced colony size by 7% (median fitness of OsTIR1+ strains relative to OsTIR1– strains of 0.93 ± 0.05, n = 624 ORFs in the “not affected” group in Fig. 2d). We added this information to Fig. S3a.

      2 - Given the possibility that OsTIR1(F74G) overexpression might cause a growth problem, it is not appropriate to compare OsTIR1+ and OsTIR1- conditions for evaluating growth fitness (Fig. 2). As shown in Fig. S4b, it is more appropriate to compare the +/- 5-Ph-IAA conditions. Additionally, the 5-Ph-IAA concentration used in this study was not clearly mentioned in the method section and figure legends.

      The two approaches, comparison of OsTIR1– and OsTIR1+ strains grown on galactose with 5-Ph-IAA (as was done for the AID-v1 library) and comparison of galactose ± 5-Ph-IAA conditions (as was done for the AID-v2 library), have advantages and disadvantages but should yield similar results. The technical noise (due to spatial effects on the screen plates) is lower for the comparison of OsTIR1– and OsTIR1+ strains, as the two strains for each ORF can be grown next to each other on the same plate (Fig. 2c). Furthermore, corrections of spatial effects are more precise with this layout as the frequency of fitness defects per plate is lower. On the other hand, comparison of galactose ± 5-Ph-IAA conditions implicitly corrects for the fitness impact of the GAL1-OsTIR1(F74G) construct, as the fitness distribution of each condition is normalized to the median of that condition, but this fitness impact of OsTir1 cannot be determine from the screen results.

      We now explicitly corrected the colony size data of the AID-v1 library for the fitness impact of OsTir1 expression (quantified in the previous point) and updated all the analyses and results shown in Fig. 3, Fig. S3b-e and Fig. S4a. The correction was performed using the multiplicative model, whereby the fitness impacts of OsTir1 expression and degradation of the AID-tagged protein are independent. Overall, our observations and conclusions stand unchanged with the corrected data.

      Finally, the 5-Ph-IAA concentration (1 µM) used in all experiments is now indicated in the figure legends and the Methods section.

      3 - The authors found that fitness defects were observed for over 60% of essential proteins (Fig. 3). In other words, depletion of the remaining 40% was not enough to induce growth defects. The authors should discuss how the current AID library can be improved to achieve better target depletion. Previous literature reported various possibilities, such as using a tandem degron tag and combining AID with the Tet promoter system (PMID 25181302, 26081484). Although optional, it would be wonderful if the authors would generate an improved library.

      Following the reviewer’s suggestion, we added the following statement to the discussion:

      “In the future, the libraries could be potentially improved with N-terminal tagging of ORFs that currently exhibit incomplete or no degradation of AID-tagged proteins or using multiple copies of the AID* tag to enhance protein degradation (Kubota et al, 2013; Nishimura & Kanemaki, 2014).”

      Minor comments

      4 - 5-Ph-IAA is not auxin because it does not induce the auxin responses in plants (PMID 29355850). Therefore, the authors should be careful when they refer to 5-Ph-IAA and should not call it auxin.

      We corrected this and now refer to 5-Ph-IAA explicitly throughout the manuscript.

      5 - The availability of the HaloTag and AID libraries should be indicated.

      We added the following statement to the Methods section: “All strains, plasmids and libraries are available upon request.”

      6 - Page 3: "Finally, the extent of AID-dependent degradation varied with protein abundance, in that highly expressed proteins were more likely to be only partially degraded compared to lowly expressed ones (Fig. 2e, Fig. S2e)". Fig. S2e should be Fig. S2d, shouldn't it?

      We corrected this mistake.

      Reviewer #1 (Significance):

      This paper is technically robust and well-conducted. It presents a comprehensive study showcasing the effectiveness of the conditional degron library. The HaloTag libraries will also be useful. The yeast libraries presented in this study will be invaluable for future screenings and studies across all aspects of yeast biology.

      Reviewer #2 (Evidence, reproducibility and clarity):

      In this study, the authors reported the development and characterization of two AID-tagged strain libraries for the model organism S. cerevisiae. The libraries are based on the latest AID technology, AID2. One library contains a fluorescent protein fused to the AID, whereas the other library does not have the fluorescent protein, thus offering better compatibility with imaging-based screens. The authors show that AID-dependent protein degradation can be achieved for most of the library strains, and a growth phenotype was induced for a high fraction of essential genes. Genetic screens for DNA damage-sensitive mutants showcased the applicability of the libraries.

      I only have the following minor comments and suggestions for the authors to consider.

      Point 1, Page 3

      "Optimized tagging of proteins with these N-terminal localization signals likely also contributes to the lack of correlation between differential fitness defects and occurrence of terminal localization signals (Fig. S1f, Table S2)."

      Is this because the genes that cannot tolerate C-terminal addition are already depleted in the C-SWAT library? In the C-SWAT library, a 15-amino-acid linker L3 is added to the C-terminus.

      That is certainly a possibility. During construction of SWAT library, tagging with N-SWAT and C-SWAT acceptor modules failed for 251 and 353 ORFs, respectively (Weill et al. 2018, Meurer et al. 2018). However, these ORFs are not enriched in N- or C-terminal localization signals, respectively (4.6% ORFs with C-terminal signals in C-SWAT library vs 3.3% among failed C-SWAT strains; 12.3% ORFs with N-terminal signals in N-SWAT library vs 2.0% among failed N-SWAT strains).

      The most significant trend in the data is enrichment of ribosomal subunits in both sets of failed strains: 3.9% and 16.3% of the genes mapped to the GO term “ribosome” in the N-SWAT library and the set of failed N-SWAT strains, respectively; 3.6% and 15.9% of the genes in the C-SWAT library and the set of failed C-SWAT strains, respectively. This is consistent with what was reported by Weill et al. for failed N-SWAT strains.

      Point 2, Page 3

      "Expression of OsTir1(F74G) from the strong galactose-inducible GAL1 promoter had a negligible impact on yeast fitness (Fig. S2a)."

      I wonder why the authors chose to use an inducible promoter to express OsTir1(F74G). In other studies, for example Snyder et al. 2019, OsTir1 has been expressed from a constitutive promoter.

      Despite the small fitness impairment, we decided to use the GAL1-OsTIR1(F74G) construct for the AID libraries for two reasons: the conditional nature of this promoter is likely to limit adaptation to expression of OsTir1(F74G) and the high expression levels of OsTir1(F74G) are less likely to limit degradation of AID-tagged proteins. We added this explanation to the Results section.

      Please see our response to reviewer 1, points 1 and 2.

      Point 3, Page 3

      "A similar frequency was previously observed with a set of AID alleles constructed for 758 essential ORFs using the original AID system (Snyder et al, 2019). However, over a third of these alleles exhibited fitness defects even in the absence of auxin, which were further compounded by off-target effects of auxin, highlighting the advantages of the AID2 system."

      Snyder et al. 2019 used a TAP-AID-6FLAG tag. The fitness defect in the absence of auxin may not necessarily be due to the AID part of the tag, as TAP tagging is known to compromise the functions of some genes.

      We corrected our statement as follows:

      “A similar frequency was previously observed with a set of AID alleles constructed for 758 essential ORFs using the original AID system (Snyder et al, 2019). However, over a third of these alleles exhibited fitness defects even in the absence of auxin, which were further compounded by off-target effects of auxin.”

      Point 4, Page 3

      "Interestingly, complete degradation of 33% of essential proteins did not result in a fitness defect. It is possible that in some cases partial degradation results in low protein levels that are below the detection limit of our assay but are sufficient for viability."

      Are these "33% of essential proteins" enriched with genes with low expression levels? I guess genes with low expression levels are more likely to fall below the detection limit even when partially depleted. Are there extreme examples where a highly expressed essential gene does not exhibit a fitness defect when the protein product is no longer detectable?

      We performed the analysis suggest by the reviewer, and observed no difference in pre-degradation protein levels between essential & degraded proteins with and without a fitness defect (now shown in Fig. S3b). This also showed that there are indeed several essential proteins with high pre-degradation proteins levels and without a fitness defects upon degradation to below our detection limit: Pgi1, Nhp2, Smt3, Gus1, Dys1, Sis1, Fas2 and Rpo26 (in the abundance bin 4 in Fig. S2f).

      In addition, we considered the nature of the essential genes in these two groups. Namely, we compared the frequency of core essential genes, which are always required for viability, and conditional essential genes, which vary in essentiality depending on the genetic background or environment (Bosch-Guiteras & van Leeuwen, 2022). Interestingly, the set of essential and degraded proteins without an accompanying fitness defect was enriched in conditional essential genes defined by two independent measures: essentiality across S. cerevisiae natural isolates (Peter et al, 2018) or with bypass suppression interactions in a laboratory strain (van Leeuwen et al, 2020) (Fig. S3c, odds ratio = 1.6, p-value = 0.04 in a Fisher’s exact test and odds ratio = 1.7, p-value = 0.02, respectively). This suggests that conditional essentiality could explain the observed lack of fitness defects upon degradation of some essential proteins.

      We added this analysis to the Results section.

      Reviewer #2 (Significance):

      This study generated highly valuable resources for functional genomic studies.

      Reviewer #3 (Evidence, reproducibility and clarity):

      Summary: In this manuscript, the authors construct and analyze a genome-wide collection of AID-tagged S. cerevisiae strains. The manuscript is clearly written and the analysis appears to be thorough. This collection will be quite useful to the yeast community. There are some issues to address, listed below.

      1. page 1, abstract - "...with protein abundance and tag accessibility as limiting factors." It's not clear what the authors mean by protein abundance as a limiting factor. Are they referring to the protein level pre-depletion? Please clarify.

      That is correct. We clarified this statement as follows:

      “Almost 90% of AID-tagged proteins were degraded in the presence of the auxin analog 5-Ph-IAA, with initial protein abundance and tag accessibility as limiting factors.”

      1. page 1, second paragraph of the Intro, end of the paragraph - There are publications prior to Van Leeuwen et al. 2016 that describe suppressors lurking in the deletion set. Here are two that should be cited: Hughes et al. 2000, DOI: 10.1038/77116 and Teng et al. 2013, DOI: 10.1016/j.molcel.2013.09.026.

      We added the references pointed out by the review.

      1. The goal of this work, stated in the first sentence of results, is to construct genome-wide AID libraries. Yet, to test whether N-terminal or C-terminal tagging is better, the authors used a Halo tag. Those results showed that, for the Halo tag, C-terminal tagging was less likely to impair function. Why weren't these tests done with the same AID tag used to build the libraries in the next section? What is the evidence that the results for a Halo tag will be the same as for an AID tag? While hard to find it documented in publications, there is a lot of anecdotal evidence that the type of tag can make a big difference, as well as its location. While this section will be of interest to those using Halo tags, it's not clear how it relates to the rest of the paper, especially given the careful characterization of the AID library in the next section.

      We chose the Halo tag due its size (33 kDa), similar to many commonly used fluorescent protein tags and to the mNG-AID*-3myc tag in the AID-v1 library, and lack of evidence for a dominant negative effect on the tagged proteins. This is now stated in the Results section.

      We agree that further work is needed to understand how the type of tag, its size and biophysical properties, and the linker between the tag and the protein of interest affect protein localization and function across the proteome. This is now stated in the Results section.

      1. Throughout this manuscript, including the Tables, in cases where the protein is no longer detected, please do not describe this as "complete degradation." Instead, please use "not detectable." This is clearly the case for essential proteins that are no longer detected but that still grow, so it is very likely the case for many or all of the others. If the authors have any understanding of the sensitivity of their fluorescence assay, then that would be helpful to know. For example, they could add a control, taking a known amount of a fluorescent protein and analyzing known dilutions to assay the level of detection.

      We appreciate the reviewer’s suggestion. We decided against “not detectable” instead of “complete degradation” to avoid confusion with proteins that are not detectable pre-degradation. Nevertheless, we replaced “complete degradation” with “degradation” and added the following explanation to the Results section:

      “Out of 5079 proteins detected in OsTIR1– strains, 4455 (~88%) were significantly depleted in OsTIR1+ strains (Fig. 2d, Table S3). 3981 proteins could not be detected specifically in the OsTIR1+ background. Hereafter, we will refer to these proteins as degraded, although it is likely that at least in some cases degradation is not complete but the remainder is below the detection limit of our plate reader assay. Nevertheless, 474 proteins were unequivocally degraded only partially, as they were detectable in the OsTIR1+ background but at reduced levels compared to the OsTIR1– background (Fig. 2d).”

      To estimate the detection limit of the colony fluorescence assay, we correlated the background-corrected mNG intensities in OsTIR1– strains with absolute levels (in molecules per cell) of 1167 proteins determined by Lawless et al. (PMID 26750110). Based on a linear fit, the threshold above which proteins are considered “detected” in our analysis, mNG/bkg(OsTIR1–) > 1.2, corresponds to 200 molecules per cell (95% confidence interval 18 to 2187 molecules per cell). We added this information to the Results section and Fig. S2c.

      This detection limit is in line with our results, where low abundance proteins such as the centromeric histone Cse4/CENP-A (with two Cse4 molecules per centromere adding to 64 molecules per cell, Aravamudhan et al. PMID: 23623551 and several times that amount elsewhere in the cell, Collins et al. PMID: 15530401) can be detected in the colony assay (Table S3).

      1. Fig. S2a and page 3, first full paragraph - The authors wrote that expression of OsTir1(F74G) from the strong GAL1 promoter had a negligible impact on growth. However, the figure shows that there is an obvious effect on growth after 48 hours of incubation, with much smaller colonies. This defect is much less obvious after 72 hours. This difference suggests that the growth effect would have been even more obvious at 24 hours. I think that the text should be modified to indicate this effect.

      We now quantified the fitness impact of the GAL1-OsTIR1(F74G) construct and rephrased this part of the manuscript. In addition, we corrected the AID-v1 library screen results for the fitness impact of the GAL1-OsTIR1(F74G) construct and updated all figures and tables. Please see our response to reviewer 1, points 1 and 2.

      1. One of the main justifications for the construction of the AID library is to allow assays for essential genes. Yet that was not a feature of the screen for DNA damage response factors. Were any essential genes identified in those screens? It would be of great interest to identify lower levels of 5-Ph-IAA that only mildly affect growth of essential genes and then to repeat the screens.

      58 out of the combined 165 potential resistance factors identified in the three screens are essential genes. We added this information to the Results section and essential genes are now indicated in Fig. S5c.

      We now show that chemical-genetic interactions for both essential and non-essential genes can be reproduced in spot tests using the MMS screen as an example (Fig. S5d). We also show that additional essential hits can be identified at lower concentrations of 5-Ph-IAA, which allow determining chemical-genetic interactions for strains that otherwise exhibit no growth in 1 μM 5-Ph-IAA (Fig. S5e). As the screens serve as a demonstration of possible uses of the AID libraries, we consider additional exhaustive screening for DNA damage response factors beyond the scope of this manuscript.

      1. A big advantage of AID depletion over deletions is the ability to look at strains very shortly after loss of the protein of interest. In many cases in the literature, experiments are done after one or two hours after depletion. Yet in this work, there are no data presented on how effective depletion is in the short term versus after a long period of growth (24 hours). It would be a strong addition to the manuscript to include a time course for at least a subset of the proteins to look at the loss of signal over time, either by fluorescence or by Western blots.

      We performed time courses of protein depletion with immunoblotting for 12 strains (4 proteins from the “degraded”, “partially degraded” and “not affected” groups each). The results in Fig. S2e show that “degraded” proteins are depleted to below the detection limit within 60min of 5-Ph-IAA addition, “partially degraded” proteins are depleted less or exhibit a degradation-resistant pool, and the levels of “not affected” proteins remain stable over time, consistent with their classification based on mNG fluorescence in the colony assay. We added this information to the Results section.

      Reviewer #3 (Significance):

      The library will be of use to the yeast community.

    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 this manuscript, the authors construct and analyze a genome-wide collection of AID-tagged S. cerevisiae strains. The manuscript is clearly written and the analysis appears to be thorough. This collection will be quite useful to the yeast community. There are some issues to address, listed below.

      1. page 1, abstract - "...with protein abundance and tag accessibility as limiting factors." It's not clear what the authors mean by protein abundance as a limiting factor. Are they referring to the protein level pre-depletion? Please clarify.
      2. page 1, second paragraph of the Intro, end of the paragraph - There are publications prior to Van Leeuwen et al. 2016 that describe suppressors lurking in the deletion set. Here are two that should be cited: Hughes et al. 2000, DOI: 10.1038/77116 and Teng et al. 2013, DOI: 10.1038/77116 .
      3. The goal of this work, stated in the first sentence of results, is to construct genome-wide AID libraries. Yet, to test whether N-terminal or C-terminal tagging is better, the authors used a Halo tag. Those results showed that, for the Halo tag, C-terminal tagging was less likely to impair function. Why weren't these tests done with the same AID tag used to build the libraries in the next section? What is the evidence that the results for a Halo tag will be the same as for an AID tag? While hard to find it documented in publications, there is a lot of anecdotal evidence that the type of tag can make a big difference, as well as its location. While this section will be of interest to those using Halo tags, it's not clear how it relates to the rest of the paper, especially given the careful characterization of the AID library in the next section.
      4. Throughout this manuscript, including the Tables, in cases where the protein is no longer detected, please do not describe this as "complete degradation." Instead, please use "not detectable." This is clearly the case for essential proteins that are no longer detected but that still grow, so it is very likely the case for many or all of the others. If the authors have any understanding of the sensitivity of their fluorescence assay, then that would be helpful to know. For example, they could add a control, taking a known amount of a fluorescent protein and analyzing known dilutions to assay the level of detection.
      5. Fig. S2a and page 3, first full paragraph - The authors wrote that expression of OsTir1(F74G) from the strong GAL1 promoter had a negligible impact on growth. However, the figure shows that there is an obvious effect on growth after 48 hours of incubation, with much smaller colonies. This defect is much less obvious after 72 hours. This difference suggests that the growth effect would have been even more obvious at 24 hours. I think that the text should be modified to indicate this effect.
      6. One of the main justifications for the construction of the AID library is to allow assays for essential genes. Yet that was not a feature of the screen for DNA damage response factors. Were any essential genes identified in those screens? It would be of great interest to identify lower levels of 5-Ph-IAA that only mildly affect growth of essential genes and then to repeat the screens.
      7. A big advantage of AID depletion over deletions is the ability to look at strains very shortly after loss of the protein of interest. In many cases in the literature, experiments are done after one or two hours after depletion. Yet in this work, there are no data presented on how effective depletion is in the short term versus after a long period of growth (24 hours). It would be a strong addition to the manuscript to include a time course for at least a subset of the proteins to look at the loss of signal over time, either by fluorescence or by Western blots.

      Significance

      The library will be of use to the yeast community.

    3. 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 study, the authors reported the development and characterization of two AID-tagged strain libraries for the model organism S. cerevisiae. The libraries are based on the latest AID technology, AID2. One library contains a fluorescent protein fused to the AID, whereas the other library does not have the fluorescent protein, thus offering better compatibility with imaging-based screens. The authors show that AID-dependent protein degradation can be achieved for most of the library strains, and a growth phenotype was induced for a high fraction of essential genes. Genetic screens for DNA damage-sensitive mutants showcased the applicability of the libraries.

      I only have the following minor comments and suggestions for the authors to consider.

      Point 1

      Page 3

      "Optimized tagging of proteins with these N-terminal localization signals likely also contributes to the lack of correlation between differential fitness defects and occurrence of terminal localization signals (Fig. S1f, Table S2). " Is this because the genes that cannot tolerate C-terminal addition are already depleted in the C-SWAT library? In the C-SWAT library, a 15-amino-acid linker L3 is added to the C-terminus.

      Point 2

      Page 3

      "Expression of OsTir1(F74G) from the strong galactose-inducible GAL1 promoter had a negligible impact on yeast fitness (Fig. S2a)." I wonder why the authors chose to use an inducible promoter to express OsTir1(F74G). In other studies, for example Snyder et al. 2019, OsTir1 has been expressed from a constitutive promoter.

      Point 3

      Page 3

      "A similar frequency was previously observed with a set of AID alleles constructed for 758 essential ORFs using the original AID system (Snyder et al, 2019). However, over a third of these alleles exhibited fitness defects even in the absence of auxin, which were further compounded by off-target effects of auxin, highlighting the advantages of the AID2 system." Snyder et al. 2019 used a TAP-AID-6FLAG tag. The fitness defect in the absence of auxin may not necessarily be due to the AID part of the tag, as TAP tagging is known to compromise the functions of some genes.

      Point 4

      Page 3

      "Interestingly, complete degradation of 33% of essential proteins did not result in a fitness defect. It is possible that in some cases partial degradation results in low protein levels that are below the detection limit of our assay but are sufficient for viability." Are these "33% of essential proteins" enriched with genes with low expression levels? I guess genes with low expression levels are more likely to fall below the detection limit even when partially depleted. Are there extreme examples where a highly expressed essential gene does not exhibit a fitness defect when the protein product is no longer detectable?

      Significance

      This study generated highly valuable resources for functional genomic studies.

    4. 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 the Khmelinskii group reports that they have successfully constructed two conditional degron libraries of budding yeast for almost all proteins. For this purpose, the authors employed an improved auxin-inducible degron (AID2). Initially, they constructed yeast libraries by fusing HaloTag to the N- or C-terminus of proteins and found that C-terminal tagging is less likely to affect the location and function of proteins (Fig. 1). Based on this finding, the authors fused mNG-AID-3Myc or AID-3Myc (AID-v1 or AID-v2 library, respectively) to more than 5600 proteins and found that 4079 proteins were significantly depleted when cells were treated with 5-Ph-IAA (Fig. 2). A fitness defect was observed for over 60% of essential proteins, indicating the target depletion showed the expected phenotype in many cases (Fig. 3). Finally, the authors screened proteins required for maintaining viability in the presence of MMS, CPT and HU, and identified common proteins involved in DNA repair (such as RAD52 epistasis proteins) and other proteins specific for MMS, CPT or HU resistance (Fig. 4). Furthermore, the authors revealed that an ER membrane protein, Gsf2, is required for HU resistance, which was not found in previous studies with the YKO library because gsf2∆ cells in the YKP library had aquired a suppressor mutation (Fig. 4e).

      Major comments

      • In Figure S2a, the authors initially checked the growth of yeast cells expressing OsTIR1(F74G) under the GAL1 promoter, saying that "expression of OsTir1(F74G) from the strong galactose-inducible GAL1 promoter had a negligible impact on yeast fitness (page 3)". To me, the OsTIR1(G74G) expressing cells showed slightly slower growth compared to the control cells. Moreover, the cells expressing it under the very strong GPD promoter showed apparent slow growth, suggesting that OstIR1(F74G) overexpression caused a side effect. The authors should carefully evaluate the cells with GAL1-OsTIR1(F74G).
      • Given the possibility that OsTIR1(F74G) overexpression might cause a growth problem, it is not appropriate to compare OsTIR1+ and OsTIR1- conditions for evaluating growth fitness (Fig. 2). As shown in Fig. S4b, it is more appropriate to compare the +/- 5-Ph-IAA conditions. Additionally, the 5-Ph-IAA concentration used in this study was not clearly mentioned in the method section and figure legends.
      • The authors found that fitness defects were observed for over 60% of essential proteins (Fig. 3). In other words, depletion of the remaining 40% was not enough to induce growth defects. The authors should discuss how the current AID library can be improved to achieve better target depletion. Previous literature reported various possibilities, such as using a tandem degron tag and combining AID with the Tet promoter system (PMID 25181302, 26081484). Although optional, it would be wonderful if the authors would generate an improved library.

      Minor comments

      • 5-Ph-IAA is not auxin because it does not induce the auxin responses in plants (PMID 29355850). Therefore, the authors should be careful when they refer to 5-Ph-IAA and should not call it auxin.
      • The availability of the HaloTag and AID libraries should be indicated.
      • Page 3: "Finally, the extent of AID-dependent degradation varied with protein abundance, in that highly expressed proteins were more likely to be only partially degraded compared to lowly expressed ones (Fig. 2e, Fig. S2e)". Fig. S2e should be Fig. S2d, shouldn't it?

      Significance

      This paper is technically robust and well-conducted. It presents a comprehensive study showcasing the effectiveness of the conditional degron library. The HaloTag libraries will also be useful. The yeast libraries presented in this study will be invaluable for future screenings and studies across all aspects of yeast biology.

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

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      Reply to the reviewers

      Response to Reviewer #1

      Major comments:

      1. * The connection between vB12 and MMA is weak, and the attempt to connect these pieces to PPI seems somehow forced. For instance, the authors do not convincingly demonstrate that MMA causes the PPI deficit. Furthermore, vB12 may rescue PPI independently of MMA. The authors should be more transparent about the lack of connection or causality between changes in metabolism and behavior.* We appreciate the reviewer's comment and acknowledge that we have not demonstrated causal relationships between increased MMA, PPI deficits in Tbx1+/- mice and their rescue by vB12. They are associations.

      In the revised manuscript, we have clarified this in the Discussion, para.4, by adding the following phrase. “The results of our study do not prove a causal relationship between elevated brain MMA and PPI impairment, nor do they tell us whether rescue of the PPI impairment by vB12 occurs by reducing MMA”.

      Regarding the comment of a weak connection between vitamin B12 and MMA, we respectfully disagree.

      The biochemistry underlying the connection is outlined clearly in the Introduction, page 4, para. 2.

      Patients with vitamin B12 deficiency typically exhibit elevated levels of MMA and administration of vitamin B12 (cobalamin) helps to normalize MMA values (Robert & Brown, 2003). Furthermore, several animal models with genetic alterations in the vitamin B12 pathway exhibit high levels of MMA. For instance, mice lacking the cobalamin transporter have increased MMA (Bernard et al., 2018). Additionally, mice lacking the mutase (Mut), which requires vitamin B12 as a cofactor for the conversion of methylmalonyl CoA to succinyl-CoA for entry into the Krebs cycle, demonstrate elevated levels of MMA and are unresponsive to vitamin B12 treatment (Peters et al. 2006). In the revised manuscript, we have cited these references (Introduction, page 4, para. 2).

      Throughout the manuscript, an important control is missing: WT+ vB12 group. Data from this group should be added to Figures 1, 3, 4, 6, and Supplemental Figures 3 and 4 to show the effect of vB12 on WT mice.

      All of the experiments reported in the original manuscript included this control group although it was not always included in the data analysis and therefore in the figures, as observed by the reviewer, In the revised manuscript all of the relevant figures and tables now include these data.

      In Figures 1C and 3, data from the respective WT controls in the Df1 and Tbx1 cohorts should be shown.

      • *

      The wild type (WT) animals serve as the control group for both Tbx1+/- and Df/+ mice because they were littermates, obtained from matings between Df1/+ and Tbx1+/- mice. This has been clarified in the Materials and Methods, and in a new cartoon which has been added to Supplementary Figure 1 (1C) showing all of the animal groups used for the various studies (NMR, transcriptomics, behavior).

      The Supplemental Table S1 includes 17 WT controls for Tbx1+/- and 6 WT controls for Df1/+, but Figure 1C includes only one group of 11 WT controls. For which group were those 11 WT controls?

      Here are several examples of inconsistency in the data: "For this, we first performed a preliminary metabolome analysis using isolated whole brains of male and female Tbx1+/- (n= 18) and WT (n= 10) mice between one and two months of age. A set of metabolites was quantified in brain extracts by liquid chromatography tandem mass spectrometry (LC-MS/MS) (Supplementary Table 1)." Again, the number of mice the authors note in the manuscript does not match that shown in Supplementary Table 1 (Tbx1+/- (n=14) and WT (N=17). "We analyzed whole brain tissue isolated from Df1/+ and WT (control) mice (n = 5 per genotype)." Again, the numbers of mice do not match those in Supplementary Table 1, which notes 6 Df1/+ mice and 6 WT mice.

      We apologize for these errors and inconsistencies in the text and tables, all of which have been corrected in the revised manuscript. In addition, we have added the aforementioned cartoon (Supplementary Figure 1C) and we have improved the presentation of the data (genotypes and treatments) in Supplementary Tables 1 and 2. We hope that these changes provide the expected clarity to the data.

      MMA is the only metabolite that is similarly changed between Tbx1+/- and Df1/+ brains. This is an interesting observation. However, there is no other overlap in metabolic changes between these two mutants. This is a concern that requires clarification

      We appreciate the reviewer's comment. The observation is not altogether surprising considering that the Df1 deletion includes at least 9 genes involved in metabolic pathways (cited refs (Maynard, 2008;Meechan, 2011; Devaraju and Zakharenko, 2017)) any of which might counteract or compensate for changes caused by Tbx1 mutation alone. In addition, heterozygosity for other genes in the deleted region (Df1 encompasses over 20 genes) might affect metabolic processes indirectly. In the revised manuscript we have added the following phrase to the Discussion, para.1 “Thus, even though the two mutants are genetically and metabolically very different, in Df1/+ mice, the MMA phenotype is not affected by heterozygosity of other genes in the deletion.

      The authors mention that MMA is not changed in pre-term Tbx1+/- embryos, but no data are provided. What about MMA levels in Df1/+ embryos?

      In pre-term Tbx1+/- and WT embryos MMA was undetectable. This is now stated in the final paragraph of the first section of the Results.

      We did not measure MMA in Df1/+ embryos. It was not a goal of the study to compare the metabolome of these two genetically very different mutants. The MMA data on Df1/+ mice are presented because they show the potential relevance of this phenotype for the human disease, and they justify the use of the single gene (Tbx1+/-) mutants for studies into metabolism-related disease mechanisms. See also response to point 12

      * * In some cases, the differences in metabolites (e.g., glutamine, glutamate, phosphoethanolamine, taurine, leucine, myo-inositol, and niacinamide) between the WT and Tbx1+/- mice is very minimal (Supplemental Figure 2). The y-axis scale should start at 0.

      We have changed the y-axis settings where necessary

      The vB12 is administered via two different regimens: 1) every 3 days for 28 days, at 4-8 weeks of age for metabolic measurements, and 2) twice a week for 2 months for PPI behavioral testing. Is there any reason the authors chose different protocols?

      We apologize for the confusion, which was due to an oversight in the Materials and Methods section that has been corrected. The weekly injection regimen was the same for mice used in the behavioral and metabolic studies, but the treatment time was shorter for the metabolic studies, for practical reasons beyond our control; mice received vB12 injections twice a week, beginning at 4 wks of age and continuing until 8 wks or 12 wks of age for metabolic and behavioral studies respectively.

      * * The authors should add the following references to the study: Long et al., Neurogenetics (2006), which shows no change in PPI in Tbx1+/- mice. This discrepancy compared with the current study results and those of Paylor et al., Proc Natl Acad Sci U S A (2006) should be discussed.

      We have not cited the study by Long et al. because there are no obvious reasons for the discrepancy (age, mouse strain, sex) that could be discussed. Beyond this of course we cannot comment on data generated by another research group. Nevertheless, the presence of the PPI deficit in Tbx1+/- mice has been confirmed in two different Tbx1 alleles Tbx1 lacZ/+ and Tbx1ΔE5/+, by two different investigators, Dr. Richard Paylor using Tbx1 lacZ/+ mice (Paylor et al. 2001) and Dr. Elvira De Leonibus (co-author of this manuscript) using Tbx1ΔE5/+ mice, in two different countries (USA and Italy) in a rederived colony of mice.

      • Figure 6B is a concern. The PPI decrease in the Tbx1+/- group appears to be driven by results from 3-4 mice. First, are those data statistical outliers? *

      With all due respect, this is not the case. Eight Tbx1+/- mice, i.e., >50% of those tested had PPI values below the minimum observed in WT mice. The behavioural data were checked for the presence of outliers in each group using the Grubbs test, which yielded negative results. Our finding of PPI deficits in Tbx1+/- mice are in line with previously published data in Tbx1+/- and other animal models of 22q11.2 microdeletion (Paylor et al., 2006; Paylor and Lindsay, 2006; Stark et al., 2008), as well as in humans (Sobin et al., 2005).

      Second, experiments in the same mice would be more informative. Do PBS-treated mutants recover PPI if they are treated with vB12 and vice versa? If the authors are concerned about the age difference, they also should include age-dependent effects on PPI.

      We decline to perform the proposed experiment for the reasons described in section 4 of the Revision Plan

      • *

      Because vB12 treatment completely rescued the MMA level in Df1/+ mice (Figure 3), the authors should include a figure showing PPI test results in Df1/+ mice.

      Vitamin B12 treatment fully rescued the MMA phenotype in both mutants (Figure 3). Whether it rescues the PPI defect in Df1/+ mice is not important for this study. We used Df1/+ mice as an entry point, in order to give validity to the pursuit of the MMA phenotype in the single gene mutant (Tbx1+/-), in which we expect that it will be easier to find disease mechanisms. For this reason, we focused our attention on identifying metabolic alterations in adult Tbx1+/- mice.

      See also response to point 7.

      *Figure 1A and B table: Did the authors mean Log2FC instead of FC? The authors also should present the *

      *source data by adding supplemental tables that include raw data and normalized conversion, etc., as described in the multivariate statistical data analysis of the LC-MS/MS data. *

      • *

      The new Figures 1A, Figure 3 and the accompanying tables now state Log2FC. New Supplementary Table 1 presents the raw data that were normalized on the basis of the amount of protein in the samples, described and referenced in the Materials and Methods

      "...we identified a new metabolic phenotype that was associated with reduced sensorimotor gating deficits in Tbx1+/- mice". Although the authors showed the PPI rescue by treating Tbx1+/- mice with vB12, that result alone does not prove the association of metabolic phenotype with sensorimotor-gating deficit; other supporting data are needed.

      • *

      This is perhaps a question of semantics; by associated we mean that the two phenotypes, metabolic alterations and reduced PPI were observed together

      The authors stated, "Results showed that there were very few differentially expressed genes in Tbx1+/- vs WT brains, (n=22 out of 14535 expressed genes (Fig. 5 and Supplementary Tab. 2)". However, they described how 3 differentially expressed genes are involved in mitochondrial activity in the Discussion. The authors should describe those 3 genes and their relation to the metabolic change.

      The results that the reviewer refers to have changed in the revised manuscript due to the inclusion of the control group WT +vB12 in the data analysis. The transcriptome analysis revealed that vB12 had a stronger impact than genotype, and as a consequence, the statistical analysis of all groups did not highlight minor differences between the two genotypes.

      Figure 5B: The authors claimed that they detected similar transcription profiles between WT+vB12 vs. Tbx1+/-+vB12, comparing Tbx1+/-+PBS vs. Tbx1+/-+vB12. This is based on 947 genes being downregulated and 834 being upregulated, which is not appropriate. The authors should normalize those data to the numbers of genes upregulated and downregulated in WT+PBS vs. WT+vB12 respective groups.

      We said that we detected similar transcription profiles in PBS-treated WT and Tbx1+/- brains; a WT+vB12 group was not present. The latter group is included in revised manuscript and the data reanalyzed comparing all groups.

      See also response to points 2 and 15.

      Minor comments

      1. Supplementary Table S1 shows the identical MMA concentration "0.2" for 6 controls. Is this correct? This was an error that has been corrected; the value is 0.00 (not detectable).

      * Remove the callout for Figure 1C at the end of the second paragraph in Results*.

      This figure is no longer present

      *There are multiple typos throughout the manuscript. *

      Here are several examples:

      1. * Fig1B graph- Df/+ => Df1/+* Figure changed in revised manuscript

      2. "Together, the hydrophilic and lipophilic results revealed a group of 6 compounds that characterized the brain metabolic differences between Tbx1+/- and WT mice (Figure 2B, 2C)". Figure 2A should be included also. Corrected

      3. "In support of this notion, is the finding that...(remove) Removed

      4. Remove double periods: "The pathways found are depicted in Figure 2C' which reports the impact of each pathway versus p values.." Corrected

      5. Panel labels in all figures are misplaced. Panel labels are aligned correctly

      We have performed a spelling and grammar check on the text

      "In support of this notion... at least nine orthologs are involved in mitochondrial metabolism". What are those 9 mitochondrial genes? Kolar et al., Schizophr Bull (2023) indicates that there are 8 mitochondrial genes within the 22q11.2 locus. The authors need to list these genes.

      This reference, which is a review, has been cited in the Introduction, para.3 along with the genes.

      The review presents nine mitochondrial genes which the authors divide into two groups, 1) Genes expressed in mitochondria (SLC25A1, TXNRD2, MRPL40, PRODH, and COMT) and 2) Genes that have been shown to have an impact on mitochondrial function (TANGO2, ZDHHC8, UFD1L, and DGCR8). In the abstract they mention only eight genes, the ninth gene COMT is mentioned in the text.

      Reviewer #2 (Significance (Required)):

      *The manuscript titled "Tbx1 haploinsufficiency causes brain metabolic and behavioral anomalies in adult mice which are corrected by vitamin B12 treatment" by Caterini et al. presents a comparative metabolomics study in the brains of mouse models carrying a heterozygous mutation in the transcription factor Tbx1. This mutation is contrasted with a chromosomal deficiency encompassing Tbx1, among other gene loci, known as Df1/+, which serves as a mouse model for 22q11 microdeletion syndrome. The primary and most significant finding of the study is that Tbx1 heterozygosity alone induces broad metabolomic alterations in the entire brain parenchyma, despite Tbx1 expression being confined to vascular endothelial cells. The authors leverage this observation to investigate the effects of dietary supplementation with vitamin B12, which alters the metabolome in a manner interpreted by the authors as rescuing or reversing the Tbx1 heterozygosity phenotype. This study holds promise for understanding the individual gene contributions to the penetrant behavioral phenotypes observed in Df1/+ and 22q11 affected subjects. This potential arises from the clear and consequential metabolic phenotypes described, notably the accumulation of methylmalonic acid.

      However, despite the intriguing metabolic phenotypes, there are significant issues hindering incontrovertible conclusions. *

      Response to Reviewer #2

      Major comments

      1. Despite the intriguing metabolic phenotypes, there are significant issues hindering incontrovertible conclusions. Chief among these problems is the experimental design's nature, where the effects of genotype and a pharmacological intervention, vitamin B12, are assessed. The current design overlooks the effects of vitamin B12 on wild-type animals in metabolic and behavioral measures, thus precluding the attribution of the effects of vitamin B12 to a rescue. See response to Reviewer 1 (point 2) who made the same criticism. This group is now included in the data analysis of the relevant experiments.

      *An alternative explanation, consistent with the measurements, is that vitamin B12 modifies metabolites and transcripts irrespective of genotype. A suggestion of this possibility is the observed effect of B12 lowering glutamate levels in Tbx1 mutant tissue below those in wild-type brain tissue (Fig. 4C). *

      This might be true for some metabolites. Indeed, we found 5 metabolites that responded similarly to vB12 in both WT and Tbx1 +/- mice. In contrast, three metabolites responded to vB12 in both WT and Tbx1+/- mice, but the response was more pronounced in Tbx1+/- mice. Finally, a group of eight metabolites was altered exclusively in Tbx1+/- mice after vB12 treatment, including inosine, glutamate and short-chain fatty acids (SCFAs), Figure 4 and Supplementary Figure 6. Thus, overall, our data suggest that with only a few exceptions, the metabolic response to vB12 treatment is genotype-dependent.

      • *

      This experimental design issue is exacerbated by the multitude of analytes measured by metabolomics, all collectively assumed to change as part of a common genotype-B12 interaction mechanism. This interpretation is feasible only if none of the analytes were to respond to B12 in wild-type animals.

      • *

      As specified above, the response to vB12 was genotype-dependent. The inclusion of the vB12-treated WT dataset should address this point.

      A second major issue arises from the assertion that Tbx1 is exclusively expressed in mouse brain endothelial cells and not in brain parenchyma. A significant unresolved question is how a gene expressed solely in endothelial cells can alter the brain parenchyma metabolome and transcriptome. This issue remains unaddressed and is not sufficiently discussed. If this assertion holds true, then the observations bear great importance in understanding how Df1/+ causes brain phenotypes and, by extension, in human 22q11.

      There are quite a lot of published data from the mouse demonstrating the brain endothelial-specific expression of Tbx1 and the lack of expression in other brain cell types. These include studies using reporter genes (Paylor, 2006; Cioffi, 2014), Tbx1Cre based cell fate mapping (Cioffi, 2014, Cioffi, 2022) and single cell whole genome transcriptions (Ximerakis et al., 2019); (https://portals.broadinstitute.org/single_cell/study/aging-mouse-brain). All are cited in the manuscript.

      HOW the mutation of Tbx1 alters the brain metabolome and transcriptome will be the object of future studies, Currently, we do not have any data. At the reviewer’s request, we have extended the discussion of this point in the revised manuscript (Discussion, para. 4).

      In this vein, the authors should consider that Tbx1 is not expressed in brain endothelial cells in humans and is minimally expressed in fetal astrocytes (see https://brainrnaseq.org/).

      https://brainrnaseq.org provides a tool to evaluate the gene expression in the fetal brain. The sequencing was performed on fetal human brain tissue after elective pregnancy termination (4wks-9wks, it is not clear). Our analysis focuses on adult mice, which may contribute to observed differences.

      Moreover, Yi et al. (2010) generated a gene expression atlas of human embryogenesis spanning from 4 to 9 weeks of gestational age, revealing downregulation of TBX1 during this timeframe. Conversely, in the normal adult human brain, TBX1 expression is identified in endothelial cells, as indicated in "The Human Brain Cell Atlas v1.0" presented for visualization and data mining through the Chan Zuckerberg Initiative’s CellxGene application, referring to the atlas ontology in Ding et al. (2016). * 3. A third major concern pertains to the general poor quality of the figures. Many figures appear to be directly exported from the software used for data analysis without proper curation. They are inadequately labeled, lack color codes to clarify differences (e.g., volcano plots), feature lettering fonts that are difficult to discern, and have lettering panels placed in awkward positions. Fig. 1 would benefit by the addition of a pathway diagram showing which metabolites are changing. Figure tables/spreadsheets either have sheets labeled in Italian or are empty. Collectively, the manuscript needs more careful data curation and presentation*.

      Many of the figures and tables have been modified with respect to the original manuscript and issues of clarity and quality have been improved where necessary.

      Other points for consideration are listed below. • The abstract results section does not mention the Df1 mutants at all, and overall the description of the results should be improved

      Corrected • The abstract would benefit from defining vB12 before using the abbreviation

      Corrected • The section of the Results describing MMA accumulation in the brain would benefit from

      • *explaining the choice of 1 month of age for terminal experiments and the choice to use whole brains (are there particularly brain regions suspected to be affected?), * The majority of animals were 2 months of age at sacrifice (age and sex of individual animals are indicated in Supplementary Table 1). Young adult mice were the object of the study for the reason described in the first paragraph of the Results section, namely “Human studies of brain metabolism have mainly been conducted on children and adolescent patients. Therefore, in order to determine whether similar anomalies were present in the mouse models, we performed our studies on young mice between 1 and 2 months of age (Dutta et al., 2016)”.

      This is also the age at which the behavioural phenotype has been demonstrated (Paylor et al., 2006), and therefore could, potentially be rescued by vB12 treatment. We do not have regional information pertaining to the adult brain.

      2) describing any sex effects for Tbx1 mutants (and clarifying what data points for Tbx1 animals correspond to which sex), and 3) including what sex was used for Df1 experiments.

      In preliminary experiment we analyzed males and females’ mice, before electing to use only males. To obtained reliable information about the impact of gender on metabolism and transcription we would have to use much larger numbers of animals. In Supplementary Table 1 pertaining to males and females are now indicated.

      • The authors demonstrate that vB12 rescues PPI but use no other behavioral paradigms. It is possible that these mutations and/or vB12 could be impacting anxiety-like behaviors or other behavioral phenotypes. By only including PPI, the authors limit the interpretation of the "rescue" of this phenotype by vB12. * Reduced PPI was the only behavioral anomaly identified in Tbx1+/- mice that were subjected to a standard battery of behavioral tests (Paylor et al., 2006). *

      * *Reduced PPI was the only behavioral anomaly identified in Tbx1+/- mice that were subjected to a standard battery of behavioral tests (Paylor et al., 2006).

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

      This is a terrific paper looking at influences of Tbx1 heterozygosity on metabolic phenotypes in mice. A weakness is that the locus on effects of B12 is totally unclear--could be neurovascular or even peripheral, but correcting this weakness might include study of Tbx1 conditional mutants, beyond the scope of this study.

      • *

      Reviewer #3 (Significance (Required)):* good significance

      Only two minor suggestions. 'We selected to study primarily Tbx1 single gene mutants because it is the primary candidate disease gene". What is the basis for this statement? Mouse +/- mutants in Mrpl40, Txnrd2, ProhD, and probably others have shown brain phenotypes.*

      • *

      The basis for TBX1 being considered as the primary candidate disease gene is the finding of TBX1 point mutations in patients who have the full spectrum of clinical phenotypes associated with 22q11.2 deletion syndrome without the chromosomal deletion, namely, congenital heart defects, immune defects, facial dysmorphism, learning defects and developmental delay. Similarly, in the mouse, Tbx1 mutation recapitulates the phenotype observed in multigene deletion mutants, such as Df1/+ mice.

      We do not say (or think) that heterozygosity of other genes from del22q11.2 does not contribute to the disease, but mutations of other genes have not been found in individuals with a 22q11.2DS phenotype but without the chromosomal deletion.

      In the discussion, the authors could close the loop on low glutamine could result in lower gaba in inhibitory interneurons, and its correction with B12 could restore gaba levels.

      Discussion, para. 3. We thank the reviewer for comment. However, the GABA concentration is not altered in Tbx1 haploinsufficient brains; it is only upregulated by Vitamin B12. Therefore, this assumption may be very speculative. Due to differences in the release and reabsorption rates of the three compounds (glutamine, glutamate, and GABA), correctly evaluating the glutamine-glutamate cycle requires separating astrocytes from neurons. We have only discussed the upregulation of glutamate and the GABA response to Vitamin B12, which may counteract the excess of glutamate.

      1. __4__Description of analyses that authors prefer not to carry out Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

      Reviewer 1, point 11. The PPI decrease in the Tbx1+/- group appears to be driven by results from 3-4 mice. First, are those data statistical outliers?

      Second, experiments in the same mice would be more informative. Do PBS-treated mutants recover PPI if they are treated with vB12 and vice versa? If the authors are concerned about the age difference, they also should include age-dependent effects on PPI.

      We are unable to perform this experiment because, as stated in the manuscript, the mice were sacrificed at the end of the experiment and the brains preserved for histological analysis (not part of this study). The generation of mice for new experiments would take about one year. With all due respect, we do not believe that the data that would be obtained are sufficiently important to justify, ethically and economically, this work.

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      Referee #3

      Evidence, reproducibility and clarity

      This is a terrific paper looking at influences of Tbx1 heterozygosity on metabolic phenotypes in mice. A weakness is that the locus on effects of B12 is totally unclear--could be neurovascular or even peripheral, but correcting this weakness might include study of Tbx1 conditional mutants, beyond the scope of this study.

      Only two minor suggestions.

      • 'We selected to study primarily Tbx1 single gene mutants because it is the primary candidate disease gene". What is the basis for this statement? Mouse +/- mutants in Mrpl40, Txnrd2, ProhD, and probably others have shown brain phenotypes.

      • In the discussion, the authors could close the loop on low glutamine could result in lower gaba in inhibitory interneurons, and its correction with B12 could restore gaba levels.

      Significance

      good significance

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

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      Referee #2

      Evidence, reproducibility and clarity

      The manuscript titled "Tbx1 haploinsufficiency causes brain metabolic and behavioral anomalies in adult mice which are corrected by vitamin B12 treatment" by Caterini et al. presents a comparative metabolomics study in the brains of mouse models carrying a heterozygous mutation in the transcription factor Tbx1. This mutation is contrasted with a chromosomal deficiency encompassing Tbx1, among other gene loci, known as Df1/+, which serves as a mouse model for 22q11 microdeletion syndrome. The primary and most significant finding of the study is that Tbx1 heterozygosity alone induces broad metabolomic alterations in the entire brain parenchyma, despite Tbx1 expression being confined to vascular endothelial cells. The authors leverage this observation to investigate the effects of dietary supplementation with vitamin B12, which alters the metabolome in a manner interpreted by the authors as rescuing or reversing the Tbx1 heterozygosity phenotype. This study holds promise for understanding the individual gene contributions to the penetrant behavioral phenotypes observed in Df1/+ and 22q11 affected subjects. This potential arises from the clear and consequential metabolic phenotypes described, notably the accumulation of methylmalonic acid.

      • However, despite the intriguing metabolic phenotypes, there are significant issues hindering incontrovertible conclusions. Chief among these problems is the experimental design's nature, where the effects of genotype and a pharmacological intervention, vitamin B12, are assessed. The current design overlooks the effects of vitamin B12 on wild-type animals in metabolic and behavioral measures, thus precluding the attribution of the effects of vitamin B12 to a rescue. An alternative explanation, consistent with the measurements, is that vitamin B12 modifies metabolites and transcripts irrespective of genotype. A suggestion of this possibility is the observed effect of B12 lowering glutamate levels in Tbx1 mutant tissue below those in wild-type brain tissue (Fig. 4C). This experimental design issue is exacerbated by the multitude of analytes measured by metabolomics, all collectively assumed to change as part of a common genotype-B12 interaction mechanism. This interpretation is feasible only if none of the analytes were to respond to B12 in wild-type animals. Given that this experimental design recurs across a substantial portion of the paper, it may constitute a factor that undermines the strength of the conclusions.

      • A second major issue arises from the assertion that Tbx1 is exclusively expressed in mouse brain endothelial cells and not in brain parenchyma. A significant unresolved question is how a gene expressed solely in endothelial cells can alter the brain parenchyma metabolome and transcriptome. This issue remains unaddressed and is not sufficiently discussed. If this assertion holds true, then the observations bear great importance in understanding how Df1/+ causes brain phenotypes and, by extension, in human 22q11. In this vein, the authors should consider that Tbx1 is not expressed in brain endothelial cells in humans and is minimally expressed in fetal astrocytes (see https://brainrnaseq.org/).

      • A third major concern pertains to the general poor quality of the figures. Many figures appear to be directly exported from the software used for data analysis without proper curation. They are inadequately labeled, lack color codes to clarify differences (e.g., volcano plots), feature lettering fonts that are difficult to discern, and have lettering panels placed in awkward positions. Fig. 1 would benefit by the addition of a pathway diagram showing which metabolites are changing. Figure tables/spreadsheets either have sheets labeled in Italian or are empty. Collectively, the manuscript needs more careful data curation and presentation.

      Other points for consideration are listed below:

      1) The abstract results section does not mention the Df1 mutants at all, and overall the description of the results should be improved

      2) The abstract would benefit from defining vB12 before using the abbreviation

      3) The section of the Results describing MMA accumulation in the brain would benefit from 1) explaining the choice of 1 month of age for terminal experiments and the choice to use whole brains (are there particularly brain regions suspected to be affected?), 2) describing any sex effects for Tbx1 mutants (and clarifying what data points for Tbx1 animals correspond to which sex), and 3) including what sex was used for Df1 experiments.

      4) The authors demonstrate that vB12 rescues PPI but use no other behavioral paradigms. It is possible that these mutations and/or vB12 could be impacting anxiety-like behaviors or other behavioral phenotypes. By only including PPI, the authors limit the interpretation of the "rescue" of this phenotype by vB12.

      Significance

      The manuscript titled "Tbx1 haploinsufficiency causes brain metabolic and behavioral anomalies in adult mice which are corrected by vitamin B12 treatment" by Caterini et al. presents a comparative metabolomics study in the brains of mouse models carrying a heterozygous mutation in the transcription factor Tbx1. This mutation is contrasted with a chromosomal deficiency encompassing Tbx1, among other gene loci, known as Df1/+, which serves as a mouse model for 22q11 microdeletion syndrome. The primary and most significant finding of the study is that Tbx1 heterozygosity alone induces broad metabolomic alterations in the entire brain parenchyma, despite Tbx1 expression being confined to vascular endothelial cells. The authors leverage this observation to investigate the effects of dietary supplementation with vitamin B12, which alters the metabolome in a manner interpreted by the authors as rescuing or reversing the Tbx1 heterozygosity phenotype. This study holds promise for understanding the individual gene contributions to the penetrant behavioral phenotypes observed in Df1/+ and 22q11 affected subjects. This potential arises from the clear and consequential metabolic phenotypes described, notably the accumulation of methylmalonic acid.

      However, despite the intriguing metabolic phenotypes, there are significant issues hindering incontrovertible conclusions.

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

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      Using mass spectrometry, nuclear magnetic resonance spectroscopy, and transcriptomics analyses, Caterino et al. identified metabolic changes in the brains of young adult Df1/+ mouse models of 22q11.2 deletion syndrome (22q11DS). They observed similar changes in Tbx1+/- mice, as Tbx1 is one of the genes encoded inside the 22q11.2 microdeletion. Among the metabolites identified, methylmalonic acid (MMA) showed the most prominent increase. Systemic vitamin B12 (vB12) administration rescued the MMA increase and had strong effects on the brain metabolomes and transcriptomes in Tbx1+/- and Df1/+ mice. Finally, the pre-pulse inhibition (PPI) deficit observed in Tbx1+/- mice was partially rescued by vB12 treatment. As such, this study provides a description of metabolic changes caused by Tbx1 haploinsufficiency and suggests vB12 as a therapeutic avenue in 22q11DS. Although intriguing, this study suffers from several shortcomings that should be corrected or clarified before publication.

      Major comments:

      1. The connection between vB12 and MMA is weak, and the attempt to connect these pieces to PPI seems somehow forced. For instance, the authors do not convincingly demonstrate that MMA causes the PPI deficit. Furthermore, vB12 may rescue PPI independently of MMA. The authors should be more transparent about the lack of connection or causality between changes in metabolism and behavior.

      2. Throughout the manuscript, an important control is missing: WT+ vB12 group. Data from this group should be added to Figures 1, 3, 4, 6, and Supplemental Figures 3 and 4 to show the effect of vB12 on WT mice.

      3. In Figures 1C and 3, data from the respective WT controls in the Df1 and Tbx1 cohorts should be shown.

      4. The Supplemental Table S1 includes 17 WT controls for Tbx1+/- and 6 WT controls for Df1/+, but Figure 1C includes only one group of 11 WT controls. For which group were those 11 WT controls?

      5. Here are several examples of inconsistency in the data: "For this, we first performed a preliminary metabolome analysis using isolated whole brains of male and female Tbx1+/- (n= 18) and WT (n= 10) mice between one and two months of age. A set of metabolites was quantified in brain extracts by liquid chromatography tandem mass spectrometry (LC-MS/MS) (Supplementary Table 1)." Again, the number of mice the authors note in the manuscript does not match that shown in Supplementary Table 1 (Tbx1+/- (n=14) and WT (N=17). "We analyzed whole brain tissue isolated from Df1/+ and WT (control) mice (n = 5 per genotype)." Again, the numbers of mice do not match those in Supplementary Table 1, which notes 6 Df1/+ mice and 6 WT mice.

      6. MMA is the only metabolite that is similarly changed between Tbx1+/- and Df1/+ brains. This is an interesting observation. However, there is no other overlap in metabolic changes between these two mutants. This is a concern that requires clarification.

      7. The authors mention that MMA is not changed in pre-term Tbx1+/- embryos, but no data are provided. What about MMA levels in Df1/+ embryos?

      8. In some cases, the differences in metabolites (e.g., glutamine, glutamate, phosphoethanolamine, taurine, leucine, myo-inositol, and niacinamide) between the WT and Tbx1+/- mice is very minimal (Supplemental Figure 2). The y-axis scale should start at 0.

      9. The vB12 is administered via two different regimens: 1) every 3 days for 28 days, at 4-8 weeks of age for metabolic measurements, and 2) twice a week for 2 months for PPI behavioral testing. Is there any reason the authors chose different protocols?

      10. The authors should add the following references to the study: Long et al., Neurogenetics (2006), which shows no change in PPI in Tbx1+/- mice. This discrepancy compared with the current study results and those of Paylor et al., Proc Natl Acad Sci U S A (2006) should be discussed.

      11. Figure 6B is a concern. The PPI decrease in the Tbx1+/- group appears to be driven by results from 3-4 mice. First, are those data statistical outliers? Second, experiments in the same mice would be more informative. Do PBS-treated mutants recover PPI if they are treated with vB12 and vice versa? If the authors are concerned about the age difference, they also should include age-dependent effects on PPI.

      12. Because vB12 treatment completely rescued the MMA level in Df1/+ mice (Figure 3), the authors should include a figure showing PPI test results in Df1/+ mice.

      13. Figure 1A and B table: Did the authors mean Log2FC instead of FC? The authors also should present the source data by adding supplemental tables that include raw data and normalized conversion, etc., as described in the multivariate statistical data analysis of the LC-MS/MS data.

      14. "...we identified a new metabolic phenotype that was associated with reduced sensorimotor gating deficits in Tbx1+/- mice". Although the authors showed the PPI rescue by treating Tbx1+/- mice with vB12, that result alone does not prove the association of metabolic phenotype with sensorimotor-gating deficit; other supporting data are needed.

      15. The authors stated, "Results showed that there were very few differentially expressed genes in Tbx1+/- vs WT brains, (n=22 out of 14535 expressed genes (Fig. 5 and Supplementary Tab. 2)". However, they described how 3 differentially expressed genes are involved in mitochondrial activity in the Discussion. The authors should describe those 3 genes and their relation to the metabolic change.

      16. Figure 5B: The authors claimed that they detected similar transcription profiles between WT+vB12 vs. Tbx1+/-+vB12, comparing Tbx1+/-+PBS vs. Tbx1+/-+vB12. This is based on 947 genes being downregulated and 834 being upregulated, which is not appropriate. The authors should normalize those data to the numbers of genes upregulated and downregulated in WT+PBS vs. WT+vB12 respective groups.

      Minor comments:

      1. Supplementary Table S1 shows the identical MMA concentration "0.2" for 6 controls. Is this correct?

      2. Remove the callout for Figure 1C at the end of the second paragraph in Results.

      3. There are multiple typos throughout the manuscript. Here are several examples:

      a) Fig1B graph- Df/+ => Df1/+

      b) "Together, the hydrophilic and lipophilic results revealed a group of 6 compounds that characterized the brain metabolic differences between Tbx1+/- and WT mice (Figure 2B, 2C)". Figure 2A should be included also.

      c) "In support of this notion, is the finding that...(remove)

      d) Remove double periods: "The pathways found are depicted in Figure 2C' which reports the impact of each pathway versus p values.."

      e) Panel labels in all figures are misplaced.

      f) "In support of this notion... at least nine orthologs are involved in mitochondrial metabolism". What are those 9 mitochondrial genes? Kolar et al., Schizophr Bull (2023) indicates that there are 8 mitochondrial genes within the 22q11.2 locus. The authors need to list these genes.

      Significance

      Caterino et al. provide the evidence of a change in brain metabolism associated with 22q11.2 deletion syndrome (22q11DS), which is a major risk factor for neuropsychiatric disease, especially schizophrenia. The authors attributed these changes to haploinsufficiency of Tbx1, which is located inside the 22q11.2 genomic locus, as Tbx1+/- mice and 22q11DS models (Df1/+ mice) demonstrated similar metabolic changes. Among these changes, the authors detected an abnormally high accumulation of methylmalonic acid (MMA), a toxic metabolite that negatively affects mitochondrial activity and glutamate uptake. The authors also showed that systemic vitamin B12 (vB12) administration in Tbx1+/- mice and 22q11DS mice returned MMA to its normal levels in the brains of both strains. Finally, administration of vB12 partially rescued a behavioral phenotype in Tbx1+/- mice. Specifically, vB12 improved pre-pulse inhibition (PPI) of the acoustic startle in these mutants. This study may potentially motivate a new direction of research toward elucidating the Tbx1-dependent metabolic mechanism and its connection to abnormal behavioral phenotypes in 22q11DS.

      • This is the first thorough characterization of metabolic changes in the brain of mouse models of 22q11DS. This work may advance our understanding of the mechanism of this disease and schizophrenia in general. Previous studies mostly focused on cell-autonomous mechanisms in 22q11DS, but because Tbx1 is not expressed in the adult brain, this study strongly argues that non-cell-autonomous mechanisms are involved in the pathogenicity of 22q11DS. This description is the strongest part of the manuscript. However, as it stands, this study does not causally connect the metabolite abnormalities with aberrant behavior in 22q11DS models. The rescue of metabolic changes by vB12 is interesting, but the interpretation of the results is a bit speculative. There are also several missing controls and other limitations that preclude this reviewer from a more enthusiastic assessment of this manuscript. The manuscript has the potential to be much stronger if the authors add more experiments and analyze their data in a more appropriate manner.

      • This manuscript describes metabolic abnormalities in 22q11DS models that are driven by the haploinsufficiency of the Tbx1 gene, which is located within the 22q11DS-related genomic region. This is an incremental advance in the 22q11DS field. The authors identified multiple metabolic abnormalities that would be of interest to researchers in the fields of psychiatry and translational and basic neuroscience. They also showed that some metabolic abnormalities are improved by vB12 treatment. They argue that vB12 improves PPI, the abnormality of which is associated with many psychiatric diseases, including schizophrenia. If confirmed, this will be a conceptual advance in the translational neuroscience field. However, making such a statement, exciting as it may be, would be speculative if based solely on the data presented in this manuscript..

      • This reviewer has expertise in basic and translational neuroscience with focus on neurodevelopmental psychiatric diseases.

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      Reply to the reviewers

      Reviewer1

      I recommend combining Figures 1 and 3 either before or after the results shown in Figure 2, so the reader's expectation for quantification is immediately satisfied.

      Response:

      Thank you for your suggestion. In the revised manuscript, images of GFP::POP-1 in compound mutants are moved to Figure 3. The schematic diagram of the gonad (previously Fig. 1A) and GFP::POP-1 images in wild type are kept in Figure 1, as they are described in Introduction.

      Major comments:

      Delving into the figure legend of Fig. 3 and the normalization procedure described in the Methods "Quantification of POP-1 asymmetry in the Z1 and Z4 division" raised concerns. The method therein described is overly complicated but also neglects background subtraction. My first question about this method: what range of distances between daughters is measured in Z? These distances are not discussed in absolute terms, and this is important for our understanding of how much correction for tissue depth might be necessary, as L1s are very thin.

      To check my understanding, the authors use as a control a nuclear-localized GFP driven in the somatic gonad precursors in otherwise wild-type worms by the sys-1 promoter. They observe that the regression on a log scale of anterior:posterior (and vice versa) Z1 and Z4 daughter fluorescence over the distance between the daughters in the Z plane is fit by y = −0.034x + 0.0148, which is practically a slope of 0 and an intercept of 0. This means that they observed an ~1:1 ratio (as log(1)=0) of fluorescence in the anterior and posterior daughters of otherwise wild-type worms, at least across the range of very small X values of relevant distances between daughters (again, the relevant range of distances really matters and should be presented), making the normalization seem unnecessary.

      Response:

      Normalization is essential to compare POP-1 signals between daughter cells since the signal intensities depend on the depth of cells. Depth differences between SGP daughter cells range from 0 to 7.5 micrometers. For example, when we input the maximum difference (7.5) into our correction equation y = −0.034x + 0.0148 (the logarithmically transformed linear regression equation), we get:

      y = −0.034 * 7.5 + 0.0148 = -0.2402

      To interpret this on the original scale, we apply the inverse logarithmic transformation:

      10^(-0.2402) ≈0.575

      This result indicates that even if GFP::POP-1 expression is the same in both cells, the depth difference alone can cause approximately a 1.74-fold (1/0. 575) difference in fluorescence intensity.

      Similarly, if we use a median value of 3.5 micrometers as the depth difference, we get: y = -0.1042. After the inverse logarithmic transformation, this corresponds to a 0.787 or 1.27 (1/0.787) fold difference in fluorescence intensity.

      Without normalization, we risk misinterpreting such differences in expression levels when in reality the expression is the same. Conversely, actual differences in GFP::POP-1 signal could be masked or overestimated due to the depth effect.

      In the revised manuscript, examples of depth differences between SGP daughters are shown in Fig. 2S which is added in response to the comment of reviewer 2, asking images of lin-17 mom-5 animals.

      In the revised manuscript, we explained the depth effects in the legend of Fig. 3 as follows.

      "Since SGP daughter cells are often present at distinct focal planes, we normalized the depth effects on fluorescence intensities (see Materials and Methods for details) for the quantification shown in (B). The images in (A) and (C) are from animals with SGP daughters at similar depths."

      Then based on this regression and 95% CI, the authors predict values that reflect true equivalence of fluorescence of POP-1::GFP in the two SGP daughters, compare the observed values to these predictions, and ultimately display in violin plots these differences of observed and expected. Correct?

      Response:

      Yes, your understanding is correct.

      Is this complicated treatment the only way to detect differences in polarity of anterior and posterior daughters of Z1 and Z4? What happens if the authors measure GFP::POP-1 and calculate the following?

      Z1p(MGV - background control from same focal plane)


      Z1a(MGV - background control from same focal plane)

      If this straightforward analysis shows asymmetric signal in the control that is made symmetrical or reversed in the mutants, the hypothesis would seem to be supported with a much more straightforward method. Samples could be analyzed separately in two bins by worm body position, which affects which cell is superficial in the sample. As it is, the Figure 3 Y axis label is hard to interpret without reading the methods at length, diminishing its impact.

      Response:

      Thank you for the suggestion. Your suggested calculation would be simple if we could assume that control signals (sys-1p::GFP::NLS or sys-1p::GFP::POP-1 in the same wild-type cell) on the same focal plane are the same among animals. However, since there are apparent variations in expression levels among individuals, your suggested method is not appropriate for evaluating differences in sys-1p::GFP::POP-1 intensities between the SGP daughter cells of the same animal.

      Missing control: The sys-1 promoter-driven NLS-tagged fluorescent protein as a control to compare to the GFP::POP-1 is analyzed only in the wild-type, and apparently not in the mutants under consideration. Phillips et al. (2007) show that sys-1p transcriptional activity is equivalent between the SGP daughters in wild-type worms, but neither those results nor the method of normalizing to a sys-1p::GFP::NLS signal in this paper address the question of whether sys-1 promoter activity is equivalent in these cells in mutants upstream in the Wnt pathway. If the current method of normalization is to be used, it seems important to normalize to the sys-1p::GFP::NLS regression in each mutant background.

      Response:

      Thank you for your suggestion. We used sys-1p::GFP::NLS as a control to normalize depth effects, which should be the same across all genotypes because the GFP molecules in SGPs should be equally distributed between SGP daughter cells, not because sys-1 promoter activities are similar among them. Since SGP daughters divide within a short time (about 2 hours), it is likely that the fluorescence of newly synthesized GFP (maturation time of about 1 hour) in SGP daughters is neglectable compared to GFP inherited from the SGP cells. Similarly, sys-1p::GFP::POP-1 signals in SGP daughters reflect the distribution of GFP::POP-1 from SGPs rather than the transcriptional activities of the sys-1 promoter in the daughter cells. sys-1p::GFP::POP-1 or sys-1p::GFP::SYS-1 has been widely used to evaluate polarity of asymmetric divisions in a number of studies, none of which consider transcriptional differences of the sys-1 promoter in the daughter cells.

      1. How was lin-17(mn589) generated? if this is the first report of this allele, full information on what the lesion is and how it was derived should to be reported.

      Response:

      Thank you for your question regarding the lin-17(mn589) allele. We would like to point out that the information about this allele is provided in the Methods section of the original manuscript as follows.

      "lin-17(mn589) (gifted by Mike Herman) carries a mutation in the seventh cysteine residue of the CRD domain (C104Y). mn589 exhibits 47% Psa phenotype (indicating T cell polarity defects)."

      The methods section lacks a description of how the mes-1 experiments were done, in terms of timing, duration, and temperature; mes-1(bn7) is a temperature sensitive allele.

      Response:

      Thank you for pointing out the lack of detailed methodology for the mes-1 experiments. The germless phenotype of mes-1 mutants is partial even at high temperatures. We have not performed temperature shifts to observe the phenotype. As per your suggestion, we added the following text to the Strains section:

      "mes-1(bn7) is a temperature-sensitive allele with higher penetrance of the germless phenotype at 25{degree sign}C than at 15{degree sign}C, and was grown at 22.5{degree sign}C. The germless phenotype of mes-1(bn7) was observed by the absence of the mex-5::GFP::PH signal through direct observation of epifluorescence."

      Minor comments

      1. The paper lacks a discussion of precedent in the literature for Wnt-independent Frizzled activity; this is a major finding that is being undersold in the current version of the manuscript.

      Response:

      Thank you very much for appreciating out finding. We have added the following paragraph to the Discussion section:

      "Wnt-independent functions of Frizzled receptors

      We have shown that lin-17/Fzd functions in a Wnt-independent manner to control SGP polarity, since the missing DTC phenotype of lin-17; cwn-2 and lin-17 mom-5 was completely rescued by ΔCRD-LIN-17. In addition, SGP polarity is normal in the quintuple Wnt mutant that has mutations in all the Wnt genes (Yamamoto et al., 2011). In seam cells, Wnt receptors including LIN-17/Fzd and MOM-5/Fzd appear to have Wnt-independent functions for cell polarization, as seam cells are still mostly polarized in the quintuple Wnt mutants, while they are strongly unpolarized in the triple receptor mutants (lin-17 mom-5 cam-1/Ror) (Yamamoto et al., 2011). In Drosophila, Fz/Fzd has been primarily considered to function Wnt-independently to coordinate planar cell polarity (PCP) between neighboring cells (Lawrence et al., 2007), though Fz function can still be regulated by Wnt, as PCP orientation can be directed by ectopically expressed Wnt proteins (Wu et al., 2013).

                In Drosophila, Fz regulates PCP by interacting with other PCP components including Van Gogh (Vang). In C. elegans, we found that vang-1/Vang does not appear to function with LIN-17/Fz, since most vang-1 single mutants and cwn-1 cwn-2 vang-1 triple mutants have two gonadal arms (215/216 and 58/58, respectively). As Fz interacts with Disheveled (DSH) in Drosophila PCP regulation, in C. elegans, the Disheveled homologs DSH-2 and MIG-5 regulate SGP polarity (Phillips et al., 2007). Therefore, LIN-17 might regulate the DSH homologs in a Wnt-independent manner. "
      

      Added Reference:

      1. Lawrence PA, Struhl G, Casal J. (2007). Planar cell polarity: one or two pathways? Nat Rev Genet. 8, 555-563.
      2. Wu, J., Roman, A.C., Carvajal-Gonzalez, J.M., & Mlodzik, M. (2013). Wg and Wnt4 provide long-range directional input to planar cell polarity orientation in Drosophila. Nature Cell Biology, 15(9), 1045-1055.

      Important: I think "Fig. 6 Germ cell independent migration of germ cells" title is a typo; should be "Germ cell independent migration of DTCs"

      Response:

      Thank you for pointing out the typo. We corrected it in the revised manuscript.

      This is a very important experiment! I think a greater description of the mes-1 phenotype would be helpful, since loss of germline was not 100% penetrant in mes-1(bn7) hermaphrodites in Strome et al., 1995. The legend says "Germless mes-1 phenotype was confirmed by the absence of the mex-5::GFP::PH signal in the gonad." Consider adding a few sentences to the results (or methods, from which the mes-1 experiments are currently missing) describing that only mes-1 animals that lacked germline fluorescence were analyzed for DTC migration.

      Response:

      Thank you for providing the context. To address the concerns, we made the following changes to our manuscript:

      1. In the Results section, we revised the sentence "We found that 84% of DTCs (n = 90) in germless mes-1 animals..." to "Among mes-1 animals that lack germ cells, we found 84% of DTCs (n = 90)...".
      2. We also modified the sentence "We noticed that some germless mes-1 animals..." to "We noticed that some mes-1 animals that lack germ cells...".

      Please correct "secreting the Notch ligand LAG-2" this is a membrane-bound, not secreted ligand

      Response:

      Thank you for your comment. In the revised manuscript, we modified the relevant sentence in the Introduction section as follows:

      "Firstly, DTCs function as niche cells for germline stem cells, inhibiting their entry into meiosis by expressing the Notch ligand LAG-2 (Henderson et al., 1994)."

      Fig 1. The qualitative loss of polarity would be better depicted with

      a grayscale image instead of green-on-black.

      Response:

      Thank you for your suggestion. The GFP::POP-1 images are raw images of the green channel of the confocal microscopy. We believe that SGP polarity is clearly depicted by them.

      Fig. 3 the presentation of these violin plots is confusing. The central text that reads "normal polarity, loss of polarity, reversed polarity" with arrows looks like a second Y axis label attached to the Z4 plot. I recommend rearranging. Consider shading the top, bottom, and central regions and explaining the meaning of the shading in the legend.

      Response:

      Thank you for your suggestions regarding the presentation of Figure 3. In response to your feedback, we have made the following modifications:

      First, we moved the text and arrows from the center to the right side of the figure, creating a clearer layout. As you recommended, we applied shading to the top, bottom, and central regions of the violin plots. Additionally, to explain the meaning of the shading, we added a new explanation to the figure legend. Specifically, we included the following text:

      "Values within the 95% CI (between the red lines; light green regions) indicate symmetric localization. Values below the lower red line (light blue regions) indicate reversed localization, while values above the upper red line (light red regions) indicate normal localization."

      We applied the same modification to Supplemental Fig. 1.

      Reviewer 2

      Major comments

      1- Are the effects of combining the different Wnts with the lin-17 allele specific to the n3091 allele? It would be important to test another allele, for example the sy277 allele has a similar phenotype and is available at CGC. A null would be even better if it is viable. Alternatively, lin-17(RNAi) could instead be used if efficient enough. This is important since the n3091 allele could differentially alter the binding to the various Wnts, resulting in their distinct phenotypes in that background. However, these distinct phenotypes may not be relevant in a wild-type context.

      Response:

      Thank you for your insightful comment. The lin-17(n3091) allele contains a nonsense mutation at the 35th codon, located between the second and third cysteine residues in the CRD domain (Wnt binding domain) (Sawa et al 1996). Therefore, it is highly unlikely that the N-terminal protein of 34 amino acids produced in lin-17(n3091) can bind to Wnts. In the revised manuscript, we added the missing-DTC phenotype of lin-17(n671) cwn-2 animals, which show a similar phenotype to lin-17(n3091) cwn-2. n671 is a reference allele in WormBase and has a nonsense mutation. Although sy277 has a deletion in the N-terminal region, its phenotype is weaker than that of n3091 and n671 (Sawa et al 1996).

      In the revised manuscript, we described lin-17(n671) cwn-2, in the Table 1, Table S1 and added the following sentence.

      "We observed a similar phenotype in lin-17(n671); cwn-2 double mutants, confirming that this genetic interaction is not allele-specific."

      2- In the lin-17; mom-5 double mutant which lacks DTCs, are Z1 and Z4 there but they do not express DTC markers, or are they never born? A lineage analysis should be presented. Also, are Z2 and Z3 still there on their own? Please show images.

      Response:

      Thank you for your comments. We quantified sys-1p::GFP::POP-1 signals in Z1 and Z4 daughter cells of lin-17 mom-5 and have not observed any animals lacking Z1, Z4 or germ cells. In the revised manuscript, as Fig. S2, we added images of sys-1p::GFP::POP-1 localizations in SGP daughters, along with germ cells in lin-17 mom-5 as well as in lin-17 cwn-1 egl-20 cwn-2, both of which were not shown in the original manuscript. In response to Reviewer 1's comment, we also included examples of depth effects on fluorescence intensities in Fig. S2 with images of different focal planes.

      Fig. S2 is quoted it at the end of the following sentence.

      "Then, we quantified the ratios (on a logarithmic scale) of sys-1p::GFP::POP-1 signal intensities proximal to distal daughter cells in various genotypes (Fig. 3A and Fig. S2)."

      The loss of polarity phenotype of lin-17 mom-5 has been described in Phillips et al. We missed to cite this in the original manuscript. We added the citation in the revised manuscript.

      "These asymmetries were strongly disrupted and weakly affected in lin-17 mom-5 double and lin-17 single mutants, respectively, as described previously (Phillips et al., 2007; Siegfried et al., 2004)."

      Minor comments

      1- The term "mirror-symmetry" is redundant. Consider using "symmetry"

      or "symmetrical polarity".

      Response:

      As noted in the cross-comment by Reviewer 1, we believe that "mirror-symmetry" is the appropriate term.

      We think that "symmetry" implies the same lineage, whereas the relationship between the Z1 and Z4 lineages is not. "Mirror symmetry" was also used in Herman & Horvitz (1994) to describe the defect in the F lineage in lin-44/Wnt mutants as follows.

      "we observed division patterns that were mirror symmetric to those of the wild type (Fig. 2). One plausible explanation is that the polarity of the first asymmetric cell division was reversed, causing the polarities of all subsequent asymmetric cell divisions also to be reversed."

      2- "... they are permissively pushed distally by germ cells while proliferating" is confusing as it is unclear what proliferating cell you are referring to - germ cells or the DTC? proliferating? sense. Replace by: "they are pushed distally by proliferating germ cells"

      Response:

      Thank you for your helpful comment. We agree with your suggestion and modify the sentence as follows:

      Original: "... they are permissively pushed distally by germ cells while proliferating" Revised: "... they are pushed distally by proliferating germ cells"

      3- Fig. 2 is cited in the text before Fig. 1.

      Response:

      Thank you for pointing this out. Figure1 is mentioned in the Introduction before Figure 2 is referenced in the Result section in the original manuscript. We think the reviewer might be confused, as the POP-1 localization defect was shown in Figure 1. In response to the reviewer 1's comment, we moved the POP-1 localization images of the compound mutants to Figure 3. In addition, we noticed that in the original manuscript, Figure 1B was mentioned before Figure 1A in the Introduction. Therefore, we have modified the sentences in the Introduction.

      The original sentence was:

      "In the gonad, at the L1 stage, somatic gonadal precursor cells (SGPs), Z1 and Z4 have LH and HL polarity, respectively (Siegfried et al., 2004) (Fig. 1B). This mirror-symmetric polarity creates their mirror-symmetric lineages producing distal tip cells (DTCs) from the distal daughters (Z1.a and Z4.p) (Fig. 1B)."

      The revised sentence now reads:

      "In the gonad, at the L1 stage, somatic gonadal precursor cells (SGPs), Z1 and Z4 have LH and HL polarity, respectively, creating their mirror-symmetric lineages producing distal tip cells (DTCs) from the distal daughters (Z1.a and Z4.p) (Siegfried et al., 2004) (Fig. 1A and 1B)."

      4- The results also suggest that MOM-5/Frizzled might be the receptor for Wnts regulating DTC production, as lin-17 mom-5 double mutants completely lack DTCs." Table 1 results rather suggest that lin-17 and mom-5 are the two frizzled receptor involved in DTC specification and that they are largely redundant.

      Response:

      As the reviewer noted, lin-17 and mom-5 function redundantly in DTC specification (SGP polarization). However, their functions are clearly different in terms of genetic interactions with Wnt genes (e.g. lin-17 cwn-2 but not mom-5 cwn-2 show the DTC-missing phenotype). We propose that MOM-5 but not LIN-17 functions as a receptor for Wnts.

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      Referee #2

      Evidence, reproducibility and clarity

      This is an interesting paper where authors study how DTC specification and migration are genetically controlled. The results show a complex interaction between the various Wnt components with partially redundant roles for the ligands and receptors. This helps understanding how the two DTCs are specified and symmetrically polarized in vivo. In addition, authors convincingly show that DTCs can significantly migrate in the absence of any push by GSC proliferation.

      Major

      1. Are the effects of combining the different Wnts with the lin-17 allele specific to the n3091 allele? It would be important to test another allele, for example the sy277 allele has a similar phenotype and is available at CGC. A null would be even better if it is viable. Alternatively, lin-17(RNAi) could instead be used if efficient enough. This is important since the n3091 allele could differentially alter the binding to the various Wnts, resulting in their distinct phenotypes in that background. However, these distinct phenotypes may not be relevant in a wild-type context.
      2. In the lin-17; mom-5 double mutant which lacks DTCs, are Z1 and Z4 there but they do not express DTC markers, or are they never born? A lineage analysis should be presented. Also, are Z2 and Z3 still there on their own? Please show images.

      Minor

      1. The term "mirror-symmetry" is redundant. Consider using "symmetry" or "symmetrical polarity".
      2. "... they are permissively pushed distally by germ cells while proliferating" is confusing as it is unclear what proliferating cell you are referring to - germ cells or the DTC? proliferating? sense. Replace by: "they are pushed distally by proliferating germ cells"
      3. Fig. 2 is cited in the text before Fig. 1.
      4. "The results also suggest that MOM-5/Frizzled might be the receptor for Wnts regulating DTC production, as lin-17 mom-5 double mutants completely lack DTCs." Table 1 results rather suggest that lin-17 and mom-5 are the two frizzled receptor involved in DTC specification and that they are largely redundant.

      Referees cross-commenting

      Dear reviewer #1, with all due respect, I do do understand your point as the Fig. 1 in Bowerman shows lineages that are left-right "asymmetrical", not "non-mirror symmetrical"? In the paper we are reviewing, the Z1-Z4 lineages are anterior-posterior symmetrical. But this is a minor issue and we can wait to see what the authors are going to reply...

      Significance

      The paper is interesting but in its current form, the genetics results around DTC specification are somewhat complex and difficult to interpret. The results linked to DTC migration are easier to take home.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary

      This manuscript illuminates the molecular regulation of mirror-image-symmetry in the C. elegans hermaphrodite somatic gonad precursor cells, reporting that a diversity of Wnt ligands and a Wnt receptor with Wnt-independent activity together polarize the two progenitors of the somatic gonad in opposite ways. The Wnt ligand genes act nonredundantly with respect to the polarity of the SGPs.

      The conclusions arise from the careful interpretation of compound genetic mutants in the Wnt pathway, including the surprising finding of a Wnt-independent effect of lin-17/Frizzled on cell polarity that is bolstered by a new allele and construct of lin-17 that affect specifically its Wnt-interacting domain.

      Major comments

      While I find the genetic analyses compelling, I think the presentation of the data undermines the strength of the quantitative analysis of expression. Recommendations follow.

      Genetic analyses: Major strength. Complex compound mutants are presented with ample sample sizes and careful interpretation of genetic interactions, presented clearly in tables that demonstrate large sample sizes. The new allele of lin-17 and delta-CRD LIN-17 construct reveal the surprising Wnt-independence of this Frizzled-type receptor. While of course I am interested in this Wnt-independent role, it is not necessary for the current manuscript to determine its mechanism.

      Statistical analysis: When I first saw Fig. 1 B and C and read the associated results sections, I thought the qualitative polarity results reported in Fig. 1 would benefit from quantification, including at a minimum the sample size and penetrance of the phenotypes reported in Fig1B and 1C; it would be even better to quantify expression levels in the daughter cells. Then I discovered this appears to be what is reported in Figure 3. I think the presentation of these data are confusing. I recommend combining Figures 1 and 3 either before or after the results shown in Figure 2, so the reader's expectation for quantification is immediately satisfied.

      Delving into the figure legend of Fig. 3 and the normalization procedure described in the Methods "Quantification of POP-1 asymmetry in the Z1 and Z4 division" raised concerns. The method therein described is overly complicated but also neglects background subtraction. My first question about this method: what range of distances between daughters is measured in Z? These distances are not discussed in absolute terms, and this is important for our understanding of how much correction for tissue depth might be necessary, as L1s are very thin.

      To check my understanding, the authors use as a control a nuclear-localized GFP driven in the somatic gonad precursors in otherwise wild-type worms by the sys-1 promoter. They observe that the regression on a log scale of anterior:posterior (and vice versa) Z1 and Z4 daughter fluorescence over the distance between the daughters in the Z plane is fit by y = −0.034x + 0.0148, which is practically a slope of 0 and an intercept of 0. This means that they observed an ~1:1 ratio (as log(1)=0) of fluorescence in the anterior and posterior daughters of otherwise wild-type worms, at least across the range of very small X values of relevant distances between daughters (again, the relevant range of distances really matters and should be presented), making the normalization seem unnecessary.

      Then based on this regression and 95% CI, the authors predict values that reflect true equivalence of fluorescence of POP-1::GFP in the two SGP daughters, compare the observed values to these predictions, and ultimately display in violin plots these differences of observed and expected. Correct?

      Question: Is this complicated treatment the only way to detect differences in polarity of anterior and posterior daughters of Z1 and Z4? What happens if the authors measure GFP::POP-1 and calculate the following?

      Z1p(MGV - background control from same focal plane)

      Z1a(MGV - background control from same focal plane)

      If this straightforward analysis shows asymmetric signal in the control that is made symmetrical or reversed in the mutants, the hypothesis would seem to be supported with a much more straightforward method. Samples could be analyzed separately in two bins by worm body position, which affects which cell is superficial in the sample. As it is, the Figure 3 Y axis label is hard to interpret without reading the methods at length, diminishing its impact.

      Missing control: The sys-1 promoter-driven NLS-tagged fluorescent protein as a control to compare to the GFP::POP-1 is analyzed only in the wild-type, and apparently not in the mutants under consideration. Phillips et al. (2007) show that sys-1p transcriptional activity is equivalent between the SGP daughters in wild-type worms, but neither those results nor the method of normalizing to a sys-1p::GFP::NLS signal in this paper address the question of whether sys-1 promoter activity is equivalent in these cells in mutants upstream in the Wnt pathway. If the current method of normalization is to be used, it seems important to normalize to the sys-1p::GFP::NLS regression in each mutant background.

      Missing methods: How was lin-17(mn589) generated? if this is the first report of this allele, full information on what the lesion is and how it was derived should to be reported.

      The methods section lacks a description of how the mes-1 experiments were done, in terms of timing, duration, and temperature; mes-1(bn7) is a temperature sensitive allele.

      Minor comments

      The paper lacks a discussion of precedent in the literature for Wnt-independent Frizzled activity; this is a major finding that is being undersold in the current version of the manuscript.

      Important: I think "Fig. 6 Germ cell independent migration of germ cells" title is a typo; should be "Germ cell independent migration of DTCs"

      This is a very important experiment! I think a greater description of the mes-1 phenotype would be helpful, since loss of germline was not 100% penetrant in mes-1(bn7) hermaphrodites in Strome et al., 1995. The legend says "Germless mes-1 phenotype was confirmed by the absence of the mex-5::GFP::PH signal in the gonad." Consider adding a few sentences to the results (or methods, from which the mes-1 experiments are currently missing) describing that only mes-1 animals that lacked germline fluorescence were analyzed for DTC migration.

      Please correct "secreting the Notch ligand LAG-2" this is a membrane-bound, not secreted ligand

      Fig 1. The qualitative loss of polarity would be better depicted with a grayscale image instead of green-on-black.

      Fig. 3 the presentation of these violin plots is confusing. The central text that reads "normal polarity, loss of polarity, reversed polarity" with arrows looks like a second Y axis label attached to the Z4 plot. I recommend rearranging. Consider shading the top, bottom, and central regions and explaining the meaning of the shading in the legend.

      Referees cross-commenting

      I have no comments to add to the points raised by Reviewer 2, other than to share my opinion that "mirror symmetry" is helpful terminology, as there are other possible developmental symmetries other than the "HL LH" mirror symmetry seen in the SGPs. For an example of a non-mirror developmental symmetry, see Fig. 1 of this dispatch by Bowerman 2006 https://www.sciencedirect.com/science/article/pii/S0960982206024481

      Significance

      Strengths: Rigorous genetics

      Limitations: Data presentation, expression level analysis, communication of results.

      Advance: Wnt signaling has highly conserved, ancient roles in the earliest polarity events in animal embryos, so learning how the Wnt signaling pathway dictates cell polarity, including a new Wnt-independent role for a major receptor, has broad implications for understanding cell polarity via this pathway in animal development. Another major advance is the finding that a conserved developmental signaling pathway with members that are redundant in certain contexts nonetheless elicits specific responses from certain cells during development, thus generating a diversity cell types.

      Audience: These findings will be of interest to a broad audience interested in animal development, symmetry-breaking, complexity, and the Wnt-signaling pathway.

      Additionally, a worm-specific audience will be interested in the finding that the DTCs are capable of germline-independent migration, as the new paradigm of Agarwal et al. ascribes DTC propulsion to germline pushing forces. How the DTC migrates is a longstanding question in our field.

      Reviewer: I study developmental genetics and cell biology in the C. elegans hermaphrodite gonad. I have sufficient expertise to evaluate all of the experiments presented here. In my opinion, this is a highly valuable developmental genetics study with significant but easily addressable flaws in presentation.

  3. Aug 2024
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      'The authors do not wish to provide a response at this time.'

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      Referee #3

      Evidence, reproducibility and clarity

      Summary:

      DNA double-strand breaks are harmful to cells. The authors used CRISPR-Cas9 to create DSBs in repetitive elements (Ty transposons) in the Saccharomyces cerevisiae genome. This method builds on previous ones that used the HO endonuclease or prokaryotic restriction enzymes. They used Cas9-based DSBs to assess the role of Tel1 (ATR) in DSB sensing, comparing it with the DSB-generating xenobiotic zeocin. The first part of the paper is fine, but it lacks information about the yield. The system is not as efficient as it is claimed to be, and it is slow. The second part of the paper is not well connected to the first half, and several controls are needed to make it sound.

      Major comments:

      1. A significant portion of the manuscript posits that the CRISPR-Cas9 system is capable of creating as many DSBs as the theoretical number of Ty targets. Nevertheless, it is clear that this is not the case. The authors can determine the number of breaks per construction. A plot of the frequency of average DSBs in chromosomes IV and III appears to be feasible based on the Southern blots presented, although this could give an underestimate, given that some broken chromosomes may become trapped in the well during DSB processing. However, the percentage of zero DSBs for a given chromosome is readily quantifiable, allowing the frequency of DSBs per cell to be determined through straightforward calculations. Once this has been achieved, the authors should revisit their assessments of Rfa1/Rad52/Tel1 foci formation and number.

      2. OPTIONAL: It seems plausible that a saturation of DSBs per cell may occur when the actual number of DSBs is plotted against the theoretical maximum. In such a scenario, the introduction of additional Cas9 molecules could enhance the efficiency of DSB generation. This could be achieved by increasing the number of copies of the CAS9 gene.

      3. The majority of the discussion chapter is dedicated to the second part of the paper (Tel1), yet no mention is made of the subject I have just commented on. Similarly, a comparison should be made between the Cas9-based system and previous methodologies for creating single and multiple DSBs (HO, I-SceI, restriction enzymes, radiation, radiomimetic drugs, etc.) in terms of efficiency, time to DSB, cell response, etc. It is surprising that the Cas9 system takes so long to generate DSBs and that the cell cycle profile indicates very little arrest in G2/M. This should also be discussed.

      4. OPTIONAL: Since the lack of a strong G2/M arrest is intriguing, it would be good to do a Western blot of Rad53 to learn more about Cas9-based DSB sensing and the DNA damage checkpoint. Comparing it to both the well-established HO system (even a single HO cut) and radiation/radiomimetics would be ideal.

      5. OPTIONAL: Given the lack of the G2/M arrest when Cas9 is expressed in asynchronous cultures, the authors may try to synchronize cells in G1 and G2/M before Cas9 is induced. This could help them find out if the G1 and G2/M peaks in Figure 2A are caused by DSBs leading to both a G1 and a G2/M arrest. Alternatively, they could film the cells after Cas9 is added and check microcolony formation.

      6. The timeframes of Rad52 foci in Figure 5 indicate an anomalous pattern, which raises concerns about the validity of the experiment setup. The selected cells did not change their morphology throughout the 140-minute observation period. The unbudded cell remained unbudded, and the bud did not grow in six out of seven cells. For cells with small buds (cells 2 to 5), the expectation was that the bud would grow until the cell either became a dumbbell (indicative of a G2/M arrest) or divided its nucleus. Furthermore, no re-budding events were observed. Is this pattern real? Why is it so? Once this issue is addressed, could the duration of the Rad52 foci be quantified? Was a single z-plane taken? If so, some Rad52 foci that appear and/or disappear could reflect their migration to an on-focus or out-of-focus plane.

      7. OPTIONAL: It would be beneficial to conduct a double labeling with known DSB factors that coexist with Tel1, or are downstream of it, in order to enhance the data shown in Figures 6 and 7. This would also address some of the queries raised about Tel1 clustering and location on the nuclear periphery.

      8. In the experiment with the condensin mutant smc2-8, a temperature shift from 24 to 37 ºC is carried out, which represents a significant physiological change. Therefore, it is essential to include a parallel control with a WT strain to rule out the possibility that the unclustering of Tel1 foci is due to the temperature shift.

      9. The sentence in the Discussion about condensin's role in maintaining Tel1 clustering is misleading. It could be interpreted as suggesting that condensin actively gathers Tel1 foci after DSBs (lines 650-651), when in fact condensin's function is simply to maintain Ty element clustering prior to DSBs, as the authors themselves cite in the text.

      10. Taking into account the importance of Cas9/sgRNA plasmid constructions, PFGE and Southern blot in this work, the author should make the effort to describe them all in much more detail in M&M.

      Minor comments:

      1. In the Figure 7 legend, panel A is missing, and the text for the other panels is consequently misplaced.

      2. The functional verification of the yEGFP-Tel1 construction (Fig. 6A & B) would be better presented as a supplementary figure. The same rationale applies to Figure 8.

      3. Please include G2/M in the abbreviations.

      4. Please clarify what is meant by "5h40". Is this 5 hours and 40 minutes? If so, please use alternative nomenclature.

      5. Some sections of the text appear superfluous. For example, the definitions of mean, SEM and SD, and the rationale for choosing SEM over SD (lines 211 to 215), as well as the information about the purpose of PFGE in a figure legend (line 322).

      Referees cross-commenting

      After reading the comments of the other reviewers, I agree with them, and some of them raise the same concerns as I do.

      Significance

      General assessment: The study addresses the generation of multiple DSBs by Cas9 when an increasing number of targets are incorporated for cutting. The strategy to create an increasing dose of DSBs based on the different Ty elements is an innovative approach, although it is constrained by the nature of the target. The assessment of DSBs by PFGE plus Southern blot is well planned, although there is potential to exploit the obtained results further to assess the actual vs theoretical DSBs, saturation effect, etc. They then sought to use their dose-dependent system to examine the role of Tel1 in the DSB response, comparing Cas9 with zeocin. However, a comparison between the two strategies is challenging without prior knowledge of the number of DSBs present in each treatment. Overall, the study represents a promising effort to use Cas9 for the generation of multiple DSBs in yeast. Nevertheless, the system is constrained for further mechanistic studies on the DSB response due to its slow kinetics, low yields, and lack of expected DNA damage responses, particularly the G2/M checkpoint.

      Advance: Despite such a dose-response assessment for the Cas9-based DSBs have not been performed in yeast, similar studies with sequence-specific DSBs have been done before in Lorraine Symington's lab (and others). Perhaps the Cas9-based system is simpler than the one that relies on multiple insertions of the HO cutting sequence, but it appears neither simpler than the one based on the expression of restriction enzymes nor more efficient. The Cas9 system has several limitations that make it less suitable for studying how cells react against multiple DSBs. It is slow, probably saturates after a few DSBs, and does not render a full DNA damage response. However, there is still value in understanding and making predictions about this important gene-editing method.

      Audience: This paper is intended for a specialized audience, including those involved in basic research on DSB sensing and repair, particularly in yeast.

      Field of expertise of the reviewer: Cell and molecular biology of S. cerevisiae, with a particular interest in the DNA damage response.

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      Referee #2

      Evidence, reproducibility and clarity

      Summary.

      The authors have developed a system to generate a variable number of double-strand breaks (DSBs) - specifically 1, 15, or 59 - in the genome of Saccharomyces cerevisiae in a galactose-inducible manner. This system relies on the galactose-inducible expression of Cas9 nuclease and the use of guide RNAs (gRNAs) targeting different classes of Ty elements. The efficiency of DSB induction was assessed through several methods, including monitoring cell viability in media containing galactose versus glucose, pulsed-field gel electrophoresis (PFGE), PFGE combined with Southern blotting using probes specific to different chromosomes, and the formation of foci by repair and checkpoint proteins. Specifically, the system was utilized to examine foci of the apical checkpoint kinase Tel1 and the repair factors RPA and Rad52.

      From their experiments, the authors conclude that the system is capable of inducing DSBs in a controlled and dose-dependent manner, and that the DSBs are indeed induced at the chromosomal loci where the Ty elements reside.From microscopy experiments, the authors conclude that some DSBs are more persistent, while many are repaired via homologous recombination (HR). New DSBs can form as a result of the continuous expression of Cas9. Finally, Tel1 appears to form multiple foci after DSB induction and these foci localize to the nuclear periphery.

      Major comments.

      In my opinion, some experiments lack appropriate quantification, particularly those evaluating the dose-response effect and the efficiency of DSB induction. Additionally, some conclusions appear to be overestimated in relation to the experimental data. Further experiments and more detailed analyses would be beneficial to fully support the claims and conclusions presented. The data and methods are presented in a manner that should allow for reproducibility. The experiments are adequately replicated, but the statistical analyses are lacking in most of the figures. For example, in Figures 4B, 4C, and 6D, it would be helpful to indicate when the increase in cells containing repair foci is significant.

      Additional experiments and modifications suggested:

      • Figure 1B: Quantify the effect of DSB induction on cell viability with a dose-response curve. No differences are observed between the 0.5% gal and 1% gal conditions. The greatest effect on viability occurs in 2% gal and in the absence of sucrose, which might be due to the absence of sucrose. This should be addressed or discussed.
      • Figure 1B and Figure 2: A quantification of galactose-induced Cas9 expression in the presence of different doses of galactose or over time, respectively, is a necessary control (mRNA or protein expression).
      • Figure 2A: From the cell cycle analysis using FACS, the authors suggest that Cas9 induction causes checkpoint activation. This can be easily confirmed by using more direct methods for checkpoint activation, such as Rad53 phosphorylation. In addition, checkpoint activation should be monitored in synchronized cells released in galactose in order to evaluate whether Cas9-induced DSBs in Ty elements can trigger checkpoint in the first cell cycle or require more time. This reflects the timing of DSB induction.
      • Figure 3: In addition to the restriction analysis, kinetics of DSB formation at specific Ty loci by classical Southern blot or qPCR is, in my opinion, necessary to demonstrate the effectiveness and efficiency of DSB induction over time, especially in relation to Cas9 expression.
      • Figure 5: In this case as well, I believe that a quantitative analysis of the number of cells in the different conditions illustrated in the figure is necessary to understand the dynamics of repair and the formation of new DSBs. Some conclusions are somewhat strong, particularly the correlation between cell cycle phase and repair kinetics (long-lasting Rad52 foci versus short-lived Rad52 foci) and would require quantitative and statistical analysis. In addition, it is not clear to me why cells in which the Rad52 focus disappears do not proceed through the cell cycle (e.g., cells represented in rows 8 and 9 of the figure).
      • Figure 7E and F: It would be interesting to see if the number of Rad52 foci per cell changes in the smc2-8 mutant to understand if RAD52 is required to form the repair center or if this depends on the clustering of Ty elements at the nuclear periphery.

      Minor comments.

      The authors have cited relevant literature to support their methodology, findings, and conclusions. The text and figures are clear. The descriptions in the text are precise and well-articulated, making the data easy to understand. The figures are well-designed and clearly labeled.

      Specific suggestions:

      • Figure 2C: Please change the order of the panel: place chromosome III at the top and chromosome IV at the bottom, as described in the text.
      • Figure 4: The dose-response effect is not evident when monitoring repair foci. It appears that the proportion of cells showing RPA and Rad52 foci is generally low, especially after the formation of 59 DSBs. This is particularly concerning given that the strain in which 59 DSBs are induced already has 20% of cells with RPA foci at time = 0. The authors attribute the lower presence of foci to improved repair caused by the clustering of multiple lesions, but could it simply be due to lower Cas9 efficiency when there are many target sites?
      • Related to Figure 4:The statement on line 400: "the proportion of nuclei displaying Rfa1 foci was consistently double than that of nuclei bearing Rad52 foci, probably reflecting the increased residence time of resected filaments in comparison with the process of homology search" is somewhat strong, considering that the proteins are labeled with different fluorophores, which might experience different rates of photobleaching.

      I believe the proposed experiments can be completed in about 6 months. The request to monitor the kinetics of DSB formation at specific Ty elements in more detail might take more time if the PCR or Southern blot techniques need to be optimized. However, the authors may have other methods in mind that are more familiar to them for evaluating these kinetics, which could be equally valid.

      Referees cross-commenting

      I have carefully read the comments on the manuscript from the other reviewers. I noticed that many of our opinions coincide, and I am convinced that all the requests are appropriate.

      Significance

      My field of expertise centers on checkpoint regulation and homologous recombination in Saccharomyces cerevisiae. I have extensively utilized the galactose-inducible HO endonuclease system for inducing DSBs. I believe that developing additional systems to induce one or more localized DSBs in specific genomic regions is crucial for addressing unresolved questions regarding DSB response. An ideal system would also operate independently of galactose. Based on my experience, an effective system for DSB induction should induce breaks rapidly and simultaneously to produce innovative and reproducible results. From the data presented, I am uncertain whether the system developed in this work meets these criteria.

      The development of a Cas9-based system capable of forming multiple DSBs could be an important tool for studying the DSB response, although I have doubts about how much it will truly enhance our understanding of damage repair. Other systems, cited by the authors, have been previously developed to produce multiple DSBs with different nucleases and using TY elements. Although the Ty-HO system to induce 1, 7, or 10 DSBs was developed in L. Symington's laboratory in 2004, the use of this system has been very limited, likely because it is not easy to monitor what happens to individual DSBs and because the efficiency of simultaneously inducing multiple DSBs may decrease with the increase in the number of target sites. I am concerned that the tool developed in this research article may have limited applicability, being relevant primarily to a small niche within the scientific community focused on DSB response, and thus might generate only a narrow interest. However, the latter part of the paper, which addresses the localization of Tel1, seems promising, despite being preliminary. Additionally, the development of a fluorescent variant of Tel1 is intriguing. This new variant appears to retain the protein's functions and forms well-visible foci within the cell, which seem to be brighter and more intense compared to those obtained with the variant previously developed by M. Lisby and R. Rothstein.

      Strengths:

      • The study presents an innovative system to induce a variable number of double-strand breaks (DSBs) in the genome of Saccharomyces cerevisiae using a galactose-inducible Cas9 and specific gRNAs for Ty elements.
      • The authors use a variety of methods to evaluate DSB induction, including cell viability assays, PFGE, Southern blotting, and foci formation of repair and checkpoint proteins. This comprehensive approach provides sufficient evidence that DSBs are induced.
      • The latter part of the article, focusing on the formation and localization of Tel1 foci, is particularly important. It sheds new light on the functions of Tel1 and its role in the DSB response. This finding is a significant preliminary indication that warrants further development, as the authors suggest in the discussion. I find the development of a tool to effectively visualize Tel1, which is a low-abundance protein in the cell, to be innovative and important for the community working in DSB repair and checkpoint.

      Limitations:

      • Some experiments lack appropriate quantification. For instance, a dose-response curve quantifying the effect of DSB induction on cell viability is missing. Additionally, quantification of galactose-induced Cas9 expression over time (mRNA or protein) is necessary.
      • Statistical analyses are lacking in most figures. It is important to indicate when increases in cells containing repair foci are significant, particularly in Figures 4B, 4C, and 6D.
      • The suggestion of checkpoint activation from cell cycle analysis using FACS should be validated with more direct methods, such as Rad53 phosphorylation, and monitored in synchronized cells to evaluate the timing of checkpoint activation.
      • Further analysis is needed to demonstrate the effectiveness and efficiency of DSB induction over time, especially in relation to Cas9 expression. Monitoring the kinetics of DSB formation at specific Ty loci by classical Southern blot or qPCR would be beneficial.
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      Referee #1

      Evidence, reproducibility and clarity

      The manuscript entitled "A CRISPR-Cas9-based system for the dose-dependent study of DNA double-strand breaks sensing and repair" by Coiffard and colleagues reports on a novel system to monitor the response to multiple DSBs in yeast by targetting Cas9 nuclease to Ty elements. The data is clearly presented, but there are several technical concerns and questions the conclusions of the manuscript. First of all, it is not clear how many DSB cells contain at any given time. The kinetics of DSB formation appears to be slow (hours) relative to the formation and progression of DNA repair foci (minutes). Tel1 foci are found primarily at the nuclear pheriphery, but given the slow kinetics and low number of foci, it is unclear whether the peripheral localization of Tel1 represents physiologically relevant repair and aberrant events where repair failed. Unfortunately, there is not assessment of the outcome of repair. Is the repair error-free or do the cells accummulate indels and/or structural changes at the Cas9 cleavage sites? Without this information, the assay will be of limited use for the scientific community.

      Other major issues:

      1. The introduction should reflect on the chemical structure of DSB ends and the fact that Cas9 remains bound to DNA after cleavage, which may delay repair.
      2. Different Ty elements may be cut with different kinetics. The authors should compare their system to (Gnügge and Symington 2020).
      3. The introduction should reflect on the physiological relevance of 15/59 DSBs.
      4. What is the copy number of the Cas9 and gRNA plasmids? Could cell-to-cell variation in copy number explain the variation in the number of Tel1.
      5. Do the authors observe mutations caused by leaky expression of gRNAs in the uninduced state?
      6. Line 413: I don't think the data in figure 4 completely warrants the conclusion the "DSBs induced by Cas9 engage into HR in a dose-dependent manner". More foci with 15 DSBs than with 59 DSBs? Interference or other explanations? I think this discrepancy warrants additional discussion.
      7. What is observed with a 1h pulse of Cas9 induction followed by glucose? Can the assay monitor the kinetics of repair?
      8. The interpretation of foci in figure 5 is difficult to follow given that only 1 focus is observed while many DSBs are induced. Without further experimentation, these speculations should be moved to the Discussion.
      9. Tel1 foci were always observed at the nuclear periphery (figure 6C). This information should be quantified and compared to Rad52, given that Rad52 foci have previously also been observed at the nuclear periphery for persistent DNA lesions (Whalen and Freudenreich, 2020; Nagai et al., 2008; Lisby et al., 2010). Do these foci perhaps reflect a small subset of Cas9-induced DSBs that are not repair?
      10. Line 699: the notion that Tel1 senses DSBs is novel and does not fit well with the literature given that Tel1 is recruited to foci downstream of Mre11 (Lisby et al., 2004). Unless the authors can provide additional evidence, I suggest to rather write that Tel1 is an early transducer of the DNA damage response.

      Minor suggestions:

      1. The manuscript could benefit from correction of English grammar.
      2. Figure 7F: please also include cells with 1 focus in the graph.
      3. Figure 7: the labels A-F do not follow the legend.
      4. Figure 3, legend: it should be stated in the legend, how long Cas9 was induced in this experiment.
      5. Line 673: it could be noted that in mammalian cells, many more foci are observed, which is probably due to the larger size of the nucleus.
      6. The conclusion that Tel1 behaves exceptionally in terms of the number of foci that are formed is perhaps an overstatement, since only three proteins were analyzed and the occurrence of 8 foci was rare (1:1000 cells).
      7. Line 685: the word "form" indicates that the DSB are already at the nuclear periphery, when bound by Tel1. How do the authors exclude that Tel1 foci form all over the nucleus and then subsequently relocalize to the nuclear periphery? Time-lapse microscopy would be able to reveal where the Tel1 foci form.

      Referees cross-commenting

      I have read and agree with the comments of the other reviewers.

      Significance

      The manuscript entitled "A CRISPR-Cas9-based system for the dose-dependent study of DNA double-strand breaks sensing and repair" by Coiffard and colleagues reports on a novel system to monitor the response to multiple DSBs in yeast by targetting Cas9 nuclease to Ty elements. The data is clearly presented, but there are several technical concerns and questions the conclusions of the manuscript. First of all, it is not clear how many DSB cells contain at any given time. The kinetics of DSB formation appears to be slow (hours) relative to the formation and progression of DNA repair foci (minutes). Tel1 foci are found primarily at the nuclear pheriphery, but given the slow kinetics and low number of foci, it is unclear whether the peripheral localization of Tel1 represents physiologically relevant repair and aberrant events where repair failed. Unfortunately, there is not assessment of the outcome of repair. Is the repair error-free or do the cells accummulate indels and/or structural changes at the Cas9 cleavage sites? Without this information, the assay will be of limited use for the scientific community.

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      Reply to the reviewers

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

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      Referee #3

      Evidence, reproducibility and clarity

      Protein kinases play an important role in regulating cell division and the dynamics of the actomyosin ring both in yeast and mammalian cells. While this raises the possibility that regulated protein dephosphorylation may also affects the division dynamics, few experimental studies have been reported. In the current study, Chrupcala and Moseley screen 9 non-essential protein phosphatases and show that the conserved protein phosphatase PP2A-B56 regulates division plane positioning in fission yeast. The authors show that Par1 localizes to the division site and that cells lacking Par1 have impaired levels of regulators of actomyosin ring positioning, including the anillin-like protein Mid1. Interestingly, restoring wildtype Mid1 levels partially suppresses the division defects observed in the par1∆ mutant.

      The study is well-executed with attention to detail and careful phenotype quantification and analyses. The conclusions of the study are largely supported by experiments to yield the novel insights. This reviewer commends the authors on reporting the negative results regarding Mid1-3xSLiM mutant (Results section) and failure to detect physical interaction between Par1 and Mid1 (Discussion section). The authors provide an interesting discussion. Furthermore, they describe very relevant additional experiments but they restrict their execution to future studies that complement the current manuscript

      Major concern

      The authors show that par1∆ cells have impaired levels of Mid1, Cdc15 and Rga7, yet propose that Mid1 reduction is the principal cause of cytokinetic defects in par1∆ cells. Even though increase in Mid1 levels rescues par1∆ defects, it is possible that increased Mid1 levels suppress another primary defect (e.g. Rga7 increased levels). Thus, it would be interesting to perform the following two experiments: 1. The authors in the discussion say "we found that cytokinesis defects arise from decreased Mid1 levels" but this is not formally shown other than in par1∆ cells. Thus I would suggest monitor cytokinesis in cells with Mid1 levels directly reduced to levels comparable to those observed in par1∆ cells (as quantified in Fig 3B). Monitoring the effects of reduced Mid1 levels on Rga7 and Cdc15 would also be interesting. 2. Monitoring the levels of Rga7 and Cdc15 in par1∆ cells rescued by the second copy Mid1.

      Minor concern

      Even though definitive evidence for Par1 mechanism of Mid1 regulation might be difficult to obtain, the authors may choose to strengthen their work on the role of dephosphorylation at the actomyosin ring. For example, using the GFP-GFPnanobody pairing to force interaction between Mid1 and Par2 in par1∆ cells may provide support for dephosphorylation playing a more direct role in actomyosin ring positioning.

      Referees cross-commenting

      Consultation regarding Review 1:

      Reviewer 3 shares the interest in points 1,3,5.

      Relating to point 2: Not sure what the reviewer specifically wishes here.

      Relating to point 4: Extensive analyses of many cytokinetic proteins in par1∆ cells, and importance of their levels for cytokinesis, would be interesting but perhaps beyond the scope of this study. I believe it would suffice to monitor Cdc15, Bgs1 and Rga7 in the 2xMid1 rescue that authors performed.

      Consultation regarding Review 2: Reviewer 3 shares the interest in major points 1 (though authors do leave open the possibility that PP2A acts indirectly),3,4,5. Regarding point 2: This might be difficult to ascertain directly and instead it might suffice to show that Mid1 levels reduced to those observed in par1∆ phenocopy the par1 mutant's division defects.

      Significance

      The study is well-executed with novel findings on regulation of the cell division and the physiological roles of phosphatases. The study will benefit cell polarity and cell division research fields as well as researchers interested in roles of protein phosphatases.

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      Referee #2

      Evidence, reproducibility and clarity

      Summary:

      In this study, the authors investigates the functional relationship of Mid1, which plays a central role in the positioning of the contractile ring (CAR) in fission yeast, with protein phosphatases. Previous studies have shown that Mid1 is phosphorylated and modified by several kinases, but its relationship with phosphatases is not well understood except of Clp1. Therefore, the authors examined whether phosphorylase gene disruption strains were able to divide symmetrically. The authors found that cells lacking par1, which encodes the regulatory subunit of PP2A, frequently divided asymmetrically. Furthermore, they found that the par1 deletion mutant showed reduced protein levels of Mid1 in the cells. Furthermore, they showed that increasing the expression level of Mid1 can partially compensate for the mitotic abnormalities of the par1 strain. Since Par1 localizes to the division site, the authors also investigated the possibility of binding with Mid1, focusing on its SLiM motif. However, at this time, it is unclear whether direct binding of Par1 to Mid1 is necessary for Mid1 to exert its cellular functions, since no conspicuous cytokinesis abnormalities were observed in Mid1 with the mutation in the SLiM motif.

      The focus of the study to be interesting and the clarity of the overall argument of the manuscript to be almost adequate. However, the authors should investigate or mention the following points. Also, a more appropriate and convincing way of presenting experimental results is required.

      Major comments:

      1. Does Par1 (PP2A) work in the dephosphorylation of Mid1? Looking at the band pattern of the western blot of Mid1 in Fig. 3E, there are several bands. This band shift probably indicates phosphorylation of Mid1, but is there any difference in the band shift between the wild-type strain and the par1 gene disrupted strain? Mid1 is phosphorylated in a cell cycle-dependent manner. So, it would be interesting to examine the cell cycle-dependent phosphorylation pattern using synchronous culture.
      2. In Fig. 5A, par1- and ppa2-deficient strains show little nuclear localization of Mid1 in interphase cells. If little or no Mid1 enters the nucleus, could it be possible that the mitotic abnormality is not due to a reduction in Mid1 protein levels, but is directly due to an effect on the shuttling of Mid1 between the cell nucleus and cell surface?
      3. The photographs showing cellular localization of proteins, such as Figs. 3, 4, 5, 6B, and 6C, are not convincing. The authors should show a typical picture of the cell population as supplemental figures, rather than trimming a single cell.
      4. Is the Mid1-deficient strains impaired in the localization of Par1 to the division plane? As shown in Fig. 3A, the fluorescence of Cdc15 and Rga7 is predominantly enhanced in the par1 deletion strain (Fig. S2 also shows a protein with a significant difference in localization). The authors should consider these points and make more comprehensive discussion.
      5. Fig. 3D and part of Fig. 5B also use the same photograph. This raises the suspicion that these data were taken only once. If so, the authors should do replicated experiments to assure the authenticity of the data. In addition, perhaps it is a careless mistake, but this way of presenting data should not be allowed unless specifically mentioned in the manuscript.

      Minor point.

      Typos. p. 11 Mid1-13my levels,.

      Lack of uniformity in description p. 13 Methyl-2-benzimidazole and p. 15 methyl-2-benzimidazole In the figure of the paper Mid1-mNeonGreen and mid1-mNeonGreen

      Significance

      The importance of this study is that it deepens our knowledge of Mid1 protein of fission yeast, an important model organism for the study of cytokinesis. Although the possibility that Par1 is involved in the maintenance of Mid1 protein levels has been demonstrated, the molecular mechanism has not been clarified. It might be expected that anilline, which is similar to Mid1 in animal cells, might have a similar relationship to protein phosphatases, but there is no evidence for this. Therefore, at this moment, the effect of these findings may be limited to the fission yeast research community.

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      Referee #1

      Evidence, reproducibility and clarity

      The study by Chrupcala and Moseley explores the role of the protein phosphatase PP2A-B56 in cytokinesis, particularly focusing on its regulatory subunit Par1 and its interaction with Mid1 in fission yeast (S. pombe). The authors report that in cells lacking Par1 (par1d), the contractile rings are mispositioned, and the levels of multiple cytokinetic proteins, including Mid1, are altered, leading to defects in cytokinesis. They suggest that the reduction in Mid1 levels is responsible for the observed cytokinetic defects and show that restoring Mid1 levels can partially rescue these defects. The study further demonstrates that Mid1 shuttling between the nucleus and cell membrane is impaired in par1d mutants. Thus, par1d seems to cause a range of defects, from altered protein levels to specifically impairing Mid1 functions. However, the study does not demonstrate a direct interaction between Par1 and Mid1, leaving the exact mechanism by which Par1 regulates Mid1 levels unclear.

      The manuscript is well-written and investigates the lesser-studied role of protein phosphatases in cytokinesis, which is of general interest. However, a major criticism is the lack of evidence supporting a direct role of PP2A-B56 and its regulatory subunit Par1 in cytokinesis. It is possible that the phenotype observed in par1d cells results from a global impairment of protein regulation rather than a specific effect on Mid1. Indirect factors, such as changes in cell size/shape, could also produce similar phenotypes.

      To strengthen the manuscript, the authors should consider the following points:

      1. Changes in cell size/shape can influence Mid1 levels and nucleus positioning. Many par1d cells shown in the manuscript have bulgy morphologies. The manuscript should address whether cell size/morphology differences contribute to the observed phenotypes.
      2. The quantification of nucleus positioning needs further consideration, as the positioning of the nucleus has been shown to be a function of cell size, etc.
      3. The manuscript proposes that Par1 acts by reducing Mid1 levels and that restoring Mid1 levels can rescue the defects. However, given the known mechanisms of Mid1 localization, it is unclear why a reduction in Mid1 levels alone would lead to cytokinetic defects. To establish that the defects are due to Mid1 reduction, the authors should demonstrate that lowering Mid1 levels (e.g., using a low-expression promoter) phenocopies the cytokinesis defects observed in par1d cells.
      4. As shown in par1d cells, other cytokinesis proteins have impaired levels. It should be investigated whether changes in the levels of other proteins (e.g., Cdc15, Rga7, Myp2, etc.) in par1d cells contribute to the cytokinetic defects. In general, it is not discussed how the par1d mutant can lead to differential levels of many cytokinesis proteins. Does the reduction of Mid1 explain this shift? It is conceivable that changes in the levels of other proteins could also produce similar cytokinesis defects.
      5. The manuscript would benefit from additional functional rescue experiments. For example, expressing a phosphatase-dead version of Par1 in par1d cells could help determine if its phosphatase activity is necessary for cytokinesis.

      Significance

      The study by Chrupcala and Moseley explores the role of the protein phosphatase PP2A-B56 in cytokinesis, particularly focusing on its regulatory subunit Par1 and its interaction with Mid1 in fission yeast (S. pombe). The authors report that in cells lacking Par1 (par1d), the contractile rings are mispositioned, and the levels of multiple cytokinetic proteins, including Mid1, are altered, leading to defects in cytokinesis. They suggest that the reduction in Mid1 levels is responsible for the observed cytokinetic defects and show that restoring Mid1 levels can partially rescue these defects. The study further demonstrates that Mid1 shuttling between the nucleus and cell membrane is impaired in par1d mutants. Thus, par1d seems to cause a range of defects, from altered protein levels to specifically impairing Mid1 functions. However, the study does not demonstrate a direct interaction between Par1 and Mid1, leaving the exact mechanism by which Par1 regulates Mid1 levels unclear.

      The manuscript is well-written and investigates the lesser-studied role of protein phosphatases in cytokinesis, which is of general interest. However, a major criticism is the lack of evidence supporting a direct role of PP2A-B56 and its regulatory subunit Par1 in cytokinesis. It is possible that the phenotype observed in par1d cells results from a global impairment of protein regulation rather than a specific effect on Mid1. Indirect factors, such as changes in cell size/shape, could also produce similar phenotypes.

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      Reply to the reviewers

      Reply to Reviewers

      We would like to thank all the reviewers for their thorough reading and helpful comments. Below, please find our point-by-point response. The reviewer comments received through ReviewCommons have not been altered except for formatting.

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

      The authors extended the existing recombination-induced tag exchange (RITE) technology to show that they can image a subset of NPCs, improving signal-to-noise ratios for live cell imaging in yeast, and to track the stability or dynamics of specific nuclear pore proteins across multiple cell divisions. Further, the authors use this technology to show that the nuclear basket proteins Mlp1, Mlp2 and Pml39 are stably associated with "old NPCs" through multiple cell cycles. The authors show that the presence of Mlp1 in these "old NPCs" correlates with exclusion of Mlp1-positive NPCs from the nucleolar territory. A surprising result is that basket-less NPCs can be excluded from the non-nucleolar region, an observation that correlates with the presence of Nup2 on the NPC regardless of maturation state of the NPC. In support of the proposal that retention of NPCs via Mlp1 and Nup2 in non-nucleolar regions, simulation data is presented to suggest that basket-less NPCs diffuse faster in the plane of the nuclear envelope.

      However, there are some points that do need addressing:

      Major Points 1. Taking into account that the Nup2 result in Figure 4B forms the basis for one half of the proposed model in Figure 6 regarding the exclusion of NPCs from the nucleolar region of the NE, there is a relatively small amount of data in support of this finding and this proposed model. For example, the only data for Nup2 in the manuscript is a column chart in Figure 4B with no supporting fluorescence microscopy examples for any Nup2 deletion. Further, the Nup60 deletion mutant will have zero basket-containing NPCs, whereas the Nup2 deletion will be a mixture of basket-containing and basket-less NPCs. The only support for the localization of basket-containing NPCs in the Nup2 deletion mutant is through a reference "Since Mlp1-positive NPCs remain excluded from the nucleolar territory in nup2Δ cells (Galy et al., 2004), the homogenous distribution observed in this mutant must be caused predominantly by the redistribution of Mlp-negative NPCs into the nucleolar territory."

      As suggested by the reviewer, we have added fluorescence microscopy examples for the Nup2 deletion to new Figure 4D. In addition, we have added data on Nup1 as suggested by reviewer 3. Since we observed a significant effect on nucleolar NPC density also upon depletion of Nup1 (new Figure 4A), we have overall revised the text and model to now reflect the shared role of Nup1 and Nup2.

      We have also localized Mlp1-GFP in a nup2Δ background as well as in the Nup60ΔC background where Nup2 can no longer bind to the NPC. In both strains, Mlp1-containing NPCs remain excluded from the nucleolus as now shown in the new Figure 4E. Although we also observed partial Mlp1 mislocalization to a nuclear focus in the nup2Δ strain, such mislocalization was only minimal in the strain with the Nup2-binding domain in Nup60 deleted (nup60ΔC), supporting our conclusion that Nup2 contributes to nucleolar exclusion of NPCs independent of Mlp1. Similarly, Mlp1-positive NPCs remained excluded from the nucleolar territory in cells depleted of Nup1 (new Figure 4B).

      1. The authors could consider utilizing this opportunity to discuss their technological innovations in the context of the prior work of Onischenko et al., 2020. This work is referenced for the statement "RITE can be used to distinguish between old and new NPCs" Page 2, Line 43. However, it is not referenced for the statement "We constructed a RITE-cassette that allows the switch from a GFP-labelled protein to a new protein that is not fluorescently labelled (RITE(GFP-to-dark))" despite Onischenko et al., 2020 having already constructed a RITE-cassette for the GFP-to-dark transition. The authors could consider taking this opportunity to instead focus on their innovative approach to apply this technology to decrease the number of fluorescently-tagged NPCs by dilution across multiple cell divisions and to interpret this finding as a measure of the stability of nuclear pore proteins within the broader NPC.

      We apologize for this imprecise citation. We have modified the text to indicate that our RITE cassette was previously used in two publications. It now reads: "We used a RITE-cassette that allows the switch from a GFP-labelled protein to a new protein that is not fluorescently labelled (RITE(GFP-to-dark)) (Onischenko et al., 2020, Kralt et al., 2022)." Together with additional changes to the text throughout, we hope that our new manuscript version more clearly highlights the innovation of our approach relative to previous use cases.

      1. The authors could also consider taking this opportunity to discuss their results in the context of the Saccharomyces cerevisiae nuclear pore complex structures published e.g. in Kim et al., 2018, Akey et al., 2022, Akey et al., 2023 in which the arrangement of proteins in the nuclear basket is presented, and also work from the Kohler lab (Mészáros et al., 2015) on how the basket proteins are anchored to the NPC. There is additional literature that also might help provide some perspective to the findings in the current manuscript, such as the observation that a lesser amount of Mlp2 to Mlp1 observed is consistent with prior work (e.g. Kim et al., 2018) and that intranuclear Mlp1 foci are also formed after Mlp1 overexpression (Strambio-de-Castillia et al., 1999).

      Following the reviewer's suggestion, we extended our discussion of basket Nup stoichiometry and organization in the discussion section including most of the citations mentioned as well as the recent articles on the nuclear basket structure and organization (Stankunas & Köhler 2024 1038/s41556-024-01484-x, Singh et al. 2024 10.1016/j.cell.2024.07.020)

      Minor Points 1. What is the "lag time" of the doRITE switching? Do the authors believe that it is comparable to the approximate 1-hour timeframe following beta-estradiol induction as shown previously in Chen et al. Nucleic Acids Research, Volume 28, Issue 24, 15 December 2000, Page e108, https://doi.org/10.1093/nar/28.24.e108

      We thank the reviewer for suggesting we analyze the kinetics of RITE switching. We carried out quantitative real-time PCR on genomic DNA and found that the half-time of switching is below 20 min. The majority of the population is switched after 1 hour, similar to the results in Chen et al. This data is now included in Supplemental Figure 1A.

      1. The authors could consider a brief explanation of radial position (um) for the benefit of the reader, in Figures 1E (right panel) and 2B (right panel), perhaps using a diagram to make it easier to understand the X-axis (um).

      To address this, we have now included a diagram and refer to it in the figure legend and the text.

      1. In Figure 1G, would the authors consider changing the vertical axis title and the figure legend wording from "mean number of NPCs per cell" to "mean labeled NPC # per cell" to reflect that what is being characterized are the remaining GFP-bearing NPCs over time?

      Thank you for spotting this inaccuracy. We have changed the label to "mean # of labeled NPCs per cell".

      1. In Figure 2C, the magenta-labeled protein in the micrographs is not described in the figure or the legend.

      A description has been added in figure and legend.

      1. In Figure S2A, there is an arrow indicating a Nup159 focus, but this is not described in the figure legend, as is done in Figure 2C.

      A description has been added to the legend.

      1. In Figure S3C, the figure legend does not match the figure. Was this supposed to be designed like Figure 3C and is missing part of the figure? Or is the legend a typographical error?

      We apologize for this error and thank the reviewer for spotting it. The legend has been corrected (now Figure S4B).

      1. In Figure S4B, the spontaneously recombined RITE (GFP-to-dark) Nup133-V5 appears in the western blot as equally abundant to pre-recombined Nup133-V5-GFP. In the figure legend, this is explained as cells grown in synthetic media without selection to eliminate cells that have lost their resistance marker from the population. In Cheng et al. Nucleic Acids Res. 2000 Dec 15; 28(24): e108, Cre-EBD was not active in the absence of B-estradiol, despite galactose-induced Cre-EBD overexpression. Would the authors be able to comment further on the Cre-Lox RITE system in the manuscript?

      We note that also in the cited publication, cells are grown in the presence of selection to select (as stated in this publication) "against pre-excision events that occur because of low but measurable basal expression of the recombinase". Although the authors report that spontaneous recombination is reduced with the b-estradiol inducible system (compared to pGAL expression control of the recombinase only), they show negligible spontaneous recombination only within a two-hour time window. Indeed, we also observe low levels of uninduced recombination on a short timeframe, but occasional events can become significant in longer incubation times (e.g. overnight growth) in the absence of selection. It should be noted that in our system, Cre expression is continuously high (TDH3-promoter) and not controlled by an inducible GAL promoter. We have added the information about the promoter controlling Cre-expression in the methods section.

      1. In Figure 6, the authors may want to consider inverting the flow of the cartoon model to start from the wild type condition and apply the deletion mutations at each step to "arrive" at the mutant conditions, rather than starting with mutant conditions and "adding back" proteins.

      Following the suggestions of this reviewer as well as reviewer 3, we have modified our model to smore clearly represent the contributions of the different basket components.

      Reviewer #1 (Significance (Required)):

      Recent work has drawn attention to the fact that not all NPCs are structurally or functionally the same, even within a single cell. In this light, the work here from Zsok et al. is an important demonstration of the kind of methodologies that can shed light on the stability and functions of different subpopulations of NPCs. Altogether, these data are used to support an interesting and topical model for Nup2 and nuclear-basket driven retention of NPCs in non-nucleolar regions of the nuclear envelope.

      We thank the reviewer for this positive assessment of our work.

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

      In this study, Zsok et al. develop innovative methods to examine the dynamics of individual nuclear pore complexes (NPCs) at the nuclear envelope of budding yeast. The underlying premise is that with the emergence of biochemically distinct NPCs that co-exist in the same cell, there is a need to develop tools to functionally isolate and study them. For example, there is a pool of NPCs that lack the nuclear basket over the nucleolus. Although the nature of this exclusion has been investigated in the past, the authors take advantage of a modification of recombination induced tag exchange (RITE), the slow turnover of scaffold nups, the closed mitosis of budding yeast, and extensive high quality time lapse microscopy to ultimately monitor the dynamics of individual NPCs over the nucleolus. By leveraging genetic knockout approaches and auxin-induced degradation with sophisticated quantitative and rigorous analyses, the authors conclude that there may be two mechanisms dependent on nuclear basket proteins that impact nucleolar exclusion. They also incorporate some computational simulations to help support their conclusions. Overall, the data are of the highest quality and are rigorously quantified, the manuscript is well written, accessible, and scholarly - the conclusions are thus on solid footing.

      We thank the reviewer for this assessment.

      Reviewer #2 (Significance (Required)):

      I have no concerns about the data or the conclusions in this manuscript. However, the significance is not overly clear as there is no major conceptual advance put forward, nor is there any new function suggested for the NPCs over nucleoli. As NPCs are immobile in metazoans, the significance may also be limited to a specialized audience.

      We respectfully disagree with this assessment. First, our work demonstrates the use of a novel approach in the application of RITE that can be useful for other researchers in the field of NPC biology and beyond. For example, doRITE could be applied to study the properties of aged NPCs, an area of considerable interest due to links between the NPC and age-related neurodegenerative diseases.

      Second, we characterize the interaction between conserved nuclear components, the NPC, the nucleolus and chromatin. While the specific architecture of the nucleus varies between species, many of these interactions are conserved. For example, Nup2's homologue Nup50 also interacts with chromatin in other systems, including mammalian cells, and thus may contribute to regulating the interplay between the nuclear basket and adjoining chromatin. This adds to our understanding of the multiple pathways and interactions that contribute to nuclear organization. Therefore, although the depletion of NPCs from the nucleolar territory in budding yeast may not be of direct importance, understanding the relationships between NPCs and their environment provide insight about nuclear organization throughout different eukaryotic lineages.

      In the revised manuscript, we attempt to better highlight and discuss these aspects.

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

      The manuscript of Zsok et al. describes the role of nuclear basket proteins in the distribution and mobility of nuclear pore complexes in budding yeast. In particular, the authors showed that the doRITE approach can be used for the analysis of stable and dynamically associated NUPs. Moreover, it can distinguish individual NUPs and follow the inheritance of individual NPCs from mother to daughter cells. The author's findings highlight that Mlp1, Mlp2, and Pml39 are stably associated with the nuclear pore; deletion of Mlp1-Mlp2 and Nup60 leads to the higher NPC density in the nucleolar territory; and NPCs exhibit increased mobility in the absence of the nuclear basket components.

      The manuscript contains most figures supporting the data, and data supports the conclusions. However, authors need to include better explanations for figures in the text and figure legends. Lack of detailed explanation can pose challenges for non-experts. In addition, the authors jump over figures and shuffle them through the manuscript, which disrupts the flow and coherence of the manuscript.

      We thank the reviewer for pointing this out. In response to the detailed comments given below, we have moved some figures and added more explicit explanations to the text to improve the flow and make it easier to follow. In addition, we have modified the figure legends throughout the manuscript to make them more accessible to the reader.

      Major comments: - The nuclear basket contains Nup1, Nup2, Nup60, Mlp1, and Mlp2 in yeast. Nup60 works as a seed for Mlp1/Mlp2 and Nup2 recruitment and plays a key role in the assembly of nuclear pore basket scaffold (PMID: 35148185). Logically, the authors focused primarily on Nup60 in the current manuscript. However, NUP153 has another ortholog of yeast - Nup1, which has not been studied in this work. I recommend adjusting the title of the manuscript to: Nup60 and Mlp1/Mlp2 regulate the distribution and mobility of nuclear pore complexes in budding yeast. I also suggest discussing why work on Nup1 was not included/performed in the manuscript.

      We thank the reviewer for suggesting we should test the role of Nup1. Although we had originally not considered it, since we were focusing on the interactors of Mlp1/2, we found that indeed Nup1 also contributes to nucleolar exclusion. We have therefore changed the title to "Nuclear basket proteins regulate the distribution and mobility of nuclear pore complexes in budding yeast".

      • Figure 2B: I suggest choosing a more representative image for Pml39. It looks not like a stable component but rather dynamic as NUP60 or Gle1 based on figure showed in Figure 2B.

      We thank the reviewer for pointing out this poor choice of panel. We selected a panel for the 14h timepoint that more clearly shows that individual foci can still be seen for Pml39 after this time. Due to its lower copy number, the foci are dimmer for Pml39 than the other stable Nups. Nevertheless, at both the 11 and 14 h timepoint, clear dots can be detected for Pml39, while e.g. Nup116 in the same figure exhibits a more distributed signal and the signal for Nup60 and Gle1 is no longer visible.

      • Depletion of AID-tagged proteins needs to be supported by Western blot analysis with protein-specific antibodies, and PCR results should be included in supplementary data to demonstrate the homozygosity of the strains.

      The correct genomic tagging of the depleted proteins by AID was confirmed by PCR. We include this PCR analysis for the reviewer below. Since we are working with haploid yeast cells, all strains only carry a single copy of the genes. Unfortunately, we do not have protein-specific antibodies against the depleted proteins. However, other phenotypes support the successful depletion of the protein: Mlp1-mislocalization upon Nup60 depletion, reduced transcript production in Pol II depletion (characterized previously: PMID: 31753862, PMID: 36220102), growth defect upon Nup1 depletion.

      • Figure 5B: Snapshots of images from the movie are required. There are no images, only quantifications.

      We have replaced the supplemental movie with a movie showing the detection by Trackmate as well as overlaid tracks. As requested, a snapshot of this movie was inserted in figure 5B. We have also moved the example tracks from the supplement to the main figure. Furthermore, we will deposit the tracking dataset in the ETH Research Collection to make it available to the community.

      Description of figure legends is more technical than supporting/explaining the figure. For example, below my suggestions for Figure 1D. Please, consider more detailed explanation for other figures. (D) Left: Schematic of the RITE cassette. NUP of interest is tagged with V5 tag and eGFP fluorescent protein where LoxP sites flank eGFP. Before the beta-estradiol-induced recombination, the old NPCs are marked with eGFP signal, whereas new NPCs lack an eGFP signal after the recombination. ORF: open reading frame; V5: V5-tag; loxP: loxP recombination site; eGFP: enhanced green fluorescent protein. Right: doRITE assay schematic of stable or dynamic Nup behavior over cell divisions in yeast after the recombination.

      We have modified the figure legends throughout the manuscript to make them more explanatory and helpful for the reader.

      In addition, I recommend highlighting the result in the title of the figures. Please, re-consider titles for Figure S3.

      We have split this figure to better group related results. The new figures S4 and S5 are entitled: " A RITE(dark-to-GFP) cassette to visualize newly assembled NPC. " and "Mlp1 truncations localize predominantly to non-nucleolar NPCs."

      Minor: P.1 Line 31. Extra period symbol before the "(Figure 1A)".

      Fixed

      P.2 Line 10. Inconsistent writing of PML39 and MLP1. Both genes are capitalized. The same for P.4 Line 16. In some cases all letters are capitalized in other only the first one.

      We are following the official yeast gene nomenclature by spelling gene names in italicized capitals and protein names with only the first letter capitalized. We are sorry that this can be confusing for readers more familiar with other model systems.

      P.2 Line 18-22. The sentence is too long and hard to read. I recommend splitting it into two sentences.

      We agree and have fixed this.

      P.2-3 Line 46-47. The sentence is unclear. Suggestion: We expected that successive cell divisions would dilute the signal of labelled and stably associated with the NPC nucleoporins. By contrast, ...

      We have modified the sentence to read: "When tagging a Nup that stably associates with the NPC, we expected that successive cell divisions would dilute labelled NPCs by inheritance to both mother and daughter cells leading to a low density of labelled NPCs. By contrast,..."

      P.4 Line 17-21. Please, consider adding extra information and clarifying lines 19-21. For example, in Line 19 Figure 2B you can add that the reader needs to compare row 1 and row 4.

      Thank you, we have fixed this as suggested.

      P. 5 Line 15. When a number begins a sentence, that number should always be spelled out. You can pe-phrase the sentence to avoid it. Also, I recommend adding an explanation/hypothesis of why new NPCs are less frequently detected in nucleolar territory.

      We have formatted the text. Interestingly, new NPCs are more frequently detected in the nucleolar territory than old NPCs. We have reformulated this section to make it clearer, also in response to the next comment.

      P.5 Line 17-22. I recommend re-phrasing these two sentences. Logically, it is clear that Mlp1/Mlp2 loss mimics "old NPCs" to look more like "new NPCs", and for that reason, they are more frequently included in the nucleolar territory, but it is not clear when you read these two sentences from the first time.

      We have reformulated this section to make it clearer.

      P6. Line 16. No figure supporting data on graph (Figure 3B).

      We have added fluorescent images of the nup2Δ strain to the figure (new Figure 4D).

      P.7 Line 10-13. The sentence is unclear.

      We have shortened the sentence and moved part of the content to the discussion in the next paragraph.

      P.13,14 etc. If 0h timepoint has been used for normalization, why is it present on the graph?

      The 0h timepoint is shown for comparison and to illustrate the standard deviation in the data.

      P.15. Line 32-33. There is no image here. Potentially wrong description of the figure.

      Thank you for spotting this. This was fixed (new Figure S4B).

      Figures: - Inconsistent labeling of figures. For example, Fig.1, Fig.1S, Figure 2 etc.

      Thank you, this has been corrected.

      • Inconsistent labeling of figures. For example, Fig.1 G "mean number of NPCs per cell" - no capitalization of the first letter. Fig.1S "Fraction in population" is capitalized. In general, titles of axis should be capitalized.

      Thank you for spotting this. This was fixed.

      Suggestions for Figure 1D and Figure 6 are attached as a separate file.

      We thank the reviewer for their suggestions to improve these figures. We have taken their recommendation and revised the figures accordingly (see also response to reviewer 1, minor point 8).

      Reviewer #3 (Significance (Required)):

      Zsok et al. used the recombination-induced tag exchange (RITE) approach, which is an interesting and powerful method to follow individual NUPs over time with respect to their localization and abundance. This approach has been used before in PMID: 36515990 to distinguish pre-existing and newly synthesized Nup2 populations and has been extended to other basket NUPs in this work. Using this method, the authors support the earlier data on basket nucleoporins and highlight new insights on how basket nucleoporins regulate NPCs distribution and mobility. Overall, the manuscript provides new details on the stability of nucleoporins in yeast and how these data align with the mass spectrometry and FRAP data performed earlier in other studies. The limitation of this study is the absence of data on Nup1. It was unclear why these data were not present. Additional data can be included on the dynamics of Pml39, for example, using the FRAP method. The dynamic of Pml39 at the pore was shown only using the doRITE method.

      As suggested, we have tested the role of Nup1 (see above).

      Unfortunately, we are not able to provide orthologous data for the dynamics of Pml39. As we discuss in the manuscript, FRAP is not suitable for the analysis of the dynamics of most nucleoporins in yeast due to the high lateral mobility of NPCs in the nuclear envelope and has previously generated misleading results for Mlp1. Furthermore, the low expression levels of Pml39 will make it difficult to obtain reliable FRAP curves for this protein. We therefore do not think that adding FRAP experiments with Pml39 will provide valuable insight.

      However, in addition to the Pml39 doRITE result itself, our observation that the Pml39-dependent pool of Mlp1 exhibits stable association with the NPC supports the interpretation of Pml39 as a stable protein as well.

      In general, this study represents a unique research study of basic research on nuclear pore proteins that will be of general interest to the nuclear transport field.

      Field of expertise: nuclear-cytoplasmic transport, nuclear pore, inducible protein degradation. I do not have sufficient expertise in ExTrack.

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

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      Referee #3

      Evidence, reproducibility and clarity

      The manuscript of Zsok et al. describes the role of nuclear basket proteins in the distribution and mobility of nuclear pore complexes in budding yeast. In particular, the authors showed that the doRITE approach can be used for the analysis of stable and dynamically associated NUPs. Moreover, it can distinguish individual NUPs and follow the inheritance of individual NPCs from mother to daughter cells. The author's findings highlight that Mlp1, Mlp2, and Pml39 are stably associated with the nuclear pore; deletion of Mlp1-Mlp2 and Nup60 leads to the higher NPC density in the nucleolar territory; and NPCs exhibit increased mobility in the absence of the nuclear basket components.

      The manuscript contains most figures supporting the data, and data supports the conclusions. However, authors need to include better explanations for figures in the text and figure legends. Lack of detailed explanation can pose challenges for non-experts. In addition, the authors jump over figures and shuffle them through the manuscript, which disrupts the flow and coherence of the manuscript.

      Major comments:

      • The nuclear basket contains Nup1, Nup2, Nup60, Mlp1, and Mlp2 in yeast. Nup60 works as a seed for Mlp1/Mlp2 and Nup2 recruitment and plays a key role in the assembly of nuclear pore basket scaffold (PMID: 35148185). Logically, the authors focused primarily on Nup60 in the current manuscript. However, NUP153 has another ortholog of yeast - Nup1, which has not been studied in this work. I recommend adjusting the title of the manuscript to: Nup60 and Mlp1/Mlp2 regulate the distribution and mobility of nuclear pore complexes in budding yeast. I also suggest discussing why work on Nup1 was not included/performed in the manuscript.
      • Figure 2B: I suggest choosing a more representative image for Pml39. It looks not like a stable component but rather dynamic as NUP60 or Gle1 based on figure showed in Figure 2B.
      • Depletion of AID-tagged proteins needs to be supported by Western blot analysis with protein-specific antibodies, and PCR results should be included in supplementary data to demonstrate the homozygosity of the strains.
      • Figure 5B: Snapshots of images from the movie are required. There are no images, only quantifications.
      • Description of figure legends is more technical than supporting/explaining the figure. For example, below my suggestions for Figure 1D. Please, consider more detailed explanation for other figures. (D) Left: Schematic of the RITE cassette. NUP of interest is tagged with V5 tag and eGFP fluorescent protein where LoxP sites flank eGFP. Before the beta-estradiol-induced recombination, the old NPCs are marked with eGFP signal, whereas new NPCs lack an eGFP signal after the recombination. ORF: open reading frame; V5: V5-tag; loxP: loxP recombination site; eGFP: enhanced green fluorescent protein. Right: doRITE assay schematic of stable or dynamic Nup behavior over cell divisions in yeast after the recombination.

      In addition, I recommend highlighting the result in the title of the figures. Please, re-consider titles for Figure S3.

      Minor:

      P.1 Line 31. Extra period symbol before the "(Figure 1A)".

      P.2 Line 10. Inconsistent writing of PML39 and MLP1. Both genes are capitalized. The same for P.4 Line 16. In some cases all letters are capitalized in other only the first one.

      P.2 Line 18-22. The sentence is too long and hard to read. I recommend splitting it into two sentences.

      P.2-3 Line 46-47. The sentence is unclear. Suggestion: We expected that successive cell divisions would dilute the signal of labelled and stably associated with the NPC nucleoporins. By contrast, ...

      P.4 Line 17-21. Please, consider adding extra information and clarifying lines 19-21. For example, in Line 19 Figure 2B you can add that the reader needs to compare row 1 and row 4.

      P. 5 Line 15. When a number begins a sentence, that number should always be spelled out. You can pe-phrase the sentence to avoid it. Also, I recommend adding an explanation/hypothesis of why new NPCs are less frequently detected in nucleolar territory.

      P.5 Line 17-22. I recommend re-phrasing these two sentences. Logically, it is clear that Mlp1/Mlp2 loss mimics "old NPCs" to look more like "new NPCs", and for that reason, they are more frequently included in the nucleolar territory, but it is not clear when you read these two sentences from the first time.

      P6. Line 16. No figure supporting data on graph (Figure 3B).

      P.7 Line 10-13. The sentence is unclear.

      P.13,14 etc. If 0h timepoint has been used for normalization, why is it present on the graph?

      P.15. Line 32-33. There is no image here. Potentially wrong description of the figure.

      Figures:

      • Inconsistent labeling of figures. For example, Fig.1, Fig.1S, Figure 2 etc.
      • Inconsistent labeling of figures. For example, Fig.1 G "mean number of NPCs per cell" - no capitalization of the first letter. Fig.1S "Fraction in population" is capitalized. In general, titles of axis should be capitalized.

      Suggestions for Figure 1D and Figure 6 are attached as a separate file.

      Significance

      Zsok et al. used the recombination-induced tag exchange (RITE) approach, which is an interesting and powerful method to follow individual NUPs over time with respect to their localization and abundance. This approach has been used before in PMID: 36515990 to distinguish pre-existing and newly synthesized Nup2 populations and has been extended to other basket NUPs in this work. Using this method, the authors support the earlier data on basket nucleoporins and highlight new insights on how basket nucleoporins regulate NPCs distribution and mobility. Overall, the manuscript provides new details on the stability of nucleoporins in yeast and how these data align with the mass spectrometry and FRAP data performed earlier in other studies. The limitation of this study is the absence of data on Nup1. It was unclear why these data were not present. Additional data can be included on the dynamics of Pml39, for example, using the FRAP method. The dynamic of Pml39 at the pore was shown only using the doRITE method.

      In general, this study represents a unique research study of basic research on nuclear pore proteins that will be of general interest to the nuclear transport field.

      Field of expertise: nuclear-cytoplasmic transport, nuclear pore, inducible protein degradation. I do not have sufficient expertise in ExTrack.

    3. 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 study, Zsok et al. develop innovative methods to examine the dynamics of individual nuclear pore complexes (NPCs) at the nuclear envelope of budding yeast. The underlying premise is that with the emergence of biochemically distinct NPCs that co-exist in the same cell, there is a need to develop tools to functionally isolate and study them. For example, there is a pool of NPCs that lack the nuclear basket over the nucleolus. Although the nature of this exclusion has been investigated in the past, the authors take advantage of a modification of recombination induced tag exchange (RITE), the slow turnover of scaffold nups, the closed mitosis of budding yeast, and extensive high quality time lapse microscopy to ultimately monitor the dynamics of individual NPCs over the nucleolus. By leveraging genetic knockout approaches and auxin-induced degradation with sophisticated quantitative and rigorous analyses, the authors conclude that there may be two mechanisms dependent on nuclear basket proteins that impact nucleolar exclusion. They also incorporate some computational simulations to help support their conclusions. Overall, the data are of the highest quality and are rigorously quantified, the manuscript is well written, accessible, and scholarly - the conclusions are thus on solid footing.

      Significance

      I have no concerns about the data or the conclusions in this manuscript. However, the significance is not overly clear as there is no major conceptual advance put forward, nor is there any new function suggested for the NPCs over nucleoli. As NPCs are immobile in metazoans, the significance may also be limited to a specialized audience.

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      Referee #1

      Evidence, reproducibility and clarity

      The authors extended the existing recombination-induced tag exchange (RITE) technology to show that they can image a subset of NPCs, improving signal-to-noise ratios for live cell imaging in yeast, and to track the stability or dynamics of specific nuclear pore proteins across multiple cell divisions. Further, the authors use this technology to show that the nuclear basket proteins Mlp1, Mlp2 and Pml39 are stably associated with "old NPCs" through multiple cell cycles. The authors show that the presence of Mlp1 in these "old NPCs" correlates with exclusion of Mlp1-positive NPCs from the nucleolar territory. A surprising result is that basket-less NPCs can be excluded from the non-nucleolar region, an observation that correlates with the presence of Nup2 on the NPC regardless of maturation state of the NPC. In support of the proposal that retention of NPCs via Mlp1 and Nup2 in non-nucleolar regions, simulation data is presented to suggest that basket-less NPCs diffuse faster in the plane of the nuclear envelope.

      However, there are some points that do need addressing:

      Major Points

      1. Taking into account that the Nup2 result in Figure 4B forms the basis for one half of the proposed model in Figure 6 regarding the exclusion of NPCs from the nucleolar region of the NE, there is a relatively small amount of data in support of this finding and this proposed model. For example, the only data for Nup2 in the manuscript is a column chart in Figure 4B with no supporting fluorescence microscopy examples for any Nup2 deletion. Further, the Nup60 deletion mutant will have zero basket-containing NPCs, whereas the Nup2 deletion will be a mixture of basket-containing and basket-less NPCs. The only support for the localization of basket-containing NPCs in the Nup2 deletion mutant is through a reference "Since Mlp1-positive NPCs remain excluded from the nucleolar territory in nup2Δ cells (Galy et al., 2004), the homogenous distribution observed in this mutant must be caused predominantly by the redistribution of Mlp-negative NPCs into the nucleolar territory."
      2. The authors could consider utilizing this opportunity to discuss their technological innovations in the context of the prior work of Onischenko et al., 2020. This work is referenced for the statement "RITE can be used to distinguish between old and new NPCs" Page 2, Line 43. However, it is not referenced for the statement "We constructed a RITE-cassette that allows the switch from a GFP-labelled protein to a new protein that is not fluorescently labelled (RITE(GFP-to-dark))" despite Onischenko et al., 2020 having already constructed a RITE-cassette for the GFP-to-dark transition. The authors could consider taking this opportunity to instead focus on their innovative approach to apply this technology to decrease the number of fluorescently-tagged NPCs by dilution across multiple cell divisions and to interpret this finding as a measure of the stability of nuclear pore proteins within the broader NPC.
      3. The authors could also consider taking this opportunity to discuss their results in the context of the Saccharomyces cerevisiae nuclear pore complex structures published e.g. in Kim et al., 2018, Akey et al., 2022, Akey et al., 2023 in which the arrangement of proteins in the nuclear basket is presented, and also work from the Kohler lab (Mészáros et al., 2015) on how the basket proteins are anchored to the NPC. There is additional literature that also might help provide some perspective to the findings in the current manuscript, such as the observation that a lesser amount of Mlp2 to Mlp1 observed is consistent with prior work (e.g. Kim et al., 2018) and that intranuclear Mlp1 foci are also formed after Mlp1 overexpression (Strambio-de-Castillia et al., 1999).

      Minor Points

      1. What is the "lag time" of the doRITE switching? Do the authors believe that it is comparable to the approximate 1-hour timeframe following beta-estradiol induction as shown previously in Chen et al. Nucleic Acids Research, Volume 28, Issue 24, 15 December 2000, Page e108, https://doi.org/10.1093/nar/28.24.e108
      2. The authors could consider a brief explanation of radial position (um) for the benefit of the reader, in Figures 1E (right panel) and 2B (right panel), perhaps using a diagram to make it easier to understand the X-axis (um).
      3. In Figure 1G, would the authors consider changing the vertical axis title and the figure legend wording from "mean number of NPCs per cell" to "mean labeled NPC # per cell" to reflect that what is being characterized are the remaining GFP-bearing NPCs over time?
      4. In Figure 2C, the magenta-labeled protein in the micrographs is not described in the figure or the legend.
      5. In Figure S2A, there is an arrow indicating a Nup159 focus, but this is not described in the figure legend, as is done in Figure 2C.
      6. In Figure S3C, the figure legend does not match the figure. Was this supposed to be designed like Figure 3C and is missing part of the figure? Or is the legend a typographical error?
      7. In Figure S4B, the spontaneously recombined RITE (GFP-to-dark) Nup133-V5 appears in the western blot as equally abundant to pre-recombined Nup133-V5-GFP. In the figure legend, this is explained as cells grown in synthetic media without selection to eliminate cells that have lost their resistance marker from the population. In Cheng et al. Nucleic Acids Res. 2000 Dec 15; 28(24): e108, Cre-EBD was not active in the absence of B-estradiol, despite galactose-induced Cre-EBD overexpression. Would the authors be able to comment further on the Cre-Lox RITE system in the manuscript?
      8. In Figure 6, the authors may want to consider inverting the flow of the cartoon model to start from the wild type condition and apply the deletion mutations at each step to "arrive" at the mutant conditions, rather than starting with mutant conditions and "adding back" proteins.

      Significance

      Recent work has drawn attention to the fact that not all NPCs are structurally or functionally the same, even within a single cell. In this light, the work here from Zsok et al. is an important demonstration of the kind of methodologies that can shed light on the stability and functions of different subpopulations of NPCs. Altogether, these data are used to support an interesting and topical model for Nup2 and nuclear-basket driven retention of NPCs in non-nucleolar regions of the nuclear envelope.

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      Reply to the reviewers

      Reviewer #1

      Evidence, reproducibility, and clarity

      Singh et al. analyze the expression and putative contribution of TEs in CD4+ T cells in HIV elite controllers. Through re-analysis of existing datasets, the authors describe broad differences in expression of TEs in ECs through analysis of RNA-seq and ATAC-seq data and come up with convincing examples where differentially-expressed innate immune genes correlate with increased accessibility of proximal TEs. Overall, the authors' conclusions are appropriately measured, though the manuscript text should be re-organized for clarity and a few further analyses are needed to support the main message of the paper.

      Major comments

      The manuscript would benefit from a re-organization of the figures to focus on TEs - in particular, Fig 1B, Fig 2, and Fig 3 reproduce known transcriptional differences between ECs and HCs and serve as quality controls for the authors' computational analysis. Conversely, Supplementary Fig 6 contains very interesting data on KZNF expression and should be included in the main figures.

      Authors: Thank you for the suggestion. We agree that Figure S6 should be featured more prominently in the manuscript. Accordingly, we have now incorporated it into the main text as Figure 6. The TE-KZNF correlation plots, previously Figure 5C, have been relocated to this new figure to provide a cohesive presentation of all KZNF-related data within the same figure.

      We’ve chosen to keep Figures 1B, 2, and 3 in their original places. We contend that they provide a foundational view of transcriptional variances in gene expression between patient groups, encompassing both previously identified and novel DEGs, which we believe warrants their placement in the main text. Furthermore, they serve as robust quality control measures for subsequent TE-centric transcriptional analyses. Given that there is no limitation in the number of figures in Genome Biology articles, we think it’s adequate to retain them as main figures.

      It remains unclear whether differences in TE expression described are specific to ECs or to EC-like CD4+ T cell states. As there are plenty of datasets available that compare the transcriptome of naïve, activated, exhausted, and regulatory CD4+ T cells, the authors should compare the TE expression patterns observed in ECs to activated CD4+ T cells, particularly those with a Th1 and cytotoxic phenotype analogous to those observed in ECs, from healthy donors.

      Authors: We thank the reviewer for this constructive suggestion to further study the foundations of HIV-1 elite control. In our initial study, we demonstrate that PBMCs from elite controllers (ECs) exhibit a heightened proportion of activated CD4+ T cells compared to PBMCs of healthy controls (HCs) and a heightened proportion of macrophages, naïve CD4+ T cells, and NK cells compared to PBMCs of treatment-naïve viremic progressors (VPs) (Figure 2D). Additionally, through clustering analysis of deconvoluted CD4+ T cell samples from elite controllers, we ascertain that the clustering pattern is not predicated on the CD4+ T cell subtype (Figure 3B). To further explore the reviewer’s inquiry, we compared the TE expression profile of ECs with that of unstimulated and stimulated CD4+ T cell subsets from HCs (data source: PMID 31570894), integrated into the revised manuscript as Figure S3B.

      “Unsupervised clustering of these samples shows that the TE expression pattern of ECs is most similar to that of Th2 progenitor cells, which are associated with HIV-1-specific adaptive immune responses (61). Still, we observed that, for the majority of families, TE expression was higher on average in all EC CD4+ T cell subsets than in CD4+ T cell subsets from HCs, regardless of stimulation (Figure S3B). While a subset of TE families exhibited an expression pattern in ECs similar to that of activated CD4+ T cells of HCs (e.g., high expression of L1s and THE1B), multiple TE families appear to be upregulated in an EC-specific way (e.g., LTR12C and LTR7). Together, these findings underscore the unique immune cell composition, transcriptome, and retrotranscriptome of ECs.” [pg.13-14, L226-235]

      While these observations are interesting, pursuing this question further falls beyond the scope of our study, as we note in the Discussion of the revised manuscript. We believe the reviewer’s inquiry pertains to a distinct research question, namely whether the potential for elite control of HIV-1 infection manifests as a detectable phenotype pre-infection within healthy CD4 T cell subsets (i.e., EC-like CD4+ T cell states) or is a unique phenotype that emerges solely after HIV-1 infection.

      “Another outstanding question is whether the gene and TE signatures revealed by our analysis of ECs exist in the general population independent of HIV-1 infection or if they are driven by the initial infection. While this inquiry is beyond the scope of this study, we have presented here evidence of common TE signatures between EC CD4+ T cells and Th2 progenitors from HCs (Figure S3B) and established that ECs possess a unique CD4+ T cell retrotranscriptome with potential implications for natural HIV-1 control. Future studies designed to assess elite control prediction should explore whether these TE profiles can serve as predictive variables for whether an individual displays enhanced viral control.” [pg. 38, L663-671]

      Therefore, while we appreciate the reviewer's suggestion and offer the addition of these preliminary findings, we believe that further investigation would be better suited for future studies specifically designed to address that question. Our manuscript aims to provide insight into the retrotranscriptome dynamics in ECs and their potential implications for natural HIV-1 control.

      In Fig 1, the authors demonstrate differential expression of both innate immune genes and TEs, but the link between the two is unclear. Is there any enrichment in differential expression for TEs located proximal to innate immune genes? This type of analysis should be possible using the authors' own software to map TE expression to specific genomic loci.

      __Authors: __Thank you for this excellent question. To answer this inquiry, we used the paired ATAC-seq and RNA-seq datasets for from ECs and HCs (used in Figures 1 and 4) to produce a new list of TE-gene pairs on which we could perform gene set enrichment analysis, the results of which have been integrated into the revised manuscript as Figure 4A.

      “We used paired ATAC-seq – which measures chromatin accessibility – and RNA-seq datasets for ECs (n=4) and HCs (n=4) to create a list of TE-gene pairs where the TE locus and gene show increased accessibility and expression, respectively, in ECs compared to HCs (Table S7, see Methods for details). These loci and genes were paired based on proximity, with a maximum distance of 10kb between the TE locus and the gene’s transcription start site, to increase the likelihood of a direct cis-regulatory influence of the TE over the nearby gene. Subsequent gene set enrichment analysis revealed that these genes were predominantly involved in cellular activation, cytokine production, and immune response regulation (Figure 4A). The enrichment for differential accessibility of TE loci near genes involved in these pathways suggests that the distinct TE landscape observed in ECs may contribute significantly to a unique immune regulome in these individuals.” [pg. 21, L357-368]

      Thus, we conclude that yes, there is an enrichment for immune-related genes with higher expression in ECs, proximal to differentially accessible TEs. We highlight six of these TE-gene pairs in Figure 4B-C. While we have high confidence in our analyses, future experimental validation is needed to confirm these regulatory relationships.

      Optional: In Fig 3, the authors cluster CD4+ T cells based on transcriptomic profiles. It would be interesting to re-cluster these samples based on TE expression alone, given the differences in TE expression described in Fig 5.

      __Authors: __Thank you for the suggestion. We agree that it would be valuable to assess how the EC clustering is altered when considering TE expression alone, as opposed to combining gene and TE family expression. To address this, we used the same graph-based k-nearest neighbors method to re-cluster the EC CD4+ T cell RNA-seq samples based only on locus-level TE expression, integrated into the revised manuscript as Figure S7.

      “To further explore locus-level expression patterns, we re-clustered the same EC samples (n=128) using only locus-level TE expression. This again resolved four EC clusters (Figure S7A), which interestingly appeared even more distinct than those identified by gene and TE family expression (Figure 3A). The TE locus-based clusters (TL-Cs) aligned well with the gene and TE family clusters (GT-Cs), with an average 70% overlap in samples between each GT-C and its corresponding TL-C (Figure S7B), indicating high consistency (Table S8). The remaining 30% of samples that shifted between clusters did so consistently within individuals, not cohorts, maintaining heterogeneous TL-C compositions similar to the GT-Cs (Figures S7C & S5A). An exception to this heterogeneity was TL-C4, comprising 22 samples from GT-C1 that were almost entirely from the CD4+ T cell subsets of only four participants in the Jiang cohort (Figure S7C, Table S8). No other samples from the Jiang cohort shifted to this cluster from other GT-Cs, suggesting that these patterns reflect individual variation rather than cohort bias. Like the GT-Cs, each TL-C included samples from all five CD4+ T cell subsets and was largely heterogeneous (Figure S7C). Notably, TL-C2 mirrored corresponding GT-C3 in its overrepresentation of EM and TM cells, while TL-C1 uniquely showed an overrepresentation of naïve CD4+ T cells. Beyond sample composition, each TL-C was characterized by a unique pattern of expressed TE loci (Figure S7D). These signatures were heterogeneous across families, with subsets of variable loci from one TE family marking separate clusters (Figure S7E), some of which did not reach the threshold of significance in earlier analyses when analyzed at the family-level, like SVA-D. Many families maintained their cluster-specific signatures, like THE1B (a marker of GT-C2), for which the majority of variable loci were found in corresponding TL-C1. However, some TE families, like the L1s that marked GT-C1, showed more heterogeneous signatures with variable loci marking multiple TL-Cs. These findings underscore the need for future locus-level investigations with high-depth sequencing to fully capture the complexity of TE expression.” [pg. 27-28, L462-488]

      We believe these findings not only validate the distinct clustering patterns observed but also highlight the potential of locus-level TE analysis to reveal additional layers of retrotranscriptomic diversity in EC CD4+ T cells.

      Significance

      The manuscript by Singh et al. describes for the first time the role of TEs in HIV elite controllers, suggesting that TEs may be co-opted for cis-regulatory function. This study builds off prior work demonstrating that HIV-infected CD4+ T cells activate LTR elements that may regulate the expression of interferon-inducible genes, demonstrating that ECs show further upregulation of innate immune genes. While these findings will need to be experimentally validated, this study constitutes a useful resource and adds to the growing body of evidence implicating TEs in cis-regulatory control of immune genes. This study will be of interest to basic scientists interested in genetic mechanisms of HIV control, and if further developed may comprise a useful source of biomarkers to predict viral kinetics in HIV-infected individuals. My expertise is in immunology, TE biology, and viral infection.

      Authors: We greatly appreciate this positive evaluation of our manuscript and recognition of its significance in uncovering novel evidence of TE co-option for immune regulatory function in HIV-1 elite control, as well as the suggestion of promising avenues for future research in this field.

      Reviewer #2

      Evidence, reproducibility and clarity

      The authors have re-analyzed published RNA-Seq data from CD4 T cells isolated from HIV elite controllers and reference cohorts, including HIV negative persons, viremic progressors and ART-treated persons. Their main finding is that in some of their comparisons, EC have higher levels of interferon-stimulated genes (ISG), paired with distinct expression patterns of transposable elements. The authors suggest that expression of transposable elements may induce altered expression of ISG, presumably due to immune recognition of TE. They also suggest that reduced expression of KZNF genes, which encode for transcription factors that can suppress TE, may be responsible for enhanced expression of TE. I have the following comments:

      1. All data included in this manuscript derive from previously published data. A new dataset, specifically designed to focus on a high-resolution analysis of TE expression, would be better suited to address the proposed questions.

      Authors: We agree that a new dataset tailored specifically for high-resolution analysis of TE expression would be optimal for addressing the proposed inquiries, and we emphasize this point in the Discussion of the revised manuscript.

      “We found that distinct sets of innate immunity genes and restriction factors are upregulated in different EC clusters even in the absence of active viremia, suggesting that elevated basal expression of these factors plays a previously underappreciated role in the EC phenotype. Further studies will be necessary to cement this idea and would especially benefit from the integration of single-cell omics to dissect TE regulation and clustering in deconvoluted CD4+ T cells of ECs. We also acknowledge that our study is limited by the small number of EC individuals with available omics data, which likely limited our ability to identify significant relationships between transcriptome clustering and available participant metadata (Figure S5). While the rarity of ECs in the seropositive population makes it challenging to study this phenotype, the transcriptomic heterogeneity revealed by our analyses underscores the need for surveying larger and more diverse EC cohorts.” [pg. 37-38, L651-662]

      Regrettably, we do not have access to elite controller samples (which are exceedingly rare), and as such the addition of a novel dataset was not feasible within the scope of this revision. Nevertheless, we assert that the publicly available sequencing data analyzed here is robust and suitable for locus- and family-level TE analysis. All sequencing runs were paired-end and of high depth, ensuring proper alignment to and high coverage of TEs at a locus-specific resolution. Additionally, we use in-house pipelines curated for TE analysis, to optimize the accuracy and quantity of TE-assigned reads (see Methods and our GitHub Repository for more details).

      Authors: We agree that a new dataset tailored specifically for high-resolution analysis of TE expression would be optimal for addressing the proposed inquiries, and we emphasize this point in the Discussion of the revised manuscript.

      “We found that distinct sets of innate immunity genes and restriction factors are upregulated in different EC clusters even in the absence of active viremia, suggesting that elevated basal expression of these factors plays a previously underappreciated role in the EC phenotype. Further studies will be necessary to cement this idea and would especially benefit from the integration of single-cell omics to dissect TE regulation and clustering in deconvoluted CD4+ T cells of ECs. We also acknowledge that our study is limited by the small number of EC individuals with available omics data, which likely limited our ability to identify significant relationships between transcriptome clustering and available participant metadata (Figure S5). While the rarity of ECs in the seropositive population makes it challenging to study this phenotype, the transcriptomic heterogeneity revealed by our analyses underscores the need for surveying larger and more diverse EC cohorts.” [pg. 37-38, L651-662]

      Regrettably, we do not have access to elite controller samples (which are exceedingly rare), and as such the addition of a novel dataset was not feasible within the scope of this revision. Nevertheless, we assert that the publicly available sequencing data analyzed here is robust and suitable for locus- and family-level TE analysis. All sequencing runs were paired-end and of high depth, ensuring proper alignment to and high coverage of TEs at a locus-specific resolution. Additionally, we use in-house pipelines curated for TE analysis, to optimize the accuracy and quantity of TE-assigned reads (see Methods and our GitHub Repository for more details).

      1. As the authors acknowledge, the described investigations are exploratory, and do not allow to draw firm conclusions. Mechanistic experiments are recommended to address the authors' hypotheses.

      Authors: We agree and have duly acknowledged throughout the Discussion the exploratory nature of our investigations and the need for future mechanistic experiments to validate our model. Below are passages from the revised manuscript which we’ve added to emphasize these points.

      “These findings underscore the need for future locus-level investigations with high-depth sequencing to fully capture the complexity of TE expression.” [pg. 28, L486-488]

      “Each step in the model will require experimental work to be validated. First and foremost, it will be important to confirm that the TEs exhibiting increased transcript levels and accessibility in ECs are indeed boosting the innate immune response and control of HIV-1 in these individuals.” [pg. 34, L583-586]

      “CRISPR-Cas9 editing was used in cell lines to demonstrate that a subset of MER41 elements function as enhancers driving the interferon-inducibility of several innate immune genes. However, the specific MER41 loci we identified here as differentially active in ECs have not been tested experimentally for enhancer activity. Thus, further work is warranted to confirm the regulatory function of these loci under the control of STAT1 or other immune TFs, as well as other TE families identified as targets of immune-related TFs (Figure S8).” [pg. 35, L594-600]

      “Overall, our results reinforce the concept that TEs are important players in the human antiviral response (25,93) and uncover specific candidate elements for boosting cellular defenses against HIV-1 in ECs. We acknowledge that these associations are drawn from correlative patterns and manipulative experiments are needed to infer causality between chromatin changes at these TEs and increased expression of nearby immunity genes.” [pg. 36, L618-623]

      “Further work is needed to validate TE-KZNF regulatory interactions in T cells, probe their connection to epigenetic variation at individual TE loci, and explore their repercussions on gene expression variation in CD4+ T cells, with and without HIV-1 infection.” [pg. 40, L715-718]

      Thus, while we appreciate and agree with the suggestion of experimental validation, we contend that these experiments fall beyond the scope of the present study, which is a computational investigation providing insight into the EC retrotranscriptome and its potential implications for natural HIV-1 control.

      1. An important limitation is that virological data of EC are not considered. For example, I believe it is a lot more likely that the upregulation of ISG in EC relates to ongoing low-level viral replication. The authors could analyze cell-associated HIV RNA and DNA levels and determine how they associate with ISG expression.

      Authors: Thank you for bringing up this important consideration. It's worth noting that the public datasets used in our study reported undetectable viremia in the EC volunteers (PMIDs 30964004, 29269040, 32848246, 27453467). Nonetheless, we sought to address this limitation and explore the potential association between ISG expression and viremia as recommended by the reviewer. These analyses were integrated into the revised manuscript as Figure S6.

      “To exclude the possibility that these gene expression signatures in ECs are associated with viremia, we quantified HIV-1 transcript levels in deconvoluted CD4+ T cell RNA-seq samples from ECs and ART-treated PLWH for comparison. In the original studies, all samples were reported to have undetected viremia by blood tests (9,37-39). Consistent with this, we found that the vast majority of the EC and ART samples taken from PBMCs exhibited very low HIV-1 transcript levels, with TPM values generally below 1. However, in samples originating from the lymph nodes of EC individuals (n = 22) (37), we detected HIV-1 expression in some subsets (Figure S6A&B). In agreement with the corresponding study (37), we found elevated HIV-1 transcript levels in germinal center and non-germinal center T follicular helper cells (GC Tfh & nGC Tfh, not included in our clustering analyses) -- and to a lesser extent in T effector memory (EM) cells (Figure S6A, average TPM This added analysis confirms that the increased expression of ISGs in ECs is not correlated with virological transcription and is therefore likely not to be driven by viremia.

      1. KZNF genes seem downregulated in EC. Can the authors propose a reason/mechanism for that?

      Authors: There is the possibility that KZNF regulatory loops are the cause of their transcriptional downregulation, which has been documented in embryogenesis (PMID 31006620) and cancer (PMID 33087347). We’ve incorporated this hypothesis into the Discussion as an additional consideration for the reader.

      “These observations suggest that interindividual variation in KZNF expression in CD4+ T cells could explain why certain TEs are variably expressed and accessible across ECs. But what are the mechanisms underlying variation in ZNF expression? It is possible that TE-KZNF regulatory loops are involved, in which a copy of the TE family targeted by a KZNF is inserted near and regulates the KZNF gene, thereby introducing a negative feedback loop. This phenomenon has been documented in prior studies of KZNF activity in embryogenesis (51) and cancer (115).” [pg. 39-40, L705-711]

      While we believe this is a viable hypothesis, it requires further experimentation to confirm the existence of this phenomenon and its impacts in the context of immune cells.

      Significance

      Overall, I think this is an interesting manuscript that proposes distinct and potentially important mechanisms that may contribute to immune control of HIV. My suggestions to improve the manuscript are complex and cannot be easily addressed through experimental work. I believe a possible option would be to publish the present manuscript without my proposed modifications but highlight the weaknesses of the current paper more clearly; mechanistic studies could then be deferred to a future study.

      Authors: We appreciate the reviewer's positive assessment of our manuscript and their recognition of its significance in elucidating novel TE-derived mechanisms that may contribute to natural HIV-1 control. We agree that mechanistic studies are required to test our predictions. As the reviewer suggests, these would be complex experiments that we feel fall beyond the scope of this study. With the additions detailed above in response to the reviewer’s point #2, we believe that we have clearly highlighted the limitations of our work and emphasized the need for future experimentation to validate our findings.

      Reviewer #3

      Evidence, reproducibility, and clarity

      Summary: This manuscript presents an analysis of published gene expression (RNA-seq and ATAC-seq) data from a couple of cohorts of HIV-infected elite controllers (EC), as compared to uninfected controls, (HC), virological progressors (VP). The authors report that HIV elite controllers may exhibit 4 distinct patterns of TE (and gene) expression and suggest that TE expression may drive some form of antiviral gene expression. Further, they show that heterogeneous TE expression may be determined by differential KZNF gene activity among the different clusters of elite controllers. These results are very interesting, even though the conclusions are very preliminary. It presents intriguing correlations between expression of certain TE groups of LINES and HERVs, and the clustering into 4 gene expression groups in EC and is a novel finding. That said, correlation is not causation, and the authors need to be more cautious in presenting their highly preliminary model in Figure 6.

      Authors: We are grateful for the reviewer's insightful assessment of our manuscript, acknowledging the novelty and interest of our findings regarding TE expression patterns in HIV-1 elite controllers. We also appreciate their constructive feedback regarding the cautious interpretation of preliminary conclusions. In the revised manuscript, we have underscored the exploratory nature of our investigations and the need for future mechanistic experiments to validate our model.

      “These findings underscore the need for future locus-level investigations with high-depth sequencing to fully capture the complexity of TE expression.” [pg. 28, L486-488]

      “Each step in the model will require experimental work to be validated. First and foremost, it will be important to confirm that the TEs exhibiting increased transcript levels and accessibility in ECs are indeed boosting the innate immune response and control of HIV-1 in these individuals.” [pg. 34, L583-586]

      “CRISPR-Cas9 editing was used in cell lines to demonstrate that a subset of MER41 elements function as enhancers driving the interferon-inducibility of several innate immune genes. However, the specific MER41 loci we identified here as differentially active in ECs have not been tested experimentally for enhancer activity. Thus, further work is warranted to confirm the regulatory function of these loci under the control of STAT1 or other immune TFs, as well as other TE families identified as targets of immune-related TFs (Figure S8).” [pg. 35, L594-600]

      “Overall, our results reinforce the concept that TEs are important players in the human antiviral response (25,93) and uncover specific candidate elements for boosting cellular defenses against HIV-1 in ECs. We acknowledge that these associations are drawn from correlative patterns and manipulative experiments are needed to infer causality between chromatin changes at these TEs and increased expression of nearby immunity genes.” [pg. 36, L618-623]

      “Further work is needed to validate TE-KZNF regulatory interactions in T cells, probe their connection to epigenetic variation at individual TE loci, and explore their repercussions on gene expression variation in CD4+ T cells, with and without HIV-1 infection.” [pg. 40, L715-718]

      We hope these passages provide sufficient caution and clarity in the presentation of our scientific inquiry.

      Major comments:

      Overall, although preliminary, as the authors note, the results are interesting and worthy of follow-up. At this point, however, a number of issues arise that need further clarification and analysis before I would consider this study complete.

      First, the analyses shown in Figures 3-5 based on data from studies on EC of CD4 cells are apparently motivated by the differential TE expression in total PBMCs shown in Fig 1 and 2. Yet, the TE groups (please don't use taxonomic terms like "subfamily") identified in Fig 2 and Fig 4 are completely different, with no overlap. This discrepancy underscores the possibility that the differential expression observed is, at least in part, due to the differences among the groups or clusters in cell type composition, as seen in Fig 2D and 3B which, themselves, could be a consequence of HIV infection and elite control (which has been shown to involve ongoing, albeit low-level, virus replication). This issue must be addressed.

      Authors: Thank you for the suggestion. First, we’d like to clarify that the data used in Figures 1 and 2 were not both derived from PBMCs. Figures 1 and S1 examine the differential expression of TEs in EC CD4+ T cells compared to HCs and ART-treated PLWH, respectively. Figure 2 examines differential expression of TEs in EC PBMCs compared to treatment-naïve VPs. Second, regarding Figure 4B-C, the TE loci that we chose to highlight were not based on our results from the PBMC analysis in Figure 2, which is why there is no overlap in the TE families presented. Instead, we selected those TE-gene pairs based on 1) known function of the genes in immunity and/or HIV-1 restriction, 2) known contribution of the TE families to immunity, and 3) differential accessibility and expression of the TEs and genes respectively in ECs compared to HCs. Thus, Figure 4B-C represents select examples that we deemed particularly relevant to the EC phenotype. We have revised the manuscript to better explain the process of TE-gene pair identification and the rationale behind our selection for Figure 4B-C.

      “We used paired ATAC-seq – which measures chromatin accessibility – and RNA-seq datasets from the CD4+ T cells of ECs (n=4) and HCs (n=4) (39) to create a list of TE-gene pairs where the TE locus and gene show increased accessibility and expression, respectively, in ECs compared to HCs (Table S7, see Methods for details). These loci and genes were paired based on proximity, with a maximum distance of 10kb between the TE locus and the gene’s transcription start site, to increase the likelihood of a direct cis-regulatory influence of the TE over the nearby gene.” [pg. 21, L357-363)

      “In Figure 4B & 4C, we have highlighted six of the TE-gene pairs from Table S7 based on the gene’s function in HIV-1 restriction and the TE family’s known contribution to immune gene regulation.” [pg. 21, L369-371]

      Regarding cell type composition, we acknowledge that the differences observed in the proportion of immune cell subtypes may contribute to the differential expression between ECs, VPs, and HCs (Figures 2D and S3A). However, we provide evidence that cell type composition cannot be the sole driver for the clustering of deconvoluted CD4+ T cell RNA-seq samples (Figure 3B and S5D). Cell subtype alone could not explain the observed clustering of EC samples by gene and TE family expression. Clusters 1 and 2, for example, had nearly identical subtype compositions, but were clearly separated on the UMAP (Figures 3A, 3B, and S5D). We remark on this in the Results of the revised manuscript.

      “[W]e visualized the samples by cellular subtype, as identified in the original studies, to assess whether the clustering could be explained by CD4+ T cell subtype composition (Figure S5D). Clusters 1 and 2 were essentially indistinguishable in cell type composition, whereas Clusters 3 and 4 showed an overrepresentation of TM/EM and naïve/CM cell types, respectively (Figure 3B). Thus, cell subtype composition could only partially explain the clustering.” [pg. 16, L271-276]

      The EC CD4+ T cell clusters also had unique gene ontology, gene & TE expression, and TE accessibility profiles (Figures 3C, 3D, 5). Moreover, while we do not have parallel RNA- and ATAC-seq data from similarly deconvoluted CD4+ T cells of ECs like those used in the clustering analysis (PMIDs 32848246 & 27453467), the original article from which we sourced the parallel RNA- and ATAC-seq data used in Figures 1 and 4 reported that these samples are predominantly effector memory CD4+ T cells (PMID 30964004). If new deconvoluted, multi-omic datasets from ECs become available, we would be interested in further exploring the contribution of cell type composition. However, the current data indicate that it is not a major contributor to the differential TE expression identified in our analyses.

      Regarding the impact of ongoing HIV-1 replication upon the unique expression patterns in the EC participants, it's worth noting that the public datasets used in our study reported undetectable viremia in the EC volunteers (PMIDs 30964004, 29269040, 32848246, 27453467). Nonetheless, we sought to address this by quantifying HIV-1 transcription and exploring its potential association with interferon-stimulated gene (ISG) expression, a group of genes that we know would be reactive to active viremia. These analyses were integrated into the revised manuscript as Figure S6.

      “To exclude the possibility that these gene expression signatures in ECs are associated with viremia, we quantified HIV-1 transcript levels in deconvoluted CD4+ T cell RNA-seq samples from ECs and ART-treated PLWH for comparison. In the original studies, all samples were reported to have undetected viremia by blood tests (9,37-39). Consistent with this, we found that the vast majority of the EC and ART samples taken from PBMCs exhibited very low HIV-1 transcript levels, with TPM values generally below 1. However, in samples originating from the lymph nodes of EC individuals (n = 22) (37), we detected HIV-1 expression in some subsets (Figure S6A&B). In agreement with the corresponding study (37), we found elevated HIV-1 transcript levels in germinal center and non-germinal center T follicular helper cells (GC Tfh & nGC Tfh, not included in our clustering analyses) -- and to a lesser extent in T effector memory (EM) cells (Figure S6A, average TPM Based on these results, we have concluded that the differential expression of genes and TEs in the EC clusters are not a consequence of low-level viral transcription in ECs.

      Finally, a remark on TE nomenclature: The reviewer suggests that we use the term “TE groups” as opposed to taxonomic terms such as TE subfamily or TE family. We respectfully disagree. This nomenclature of TEs has been well defined (PMIDs 26612867, 26612867, 17984973) and is widely used in TE literature. Throughout the manuscript, we have conformed to the nomenclature used to annotate the human genome. One can debate the way TE families and subfamilies have been classified in Dfam (the database through which repetitive elements in the human genome have been annotated), but it is outside the scope of this study to revisit that nomenclature.

      Similarly, of the 12 DE TE groups in EC in Fig 5A, only 3 overlap with the 16 in EC Fig S1.

      Authors: This is correct, but we don’t believe it’s concerning. In Figure 5A, we are comparing the expression of TE families between separate EC clusters. In Figure S1, we are comparing the expression of TE families in ECs compared to ART-treated PLWH. These are fundamentally different comparisons and thus the differences in the identified DE-TEs between the two figures reflect the distinct biological contexts being investigated in each analysis.

      Second, the introduction points out the strongly supported association between elite control and immunogenetic determinants, most notably specific HLA-B types, but also innate immunity factors. This cries out for inclusion of these factors in the analyses of this manuscript, in the format of Figure S4, for example, but none is to be found. The relevant genotypes are likely available in the metadata in the references cited, but, if not, could be inferred from the RNA-seq data.

      Authors: Thank you for the recommendation. While our project’s primary focus is on the transcriptomic and epigenomic signatures, we agree that studying the HLA-B genotypes of all EC participants could provide valuable context for understanding the clustering of elite controllers. To explore this, we inferred the HLA-B alleles in each EC participant whose RNA-seq data was included in the clustering analysis, utilizing the arcasHLA tool (PMID: 31173059) on the total CD4+ T cell samples. We then validated these inferred HLA-B alleles against the available metadata from one of the source studies (PMID 27453467) and found that they matched for all participants. This strengthened our confidence in the accuracy of the HLA-B genotype inferences for the other samples where comprehensive HLA-B data was not provided.

      In order to assess how these protective HLA-B alleles segregated between the four EC clusters derived from gene and TE family expression, we chose to visualize three of the most common alleles associated with HIV-1 elite control: HLA-B*27:03, *57:01, and *57:03 (PMIDs 30964004, 25119688, 21051598) (Figure R1, available in the Response to Reviewers PDF).

      Our analysis revealed that these major protective alleles were not significantly overrepresented in any particular cluster. Consequently, we believe that HLA-B genotype does not have a major impact on the clustering observed in Figure 3.

      It would also be very useful to present the KZNF data in Figure 5 the same way, since, looking at Fig 5C, the correlation of high and low KZNF expression, while clearly correlated with a that of few groups of elements, with clustering into specific groups does not appear to be well supported.

      Authors: Thank you for the insightful suggestion. While the KZNF genes are included in the gene set used for the clustering analysis in Figure 3, we agree that clustering based solely on KZNF expression and displaying it as we have in Figures 3A and S5 could provide valuable insights. However, when we attempted to cluster the EC RNA-seq samples using only KZNF expression data, we were limited by the relatively low number of KZNF genes that showed sufficient variability across samples (n = 120). For robust statistical power, we require at least 200 features to reliably cluster the 128 EC CD4+ T cell samples. We believe this limitation does not diminish the relevance of KZNFs in the observed clustering patterns but rather highlights the nuanced role each KZNF plays in the regulation of the transcriptome. Each individual KZNF is responsible for the regulation of hundreds to thousands of TE loci (PMID 37730438). Thus, while a clustering approach based solely on KZNF expression may not be feasible, the integral role of KZNFs in modulating the transcriptome through TE regulation remains evident and supports their inclusion in Figure 6 of the revised manuscript.

      In general, other than the cell type composition differences, there is no presentation of evidence for any biologically important feature associated with the clusters found.

      Authors: We agree that the root cause of the transcriptomic differences between the EC clusters is hard to pin down but we do identify several distinctive features of the clusters that we believe are biologically significant. First, having extracted the lists of genes whose differential expression defined the four EC clusters, gene set enrichment analysis revealed that the clusters were functionally distinct, each characterized by a unique list of top GO terms (Figure 3C). Second, we provide evidence that KZNFs expressed in CD4+ T cells significantly bind to the candidate TE families whose expression defines each of these clusters (Figure 6D) and have significantly decreased expression in ECs compared to VPs (Figure 6C). This is corroborated by pairwise correlation analysis that revealed cluster-specific anticorrelation patterns between these KZNFs and their target TEs (Figure 6A). We present this data in support of our hypothesized KZNF-based mechanism for TE co-option in viral immunity. We do not yet have data indicative of the mechanism by which KZNF expression is in turn regulated. However, we speculate that negative feedback loops may be contributing to changes in KZNF expression.

      “These observations suggest that interindividual variation in KZNF expression in CD4+ T cells could explain why certain TEs are variably expressed and accessible across ECs. But what are the mechanisms underlying variation in ZNF expression? It is possible that TE-KZNF regulatory loops are involved, in which a copy of the TE family targeted by a KZNF is inserted near and regulates the KZNF gene, thereby introducing a negative feedback loop. This phenomenon has been documented in prior studies of KZNF activity in embryogenesis (51) and cancer (115).” [pg. 39-40, L705-711]

      Overall, our study presents preliminary evidence that the four EC clusters derived from gene & TE family expression may be distinguished by complex interplay of activators (Figure S8) and repressors (Figure 6) altering the activity of infection-responsive TE families to co-opt specific elements for immune regulatory function. While not yet validated in an experimental setting, we believe these results are of biological significance.

      Third, the figures present values that have been very heavily analyzed, and it is difficult to impossible to infer what the underlying data look like. For example, with the exception of a few selected examples in Figs 4 and 5, individual provirus data are lacking. Nor can we tell how consistent the distribution of expression values within a TE group is, whether the TEs included solo LTRs (which constitute the majority of all ERVs), the possible contribution of other TFs to expression (with the exception of a brief mention of STAT1).

      Authors: We respectfully disagree that the values presented in our figures are heavily analyzed. As this manuscript represents the first investigation of TEs’ role in HIV-1 elite control, we believe the most reasonable initial approach was to compile and visualize the data at the family level, rather than at the level of individual loci, which is harder to interpret due to mapping issues, commonly low transcription, and often idiosyncratic behavior of individual loci. Nonetheless, we did not limit our analysis to full-length HERVs (proviruses) and thus retain all solo LTR data in our analyses. This was added to the Methods of the revised manuscript.

      “To facilitate comprehensive expression quantification, we curated a reference transcriptome by combining gene, TE, and HIV-1 genomic sequences. This was achieved by integrating the locus-level TE classification from RepeatMasker, the hg19 GenCode gene annotation,

      and the HXB2 reference HIV-1 annotation. For the TEs, we removed simple repeats, SINE elements, and DNA transposons, retaining LINE and HERV loci, including all solo LTRs. We also removed any loci within gene exons/UTRs. The remaining sequences were appended in fasta format, and all sequences were annotated with their respective gene, TE locus, or HIV subunit and modeled in GTF format.” [pg. 55, L869-878]

      For the sake of transparency, all relevant details on sequencing data analysis and the corresponding scripts are available in the Methods and our GitHub Repository.

      Additionally, while most of our figures make comparisons at the family level, we do visualize multiple TE loci (Figure 4C) and provide a list of putative locus-level TE-gene pairs from which those shown in Figure 4C were selected (Table S7). In our revisions, we also re-clustered the 128 EC CD4+ T cell RNA-seq samples based only on locus-level TE expression, using the same graph-based k-nearest neighbors method as in Figure 3. The results of this new analysis have been integrated into the revised manuscript as Figure S7.

      “To further explore locus-level expression patterns, we re-clustered the same EC samples (n=128) using only locus-level TE expression. This again resolved four EC clusters (Figure S7A), which interestingly appeared even more distinct than those identified by gene and TE family expression (Figure 3A). The TE locus-based clusters (TL-Cs) aligned well with the gene and TE family clusters (GT-Cs), with an average 70% overlap in samples between each GT-C and its corresponding TL-C (Figure S7B), indicating high consistency (Table S8). The remaining 30% of samples that shifted between clusters did so consistently within individuals, not cohorts, maintaining heterogeneous TL-C compositions similar to the GT-Cs (Figures S7C & S5A). An exception to this heterogeneity was TL-C4, comprising 22 samples from GT-C1 that were almost entirely from the CD4+ T cell subsets of only four participants in the Jiang cohort (Figure S7C, Table S8). No other samples from the Jiang cohort shifted to this cluster from other GT-Cs, suggesting that these patterns reflect individual variation rather than cohort bias. Like the GT-Cs, each TL-C included samples from all five CD4+ T cell subsets and was largely heterogeneous (Figure S7C). Notably, TL-C2 mirrored corresponding GT-C3 in its overrepresentation of EM and TM cells, while TL-C1 uniquely showed an overrepresentation of naïve CD4+ T cells. Beyond sample composition, each TL-C was characterized by a unique pattern of expressed TE loci (Figure S7D). These signatures were heterogeneous across families, with subsets of variable loci from one TE family marking separate clusters (Figure S7E), some of which did not reach the threshold of significance in earlier analyses when analyzed at the family-level, like SVA-D. Many families maintained their cluster-specific signatures, like THE1B (a marker of GT-C2), for which the majority of variable loci were found in corresponding TL-C1. However, some TE families, like the L1s that marked GT-C1, showed more heterogeneous signatures with variable loci marking multiple TL-Cs. These findings underscore the need for future locus-level investigations with high-depth sequencing to fully capture the complexity of TE expression.” [pg. 27-28, L462-488]

      With this addition, we include significantly more data analyzed at the locus level, which we believe not only validate the distinct clustering observed in Figure 3, but also underscore the potential for locus resolution analysis to reveal additional layers of retrotranscriptomic diversity in EC CD4+ T cells.

      Finally, we agree with the reviewer that TFs other than STAT1 may contribute to the observed changes in TE expression. To investigate this, we analyzed several TFs expressed in CD4+ T cells and, for TFs enriched over TEs of interest, subsequently examined the correlation between TF and target TE expression in the deconvoluted EC CD4+ T cell samples used for the clustering. The results of this analysis have been integrated into the revised manuscript at Figure S8.

      “In addition to KZNF repressors, transcriptional activators may also drive the differential expression of specific TE families across ECs (83). To investigate this, we focused on transcription factors (TFs) expressed in CD4+ T cells and mined ChIP-seq data from the ENCODE Consortium (84) to identify TFs with binding enrichment to TE families of interest, selected for their elevated, cluster-specific expression in ECs (highlighted in Figures 4, 5, and S4). We then examined the correlation between TF and target TE expression in the deconvoluted CD4+ T cell samples from ECs used for our clustering analysis (Figure 3) (9,37). We observed several significant positive correlations between TF and TE expression across ECs (Figure S8). Thus, differential expression of immune-related TFs may also contribute to the variation in TE expression and cis-regulatory activity across ECs, in tandem with the repressive activities of KZNFs.” [pg. 30, L517-527]

      This evidence supports the reviewer’s suggestion that other TFs may be contributing to the unique EC retrotranscriptome we profile in this study. These added analyses, mimicking those conducted for KZNFs in Figure 6B & 6D, demonstrate that transcriptional activators may indeed play a crucial role in shaping the TE landscape in ECs.

      Other issues

      Figure 1:

      A) Log2 fold change of what? TPM values? Needs to be specified.

      Authors: Thank you for pointing out this ambiguity. The log2-transformed fold change values plotted in Figure 1A refer to DESeq2-normalized expression. They were extracted from the results of the DESeq2 pipeline, which we applied to the raw count expression matrix (see our Methods for more details). Following your suggestion, we have clarified this point in the figure legend in the revised manuscript.

      “Total detected genes and TE loci are plotted by log2-transformed fold change of DESeq2-normalized counts (EC vs. HC).” [pg. 10, L163-164]

      We have similarly made these changes to any figure legend which was ambiguous in its description of the expression data.

      Why Bonferroni correction? Usually BH q values or other less stringent adjustments are used nowadays.

      Authors: In our analysis, we opted for the Bonferroni correction due to its well-established reliability and stringent control of the family-wise error rate when conducting multiple tests. Given the exploratory nature of our investigation and the desire to minimize the risk of false positive findings, we chose to employ this traditional correction method within our analytical pipelines.

      B,C): Z-score of what? Scaled, normalized counts? Scaled TPM values?

      Authors: Thank you again for highlighting this point of uncertainty. We now clarify this in the figure legend in the revised manuscript.

      “Heatmap displaying the expression of the top differentially expressed genes in CD4+ T cells of ECs (n=4; red bar) vs. HCs (n=5; blue bar). Relative expression levels are representative of row-wise scaled, log2-transformed expression in transcripts per million (TPM). Heatmap coloration is based on the z-score distribution from low (gold) to high (purple) expression.” [pg. 11, L167-171]

      Figure 2:

      B) The blue font color is very difficult to see.

      Authors: We have changed the blue font color to make it more easily distinguishable from the black.

      C) This heatmap should demarcate or separate genes versus TE clades. If that's not possible, then the two should be shown separately.

      Authors: We appreciate your suggestion regarding the heatmap presentation. While we understand the rationale for demarcating genes versus TE clades, we have chosen to retain the original figure layout. In this analysis, TEs were analyzed simultaneously with genes. The order in which they are shown was obtained by default clustering of the expression matrix using the hclust function. We chose to present them together and in this order to provide a comprehensive visualization of the differential expression patterns between the two groups and highlight the homogenous nature of gene and TE expression across VPs.

      L191: How many groups (NOT families) and how many total elements were examined?

      Authors: We begin with the RepeatMasker annotation of the hg19 assembly and filter out the SINE elements, DNA transposons, simple repeats, and all loci within gene exons/UTRs. These details are provided in the Methods of the revised manuscript, as was quoted above. In total, our analyses examine 1,104,828 loci from 603 TE groups (which we refer to as families). We apologize if this figure is not accurate to a separate classification of TEs into groups, rather than families. Any such method of grouping TEs is unfamiliar to us and outside of the Dfam annotation.

      L198: 2B, not C

      Authors: Thank you for catching this. The figures labelled were swapped in error and have been changed to reflect in Figure 2 to match the in-text references.

      L205: Did the expressed proviruses have STAT1 sites?

      Authors: Thank you for your question. The identification of LTR13’s increased expression in ECs compared to VPs was the result of a family level analysis which considered expression additively across the LTR13 loci in our annotation. To answer your question, we analyzed STAT1 ChIP-seq data from the ENCODE Consortium to characterize which LTR13 loci were bound by STAT1 (corroborated by motif prediction calls). We then integrated the EC RNA-seq data and found that the expressed LTR13 proviruses significantly overrepresented those with bound STAT1 sites (Figure R2, available in the Response to Reviewers PDF).

      These data suggest that STAT1 binding may play a critical role in the transcriptional regulation of LTR13 in ECs, contributing to their differential expression profile. Further exploration into the contribution of activating, immune-related TFs is explored in Figure S8 in the revised manuscript.

      L333: 10 kb is very close. Why was it chosen?

      Authors: We chose 10 kb as our cutoff for selection because it allowed for very high confidence in the TE loci’s cis-regulatory capacity over the nearby genes. For transparency, we have made this clearer in the Results text of the revised manuscript.

      “These loci and genes were paired based on proximity, with a maximum distance of 10kb between the TE locus and the gene’s transcription start site, to increase the likelihood of a direct cis-regulatory influence of the TE over the nearby gene.” [pg. 21, L360-363]

      However, if desired, a less stringent cutoff could also be used with relative confidence (e.g., 50 kb).

      L351-352: Again, correlation is not causation. How do the authors know it's not the other way around?

      Authors: The candidates that we chose to display in Figure 4 (the figure to which these lines refers) are from MER41, ERV3-16, and LTR12C. Our lab and others have shown that these specific loci or other loci in these TE families are capable of regulating neighboring genes’ expression, with specific evidence in the context of immunity (PMID Smitha, Ed, APOBEC, etc.). Based on this knowledge, we believe that it’s most likely that TE-derived regulatory sequences are the cause of the increased restriction factor expression, rather than TE accessibility being a consequence of the transcriptional activation of the neighboring genes. However, we recognize that these results are correlative, as the reviewer notes, and we emphasize this in the revised manuscript. Most notably:

      “We acknowledge that these associations are drawn from correlative patterns and manipulative experiments are needed to infer causality between chromatin changes at these TEs and increased expression of nearby immunity genes.” [pg. 36, L620-623]

      Figure 4

      B) Need to show a scale of the genome region, the orientation of both the gene and the TE, whether it is a solo LTR

      Authors: Thank you for the suggestion. Genomic scale and orientation have been added to Figure 4C. All loci visualized were solo LTRs, save for HCP5, which is a lncRNA derived from a full-length ERV3 element.

      Figure 5

      A) Would benefit from also showing HCs

      Authors: Thank you for the recommendation. The RNA-seq datasets used in this analysis do not include HC samples. Additionally, this analysis is meant to highlight differences in TE expression between the four EC clusters. Thus, we have chosen to keep Figure 5A as it appears in the original manuscript.

      C) Would be helped by showing adjusted p-values, and also should show examples of non-correlating relationships between these KZNF genes and other TEs.

      Authors: Thank you for the suggestion. All correlation analyses had adjusted p-values below 0.01, derived from corr.test in R. We’ve added this to the figure legends of Figure 6B [pg. 32, L539] and S8B [pg. 53, L835]. However, we have chosen not to integrate non-correlating examples into the revised manuscript for the sake of space.

      Figure 6

      Title: should start with "proposed model for.." or some such.

      Authors: Thank you for the suggestion. The title has been changed to “Proposed model for the interplay of KZNFs and TEs regulating proximal antiviral gene expression in elite controllers of HIV-1” in the revised manuscript [pg. 34, L580-581].

      L 537: Again, how do the alleles segregate in the clusters?

      Authors: This question has been addressed in response to an earlier comment from Reviewer #3.

      Generally, in the correlation analyses, I'd like to see adjusted p-values and examples of non-correlated results.

      Authors: Thank you for the suggestion. As mentioned above, all correlation analyses have been annotated with the adjusted p-value threshold. Additionally, below we’ve included examples of non-correlated results from two analyses. First, we show a TE-gene pair whose increased TE accessibility in HCs compared to ECs does not correlate with increased expression of the proximal gene (Figure R3, available in the Response to Reviewers PDF). Notably, this gene does not play a role in HIV-1 infection response. Here, we show that genes with proximal (Second, we show the pairwise correlation and linear regression results of L1PA6 and ZNF2 (Figure R4, available in the Response to Reviewers PDF). ZNF2 is one of the KZNFs highlighted in Figure 6 for its low expression in ECs, anticorrelated to its repressive target LTR12C. On the other hand, L1PA6 is active in ECs, with variably high expression across samples. ZNF2 ChIP-exo revealed that ZNF2 has no capacity to bind to L1PA6 loci (adj. p-value = 1; PMID 37730438). Thus, even though both genes are variable across samples, we observe no significant (anti)correlation between the two variables (rho = 0.051 & p-value = 0.866).

      While we have not integrated these results into the revised manuscript for the sake of space, we hope that the provided examples satisfactorily demonstrate the presence of non-correlated results in our analyses, further reinforcing the specificity and robustness of our significant findings.

      Significance:

      This study presents an in-depth analysis of the reverse transcriptome in Elite controllers. It will be of interest to both HIV researchers and those interested in the regulation of the human retrotranscriptome and its consequences.

      Provides an avenue for future explanation into elite controllers and TE involvement in the phenotype.

      Does a good job of placing the work in the context of existing lit, synthesizing other papers regarding TEs and immune control.

      Potential immune regulatory involvement of specific HERV clades.

      Authors: We’d like to thank the reviewer for their encouraging feedback. We’re pleased that they found our analysis of the EC retrotranscriptome to be of broad interest and appreciate their recognition of our efforts to synthesize existing literature, contextualizing our findings within the broader field. We agree that our study opens new avenues for exploring the role of TEs, particularly specific HERV clades, in not only the EC phenotype but immune regulation as a whole.

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      Referee #3

      Evidence, reproducibility and clarity

      Summary:

      This manuscript presents an analysis of published gene expression (RNA-seq and ATAC-seq) data from a couple of cohorts of HIV-infected elite controllers (EC), as compared to uninfected controls, (HC), virological progressors (VP). The authors report that HIV elite controllers may exhibit 4 distinct patterns of TE (and gene) expression and suggest that TE expression may drive some form of antiviral gene expression. Further, they show that heterogeneous TE expression may be determined by differential KZHF gene activity among the different clusters of elite controllers. These results are very interesting, even though the conclusions are very preliminary. It presents intriguing correlations between expression of certain TE groups of LINES and HERVs, and the clustering into 4 gene expression groups in EC and is a novel finding. That said, correlation is not causation, and the authors need to be more cautious in presenting their highly preliminary model in Figure 6.

      Major comments:

      Overall, although preliminary, as the authors note, the results are interesting and worthy of follow-up. At this point, however, a number of issues arise that need further clarification and analysis before I would consider this study complete. First, the analyses shown in Figures 3-5 based on data from studies on EC of CD4 cells are apparently motivated by the differential TE expression in total PBMCs shown in Fig 1 and 2. Yet, the TE groups (please don't use taxonomic terms like "subfamily") identified in Fig 2 and Fig 4 are completely different, with no overlap. This discrepancy underscores the possibility that the differential expression observed is, at lest in part, due to the differences among the groups or clusters in cell type composition, as seen in Fig 2D and 3B which, themselves, could be a consequence of HIV infection and elite control (which has been shown to involve ongoing, albeit low-level, virus replication). This issue must be addressed. Similarly, of the 12 DE TE groups in EC in Fig 5A, only 3 overlap with the 16 in EC Fig S1.<br /> Second, The introduction points out the strongly supported, association between elite control and immunogenetic determinants, most notably specific HLA-B types, but also innate immunity factors. This cries out for inclusion of these factors in the analyses of this manuscript, in the format of Figure S4, for example, but none is to be found. The relevant genotypes are likely available in the metadata in the references cited, but, if not, could be inferred from the RNA-seq data. It would also be very useful to present the KZNF data in Figure 5 the same way, since, looking at Fig 5C, the correlation of high and low KZNF expression, while clearly correlated with a that of few groups of elements, with clustering into specific groups does not appear to be well supported. I n general, other than the cell type composition differences, there is no presentation of evidence for any biologically important feature associated with the clusters found.<br /> Third, the figures present values that have been very heavily analyzed, and it is difficult to impossible to infer what the underlying data look like. For example, with the exception of a few selected examples in Figs 4 and 5, individual provirus data are lacking. Nor can we tell how consistent the distribution of expression values within a TE group is, whether the TEs included solo LTRs (which constitute the majority of all ERVs), the possible contribution of other TFs to expression (with the exception of a brief mention of STAT1).

      Other issues

      Figure 1: A) Log2 fold change of what? TPM values? Needs to be specified.

      Why Bonferroni correction? Usually BH q values or other less stringent adjustments are used nowadays. B,C): Z-score of what? Scaled, normalized counts? Scaled TPM values?

      Figure 2: B) The blue font color is very difficult to see C) This heatmap should demarcate or separate genes versus TE clades. If that's not possible, then the two should be shown separately.

      L191: How many groups (NOT Fam1lies) and how many total elements were examined?

      L198: 2B, not C

      L205: Did the expressed proviruses have STAT1 sites?

      L333: 10 kb is very close. Why was it chosen?

      L351-352: Again., correlation is not causation. How do the authors know it's not the other way around?

      Figure 4 Title: For "induction" Substitute "correlation"

      Panel B: Need to show a sclae of the genome region, the orientation of both the gene and the TE, whether it is a solo LTR 5 Panel A: Would benefit from also showing HCs C: Would be helped by showing adjusted p-values, and also should show examples of non-correlating relationships between these KZNF genes and other TEs. 6 Title: should start with "proposed model for.." or some such. L 537: Again, how do the alleles segregate in the clusters?

      General

      In the correlation analyses, I'd like to see adjusted p-values and examples of non-correlated results.

      Significance

      This tudy presents an in depth analysis of the reverse transcriptome in Elite controllers. It will be of interest to both HIV researchers and thos interested in the regulation of the human retrotranscriptome and its consequences

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

      Provides an avenue for future explanation into elite controllers and TE involvement in the phenotype. - Place the work in the context of the existing literature (provide references, where appropriate).

      Does a good job of this, synthesizing other papers regarding TEs and immune control. - State what audience might be interested in and influenced by the reported findings.

      Potential immune regulatory involvement of specific HERV clades. - 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.

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      Referee #2

      Evidence, reproducibility and clarity

      The authors have re-analyzed published RNA-Seq data from CD4 T cells isolated from HIV elite controllers and reference cohorts, including HIV negative persons, viremic progressors and ART-treated persons. Their main finding is that in some of their comparisons, EC have higher levels of interferon-stimulated genes (ISG), paired with distinct expression patterns of transposable elements. The authors suggest that expression of transposable elements may induce altered expression of ISG, presumably due to immune recognition of TE. They also suggest that reduced expression of KZNF genes, which encode for transcription factors that can suppress TE, may be responsible for enhanced expression of TE. I have the following comments:

      1. All data included in this manuscript derive from previously published data. A new dataset, specifically designed to focus on a high-resolution analysis of TE expression, would be better suited to address the proposed questions.
      2. As the authors acknowledge, the described investigations are exploratory, and do not allow to draw firm conclusions. Mechanistic experiments are recommended to address the authors' hypotheses.
      3. An important limitation is that virological data of EC are not considered. For example, I believe it is a lot more likely that the upregulation of ISG in EC relates to ongoing low-level viral replication. The authors could analyze cell-associated HIV RNA and DNA levels and determine how they associate with ISG expression.
      4. KZNF genes seem downregulated in EC. Can the authors propose a reason/mechanism for that?

      Significance

      Overall, I think this is an interesting manuscript that proposes a distinct and potentially important mechanisms that may contribute to immune control of HIV. My suggestions to improve the manuscript are complex and cannot be easily addressed through experimental work. I believe a possible option would be to publish the present manuscript without my proposed modifications, but highlight the weaknesses of the current paper more clearly; mechanistic studies could then be deferred to a future study.

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      Referee #1

      Evidence, reproducibility and clarity

      Singh et al. analyze the expression and putative contribution of TEs in CD4+ T cells in HIV elite controllers. Through re-analysis of existing datasets, the authors describe broad differences in expression of TEs in ECs through analysis of RNAseq annd ATACseq data, and come up with convincing examples where differentially-expressed innate immune genes correlate with increased accessibility of proximal TEs. Overall, the authors' conclusions are appropriately measured, though the manuscript text should be re-organized for clarity and a few further analyses are needed to support the main message of the paper.

      Major comments: The manuscript would benefit from a re-organization of the figures to focus on TEs - in particular, Fig 1B, Fig 2, and Fig 3 reproduce known transcriptional differences between ECs and HCs and serve as quality controls for the authors' computational analysis. Conversely, Supplementary Fig 6 contains very interesting data on KZNF expression and should be included in the main figures.

      It remains unclear whether differences in TE expression described are specific to ECs or to EC-like CD4+ T cell states. As there are plenty of datasets available that compare the transcriptome of naïve, activated, exhausted, and regulatory CD4+ T cells, the authors should compare the TE expression patterns observed in ECs to activated CD4+ T cells, particularly those with a Th1 and cytotoxic phenotype analogous to those observed in ECs, from healthy donors.

      In Fig 1, the authors demonstrate differential expression of both innate immune genes and TEs, but the link between the two is unclear. Is there any enrichment in differential expression for TEs located proximal to innate immune genes? This type of analysis should be possible using the authors' own software to map TE expression to specific genomic loci.

      Optional: In Fig 3, the authors cluster CD4+ T cells based on transcriptomic profiles. It would be interesting to re-cluster these samples based on TE expression alone, given the differences in TE expression described in Fig 5.

      Significance

      The manuscript by Singh et al. describes for the first time the role of TEs in HIV elite controllers, suggesting that TEs may be co-opted for cis-regulatory function. This study builds off prior work demonstrating that HIV-infected CD4+ T cells activate LTR elements that may regulate expression of interferon-inducible genes, demonstrating that ECs show further upregulation of innate immune genes. While these findings will need to be experimentally validated, this study constitutes a useful resource and adds to the growing body of evidence implicating TEs in cis-regulatory control of immune genes. This study will be of interest to basic scientists interested in genetic mechanisms of HIV control, and if further developed may comprise a useful source of biomarkers to predict viral kinetics in HIV-infected individuals.

      My expertise is in immunology, TE biology, and viral infection

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      Reply to the reviewers

      Reviewer #1

      Evidence, reproducibility and clarity

      Sanial et al. carefully analyze the use of in-gel fluorescence as an alternative to immunoblotting. The authors show that simple modifications of common protein extraction protocols can preserve (to varying extents) fluorescent proteins in their native, fluorescent states. This can be exploited in different applications for in-gel fluorescence quantification, bypassing immunoblotting. The experimental results are clear, showcasing the ease and linearity of in-gel fluorescence quantification.

      In my opinion, the trick of this approach is also potentially its main drawback, the partial denaturation conditions. I think the manuscript could be strengthened with more extensive benchmarking of the approach and further discussion of potential caveats as detailed below.

      Major points:

      1. Protein abundance in the original GFP library (and in other FP-tagged libraries constructed in the meanwhile) have been quantified using fluorescence (flow cytometry, microscopy, colony fluorescence) (Ho et al. 2018 10.1016/j.cels.2017.12.004, Weill et al. 2018 10.1038/s41592-018-0044-9, Meurer et al. 2018 10.1038/s41592-018-0045-8). This provides an opportunity to significantly strengthen the manuscript (where most of the test have been done using two abundant cytosolic proteins Bmh1 and Hxk1) if the authors could apply their approach to a representative fraction of the yeast proteome (sampling from such libraries FP-tagged proteins that differ in abundance, localization, membrane vs cytosolic/nuclear, subunits of large stable complexes vs proteins not part of complexes, etc.) and compare their quantification with previous relative abundance estimates. This information would also help future users in case protein-specific issues are identified.

      Indeed, Hxk1 and Bmh1 are quite strongly expressed (41,000 and 65,000 copies/cell, according to SGD, ____www.yeastgenome.org____). In the course of our experiments we were able to detect proteins with a much lower expression level (eg. Reg1, 4000 copies/cell). We have selected a number of proteins based on their expression level as detailed in SGD, ranging from 700 to 75000, and plan to detect the signal by IGF and compare it with published data on absolute protein quantifications for ecah protein. However, this will take a bit of time as each gene must be tagged with EGFP – we cannot use the GFP-S65T from the GFP collection which is poorly amenable to IGF because of its sensitivity to denaturation, as we show in our manuscript.

      The authors discuss several drawbacks, including the change in apparent molecular weight compared to denatured proteins; differential recognition of folded vs denatured proteins by antibodies.

      Other potentials drawbacks should be discussed. For instance, the need of additional steps post-fluorescence imaging for signal normalization against a loading control; the need of antibodies and immunoblotting to decide on the best denaturing temperature for a specific protein or FP tag; complexity of the native protein extraction protocol compared for example to alkaline lysis followed by TCA precipitation (Knop et al. 1999 PMID: 10407276).

      • Regarding the the need of additional steps post-fluorescence imaging for signal normalization against a loading control – this doesn’t take extra time for people using gels with protein stain included in the gel (eg. Stain-Free from BioRad). There are other possibilities of total protein fluorescent labeling that will be discussed. We will provide an example of this application.
      • On the need of antibodies and immunoblotting to decide on the best denaturing temperature for a specific protein or FP tag – we believe that the system could be set up for a protein of interest for which antibodies are available (as we did for Bmh1 or Hxk1), and once this is done, there is no need to do these controls anymore. We will mention this in the manuscript.
      • On the complexity of the native protein extraction protocol compared for example to alkaline lysis followed by TCA precipitation – indeed the protocol is a bit more time-consuming compared to the mentioned method, and we will mention this in the text. However, please note that people studying mammalian cells, for instance, often use this native protocol for total extracts so this is mostly a yeast-model issue. Yet, we will add this comment. Moreover, although the denatured fraction is FP- and temperature-dependent, even under the milder 30{degree sign}C conditions there is a detectable denatured fraction (Fig.s3b). This would seem to preclude the use of this approach for absolute protein quantification.

      True, but it depends a lot on the FP used. For instance, sfGFP is not denatured and could potentially be used for absolute quantification. We will comment in the text.

      Finally, any evidence that the denatured fraction would depend on the protein tagged with the FP?

      We will use several proteins used for point 1 but fused to the most sensitive FP, GFP-S65T, and do a western blot using anti-GFP antibodies to estimate the variation in native vs. denatured forms of the protein.

      Minor points: 1. In the experiments designed to test the linearity and sensitivity of the approach, an alternative approach that would not result in dilution of cell extract is to mix wild type cell extract (no GFP fusion) with extract of the GPF-tagged strain in different ratios.

      Yes, this was an alternative but it seemed that dilution was easier to control than mixing two extracts.

      Define all acronyms at first appearance. For example, DTT and LDS on page 4.

      Thank you, we will address all acronyms in the text.

      Fig.4D: the colors chosen to represent EGFP and sfGFP data make them hard to tell apart. The same comment to Fig.S6.

      Agreed, we will change the figures accordingly.

      As the temperature steps are not uniform in Figures 4 and 5, it would be more informative to indicate the exact temperate above each lane (in addition/instead of the ramp cartoon).

      Agreed, we will change the figures accordingly.

      Regarding linearity, that HRP-based quantification is not linear is expected. A fairer comparison would be to use fluorescently labeled secondary antibodies. It is also puzzling that detection with signal amplification (HRP) is less sensitive than direct quantification of the fluorescence signal from the FP tag.

      We will do a sensitivity tets (dilutions) to compare IGF with HRP-based and fluorescent-based antibody-mediated detection.

      I appreciate the workflow Figure 10. But in my opinion it is trying to show too much (protocol, troubleshooting, calls to figure panels). Perhaps it could be made clearer by separating the protocol steps/settings from the optimization/troubleshooting tips.

      Thank you, we will work on this to make the workflow clearer.

      Some of the discussion of different fluorescent proteins, and expression levels of tagged proteins, could be confounded by the different linkers used in the tagging constructs.

      Thank you for this remark. Indeed, there are various linkers on these constructs and we don’t know to which extent they contribute to the effect on protein expression level. We will comment his in the text.

      Significance

      Could be a generally useful and simple approach for in-gel quantification using fluorescent protein tags.

      __ ____Thank you for your comments and overall assesment.__


      Reviewer #2

      Evidence, reproducibility and clarity

      The present manuscript "Direct observation of fluorescent proteins in gels: a rapid cost-efficient, and quantitative alternative to immunoblotting" describes a method how to visualize bands of fluorescent protein fusions onto a common SDS-PAGE without antibody staining. It is based on ability of GFP-like fluorescent proteins (FPs) to retain their fluorescence under conditions of SDS-PAGE if step of extensive heating (boiling) of protein sample is omitted. This property of FPs is not novel; it was known for more than 20 years (for example, see Fig. 2 in Yanushevich et al. FEBS Lett. 2002 Jan 30, 511:11-4; Supporting Fig. 7 in Campbell et al. Proc Natl Acad Sci USA. 2002 Jun 11, 99:7877-82). However, the authors did perform a very accurate and robust study to quantitatively assess the behavior of several FP fusion protein in SDS-PAGE. A thorough analysis of different conditions for a variety of FPs and target proteins was done; detailed protocols were developed. A surprisingly high sensitivity of FP detection (even superior to that of standard Western blotting) was demonstrated. Considering the simplicity of the proposed approach, it appears to be the method of choice for those working with FP fusion proteins.

      Thank you for this comment. Indeed we do not claim to discover that FP remain fluorescent in mild denaturing conditions, as presented in the text. We did our best to include original publications showing precedent for this and we missed Yanushevich et al. FEBS Lett. 2002 that we will add. However the Campbell paper is cited, precisely for the Supplementary figure 7 that the reviewer mentions.

      I have only minor, discretionary comments:

      1. It is known that under conditions of SDS-PAGE without heating, FPs retain not only fluorescence but also their oligomeric state. The same can be true for proteins of interest (POIs). If so, even for monomeric FPs, the POI-FP band can potentially migrate much slower than expected because of oligomerization of the POI.

      __Thank you for this suggestion. Our data in the manuscript already show that Bmh1 and Bmh2, which are tighlty associated 14-3-3 proteins, no longer intereact in these mild denaturation conditions. In the set of proteins that we will use to answer to Reviewer #1 (point 1), we will include proteins in large complexes to assess whether this can happen. __

      It might be useful to briefly discuss a possibility to use other types of fluorescent proteins (namely, Flavin-binding FPs, bacteriophytochrome-based FPs, bilirubin-binding FP UnaG) in the same way as proposed here. In particular, biliverdin-binding near-infrared FPs (IFP, iRFP, etc.) can be detected even after fully denaturing SDS-PAGE by zinc-induced orange fluorescence of proteins carrying covalently attached bilin chromophore (Berkelman TR, Lagarias JC. Visualization of bilin-linked peptides and proteins in polyacrylamide gels. Anal Biochem. 1986, 156, 194-201; Stepanenko OV, Kuznetsova IM, Turoverov KK, Stepanenko OV. Impact of Double Covalent Binding of BV in NIR FPs on Their Spectral and Physicochemical Properties. Int J Mol Sci. 2022, 23, 7347).

      __Agreed. ____We will extend the discussion to other fluorescent approaches to visualize proteins in gels and compare them. __


      Significance

      A simple method of specific visualization of fluorescent protein fusion bands on SDS-PAGE is proposed.

      Thank you for your comments and overall assesment.

      Reviewer #3

      Evidence, reproducibility and clarity

      In this paper, Sanial et al present in-gel fluorescence detection (IGF), a method that allows the direct detection of fluorescent proteins from SDS-PAGE gels with minimal adaptation of existing protocols. The authors test a range of fluorescent proteins routinely used, especially when working with yeast, and describe their behavior in IGF. They identify heat-induced denaturation of fluorescent proteins as the main component influencing their assay and systematically test this on a selection of fluorescent proteins. Next, they compare the detection limit and the linearity of the signal between IGF and chemiluminescence, showing that IGF is not only comparable but also superior to chemiluminescence. This is particularly significant given that chemiluminescence can suffer from issues such as a limited dynamic range and limitations in accurately quantifying very low or high-abundance proteins. The authors further demonstrate the utility of IGF in co-immunoprecipitation experiments and test whether the mild denaturing conditions are compatible with proteins from other organisms. Overall, the study is well-presented and is an asset to the scientific community. I have one major and some minor comments that, in my opinion, would improve this already informative paper: Major comment 1. In all cases where there is signal quantification the authors should perform replicates to account for variability of the signal (in Fig 6, S6 and S7).

      __Agreed, we will perform triplicates for the indicated experiments. __

      Minor comments 1. The study mainly focuses on soluble protein. While the authors have tested one plasma membrane protein, the study would benefit from including more membrane proteins from different environments (e.g., cell wall, nuclear envelope, mitochondrial). This would help determine if incubation at higher temperatures is necessary to properly solubilize these proteins, in which case the experiment would need adaptation.

      Thank you for this suggestion. __In the set of proteins that we will use to answer to Reviewer #1 (point 1), we will include proteins from various subcellular locations. __

      The authors show that when fluorescent proteins are partially denatured, their migration behavior changes. One cannot exclude that in some cases, the tagged proteins themselves might also be partially resistant to denaturing at the low temperatures used for IGF. This would lead to more than one fluorescent bands. In such cases one should be careful with interpretation, especially in the context of PTMs or isoforms. Could the authors briefly discuss this?

      Thank you for this comment. __We will discuss this in the text. __

      Based on Fig 4D and 5D, some fluorescent proteins seem to have a higher signal variability between replicates than others. It would be helpful to add this information next to the behavior of the proteins in different temperatures so it would be easier to choose the fluorescent protein for specific experiments.

      __Indeed, there are variations between experiments, but it is not clear whether this inherent to the FP considered or the experiment. We will look back at the data and modify the text accordingly if pertinent. __

      The sensitivity experiment (Figure 6) is convincing and important for IP conditions, where the total protein concentration of the sample is radically decreased. Could the authors additionally test if very low abundant proteins can be detected (without any dilution of the total protein content), and compare this to chemiluminescence? This could be done either by tagging some very low abundant proteins (for example a few hundred copies per cell) or diluting the lysate in wild-type lysate to artificially reduce their concentration while maintaining the overall protein load the same.

      __We have planned an experiment in which low abundant proteins will be tagged in response to reviewer 1 (point 1) which should address this point. __

      It would be useful to address the detection of very high molecular weight proteins - or proteins that are problematic in terms of transfer during western blotting.

      Again, in the experiment planned in ____response to reviewer 1 (point 1), proteins or various MW as well as membrane proteins will be studied, which should address this point. __ __

      Significance

      The authors already discuss the strengths and limitations of their approach. The main strength of IGF is that it does not require transfer of the proteins to a membrane and also does not rely on antibody binding and (potential) chemical reactions. In addition to the fact that this is time, cost, equipment, waste and expertise effective, the sensitivity and signal linearity of IGF seems to not only compare but outperforme western blotting. There are two main limitations. First, IGF relies on the resilience to denaturing of the chosen fluorescent protein that depends, according to the authors, at least on the temperature and overall protein concentration and pH. Second, IGF relied on tagging proteins with fluorescent proteins which might affect the stability or even function of the tagged protein. As the authors mention, these factors do not diminish the value of IGF, they highlight the need for appropriate controls.

      A potential development of the technique (not at the present study) could be the compatibility of IGF with different self-labelling proteins (Halo, Snap) and fluorescent dyes.

      We have conducted experiments in which we show the applicability of IGF in combination to SNAP-tagging, that we could show if needed.

      I think IGF will benefit a rather broad range of scientists. As already mentioned by the authors, there are different applications of IGF. From checking of clones when creating strains, to comparison of protein levels in different conditions and coIP experiments.

      Thank you for your comments and overall assesment.

      Cross reviews. Reviewer 1: I agree with the assessment by Reviewer #2. Considering the comment about potential oligomerization of a protein of interest, I stand by my point about testing the method with more proteins of interest. How extensive this testing should be or whether additional discussion of possible issues would suffice is a matter of opinion. It is clear from the manuscript in it's current form that the method works and that it has caveats.

      We believed that the experiments we have planned will clarify these points.

      Reviewer 2: In general, I agree with the points raised by Reviewer #1. However, in my opinion, there is already a large body of reliable experimental results in the manuscript that are worth publishing without a new round of extensive experiments.

      Reviewer 1: Fair enough, I don't insist on the experiments in my point 1.

      We think that this is an important point that will likely be a common question for readers so we will still do our best to provide data for this point.

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      Referee #3

      Evidence, reproducibility and clarity

      In this paper, Sanial et al present in-gel fluorescence detection (IGF), a method that allows the direct detection of fluorescent proteins from SDS-PAGE gels with minimal adaptation of existing protocols. The authors test a range of fluorescent proteins routinely used, especially when working with yeast, and describe their behavior in IGF. They identify heat-induced denaturation of fluorescent proteins as the main component influencing their assay and systematically test this on a selection of fluorescent proteins. Next, they compare the detection limit and the linearity of the signal between IGF and chemiluminescence, showing that IGF is not only comparable but also superior to chemiluminescence. This is particularly significant given that chemiluminescence can suffer from issues such as a limited dynamic range and limitations in accurately quantifying very low or high-abundance proteins. The authors further demonstrate the utility of IGF in co-immunoprecipitation experiments and test whether the mild denaturing conditions are compatible with proteins from other organisms.

      Overall, the study is well-presented and is an asset to the scientific community. I have one major and some minor comments that, in my opinion, would improve this already informative paper:

      Major comment

      1. In all cases where there is signal quantification the authors should perform replicates to account for variability of the signal (in Fig 6, S6 and S7). Minor comments
      2. The study mainly focuses on soluble protein. While the authors have tested one plasma membrane protein, the study would benefit from including more membrane proteins from different environments (e.g., cell wall, nuclear envelope, mitochondrial). This would help determine if incubation at higher temperatures is necessary to properly solubilize these proteins, in which case the experiment would need adaptation.
      3. The authors show that when fluorescent proteins are partially denatured, their migration behavior changes. One cannot exclude that in some cases, the tagged proteins themselves might also be partially resistant to denaturing at the low temperatures used for IGF. This would lead to more than one fluorescent bands. In such cases one should be careful with interpretation, especially in the context of PTMs or isoforms. Could the authors briefly discuss this?
      4. Based on Fig 4D and 5D, some fluorescent proteins seem to have a higher signal variability between replicates than others. It would be helpful to add this information next to the behavior of the proteins in different temperatures so it would be easier to choose the fluorescent protein for specific experiments
      5. The sensitivity experiment (Figure 6) is convincing and important for IP conditions, where the total protein concentration of the sample is radically decreased. Could the authors additionally test if very low abundant proteins can be detected (without any dilution of the total protein content), and compare this to chemiluminescence? This could be done either by tagging some very low abundant proteins (for example a few hundred copies per cell) or diluting the lysate in wild-type lysate to artificially reduce their concentration while maintaining the overall protein load the same.
      6. It would be useful to address the detection of very high molecular weight proteins - or proteins that are problematic in terms of transfer during western blotting.

      Significance

      The authors already discuss the strengths and limitations of their approach. The main strength of IGF is that it does not require transfer of the proteins to a membrane and also does not rely on antibody binding and (potential) chemical reactions. In addition to the fact that this is time, cost, equipment, waste and expertise effective, the sensitivity and signal linearity of IGF seems to not only compare but outperforme western blotting. There are two main limitations. First, IGF relies on the resilience to denaturing of the chosen fluorescent protein that depends, according to the authors, at least on the temperature and overall protein concentration and pH. Second, IGF relied on tagging proteins with fluorescent proteins which might affect the stability or even function of the tagged protein. As the authors mention, these factors do not diminish the value of IGF, they highlight the need for appropriate controls.

      A potential development of the technique (not at the present study) could be the compatibility of IGF with different self-labelling proteins (Halo, Snap) and fluorescent dyes.

      I think IGF will benefit a rather broad range of scientists. As already mentioned by the authors, there are different applications of IGF. From checking of clones when creating strains, to comparison of protein levels in different conditions and coIP experiments.

      Keywords/field of expertise: yeast genetics, organelle homeostasis, biochemistry, molecular biology, cell biology, fluorescence microscopy, functional proteomics, gut microbiology

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      Referee #2

      Evidence, reproducibility and clarity

      The present manuscript "Direct observation of fluorescent proteins in gels: a rapid cost-efficient, and quantitative alternative to immunoblotting" describes a method how to visualize bands of fluorescent protein fusions onto a common SDS-PAGE without antibody staining. It is based on ability of GFP-like fluorescent proteins (FPs) to retain their fluorescence under conditions of SDS-PAGE if step of extensive heating (boiling) of protein sample is omitted. This property of FPs is not novel; it was known for more than 20 years (for example, see Fig. 2 in Yanushevich et al. FEBS Lett. 2002 Jan 30, 511:11-4; Supporting Fig. 7 in Campbell et al. Proc Natl Acad Sci USA. 2002 Jun 11, 99:7877-82). However, the authors did perform a very accurate and robust study to quantitatively assess the behavior of several FP fusion protein in SDS-PAGE. A thorough analysis of different conditions for a variety of FPs and target proteins was done; detailed protocols were developed. A surprisingly high sensitivity of FP detection (even superior to that of standard Western blotting) was demonstrated. Considering the simplicity of the proposed approach, it appears to be the method of choice for those working with FP fusion proteins.

      I have only minor, discretionary comments:

      1. It is known that under conditions of SDS-PAGE without heating, FPs retain not only fluorescence but also their oligomeric state. The same can be true for proteins of interest (POIs). If so, even for monomeric FPs, the POI-FP band can potentially migrate much slower than expected because of oligomerization of the POI.
      2. It might be useful to briefly discuss a possibility to use other types of fluorescent proteins (namely, Flavin-binding FPs, bacteriophytochrome-based FPs, bilirubin-binding FP UnaG) in the same way as proposed here. In particular, biliverdin-binding near-infrared FPs (IFP, iRFP, etc.) can be detected even after fully denaturing SDS-PAGE by zinc-induced orange fluorescence of proteins carrying covalently attached bilin chromophore (Berkelman TR, Lagarias JC. Visualization of bilin-linked peptides and proteins in polyacrylamide gels. Anal Biochem. 1986, 156, 194-201; Stepanenko OV, Kuznetsova IM, Turoverov KK, Stepanenko OV. Impact of Double Covalent Binding of BV in NIR FPs on Their Spectral and Physicochemical Properties. Int J Mol Sci. 2022, 23, 7347).

      Referee cross-commenting

      In general, I agree with the points raised by Reviewer #1. However, in my opinion, there is already a large body of reliable experimental results in the manuscript that are worth publishing without a new round of extensive experiments.

      Significance

      A simple method of specific visualization of fluorescent protein fusion bands on SDS-PAGE is proposed.

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

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      Referee #1

      Evidence, reproducibility and clarity

      Sanial et al. carefully analyze the use of in-gel fluorescence as an alternative to immunoblotting. The authors show that simple modifications of common protein extraction protocols can preserve (to varying extents) fluorescent proteins in their native, fluorescent states. This can be exploited in different applications for in-gel fluorescence quantification, bypassing immunoblotting. The experimental results are clear, showcasing the ease and linearity of in-gel fluorescence quantification.

      In my opinion, the trick of this approach is also potentially its main drawback, the partial denaturation conditions. I think the manuscript could be strengthened with more extensive benchmarking of the approach and further discussion of potential caveats as detailed below.

      Major points:

      1. Protein abundance in the original GFP library (and in other FP-tagged libraries constructed in the meanwhile) have been quantified using fluorescence (flow cytometry, microscopy, colony fluorescence) (Ho et al. 2018 10.1016/j.cels.2017.12.004, Weill et al. 2018 10.1038/s41592-018-0044-9, Meurer et al. 2018 10.1038/s41592-018-0045-8). This provides an opportunity to significantly strengthen the manuscript (where most of the test have been done using two abundant cytosolic proteins Bmh1 and Hxk1) if the authors could apply their approach to a representative fraction of the yeast proteome (sampling from such libraries FP-tagged proteins that differ in abundance, localization, membrane vs cytosolic/nuclear, subunits of large stable complexes vs proteins not part of complexes, etc.) and compare their quantification with previous relative abundance estimates. This information would also help future users in case protein-specific issues are identified.
      2. The authors discuss several drawbacks, including the change in apparent molecular weight compared to denatured proteins; differential recognition of folded vs denatured proteins by antibodies.

      Other potentials drawbacks should be discussed. For instance, the need of additional steps post-fluorescence imaging for signal normalization against a loading control; the need of antibodies and immunoblotting to decide on the best denaturing temperature for a specific protein or FP tag; complexity of the native protein extraction protocol compared for example to alkaline lysis followed by TCA precipitation (Knop et al. 1999 PMID: 10407276).

      Moreover, although the denatured fraction is FP- and temperature-dependent, even under the milder 30{degree sign}C conditions there is a detectable denatured fraction (Fig.s3b). This would seem to preclude the use of this approach for absolute protein quantification.

      Finally, any evidence that the denatured fraction would depend on the protein tagged with the FP?

      Minor points:

      1. In the experiments designed to test the linearity and sensitivity of the approach, an alternative approach that would not result in dilution of cell extract is to mix wild type cell extract (no GFP fusion) with extract of the GPF-tagged strain in different ratios.
      2. Define all acronyms at first appearance. For example, DTT and LDS on page 4.
      3. Fig.4D: the colors chosen to represent EGFP and sfGFP data make them hard to tell apart. The same comment to Fig.S6.
      4. As the temperature steps are not uniform in Figures 4 and 5, it would be more informative to indicate the exact temperate above each lane (in addition/instead of the ramp cartoon).
      5. Regarding linearity, that HRP-based quantification is not linear is expected. A fairer comparison would be to use fluorescently labeled secondary antibodies. It is also puzzling that detection with signal amplification (HRP) is less sensitive than direct quantification of the fluorescence signal from the FP tag.
      6. I appreciate the workflow Figure 10. But in my opinion it is trying to show too much (protocol, troubleshooting, calls to figure panels). Perhaps it could be made clearer by separating the protocol steps/settings from the optimization/troubleshooting tips.
      7. Some of the discussion of different fluorescent proteins, and expression levels of tagged proteins, could be confounded by the different linkers used in the tagging constructs.

      Referee Cross-commenting

      This session contains comments from all reviewers.

      Reviewer 1: I agree with the assessment by Reviewer #2. Considering the comment about potential oligomerization of a protein of interest, I stand by my point about testing the method with more proteins of interest. How extensive this testing should be or whether additional discussion of possible issues would suffice is a matter of opinion. It is clear from the manuscript in it's current form that the method works and that it has caveats.

      Reviewer 2: In general, I agree with the points raised by Reviewer #1. However, in my opinion, there is already a large body of reliable experimental results in the manuscript that are worth publishing without a new round of extensive experiments.

      Reviewer 1: Fair enough, I don't insist on the experiments in my point 1.

      Significance

      Could be a generally useful and simple approach for in-gel quantification using fluorescent protein tags.

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      Reply to the reviewers

      Thank you very much for your editorial handling of our manuscript entitled 'A conserved fungal Knr4/Smi1 protein is vital for maintaining cell wall integrity and host plant pathogenesis'. We have taken on board the reviewers' comments and thank them for their diligence and time in improving our manuscript.

      Please find our responses to each of the comments below.

      Reviewer(s)' comments

      Reviewer #1


      Major comments:


      __1.1. As a more critical comment, I find the presentation of the figures somewhat confusing, especially with the mixing of main figures, supplements to the main figures, and actual supplemental data. On top of that, the figures are not called up in the right order (e.g. Figure 4 follows 2D, while 3 comes after 4; Figure 6 comes before 5...), and some are never called up (I think) (e.g. Figure 1B, Figure 2B). __


      __Response: __The figure order has been revised according to the reviewer's suggestion, while still following eLife's formatting guidelines for naming supplementals. Thank you.

      1.2. I agree that there should be more CWI-related genes in the wheat module linked to the FgKnr4 fungal module, or, vice-versa, CW-manipulating genes in the fungal module. It would at least be good if the authors could comment further on if they find such genes, and if not, how this fits their model.


      Response: Thank you for your insightful suggestion regarding the inclusion of more CWI-related genes in the wheat module linked to the FgKnr4 fungal module F16, or vice versa. We did observe a co-regulated response between the wheat module W05 which is correlated to the FgKnr4 module F16. Namely, we observed an enrichment of oxidative stress genes including respiratory burst oxidases and two catalases (lines 304 - 313) in the correlated wheat module (W05). Early expression of these oxidative stress inducing genes likely induces the CWI pathway in the fungus, which is regulated by FgKnr4. Knr4 functions as both a regulatory protein in the CWI pathway and as a scaffolding protein across multiple pathways in S. cerevisiae (Martin-Yken et al., 2016, https://onlinelibrary.wiley.com/doi/10.1111/cmi.12618 ). Scaffolding protein-encoding genes are typically expressed earlier than the genes they regulate to enable pre-assembly with their interacting partners, ensuring that signaling pathways are ready to activate when needed. In this context, the CWI integrity MAPKs Bck1 and Mkk1 are part of module F05, which includes two chitin synthases and a glucan synthase. This module is highly expressed during the late symptomless phase. The MAPK Mgv1, found in module F13, is expressed consistently throughout the infection process, which aligns with the expectation that MAPKs are mainly post-transcriptionally regulated. Thank you for bringing our attention to this, this is now included in the discussion (lines 427 - 443) along with eigengene expression plots of all modules added to the supplementary (Figure 3 - figure supplement 1).

      To explore potential shared functions of FgKnr4 with other genes in its module, we re-analyzed the high module membership genes within module F16, which includes FgKnr4, using Knetminer (Hassani-Pak et al., 2021; https://onlinelibrary.wiley.com/doi/10.1111/pbi.13583 ). This analysis revealed that 8 out of 15 of these genes are associated with cell division and ATP binding. Four of the candidate genes are also part of a predicted protein-protein interaction subnetwork of genes within module F16, which relate to cell cycle and ATP binding. In S. cerevisiae, the absence of Knr4 results in cell division dysfunction (Martin-Yken et al., 2016, https://onlinelibrary.wiley.com/doi/10.1111/cmi.12618 ). Accordingly, we tested sensitivity of ΔFgknr4 to microtubule inhibitor benomyl (a compound commonly used to identify mutants with cell division defects; Hoyt et al., 1991 https://www.cell.com/cell/pdf/0092-8674(81)90014-3.pdf). We found that the ΔFgknr4 mutant was more susceptible to benomyl, both when grown on solid agar and in liquid culture. This data has now been added Figure 7, and referred to in lines 338-348.

      __Specific issues: __


      1.3. In the case of figure 5, I generally find it hard to follow. In the text (line 262/263), the authors state that 5C shows "eye-shaped lesions" caused by ΔFgknr4 and ΔFgtri5, but I can't see neither (5C appears to be a ΔFgknr4 complementation experiment). The figure legend also states nothing in this regard.

      __Response: __Thank you for your suggestion. We have amended the manuscript to include an additional panel that shows the dissected spikelet without its outer glumes, making the eye shaped diseased regions more visible in Figure 5.

      __1.4. Figure 5D supposedly shows 'visibly reduced fungal burden' in ΔFgknr4-infected plants, but I can't really see the fungal burden in this picture, but the infected section looks a lot thinner and more damaged than the control stem, so in a way more diseased. __


      Response: __Thank you for your insight. We have revised our conclusions based on this image to state that while ΔFgknr4 can colonise host tissue, it does so less effectively compared to the wild-type strain as we are unable to quantitatively evaluate fungal burden using image-colour thresholding due to the overlapping colours of the fungal cells and wheat tissues. Decreased host colonisation is evidenced by (i) reduced fungal hyphae proliferation, particularly in the thicker adaxial cell layer, (ii) collapsed air spaces in wheat cells, and (iii) increased polymer deposition at the wheat cell walls, indicating an enhanced defence response. __Figure 5 has been amended to include these observations in the corresponding figure legend and the resin images now include insets with detailed annotation.

      __1.5. The authors then go on to state (lines 272-273) that they analyzed the amounts of DON mycotoxin in infected tissues, but don't seem to show any data for this experiment. __

      Response: __We have amended this to now include the data in __Figure 5 - figure supplement 2B, thank you.

      Reviewer #2


      __Major issues: __


      2.1 If Knf4 is involved in the CWI pathway, what other genes involved in the CWI pathway are in this fungal module? one of the reasons for developing modules or sub-networks is to assign common function and identify new genes contributing to the function. since FgKnr4 is noted to play a role in the CWI pathways, then genes in that module should have similar functions. If WGCN does not do that, what is the purpose of this exercise?


      Response: __Thank you for raising this point regarding the role of FgKnr4 in the CWI pathway and the expectations for genes of shared function within the FgKnr4 module F16. We did observe that the module containing FgKnr4 (F16) was also correlated to a wheat module (W05) which was significantly enriched for oxidative stress genes. This pathogen-host correlated pattern led us to study module F16, which otherwise lacks significant gene ontology term enrichment, unique gene set enrichments, and contains few characterised genes. This is now highlighted in __lines 233-246. This underscores the strength of the WGCNA. By using high-resolution RNA-seq data to map modules to specific infection stages, we identified an important gene that would have otherwise been overlooked. This approach contrasts with other network analyses that often rely on the guilt-by-association principle to identify novel virulence-related genes within modules containing known virulence factors, potentially overlooking significant pathways outside the scope of prior studies. Therefore, our analysis has already benefited from several advantages of WGCNA, including the identification of key genes with high module membership that may be critical for biological processes, as well as generating a high-resolution, stage-specific co-expression map of the F. graminearum infection process in wheat. This point is now emphasised in lines 233-252. As discussed in response to reviewer 1, Knr4 functions as both a regulatory protein in the CWI pathway and as a scaffolding protein across multiple pathways in S. cerevisiae (Martin-Yken et al., 2016, https://onlinelibrary.wiley.com/doi/10.1111/cmi.12618 ) which would explain its clustering separate from the CWI pathway genes. The high module membership genes within module F16 containing FgKnr4 were re-analysed using Knetminer (Hassani-Pak et al., 2021; https://onlinelibrary.wiley.com/doi/10.1111/pbi.13583 ), which found that 8/15 of these genes were related to cell division and ATP binding. Four of the candidate genes are also part of a predicted protein-protein interaction subnetwork of genes within module F16, which relate to cell cycle and ATP binding. In S. cerevisiae, the absence Knr4 leads to dysfunction in cell division. Accordingly, we tested sensitivity of ΔFgknr4 to the microtubule inhibitor benomyl (a compound commonly used to identify mutants with cell division defects; Hoyt et al., 1991 https://www.cell.com/cell/pdf/0092-8674(81)90014-3.pdf). We found that the ΔFgknr4 mutant was more susceptible to benomyl, both when grown on solid agar and in liquid culture. This data has now been added as Figure 7 and referred to in lines 338-348.


      2.2. Due to development defects in the Fgknr1 mutant, I would not equate to as virulence factor or an effector gene.


      __Response: __We are in complete agreement with the reviewer and are not suggesting that FgKnr4 is an effector or virulence factor, we have been careful with our wording to indicate that FgKnr4 is simply necessary for full virulence and its disruption results in reduced virulence and have outlined how we believe FgKnr4 participates in a fungal signaling pathway required for infection of wheat.


      2.3. What new information is provided with WGCN modules compared with other GCN network in Fusarium (examples of GCN in Fusarium is below) ____https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5069591/ https://doi.org/10.1186/s12864-020-6596-y____ DOI: 10.1371/journal.pone.0013021. The GCN networks from Fusarium have already identified modules necessary/involved in pathogenesis.

      Response: __The 2016 New Phytologist gene regulatory network (GRN) by Guo et al. is large and comprehensive. However, only three of the eleven datasets are in planta, with just one dataset focusing on F. graminearum infection on wheat spikes. The other two in planta datasets involve barley infection and Fusarium crown rot. By combining numerous in planta and in vitro datasets, the previous GRNs lack the fine resolution needed to identify genetic relationships under specific conditions, such as the various stages of symptomatic and symptomless F. graminearum infection of mature flowering wheat plants. This limitation is highlighted in the 2016 paper itself. This network is expanded in the Guo et al., 2020 BMC genomics paper where it includes one additional in planta and nine in vitro datasets. However, the in planta dataset involves juvenile wheat coleoptile infection, which serves as an artificial model for wheat infection but is not on mature flowering wheat plants reminiscent of Fusarium Head Blight of cereals in the field. This model differs significantly in the mode of action of F. graminearum, notably DON mycotoxin is not essential for virulence in this context (Armer et al. 2024, https://pubmed.ncbi.nlm.nih.gov/38877764/ ). The Guo et al., 2020 paper still faces the same issues in terms of resolution and the inability to draw conclusions specific to the different stages of F. graminearum infection. Additionally, these GRNs use Affymetrix data, which miss over 400 genes (~ 3 % of the genome) from newer gene models. In contrast, our study addresses these limitations by analysing a meticulously sampled, stage- and tissue-specific in planta RNA-seq dataset using the latest reference annotation. Our approach provides higher resolution and insights into host transcriptomic responses during the infection process. The importance of our study in the context of these GRNs is now addressed in the introduction (__lines 85-92).


      2.4. Ideally, the WGCN should have been used identify plant targets of Fusarium pathogenicity genes. This would have provided credibility and usefulness of the WGCN. Many bioinformatic tools are available to identify virulence factors and the utility of WGCN in this regard is not viable. However, if the authors had overlapped the known virulence factors in a fungal module to a particular wheat module, the impact of the WGCN would be great. The module W12 has genes from numerous traits represented and WGCN could have been used to show novel links between Fg and wheat. For example, does tri5 mutant affect genes in other traits?

      __Response: __Thank you for your suggestions. In this study we have shown the association between the main fungal virulence factor of F. graminearum, DON mycotoxin, with wheat detoxification responses. Through this we have identified a set of tri5 responsive genes and validated this correlation in two genes belonging to the phenylalanine pathway and one transmembrane detoxification gene. Although we could validate more genes in this tri5 responsive wheat module, our paper aimed to investigate previously unstudied aspects of the F. graminearum infection process and how the fungus responded to changing conditions within the host environment. We accomplished this by characterising a gene within a fungal module that had limited annotation enrichment and few characterised genes. Tri5 on the other hand is the most extensively studied gene in F. graminearum and while the network we generated may offer new insights into tri5 responsive genes, this is beyond the scope of our current study. In addition to the tri5 co-regulated response, we have also demonstrated the coordinated response between the fungal module F16, which contains FgKnr4 that is necessary for tolerance to oxidative stress, and the wheat module W05, which is enriched for oxidative stress genes.


      While our co-expression network approach can be used to explore and validate other early downstream signaling and defense components in wheat cells, several challenges must be considered: (a) the poor quality of wheat gene calls, (b) genetic redundancy due to both homoeologous genes and large gene families, and (c) the presence of DON, which can inhibit translation and prevent many transcriptional changes from being realised within the host responses. Additionally, most plant host receptors are not transcriptionally upregulated in response to pathogen infection (most R gene studies for the NBS-LRR and exLRR-kinase classes), making their discovery through a transcriptomics approach unlikely. These points will be included in our discussion (lines 408-413), thank you.

      Specific issues

      • *

      2.5. Since tri5 mutant was used a proof of concept to link wheat/Fg modules, it would have been useful to show that TRI14, which is not involved DON biosynthesis, but involved in virulence ( https://doi.org/10.3390/applmicrobiol4020058____) impact the wheat module genes.


      Response: __Our goal was to show that wheat genes respond to the whole TRI cluster, not just individual TRI genes. Therefore, the tri5 mutant serves as a solid proof-of-concept, because TRI5 is essential for DON biosynthesis, the primary function of the TRI gene cluster, thereby representing the function of the cluster as a whole. This is now clarified in __lines 217-219. Additionally, the uncertainties surrounding other TRI mutants would complicate the question we were addressing-namely, whether a wheat module enriched in detoxification genes is responding to DON mycotoxin, as implied by shared co-expression patterns with the TRI cluster. For instance, the referenced TRI14 paper indicates that DON is produced in the same amount in vitro in a single media. Although the difference is not significant, the average DON produced is lower for the two Δtri14 transformants tested. Therefore, we cannot definitively rule out that TRI14 is involved in DON biosynthesis and extrapolate this to DON production in planta. Despite this, the suggestion is interesting, and would make a nice experiment but we believe it does not contribute to the overall aim of this study.

      2.6. Moreover, prior RNAseq studies with tri5 mutant strain on wheat would have revealed the expression of PAL and other phenylpropanoid pathway genes?

      __Response: __We agree that this would be an interesting comparison to make but unfortunately no dataset comparing in planta expression of the tri5 mutant within wheat spikes exists.

      2.7. Table S1 lists 15 candidate genes of the F16 module; however, supplementary File 1 indicates 74 genes in the same module. The basis of exclusion should be explained. The author has indicated genes with high MM was used as representative of the module. The 59 remaining genes of this module did not meet this criteria? Give examples.


      Response: __The 15 genes with the highest module membership were selected as initial candidates for further shortlisting from the 74 genes within module F16. In WGCNA, genes with high module membership (MM) (i.e. intramodular connectivity) are predicted to be central to the biological functions of the module (Langfelder and Horvath, 2008; https://bmcbioinformatics.biomedcentral.com/articles/10.1186/1471-2105-9-559 ) and continues to be a metric to identify biologically significant genes within WGCN analyses (https://bmcplantbiol.biomedcentral.com/articles/10.1186/s12870-024-05366-0 Tominello-Ramirez et al., 2024; https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9151341/ ;Zheng et al., 2022; https://www.nature.com/articles/s41598-020-80945-3 Panahi and Hejazi et al 2021). Following methods by Mateus et al. (2019) (https://academic.oup.com/ismej/article/13/5/1226/7475138 ) key genes were defined as those exhibiting elevated MM within the module, which were also strongly correlated (R > |0.70|) with modules of the partner organism (wheat). We have clarified this point in the manuscript. Thank you for the suggestion. (__Lines 253-263).

      2.____8. A list from every module that pass this criteria will be useful resource for functional characterization studies.


      __Response: __A supplementary spreadsheet has been generated which includes full lists of the top 15 genes with the highest module membership within the five fungal modules correlated to wheat modules and a summary of shared attributes among them. Thank you for this suggestion.

      2.9. Figure 3 indicates TRI genes in the module F12; your PHI base in Supp File S2 lists only TRI14. Why other TRI genes such as TRI5 not present in this File?


      Response: For clarity, the TRI genes in module F12 are TRI3, TRI4, TRI11, TRI12, and TRI14 which was stated in Table 1. TRI5 clusters with its neighboring regulatory gene TRI6 in module F11, which exhibits a similar but reduced expression pattern compared to module F12. To improve clarity on this the TRI genes in module F12 are also listed in-text in line 168 and added to Figure 4. The enrichment and correlated relationship of W12 to a cluster's expression still imply a correlated response of the wheat gene to the TRI cluster's biosynthetic product (DON), which is absent in the Δtri5 mutant.

      TRI14 and TRI12 are listed in PHI-base. TRI12 was mistakenly excluded due to an unmapped Uniprot ID, which were added separately in the spreadsheet. We will recheck all unmapped ID lists to ensure all PHI-base entries are included in the final output. Thank you for pointing out this error.


      2.10. What is purpose of listing the same gene multiple times? Example, osp24 (a single gene in Fg) is listed 13 times in F01 module.


      __Response: __This is a consequence of each entry having a separate PHI ID, which represents different interactions including inoculations on different cultivar. Cultivar and various experimental details were omitted from the spreadsheet to reduce information density, however the multiple PHI base ID's will be kept separate to make the data more user friendly when working with the PHI-base database. An explanation for this is now provided in the file's explanatory worksheet, thank you.

      Reviewer #3:


      3.1. Why only use of high confidence transcripts maize to map the reads and not the full genome like Fusarium graminearum? I have never analyzed plant transcriptome.


      __Response: __ In the wheat genome, only high-confidence gene calls are used by the global community (Choulet et al., 2023; https://link.springer.com/chapter/10.1007/978-3-031-38294-9_4 ) until a suitable and stable wheat pan-genome becomes available.

      3.2. The regular output of DESeq are TPMs, how did the authors obtain the FPKM used in the analysis?


      Response: FPKM was calculated using the GenomicFeatures package and included on GitHub to enhance accessibility for other users. However, the input for WGCNA and this study as a whole was normalised counts rather than FPKM. The FPKM analysis was done to improve interoperability of the data for future users and made available on Github. To complement this, the information regarding FPKM calculation is now included in the methods section of the revised manuscript (line 491).

      3.3. Do the authors have a Southern blot to prove the location of the insertion and number of insertions in Zymoseptoria tritici mutant and complemented strains?


      __Response: __No, but the phenotype is attributed to the presence or absence of ZtKnr4, as the mutant was successfully complemented in multiple phenotypic aspects. This satisfies Koch's postulates which is the gold standard for reverse genetics experimentation (Falkow 1988; https://www.jstor.org/stable/4454582 ).

      __3.4. Boxplots and bar graphs should have the same format. In Figures 5 B and F and supplementary figure 6.3 the authors showed the distribution of samples but it is lacking in figure 3 B and all bar graphs. __


      __Response: __Graphs have been modified to display the distribution of all samples, thank you.

      3.5. Line 247 FGRAMPH1_0T23707 should be FGRAMPH1_01T23707


      __Response: __Thank you this has now been amended.

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      Referee #3

      Evidence, reproducibility and clarity

      The authors of the manuscript entitled "A conserved fungal Knr4/Smi1 protein is vital for maintaining cell wall integrity and host plant pathogenesis" used a weighted gene co-expression network to identify Fusarium graminearum genes highly expressed during early symptomless infection of wheat. Based on its sequence and previous studies, authors selected FgKnr4 from the early symptomless Fusarium modules. The characterization of knockout strains revealed a role in morphogenesis, growth, cell wall stress tolerance, and virulence in F. graminearum and the phylogenetically distant fungus Zymoseptoria tritici.

      The methods are properly described and statistical analysis are reasonable so reproducibility is possible. The RNA-seq dataset is already published and the authors provided a repository with the code used to create the co-expression network. However, I have the following questions:

      • Why only use of high confidence transcripts maize to map the reads and not the full genome like Fusarium graminearum? I have never analyzed plant transcriptome.
      • The regular output of DESeq are TPMs, how did the authors obtain the FPKM used in the analysis?
      • Do the authors have a southern blot to prove the location of the insertion and number of insertions in Zymoseptoria tritici mutant and complemented strains?
      • Boxplots and bar graphs should have the same format. In Figures 5 B and F and supplementary figure 6.3 the authors showed the distribution of samples but it is lacking in figure 3 B and all bar graphs.
      • Line 247 FGRAMPH1_0T23707 should be FGRAMPH1_01T23707

      Referees cross-commenting

      I agree with reviewer 1, the order in which the figures are called in the text is confusing. Regardless of figures 5C-D I am no expert in the field therefore I can only say they look like they have not been edited.

      I agree with reviewer 1, data of DON mycotoxin production in infected issues is need it to support statement in line 272-273.

      I agree with Reviewer 2, the criteria to exclude genes from the final selection list should be explained.

      Significance

      The study showed, once again, that a weighted gene co-expression network is a great method to identify new genes of interest regardless of the organism or condition even if not very popular in the fungal pathogen field yet. The study proved that functions identified in a WGCN module from a pathogen have their opposite in the host module. The authors go beyond the theory and demonstrate the effect of the highest expressed gene during the early symptomless stage of infection in maize and wheat fungal pathogens.

      Fungal pathogen, RNA-seq, metabolic models, metabolism, comparative genomics

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      Referee #2

      Evidence, reproducibility and clarity

      Summary: The authors in this manuscript use "dual weighting" to identify clusters or modules of genes from the fungus F. graminearum (Fg) with coordinated expression patterns with genes in wheat modules - potentially uncover key regulators or pathways linking Fg genes with plant traits, including plant pathogenesis. As proof of concept, the authors use one of the fungal genes FgKnr4 identified in a fungal module that has strong link with the wheat module. They were able to show that this gene is likely involved in CWI pathway and affects virulence properties of the fungus

      Major comments:

      Does the WGCN provide useful framework to link fungal genes affecting plant traits? If Knf4 is involved in the CWI pathway, what other genes involved in the CWI pathway are in this fungal module? This is not forthcoming. Due to development defects in the Fgknr1 mutant, I would not equate to as virulence factor or an effector gene.

      Since tri5 mutant was used a proof of concept to link wheat/Fg modules, it would have been useful to show that TRI14, which is not involved DON biosynthesis, but involved in virulence ( https://doi.org/10.3390/applmicrobiol4020058) impact the wheat module genes. Moreover, prior RNAseq studies with tri5 mutant strain on wheat would have revealed the expression of PAL and other phenylpropanoid pathway genes?

      Table S1 lists 15 candidate genes of the F16 module; however, supplementary File 1 indicates 74 genes in the same module.

      The basis of exclusion should be explained. The author has indicated genes with high MM was used as representative of the module. The 59 remaining genes of this module did not meet this criteria? Give examples. Did similar exclusion criteria used for other modules and if so, how many genes in each module pass the criteria? For example, Did TRI5 in module F12 pass this criteria. A list from every module that pass this criteria will be useful resource for functional characterization studies.

      Minor comments:

      Figure 3 indicates TRI genes in the module F12; your PHI base in Supp File S2 lists only TRI14. Why other TRI genes such as TRI5 not present in this File? What is purpose of listing the same gene multiple times? Example, osp24 (a single gene in Fg) is listed 13 times in F01 module.

      Referees cross-commenting

      agree with both reviewers regarding clarification of Figures.

      one of the reasons for developing modules or sub-networks is to assign common function and identify new genes contributing to the function. since FgKnr4 is noted to play a role in the CWI pathways, then genes in that module should have similar functions. If WGCN does not do that, what is the purpose of this exercise?

      Significance

      What new information is provided with WGCN modules compared with other GCN network in Fusarium (examples of GCN in Fusarium is below)

      https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5069591/ https://doi.org/10.1186/s12864-020-6596-y DOI: 10.1371/journal.pone.0013021

      The GCN networks from Fusarium have already identified modules necessary/involved in pathogenesis. Ideally, the WGCN should have been used identify plant targets of Fusarium pathogenicity genes. This would have provided credibility and usefulness of the WGCN.

      Many bioinformatic tools are available to Identify virulence factors and the utility of WGCN in this regard is not viable. However, if the authors had overlapped the known virulence factors in a fungal module to a particular wheat module, the impact of the WGCN would be great. The module W12 has genes from numerous traits represented and WGCN could have been used to show novel links between Fg and wheat. For example, does tri5 mutant affect genes in other traits?

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      A public mRNA-seq dataset from Dilks et al. (2019) for wheat spikelets infected by Fusarium graminearum was used to generate a dual weighted gene co-expression network (WGCN). Since colonization of the spike by F. graminearum progresses from spikelet to spikelet, thereby forming an infection-gradient from early to late stages, quasi spatio-temporal resolution for the transcriptomic dataset can be achieved by cutting the spike into equal pieces along this gradient (in this case cuts were done at rachis internodes 1-2, 3-4, 5-6, and 7-8. The authors created co-expression networks for both, fungal and plant genes, and cross-correlated them. They identify several modules specific for each infection stage. For further analysis, the authors focus on two module pairs. (1) the wheat module 12 (W12), which correlates to Fusarium module 12 (F12), and (2) the Fusarium module 16 (F16) and the correlated wheat modules 1 and 5 (W01/W05). The W12/F12 modules were deemed of interest because they were specific to the transition from symptomless to symptomatic infection stage. Here, the authors find genes related to mycotoxin production to be upregulated in the F12 module, while the W12 is enriched in genes involved in detoxification. F16 and W01/W05 are specific to the earliest stages of infection, and thus most likely involved in fungal virulence. Here, one of the key genes identified is FgKnr4, which the authors show to be important for fungal virulence, as gene knockout leads to a premature stop of disease progression. As the authors show that FgKnr4 is involved in activating cell wall-integrity mechanisms, and may function in oxidative stress-resistance, this reduced virulence may be the result a reduced ability of the fungus to withstand plant defense mechanisms. Interestingly, knocking out an orthologue of FgKnr4 in Zymoseptoria tritici led to similarly reduced virulence of this pathogenic fungus on wheat plant.

      Comments:

      Overall, I find the WGCN analysis to be very interesting and informative, especially because of the different stages of infection. As the dataset is made public (I believe), I think that this will be a really important resource for the community. The exemplary functional analysis of the F16/W01/W05 modules via FgKnr4 is very interesting and demonstrates that novel genes involved in virulence can be identified via this approach. A similar more detailed analysis of the W12/F12 modules with a focus on detoxification mechanisms in the plant (i.e. the W12 module) would be a very interesting bonus, but as much as I would be interested in reading about it, functional gene analyses in wheat are obviously time-consuming, and it is not essential to this manuscript. As a more critical comment, I find the presentation of the figures somewhat confusing, especially with the mixing of main figures, supplements to the main figures, and actual supplemental data. On top of that, the figures are not called up in the right order (e.g. Figure 4 follows 2D, while 3 comes after 4; Figure 6 comes before 5...), and some are never called up (I think) (e.g. Figure 1B, Figure 2B). In the case of figure 5, I generally find it hard to follow. In the text (line 262/263), the authors state that 5C shows "eye-shaped lesions" caused by ΔFgknr4 and ΔFgtri5, but I can't see neither (5C appears to be a ΔFgknr4 complementation experiment). The figure legend also states nothing in this regard. Figure 5D supposedly shows 'visibly reduced fungal burden' in ΔFgknr4-infected plants, but I can't really see the fungal burden in this picture, but the infected section looks a lot thinner and more damaged than the control stem, so in a way more diseased. The authors then go on to state (lines 272-273) that they analyzed the amounts of DON mycotoxin in infected tissues, but don't seem to show any data for this experiment. In contrast to the sometimes confusing data presentation, I find the table of correlated modules (table 1) very helpful, and obviously am happy to see that all data is available in the first author's GitHub account.

      Referees cross-commenting

      just to clarify in regards to my comment on Figures 5C-D, and Reviewer #3's comment "Regardless of figures 5C-D I am no expert in the field therefore I can only say they look like they have not been edited." - I didn't want to insinuate that the images have been edited. Based on the images provided, I just can't see what the authors state is shown. So this is not about editing/manipulation - just about image quality/choice. The phenotypic descriptions by the authors are quite detailed ("eye-shaped lesions", 'visibly reduced fungal burden'...), but at least for me, the images aren't good enough to illustrate and underpin their statements. Maybe better images are needed, maybe magnifications of the exact regions showing the phenotypes? But this is simply a matter of presentation, not of editing/manipulation.

      Second, I agree that there should be more CWI-related genes in the wheat module linked to the FgKnr4 fungal module, or, vice-versa, CW-manipulating genes in the fungal module. It would at least be good if the authors could comment further on if they find such genes, and if not, how this fits their model.

      Significance

      In summary, I think that the presented WGCN analysis of mRNA-seq data with quasi-spatio-temporal resolution is a very helpful approach to identify novel fungal virulence and plant immunity genes, and with the created datasets made public, this will be an interesting and valuable resource for the community. The identification and functional analysis of FgKnr4 works as proof-of-principle. If the data presentation is improved, I believe that this will be an interesting publication.

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      Reply to the reviewers

      Manuscript number:

      RC-2024-02569

      Corresponding author(s): Mary O'Riordan, Teresa O'Meara

      1. General Statements

      We thank the reviewers for their positive feedback, highlighting the significance and novelty of our work, especially regarding the novel functions of IRE1a in regulating phagosome biology during infection. We also appreciate some overarching themes that were focused on by multiple reviewers, including the role of XBP1S protein and RIDD activity, which we have addressed here. We have also added additional data, made adjustments to data presentation, and added clarifying language to address concerns from Reviewer 3. We appreciate these constructive suggestions and include our planned experiments to address reviewer concerns here. Our specific responses to the reviewer comments are below.

      Specific figures used in the response to reviewers are in the attached file as they cannot be pasted here.

      2. Description of the planned revisions

      Reviewer 1:

      1) The demonstration of protein misfolding independent IRE1 activation should also be demonstrated using molecules such as TUDCA or 4PBA that should be innocuous regarding the splicing of XBP1s. It would also be interesting to evaluate the activation of the other arms of the UPR in particular through the phosphorylation of eIF2a, expression of ATF4 and cleavage of ATF6.

      We appreciate the suggestion to strengthen our data regarding protein misfolding-independent activation of IRE1 more robust. We note that canonical UPR transcriptional targets are not induced during C. albicans infection (Fig. 2G,H), suggesting that IRE1 is activated in the absence of a standard unfolded protein response. However, we agree that we can use additional chemical chaperones to assay this. To address this point, we will perform the suggested experiments in the presence or absence of TUDCA with C. albicans, LPS, thapsigargin, and tunicamycin. As 4PBA has been shown to inhibit protein synthesis, rather than promoting protein folding or preventing aggregation (PMC9741500), we will avoid using this compound for these assays.

      We will also perform western blots for ATF6 cleavage and eIF2a phosphorylation, although we note that eIF2a can be phosphorylated by multiple kinases and can be triggered by nutrient deprivation or changes in intracellular calcium, both of which occur during C. albicans infection (glucose: PMC6709535; calcium: data within this manuscript).

      3) The authors use thioflavin to evaluate the extent of protein misfolding. This type of stain can lead to artefactual results and in general it is rather safer to test several stainers (see for instance the work presented in PMC10720158)

      We thank the reviewer for this suggestion. We have previously tried Proteostat staining as an additional method to measure protein misfolding, but we found that it bound strongly to the C. albicans cell wall, which would result in a strong false positive signal that is not indicative of host protein misfolding (see below). Congo Red, an additional dye used in the listed reference, is also known to bind to C. albicans and perturbs cell wall synthesis (PMC266468), therefore we have avoided these dyes.

      However, to address this point, we will perform experiments utilizing poly-ubiquitin blotting, as in the suggested reference, as an orthogonal readout of protein misfolding during C. albicans infection or treatment with LPS, depleted zymosan, and thapsigargin.

      __Figure legend: Proteostat staining with _C. albicans_ infection. __Macrophages were infected with C. albicans, and subsequently stained with Proteostat to measure protein misfolding. Proteostat bound and displayed strong fluorescence on the C. albicans cell wall.

      6) The whole study relies on the use of IRE1deltaR to impair IRE1 signaling. The authors should validate their hypothesis with an orthogonal approach, for instance with IRE1 pharmacological inhibitors (eg MKC8866 or KIRA8).

      We consider the use of genetic perturbation of IRE1 to be a strength of this manuscript, as IRE1 inhibitors have been shown to cause off-target effects (KIRA8: PMC9600248). However, to address this point, we will attempt to replicate important phenotypes, including the effect of IRE1 on calcium flux and phagolysosome fusion, using MKC8866 and KIRA8 as representative inhibitors.

      3. Description of the revisions that have already been incorporated in the transferred manuscript

      __Reviewer 1: __

      5) The authors focus on the IRE1/XBP1s signaling arm of the UPR but do not explore RIDD activity which has been linked to several infection mechanisms and lysosomal integrity (in particular by regulating the expression of BLOS1 - see PMC9119680 and PMC6446841). The authors should definitely evaluate how RIDD is activated (or not) in their experimental systems.

      We thank the reviewer for this suggestion, as we have considered potential effects of RIDD when analyzing our RNA-seq data, and are aware of the potential links between IRE1, BLOS1 (encoded by Bloc1s1) expression, and lysosome perturbations. We now add additional figures to our supplemental data (Fig. S3C-D; also shown below) showing that established RIDD targets, including Bloc1s1 are not depleted during C. albicans infection, and also not increased in IRE1 null macrophages. We add the following text to describe these findings (lines 322-326): "Additionally, we did not observe depletion of published RIDD targets (14, 65, 66) during C. albicans infection in WT macrophages (Fig. S3C; Table S2), nor increased expression of RIDD targets in IRE1ΔR macrophages, compared to IRE1 WT macrophages (Fig. S3D; Table S1.1), suggesting minimal RIDD activity during C. albicans infection." We also note that experiments with LysoSensor (Fig. 3E) suggested lysosome biogenesis is not impaired in IRE1 null macrophages. Therefore, we expect RIDD activity has negligible effects on our reported phenotypes.

      Reviewer #1 (Significance (Required)):

      The manuscript is interesting and highlights novel aspects towards the interaction between macrophages and a pathogen, candida albicans, involving the likely selective activation of IRE1. The data are novel and experimentally sound. Several controls are however missing.

      The strengths of the study are associated with the novelty of the findings, with the links that could potentially derive from this study to connect ER biology, UPR signaling and phagosome maturation

      The main weaknesses are associated i) with the fact that the authors did not evaluate RIDD activity which has already been linked with pathogen infection and with lysosome integrity, ii) with methodological aspects, in particular regarding the demonstration of the IRE1 activation independent on protein misfolding and the sole use of a genetic variant of IRE1 to test their hypotheses

      We thank Reviewer 1 for their constructive feedback and for noting the novelty of our findings. We believe that the data we have added regarding RIDD activity and our planned experiments to address additional concerns will add additional evidence to support our findings.

      Reviewer 2:

      1. A point that should be addressed with more detail is the correlation of fungal killing with Ca2+ fluxes and Ire1α activity, given the well-known data regarding the strong ability of the axis dectin/SYK/phospholipase Cγ to induce Ca2+ transients, a response not shared by LPS signaling, and the sequential activation of mitochondrial Ca2+ uniporter (MCU), which is a critical element of fungal killing associated with the citrate-pyruvate shuttle as a NADPH source (Seegren et al., Cell Rep. 33: 108411, 2020). Incidentally, this paper is referred in ref. 46 as a preprint, although it was accessible in Cell Reports in 2020.

      This is an excellent suggestion; we have added this topic to our discussion (lines 605-608) and have corrected the citation.

      The assay of the expression of V-ATPase complex, mitochondrial calcium uniporter, and mitochondrial uptake 1 and 2 could shed light on the dependence of fungal killing on Ire1α function.

      Thank you for this suggestion - below, we plot the transcripts comprising the V-ATPase, as well as Mcu, Micu1, and Micu2. We note that these transcripts are not perturbed in IRE1 null macrophages, suggesting that the basic functions of the V-ATPase complex and mitochondrial calcium uptake are intact in IRE1 null macrophages.

      These data are in agreement with our LysoSensor assay (Fig. 3E), which suggested that lysosome biogenesis is not impaired in IRE1 null macrophages.

      While we cannot rule out a defect in mitochondrial calcium flux from our RNA-seq data, we have added discussion around this topic to our discussion, as mentioned above.

      Expression of V-ATPase subunits and mitochondrial calcium uptake genes in C. albicans-infected IRE1 null macrophages vs C. albicans-infected IRE1 WT macrophages.

      Fig. 1A should be explained with more detail to disclose the products of PstI digestion.

      Thank you for the suggestion. We have added this information to the Figure 1 legend, "RT-PCR-amplified Xbp1 cDNA was treated with PstI, which recognizes a cleavage site within the 26 base pair intron that is removed by IRE1α activity, resulting in cleavage of the unspliced isoform, specifically."

      The anti-XBP1 antibody used to construct the blots in Fig.S1A recognizes epitopes not disclosed by the manufacturers, but they have to pertain to the N-terminal peptide sequence shared by sXBP1 and uXBP1. Showing full lanes encompassing both protein isoforms would allow a better appraisal of protein expression. In connection to point 4, the use of an antibody reactive to the epitopes expressed in sXBP1 in cell lysates or, preferentially in nuclear fractions, could be most valuable to rule out the dependence of the effect of Ire1α on the trans-activating function of sXBP1.

      We have un-cropped these westerns and now show spliced and unspliced XBP1 products on a single image in Fig. S1A.

      On page 23, the mention to Fig. 5A should be changed to Fig. 5B.

      We have fixed this mis-labeling, thank you for calling this to our attention.

      Line 209. I understand gene synthesis refers to gene expression.

      We have clarified this in the text, thank you for the suggestion.

      Line 394. What is the reason to study the cytokine-signature of Candida in LPS-primed cells?

      Thank you for the question; we have added the following text (lines 413-414) to clarify that LPS is used for inflammasome priming:

      "Therefore, we tested secretion of IL-1β, TNF, and IL-6 from WT and IRE1ΔR macrophages after LPS treatment to transcriptionally prime the NLRP3 inflammasome components, followed by C. albicans infection (Fig. 5D-F)."

      Numerous studies have shown that C. albicans can trigger macrophage pyroptosis, resulting in production of pro-inflammatory cytokines like IL-1b, which can also be influenced by phagosome rupture (PMC3910967). However, this requires inflammasome transcriptional priming, and LPS is commonly used to prime macrophages for inflammasome activation in vitro. Therefore, we perform a short pre-treatment with LPS for NLRP3 inflammasome priming to subsequently measure its activation following C. albicans infection, using secreted cytokines as a readout. We also note that macrophages in vivo may not be naive and are often M1-polarized by the microbial or cytokine environment, thus inflammasome priming is likely common during in vivo infection.

      Reviewer #2 (Significance (Required)):

      This study focuses on an aspect not usually addressed in papers devoted to the UPR.

      If more data are shown as suggested, the paper could be of interest for a wider audience

      We thank the reviewer for their positive feedback about the novelty of our work and agree that the suggested experiments will bolster our data and story.


      Reviewer 3:

      Fig. 2:

      Panel A-B: same question as for Fig. 1. The variation in TG DMSO-induced splicing is huge. The effects of the treatments with CHX or Act D are smaller than the variation between experiments with TG DMSO alone. As long as that variation is not controlled for, it is impossible to draw any conclusion from the inhibitors. In this regard, it is very difficult to interpret data if they are not done in one and the same experiment.

      The variability in thapsigargin fold change over mock likely represents differences in basal Xbp1 expression. We consistently see complete Xbp1 splicing in response to thapsigargin treatment (see Fig. 1A). Additionally, we note that thapsigargin treatment is used only as a positive control, not as a physiologically relevant treatment, as it results in unmitigated ER stress that triggers cell death (PMC6986015).

      We have removed the following sentence, "Translation inhibition using cycloheximide was sufficient to alleviate Xbp1 splicing specifically in response to thapsigargin, likely by reducing the nascent protein folding burden (Fig. 2B)," since our data are plotted on separate graphs, matched to their respective controls, for appropriate comparisons.

      4. Description of analyses that authors prefer not to carry out


      Reviewer 1:

      2) Since the IRE1/XBP1 arm of the UPR is also involved in lipid biosynthesis which might be required for phagosome maturation, the authors should perform XBP1s rescues in IRE1 deficient cells to ensure that their observation is XBP1s dependent or IRE1 dependent.

      As we do not see XBP1S protein induced in wild-type macrophages at any timepoint during our C. albicans infection scheme (Fig. S1A-B), we interpret our results as being XBP1S-independent. If we were to add back XBP1S with constitutive expression, we would be overexpressing the protein relative to C. albicans infected wild-type macrophages (in which we do not see measurable XBP1S expression). Therefore, we believe these experiments would not address a physiologically-relevant scenario.

      4) The authors should evaluate in what compartment IRE1 is activated upon CA infection, does that happen in the ER or in the ER fraction fused to phagosomes?

      This is an interesting question for future exploration. In order to answer this question with existing tools, we would need to perform biochemical fractionation of infected cells to isolate an ER-phagosome contact site fraction, followed by phos-tag gel analysis of IRE1 activation in the ER fraction, compared to the ER-phagosome contact site fraction. However, a biochemical fractionation protocol to distinguish the ER fraction from ER-phagosome contact sites has not yet been developed, to our knowledge, and we believe it is outside the scope of this study to develop such a technique.

      We have added additional text regarding this intriguing question to our discussion (lines 549-553).

      Reviewer 2:


      Infection at a MOI 1 of C. albicans is a ratio of infecting agent/susceptible targets not very high for a non-soluble stimulus with limited diffusion in the culture medium. Although I recognize the difficulty of quantitating adhered cell, the mention to 80% confluence makes it more difficult the appraisal of the actual MOI. The delayed time-course of Xbp splicing under these conditions can be explained by the time required for in vitro proliferation, Candida damage, and diffusion of fungal patterns. A study with viable Candida at MOI 5 in human monocyte-derived dendritic cells, which show a robust capacity for non-opsonic phagocytosis associated with C-type lectin receptors only showed initial hypha formation after 2 hours (Rodriguez et al., J. Biol. Chem. 289, P22942-22957, 2014). Consistent with the requirement of a time lag for infecting agent to attain levels of expression consistent with a net response, 16 hours have been considered an appropriate time-course to assay sXBP1 expression following SARS-CoV2 infection (Fernandez et al., Biochim Biophys Acta Mol Basis Dis. 1870(5):167193, 2024). I wonder if a higher MOI could show a similar kinetics.

      We use lower MOI in part due to the size and ability of C. albicans to undergo extensive hyphal growth if its numbers greatly exceed the number of host cells. From our microscopy data, we can see that C. albicans spreads well throughout the culture plate (see Fig. 3A, Fig. 4A). We and others have observed considerable death of macrophage cultures after 12 hours with Candida infection, even at low MOI (PMC6709535), therefore we avoid later timepoints in these assays and all other in vitro assays in our manuscript.

      As all of our in vitro experiments are performed within an 8 hour window of infection, whether XBP1S is induced at later timepoints by C. albicans or depleted zymosan would not alter the conclusions of the rest of our results.

      sXBP1 can be present in nuclear fractions in resting cells, which suggests the involvement of post-translational modifications for the display of transcriptional activity.

      As we do not see induction of XBP1S in our lysates after C. albicans infection, it is unlikely that post-translational modification is influencing its function, although we agree post-translational modification is a likely regulatory control over XBP1S during the unfolded protein response.

      The independence of sXBP1 transcriptional activity from canonical UPR associated with misfolded protein stress is well known from the seminal paper by Martinon et al., (ref.6). Moreover, the expression of CHOP, the final effector of the PERK route, encoded by DDIT3 gene, has been found to be blunted by Candida (Rodriguez et al., J. Biol. Chem. 289, P22942-22957,2014). This is additional evidence for the recruitment of sXBP1 transcriptional activity in the absence of canonical UPR.

      As mentioned, we found that XBP1S protein is not induced during C. albicans infection at any timepoint in our experiments (Fig. S1A-B). Importantly, the work referenced by the reviewer uses RAW267.7 cells, which (as mentioned by the authors) constitutively express CHOP as a result of Abel leukemia virus infection. Based on this specific overexpression, we believe this phenotype is not comparable to our bone marrow-derived macrophages.

      Reviewer 3:

      Fig. 1:

      Panel 1C: please remove outlier in 4h timepoint. This implies that the experiment needs to be redone to reduce variation

      We have performed an outlier test on these data, which revealed that this data point is not a statistical outlier, therefore we do not feel that its removal is appropriate (see below).

      Panel 1E-H: how is the splicing efficiency determined and normalized? How to explain the big differences in splicing efficiency of Xbp1 upon LPS stimulation (appr. 4 to 6 times in E, G and H versus 30-fold in panel F). Where does this difference come from?

      Panel H, outlier needs to be removed.

      We do occasionally see differences in magnitude of Xbp1 splicing in different cell lines or experiments, especially with controls, which may be caused by differences in the basal level of Xbp1 expression, especially as Xbp1 levels have been shown to be affected by circadian rhythm in certain cell types (PMCID: PMC11214543; PMCID: PMC6959563).

      In panel H, an outlier test reveals that these are not statistical outliers, therefore we feel their removal is inappropriate as we do not wish to mask biological variation. Moreover, this graph includes two cell lines (open and closed circles), showing that our data are robust across multiple independent cell lines and are an appropriate measure of experimental replicates.

      Fig. 2:

      Panel A-B: same question as for Fig. 1. The variation in TG DMSO-induced splicing is huge. The effects of the treatments with CHX or Act D are smaller than the variation between experiments with TG DMSO alone. As long as that variation is not controlled for, it is impossible to draw any conclusion from the inhibitors. In this regard, it is very difficult to interpret data if they are not done in one and the same experiment.

      The variability in thapsigargin fold change over mock likely represents differences in basal Xbp1 expression. We consistently see complete Xbp1 splicing in response to thapsigargin treatment (see Fig. 1A). Additionally, we note that thapsigargin treatment is used only as a positive control, not as a physiologically relevant treatment, as it results in unmitigated ER stress that triggers cell death (PMC6986015).

      We have removed the following sentence, "Translation inhibition using cycloheximide was sufficient to alleviate Xbp1 splicing specifically in response to thapsigargin, likely by reducing the nascent protein folding burden (Fig. 2B), since our data are plotted on separate graphs, matched to their respective controls, for appropriate comparisons.

      Below, we plot all data together with replicate matching, although our major interpretation of these data is that C. albicans infection can trigger Xbp1 splicing with or without new gene expression, and not about the impact of the inhibitors on the control treatment thapsigargin.

      Please provide a scheme of how the experiment was performed, at what time were the inhibitors provided, at what time point the inducers? What are matched mock samples. Which mock samples were chosen since they differ from one experiment to the next? Please plot all the data for one and the same experiment in one graph so that the reader can easily compare the results of DMSO, DMSO + inducer, DMSO + inducer + inhibitor. Indicate whether the points in the graph are technical or experimental repetitions.

      -How to explain the increase in XBP1 splicing in combination with ActD? Was this due to differences in Gapdh expression? Where did the authors control for cell death? Please provide the data.

      Below is a scheme of the experimental treatments. We have now clarified in the figure legend that inhibitors (ActD and CHX) are added at the same time as experimental treatments (Mock, Ca, TG). All data included in the original submission are biological replicates, as stated in the figure legend. We have now re-written the figure legend to clearly indicate that these are biological replicates.

      All data are normalized such that the effects of the drugs are directly compared (for example, the fold change over Mock for Candida is matched to its drug treatment; Mock DMSO vs Ca DMSO and Mock ActD vs Ca ActD, or Mock CHX vs Ca CHX). Actinomycin D does inhibit new transcription, although IRE1 can cleave existing Xbp1 transcript. We now show conditions normalized to DMSO Mock in Supplemental Figure 2, which allows visualization of the effects of ActD and CHX on Xbp1-S abundance in comparison to control DMSO treatment, while also seeing the relative changes in Xbp1 splicing caused by C. albicans or thapsigargin treatment (see below).

      -Is RT-qPCR a reliable readout when actinomycinD is used? How can new genes be transcribed.

      We interpret RT-qPCR data as a readout of transcript abundance, rather than transcription. Therefore, we are not measuring new gene expression here, but whether the existing Xbp1 transcript can be cleaved by IRE1. Based on the technique, we can still measure changes in Xbp1-S abundance.

      Panel D: where is TG at 4h and 6h?

      We do not include thapsigargin at later timepoints to avoid autofluorescence from excessive cell death. We include thapsigargin as a positive control at the early 2h timepoint, but note that LPS is sufficient to increase thioflavin T intensity at the 8h timepoint.

      Panel G, why was Ddit3 included here as this is not a typical IRE1 dependent gene (rather PERK dependent). What about IRE1 specific genes such as Sec61 or Sec24a?

      We have added additional text (lines 235-240; "Finally, we measured induction of UPR-responsive genes by RT-qPCR in response to C. albicans infection, LPS and depleted zymosan treatment, or thapsigargin treatment, to further test whether IRE1α activation occurs without canonical UPR induction (Fig. 2G-H). C. albicans infection and depleted zymosan treatment did not lead to induction of UPR-responsive genes (Ddit3, Grp78, Grp94, and total Xbp1) at 4 or 6 hours.") to clarify that the purpose of this figure is to add evidence that IRE1 activation is independent of the canonical UPR response (indicating that IRE1 is likely specifically activated independently of the other UPR branches) during C. albicans infection. Therefore, the transcripts measured are canonical UPR-responsive transcripts, rather than IRE1/XBP1S targets (although some are overlapping).

      Below are RNA-seq data comparing Sec61a1, Sec61a2, and Sec24a in IRE1 null macrophages, compared to IRE1 WT macrophages. While there is less expression of Sec61a1 in IRE1 null macrophages, Sec61a2 and Sec24a are largely unaffected. These data support our finding that XBP1S protein is not induced during C. albicans infection.

      Did the authors also check for RIDD activity?

      As mentioned above in response to Reviewer 1, we now add additional figures to our supplemental data (Fig. SX; also shown below) showing that established RIDD targets are not depleted during C. albicans infection in WT macrophages, and also not increased in IRE1 null macrophages. Therefore, we expect RIDD activity has negligible effects on our reported phenotypes.

      Fig. 3:

      Panel C and D look convincing. Lamp1 is a well-known RIDD target gene (see Osorio et al., Nat Imm, 2014). Did the authors check Lamp1 expression in presence and absence of IRE1 and could RIDD explain their phenotype?

      As shown above, Lamp1 transcript expression is not strongly perturbed in IRE1 null macrophages. If RIDD activity were depleting Lamp1 transcript abundance, we would expect to see increased Lamp1 expression in IRE1 null macrophages. We also note that our experiments using LysoSensor (Fig. 3E) suggested that lysosome biogenesis is not impaired, but more specifically, lysosome recruitment to the phagosome is impaired in IRE1 null macrophages.

      Fig. 4, but especially Fig 5 and Fig 6 suffer from very bad imaging quality. Both Fig 5A and Fig 6A are completely uninterpretable. The SRB staining is all over the cells and it is totally unclear how the authors interpret this as phagosomal leakage or not. Fig. 6A is even worse and appears nothing but vague background. It is difficult to understand how the authors make graphs based on these types of images and dare to draw any conclusions.

      In Figure 4, we observe some photobleaching from frequent image acquisition, which is necessary to capture calcium flux dynamics. Image brightness across the timecourse is adjusted in the same way such that we do not attempt to hide the effects of photobleaching. However, our analyses account for photobleaching over time, and the phagosomal calcium flux is clear and quantifiable. `

      In Figure 5, the sulforhodamine B pulse-chase assay involves loading of the endosomal system with SRB, thus the cells are expected to ingest a considerable amount of SRB and it will distribute throughout the endosomal network. However, as endosomes fuse, we also observe fusion with the C. albicans-containing phagosome and SRB will surround C. albicans hyphae. Our analysis pipeline first segments C. albicans hyphae (see below) and measures SRB signal in proximity to the phagosome. Thus, we measure loss of phagosome-associated SRB over time, as C. albicans ruptures the phagosome, in hundreds of macrophages. This is a standard assay that has been previously used for this purpose (PMID: 33022213; PMID: 30131363).

      For Figure 6, we have added additional wide-field images that we believe will clarify how these images can be readily quantified (Fig. 6A, shown below). The purpose of the previous Fig. 6A (now Fig. 6B) is to demonstrate single cell examples of live and dead C. albicans using the dual-fluorescence assay, although we quantify much wider fields for sufficient numbers. We hope the amended figures provide additional clarity.

      Fig. 7 is again an example where differences in expression are mainly due to one or a few complete outliers, and it is hard to understand why the authors did not repeat these experiments to reduce the problems in variation to get proper data sets before submission.

      After performing outlier tests, we have found a total of 4 data points that are statistical outliers from all of the panels in Figure 7. These included the highest data point in each genotype in the female IL-1Ra levels (Fig. 7A, second graph), the highest data point among the male IRE1 fl/fl mice IL-1Ra levels (Fig. 7B, second graph), and the highest data point among the male TNF levels in IRE1 fl/fl + LysM-Cre mice (Fig. 7B, third graph). We have removed these data points in our updated graphs and changed the text to only point out differences in serum TNF and IL-6 levels. Moreover, our interpretation includes that serum cytokine levels are not different in male mice. However, no other data points are statistical outliers, therefore we believe their removal is inappropriate.

      While the paper started nicely and showed an interesting hypothesis (Fig. 3), the remaining part of the paper was of very poor quality and was not ready for submission.

      We thank the reviewer for the constructive feedback and believe that the addition of data and clarifications we have added will demonstrate that our data are of sufficient quality to support our conclusions.

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      Referee #3

      Evidence, reproducibility and clarity

      Reviewer comments for "Non-canonical activation of IRE1a by Candida albicans infection promotes macrophage phagosomal calcium flux to enhance fungal killing"

      This paper describes a role for IRE1 in controlling Candida albicans (Ca) infection in macrophages. The authors show that Ca infection slightly induces IRE1 activity as monitored by XBP1 splicing, however this does not result in XBP1 protein expression, nor in IRE1-dependent target gene expression. The authors propose that IRE1 controls phagosomal maturation, as measured by defects in LAMP1 recruitment to Ca containing phagosomes. This would be due to a defect in calcium flux at the phagosomal level leading to an increased propensity to rupture and cytosolic escape of the pathogen. While the data are interesting and the defect in LAMP1 recruitment to the phagosome convincing, the majority of the data are difficult to interpret due to the poor quality. This concerns specifically all imaging experiments but also the ELISAs and qPCRs where differences are due to the effect of outliers rather than to the behavior of a complete population. Therefore, most experiments need to be redone and complemented with additional approaches before any firm conclusions can be drawn. Specific details and examples are provided below.

      Fig. 1:

      Panel 1C: please remove outlier in 4h timepoint. This implies that the experiment needs to be redone to reduce variation

      Panel 1E-H: how is the splicing efficiency determined and normalized? How to explain the big differences in splicing efficiency of Xbp1 upon LPS stimulation (appr. 4 to 6 times in E, G and H versus 30-fold in panel F). Where does this difference come from?

      Panel H, outlier needs to be removed.

      Fig. 2:

      Panel A-B: same question as for Fig. 1. The variation in TG DMSO-induced splicing is huge. The effects of the treatments with CHX or Act D are smaller than the variation between experiments with TG DMSO alone. As long as that variation is not controlled for, it is impossible to draw any conclusion from the inhibitors. In this regard, it is very difficult to interpret data if they are not done in one and the same experiment. Please provide a scheme of how the experiment was performed, at what time were the inhibitors provided, at what time point the inducers? What are matched mock samples. Which mock samples were chosen since they differ from one experiment to the next? Please plot all the data for one and the same experiment in one graph so that the reader can easily compare the results of DMSO, DMSO + inducer, DMSO + inducer + inhibitor. Indicate whether the points in the graph are technical or experimental repetitions.

      • How to explain the increase in XBP1 splicing in combination with ActD? Was this due to differences in Gapdh expression? Where did the authors control for cell death? Please provide the data.
      • Is RT-qPCR a reliable readout when actinomycinD is used? How can new genes be transcribed.

      Panel D: where is TG at 4h and 6h?

      Panel G, why was Ddit3 included here as this is not a typical IRE1 dependent gene (rather PERK dependent). What about IRE1 specific genes such as Sec61 or Sec24a?

      Did the authors also check for RIDD activity?

      Fig. 3:

      Panel C and D look convincing. Lamp1 is a well-known RIDD target gene (see Osorio et al., Nat Imm, 2014). Did the authors check Lamp1 expression in presence and absence of IRE1 and could RIDD explain their phenotype?

      Fig. 4, but especially Fig 5 and Fig 6 suffer from very bad imaging quality. Both Fig 5A and Fig 6A are completely uninterpretable. The SRB staining is all over the cells and it is totally unclear how the authors interpret this as phagosomal leakage or not. Fig. 6A is even worse and appears nothing but vague background. It is difficult to understand how the authors make graphs based on these types of images and dare to draw any conclusions.

      Fig. 7 is again an example where differences in expression are mainly due to one or a few complete outliers, and it is hard to understand why the authors did not repeat these experiments to reduce the problems in variation to get proper data sets before submission.

      While the paper started nicely and showed an interesting hypothesis (Fig. 3), the remaining part of the paper was of very poor quality and was not ready for submission.

      Significance

      The study presents interesting hypothesis but unfortunately the data are not of sufficient quality

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      Referee #2

      Evidence, reproducibility and clarity

      This an interesting report in a widely explored area. This makes it necessary to pigeonhole the new data provided by the study. The paper addresses two issues encompassing a scope distinct from studies focusing on the cytokine-signature and the role of sXbp1. This research singles out fungal killing and Ire1α versus sXbp1 function. More precisely, the reduction of cytokine expression in Ire1fl/fl LysMCre as compared to WT discloses an opposing function of Ire1α and its target sXbp1 in cytokine expression that requires mechanistic explanation.

      1. A point that should be addressed with more detail is the correlation of fungal killing with Ca2+ fluxes and Ire1α activity, given the well-known data regarding the strong ability of the axis dectin/SYK/phospholipase Cγ to induce Ca2+ transients, a response not shared by LPS signaling, and the sequential activation of mitochondrial Ca2+ uniporter (MCU), which is a critical element of fungal killing associated with the citrate-pyruvate shuttle as a NADPH source (Seegren et al., Cell Rep. 33: 108411, 2020). Incidentally, this paper is referred in ref. 46 as a preprint, although it was accessible in Cell Reports in 2020.
      2. The assay of the expression of V-ATPase complex, mitochondrial calcium uniporter, and mitochondrial uptake 1 and 2 could shed light on the dependence of fungal killing on Ire1α function.
      3. Infection at a MOI 1 of C. albicans is a ratio of infecting agent/susceptible targets not very high for a non-soluble stimulus with limited diffusion in the culture medium. Although I recognize the difficulty of quantitating adhered cell, the mention to 80% confluence makes it more difficult the appraisal of the actual MOI. The delayed time-course of Xbp splicing under these conditions can be explained by the time required for in vitro proliferation, Candida damage, and diffusion of fungal patterns. A study with viable Candida at MOI 5 in human monocyte-derived dendritic cells, which show a robust capacity for non-opsonic phagocytosis associated with C-type lectin receptors only showed initial hypha formation after 2 hours (Rodriguez et al., J. Biol. Chem. 289, P22942-22957, 2014). Consistent with the requirement of a time lag for infecting agent to attain levels of expression consistent with a net response, 16 hours have been considered an appropriate time-course to assay sXBP1 expression following SARS-CoV2 infection (Fernandez et al., Biochim Biophys Acta Mol Basis Dis. 1870(5):167193, 2024). I wonder if a higher MOI could show a similar kinetics.
      4. Fig. 1A should be explained with more detail to disclose the products of PstI digestion.
      5. sXBP1 can be present in nuclear fractions in resting cells, which suggests the involvement of post-translational modifications for the display of transcriptional activity.
      6. The independence of sXBP1 transcriptional activity from canonical UPR associated with misfolded protein stress is well known from the seminal paper by Martinon et al., (ref.6). Moreover, the expression of CHOP, the final effector of the PERK route, encoded by DDIT3 gene, has been found to be blunted by Candida (Rodriguez et al., J. Biol. Chem. 289, P22942-22957,2014). This is additional evidence for the recruitment of sXBP1 transcriptional activity in the absence of canonical UPR.
      7. The anti-XBP1 antibody used to construct the blots in Fig.S1A recognizes epitopes not disclosed by the manufacturers, but they have to pertain to the N-terminal peptide sequence shared by sXBP1 and uXBP1. Showing full lanes encompassing both protein isoforms would allow a better appraisal of protein expression. In connection to point 4, the use of an antibody reactive to the epitopes expressed in sXBP1 in cell lysates or, preferentially in nuclear fractions, could be most valuable to rule out the dependence of the effect of Ire1α on the trans-activating function of sXBP1.
      8. On page 23, the mention to Fig. 5A should be changed to Fig. 5B.
      9. Line 209. I understand gene synthesis refers to gene expression.
      10. Line 394. What is the reason to study the cytokine-signature of Candida in LPS-primed cells?

      Significance

      This study focuses on an aspect not usually addressed in papers devoted to the UPR. If more data are shown as suggested, the paper could be of interest for a wider audience

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      Referee #1

      Evidence, reproducibility and clarity

      The authors show that in macrophages, IRE1 activation (independent of improperly folded proteins) is essential to promote fungicidal activity towards candida albicans (CA) in vitro and in vivo by ensuring phagosome maturation through the preservation of calcium fluxes

      Major comments

      1. The demonstration of protein misfolding independent IRE1 activation should also be demonstrated using molecules such as TUDCA or 4PBA that should be innocuous regarding the splicing of XBP1s. It would also be interesting to evaluate the activation of the other arms of the UPR in particular through the phosphorylation of eIF2a, expression of ATF4 and cleavage of ATF6.
      2. Since the IRE1/XBP1 arm of the UPR is also involved in lipid biosynthesis which might be required for phagosome maturation, the authors should perform XBP1s rescues in IRE1 deficient cells to ensure that their observation is XBP1s dependent or IRE1 dependent.
      3. The authors use thioflavin to evaluate the extend of protein misfolding. This type of stain can lead to artefactual results and in general it is rather safer to test several stainers (see for instance the work presented in PMC10720158)
      4. The authors should evaluate in what compartment IRE1 is activated upon CA infection, does that happen in the ER or in the ER fraction fused to phagosomes?
      5. The authors focus on the IRE1/XBP1s signaling arm of the UPR but do not explore RIDD activity which has been linked to several infection mechanisms and lysosomal integrity (in particular by regulating the expression of BLOS1 - see PMC9119680 and PMC6446841). The authors should definitely evaluate how RIDD is activated (or not) in their experimental systems.
      6. The whole study relies on the use of IRE1deltaR to impair IRE1 signaling. The authors should validate their hypothesis with an orthogonal approach, for instance with IRE1 pharmacological inhibitors (eg MKC8866 or KIRA8).

      Significance

      The manuscript is interesting and highligths novel aspects towards the interaction between marcrophages and a pathogen, candida albicans, involving the likely selective activation of IRE1. The data are novel and experimentally sound. Several controls are however missing.

      The strengths of the study are associated with the novelty of the findings, with the links that could potentially derive from this study to connect ER biology, UPR signaling and phagosome maturation

      The main weaknesses are associated i) with the fact that the authors did not evaluate RIDD activity which has already been linked with pathogen infection and with lysosome integrity, ii) with methodological aspects, in particular regarding the demonstration of the IRE1 activation independent on protein misfolding and the sole use of a genetic variant of IRE1 to test their hypotheses

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      Reply to the reviewers

      Manuscript number: RC-2024-02555

      __Corresponding author(s): __Maurizio Molinari

      [Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

      • *

      If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

      1. General Statements [optional]

      We thank the 3 reviewers for the positive and constructive comments to our manuscript.

      Please see below the point-by-point responses to their suggestions.

      2. Point-by-point description of the revisions

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

      The paper proposes an interesting role for ERp44 in TMX5 retention. The authors identified a list of proposed TMX5 clients which include many Golgi localised proteins but do not discuss the role for TMX for instance in protein folding. In this context it is not absolutely clear whether TMX5 acts as a trafficking chaperone? are clients functionally engaged in the Golgi or ER or both?

      This work focuses on the crosstalk between a member of the PDI superfamily lacking a conventional cytosolic ER retention motif (TMX5), and ERp44, a PDI family member previously reported to retrieve in the ER proteins that lack the ER retention motif (ERp44). To support our conclusions on the involvement of ERp44 in control of TMX5’s intracellular distribution, we have added new data obtained by characterization of a cell line lacking ERp44, where more than 50% of TMX5 escapes ER retention (new Fig. 6).

      __We agree with the referee that the assessment of the biological role of TMX5 is of interest. We mention in this manuscript that there is a follow-up study (ongoing in the lab) on TMX5 clients and TMX5 function. More specifically, we are monitoring the action of TMX5 on the biogenesis and intracellular trafficking of class I HLA molecules, which are, besides PDI, ERp57 and ERp44, major interactors (clients) of TMX5 (please also refer to the initial and final parts of the new discussion). __

      The defining criteria for the client proteins were not included. At last, it might be of interest to evaluate for how long TMX5 clients are retained on the protein, whether it is temporary (as for instance a folding sensor) or more permanent.

      The list of interacting proteins is now available (__Data are available via ProteomeXchange with identifier PXD054716."), their selection for presentation in Figure 3B is now explained more clearly (Results, page 6). Also better explained is that we define as “clients of TMX5” those endogenous proteins that associate with TMX5, covalently, via the catalytic Cys220. The mutation of the TMX5 active site cysteine residue does not impact the covalent association of PDI, ERp57 and ERp44 with TMX5. For this reason, we do not consider these PDI family members clients of TMX5. In this submission, we explore the covalent association of ERp44 and its consequences on TMX5 subcellular distribution. Interacting via non-catalytic Cysteine residues 114 and 124 with the catalytic cysteine 29 of ERp44, we identify TMX5 as a client of the latter.__

      The preparation of figures could be greatly improved and there is some inconsistency among similar gels.


      Please refer to the point-by-point answers below.


      The proposed model of ERp44, ER retention vs ER retrieval, is unclear. Overall, there is more room for improved discussion beyond the conclusions from experiments.

      __We thank the referee for these comments. We have improved the description of the results, and we separated the Discussion (written de novo) from the Results section. __

      The ERp44 interaction is interesting especially since the protein contains an incomplete thioredoxin domain (such as ERp29, PDIA17 and 18), would the interaction between Erp44 and TMX5 be involved in some holdase/competitor role thereby allowing for client selectivity (or kinetics)? In addition, all the experiments were carried out in Hek293T or MEF cells, would the authors anticipate some interactions of TMX5 with PDIA17/18 in cells where those proteins are highly expressed? Testing whether the observation is a general mechanism occurring between TMX5 and PDI family members with incomplete thioredoxin sites would be an asset.

      __We thank the referee for this comment that we implemented in the new discussion. __

      Major comments Fig 2 - avoid labels on the blots that might obscure information and impede clarity and interpretation. o The % of resistant protein can be otherwise placed.


      __This has been modified, thank you. __

      • What does the asterix in 2B signify? This should be included in the legend.

      We have now specified in the legend of figures that asterisks show cross-reacting polypeptide bands.

      • A label for 'deglycosylated' proteins could be included.

      __We added a label for de- and for glycosylated proteins in the EndoH essays in Figs. 2A, 2B and 5B. __

      • Consider treating with PNGase.

      This is now showy in panel 2A, lane 5.

      • There is a change in EndoH resistance of about 3-4% among wt, C220A & C114A, is this significant?

      We do not consider significant these variations. Our data show that the mutation of TMX5 Cys 114 or of Cys124 to alanine substantially reduce (without abolishing) the co-IP with ERp44. This means that the proteins interact less, or that the interaction is more short living. The EndoH experiment shown in Fig. 2B and the CLSM analyses in Figs. 2D-2O fail to reveal significant differences showing that these reduced or more short living associations with ERp44 are sufficient to control TMX5 distribution.

      In the previous submission, the function of ERp44 in retaining TMX5 in the ER was supported by data showing that the co-expression of ERp44 retains TMX5 in the ER, but co-expression of ERp44C29S that cannot bind TMX5 fails to retain TMX5 in the ER. These model is further supported in this new submission by the release of 50% of TMX5 from the ER in cells lacking ERp44, which is substantially inhibited to the levels measured in wild type cells upon back-transfection of ERp44, but not upon the co-transfection of the ERp44C29S mutant (new Figure 6).


      • Equivalent inputs (cell lysates) for the IPs should be included.

      __ These have now been added in Figs. 4, 5 6, and 7.__

      Fig 3A - Indicate the specific bands that were subject to MS. How did the authors correct for non-specific interactors and false positives? Perhaps a more specifically targeted approach could be utilised.

      • How do the authors explain the absence of bands representing the reduced form of interacting TMX5 interactors?

      • What was the inclusion and exclusion criteria used to determine which of the proteins listed were clients?

      The endogenous proteins present in the entire region of the gel labeled with the red and blue rectangles have been sequenced (see methods section and this is now also better explained in the results section, page 6). Only the proteins that disappear from the corresponding region of the gel when the samples have been reduced are listed in the table. This is also better explained in the text (page 6). These experiments have been repeated few times with a series of controls (e.g., mock-transfected cells and cells transfected with other members of the TMX family (shown to capture and to impact on the fate of other endogenous polypeptides in previous publications from our lab)). An in parallel analysis of mock, TMX3, TMX4 and TMX5 interactors has been published in (Kucinska et al Nature Comm 2023), where we focused on the biological function of TMX4. The references referring to the TMX1 study (Brambilla et al 2015) and the TMX4 study (Kucinska et al) are given in the text.

      The Table in Fig. 3B only lists the interacting polypeptides that have a MW __- It might be useful to perform MS on the C220A mutant and compare those results to the WT.

      __To validate few interactions with endogenous proteins detected in MS, and to compare the interactions of TMX5 and TMX5C220A, we have used the specifically targeted approach suggested above by the referee (i.e., co-IP validated by WB, Figs. 3C-3F).

      __

      Fig 4 - Equivalent inputs (cell lysates) for the IPs should be included.

      __This is now shown as panel A in Fig. 4.____

      __

      Fig 5 - Equivalent inputs (cell lysates) for the IPs should be included.

      This is now Figure 7, see new panel 7A

      Fig 6 - A loading control should be included.

      __This is now Fig. 5. Both panels A and B in Fig. 5 show total cell extracts____

      __

      • Blot using anti-HA to identify ERp44 should be included to substantiate claims.

      The ERp44 and TMX5 components of the ERp44-s-s-TMX5 mixed disulfides are detected upon IP:HA followed by WB:V5 (to show the TMX5 component) and upon IP:V5 followed by WB:HA to show the ERp44 component) in Figs. 4B-4E and 7B-7C.

      • How do the authors account for the huge difference in TMX5 associated complexes shown in Fig 6A compared to Fig 3A.

      Fig. 6 is now Fig. 5. As specified in the legends of the figures, Fig. 3A shows a gel, where the complexes are stained with silver, Fig. 5A is a WB, where the complexes are stained with an antibody. The intensities of the signals cannot be compared.

      • Inappropriate marking on the gel area.
      • Inconsistencies in protein standard labeling

      This has carefully been checked and corrected where needed. Please note that we used two different MW standards for our figures (200, 117, 97, 66, 45, 31 kDa and 270, 175, 130, 95, 66, 53, 37 kDa)

      • It might be useful to demonstrate the colocalisation of ERp44 and ERp44C29S with Giantin and with TMX5 considering that ERp44 is known to cycle between the Golgi and ER.

      These data are shown in Fig. 5D-5I.

      Reviewer #1 (Significance (Required)):

      This work provides an additional understanding on how the regulation of Erp44 trafficking might occur (and perhaps additional PDIs), and lead to the characterization of kinetic value that might explain better productive protein folding in the early secretory pathway. This represents a significant advance in the field and may in turn unveil uncharacterized pathophysiological functions in various diseases. This is a serious study well conducted and original by an expert in the field that desserves publication.

      Field of expertise: ER homeostasis control

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

      The manuscript by Solda et al, investigates TMX5, a poorly understood member of the PDI family that lacks an ER-retrieval motif. They find that it localizes to the ER and the Golgi and that it interacts with ERp44. This interaction requires formation of a mixed disulfide and they identify the cysteine residues in both proteins that mediate this interaction. Overall, this is a well written manuscript that is easy to follow and the story is compact and straight-forward. It provides some new and solid insight into the biology of TMX5 without going into depth of what the cellular role of TMX5 is or might be. I have only very few comments and suggestions:

      1- The authors conclude that ERp44 associates only with ER-localized TMX5. I am not sure that this is a valid conclusion based on the data. EndoH sensitivity just means that the protein has not gone to the medial Golgi. The pool of TMX5 could therefore be an ERGIC-based pool, or it could interact with a TMX5 that is recycled directly from the first Golgi cisterna, where complex glycosylation is unlikely to occur. Can this be validated using another type of experiment? Alternatively, the wording could be changed.

      We thank the reviewer. We agree with this insightful comment that led us to change the wording used in some part of the text.

      2- Is the trafficking of TMX5 dependent on its glycosylation?

      This is another insightful comment that we report in the ____new discussion, where we write, page 14 “____It should be noted that in the case of TMX5 the extensive N-glycosylation could engage____ leguminous L-type lectins located in the ER (VIPL), cycling between the ER and the intermediate compartment (ERGIC) (ERGIC-53) or between the ERGIC and the cis-Golgi (VIP36)_33-36_ and have an impact on the subcellular distribution and activity of TMX5.____”

      3- Figure 6: The data are not really convincing. Just because the color turns yellow, it does not mean that there is colocalization. The green channel is overexposed in this area of the cell, and anything will produce a yellow color, even if there is no genuine colocalization. Maybe the authors could provide a different example and even better would be a quantification of the colocalization.

      __We thank the referee for this comment. We show images of better quality, where the black/white channels clearly show the co-localization (or lack thereof) of TMX5 with the Golgi marker Giantin in cells mock-transfected (co-localization TMX5:Giantin, Fig. 5D), co-transfected with ERp44 (no co-localization TMX5:Giantin, Fig. 5E), or co-transfected with ERp44C29S, co-localization TMX5:Giantin, Fig. 5F). Figs. 5G-5I show the corresponding results for the co-localization or lack thereof between TMX5C220A and Giantin. Importantly, the IF data match the data shown in Fig. 5B, where release from the ER (or arrival in the medial Golgi, see text of the manuscript and comment 1 by the referee) is assessed by monitoring complex glycosylation. __

      Reviewer #2 (Significance (Required)):

      This is a solid story that will be of interest of scientists working on various aspects of the secretory pathway and protein quality control. The advance is rather incremental, because there are no experiments that provide insight into the cellular roles of TMX5.

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

      Solda et al have assembled data on the transmembrane redox enzyme TMX5, on which currently very little information is available. TMX5 does not contain any obvious targeting signal, unlike the other TMX family proteins, which localize to the ER. TMX5 has 5 glycosylation sites, which can be used to determine its intracellular localization biochemically. Indeed, about 20% of TMX5 is found as endoH-resistant, indicating Golgi localization. This is confirmed with beautiful IF imagery and giantin co-localization. The Golgi localization requires two luminal cysteines (C212, 177), which likely form a disulfide bond. TMX5 acts as a natural cysteine-trapping protein, allowing for easy assessment of its interactors. Within its interactome, the authors found multiple members of the thioredoxin family. Many of these interactions occur within the CXXS motif, but notably ERp44 does not require this motif to interact, indicating this and other interactions are not of a catalytic nature. Instead, the authors found this interaction to be essential for ER retention or retrieval and depends on the cysteine within the ERp44 "active" site. The study provides critical first insight about the potential functions and sites of activity of TMX5.

      Specific Points: 1. The results are very convincing and of high quality. 2. The cytosolic tail of TMX5 contains an LI motif, which could act as a post-ER localization signal. Since the protein might play a role in ciliogenesis, this motif could be critical. In this context, I am wondering which mutations are known to lead to the disease spectrum.


      The position of disease-related TMX5 mutations identified so far are given in Xu H, et al (2024) Mol Genet Genomic Med 12: e2340 _https://www.ncbi.nlm.nih.gov/pubmed/38073519_ and in ____Deng T, Xie Y (2024) Mol Genet Genomic Med 12: e2343 https://www.ncbi.nlm.nih.gov/pubmed/38156946____.

      They are all distributed in the luminal part of the protein____.


      Mutation of C114 and C124 abrogates interaction with ERp44. Therefore, I would expect these mutations to increase endoH resistance and Golgi staining. This should be investigated by the authors.

      __The mutations C114 and C124 reduce (or make short-living), without abrogating the covalent association between TMX5 and ERp44. The EndoH experiment shown in Fig. 2B and the IF in Figs. 2D-2O fail to reveal significant differences showing that these reduced or more short living associations with ERp44 are sufficient to control TMX5 distribution. To strengthen our conclusion that ERp44 is involved in regulation of the intracellular TMX5 distribution, we have now added data in ERp44 cell (50% of TMX5 displays complex glycans as symptom of traffic to the medial Golgi compartment), back-transfection of ERp44 (but not of the ERp44C29S mutant that does not associate with TMX5) restores the complex glycan fraction to the level measured in wild type cells (Fig. 6). __

      Minor Points: 1. The position of the % endoH resistance in Figures 1B and 6B is not ideal, as it obstructs a visual inspection of TMX5 resistance to endoH.

      This has been modified, thank you.

      Reviewer #3 (Significance (Required)):

      Given that no information about TMX5 is currently available, the study provides critical first insight that should allow researchers to tackle the disease relevance of TMX5 in the future.

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      Referee #3

      Evidence, reproducibility and clarity

      Solda et al have assembled data on the transmembrane redox enzyme TMX5, on which currently very little information is available. TMX5 does not contain any obvious targeting signal, unlike the other TMX family proteins, which localize to the ER. TMX5 has 5 glycosylation sites, which can be used to determine its intracellular localization biochemically. Indeed, about 20% of TMX5 is found as endoH-resistant, indicating Golgi localization. This is confirmed with beautiful IF imagery and giantin co-localization. The Golgi localization requires two luminal cysteines (C212, 177), which likely form a disulfide bond. TMX5 acts as a natural cysteine-trapping protein, allowing for easy assessment of its interactors. Within its interactome, the authors found multiple members of the thioredoxin family. Many of these interactions occur within the CXXS motif, but notably ERp44 does not require this motif to interact, indicating this and other interactions are not of a catalytic nature. Instead, the authors found this interaction to be essential for ER retention or retrieval and depends on the cysteine within the ERp44 "active" site. The study provides critical first insight about the potential functions and sites of activity of TMX5.

      Specific Points:

      1. The results are very convincing and of high quality.
      2. The cytosolic tail of TMX5 contains an LI motif, which could act as a post-ER localization signal. Since the protein might play a role in ciliogenesis, this motif could be critical. In this context, I am wondering which mutations are known to lead to the disease spectrum.
      3. Mutation of C114 and C124 abrogates interaction with ERp44. Therefore, I would expect these mutations to increase endoH resistance and Golgi staining. This should be investigated by the authors.

      Minor Points:

      1. The position of the % endoH resistance in Figures 1B and 6B is not ideal, as it obstructs a visual inspection of TMX5 resistance to endoH.

      Significance

      Given that no information about TMX5 is currently available, the study provides critical first insight that should allow researchers to tackle the disease relevance of TMX5 in the future.

    3. 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 Solda et al, investigates TMX5, a poorly understood member of the PDI family that lacks an ER-retrieval motif. They find that it localizes to the ER and the Golgi and that it interacts with ERp44. This interaction requires formation of a mixed disulfide and they identify the cysteine residues in both proteins that mediate this interaction.

      Overall, this is a well written manuscript that is easy to follow and the story is compact and straight-forward. It provides some new and solid insight into the biology of TMX5 without going into depth of what the cellular role of TMX5 is or might be. I have only very few comments and suggestions:

      1. The authors conclude that ERp44 associates only with ER-localized TMX5. I am not sure that this is a valid conclusion based on the data. EndoH sensitivity just means that the protein has not gone to the medial Golgi. The pool of TMX5 could therefore be an ERGIC-based pool, or it could interact with a TMX5 that is recycled directly from the first Golgi cisterna, where complex glycosylation is unlikely to occur. Can this be validated using another type of experiment? Alternatively, the wording could be changed.
      2. Is the trafficking of TMX5 dependent on its glycosylation?
      3. Figure 6: The data are not really convincing. Just because the color turns yellow, it does not mean that there is colocalization. The green channel is overexposed in this area of the cell, and anything will produce a yellow color, even if there is no genuine colocalization. Maybe the authors could provide a different example and even better would be a quantification of the colocalization.

      Significance

      This is a solid story that will be of interest of scientists working on various aspects of the secretory pathway and protein quality control. The advance is rather incremental, because thereare no experiments that provide insight into the cellular roles of TMX5.

    4. 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 paper proposes an interesting role for ERp44 in TMX5 retention. The authors identified a list of proposed TMX5 clients which include many Golgi localised proteins but do not discuss the role for TMX for instance in protein folding. In this context it is not absolutely clear whether TMX5 acts as a trafficking chaperone? are clients functionally engaged in the Golgi or ER or both? The defining criteria for the client proteins were not included. At last, it might be of interest to evaluate for how long TMX5 clients are retained on the protein, whether it is temporary (as for instance a folding sensor) or more permanent.

      The preparation of figures could be greatly improved and there is some inconsistency among similar gels. The proposed model of ERp44, ER retention vs ER retrieval, is unclear. Overall, there is more room for improved discussion beyond the conclusions from experiments.

      The ERp44 interaction is interesting especially since the protein contains an incomplete thioredoxin domain (such as ERp29, PDIA17 and 18), would the interaction between Erp44 and TMX5 be involved in some holdase/competitor role thereby allowing for client selectivity (or kinetics)? In addition, all the experiments were carried out in Hek293T or MEF cells, would the authors anticipate some interactions of TMX5 with PDIA17/18 in cells where those proteins are highly expressed? Testing whether the observation is a general mechanism occurring between TMX5 and PDI family members with incomplete thioredoxin sites would be an asset.

      Major comments

      Fig 2

      • avoid labels on the blots that might obscure information and impede clarity and interpretation.
      • The % of resistant protein can be otherwise placed.
      • What does the asterix in 2B signify? This should be included in the legend.
      • A label for 'deglycosylated' proteins could be included.
      • Consider treating with PNGase to .....
      • There is a change in EndoH resistance of about 3-4% among wt, C220A & C114A, is this significant?
      • Equivalent inputs (cell lysates) for the IPs should be included.

      Fig 3A

      • Indicate the specific bands that were subject to MS. How did the authors correct for non-specific interactors and false positives? Perhaps a more specifically targeted approach could be utilised.
      • How do the authors explain the absence of bands representing the reduced form of interacting TMX5 interactors?
      • What was the inclusion and exclusion criteria used to determine which of the proteins listed were clients?
      • It might be useful to perform MS on the C220A mutant and compare those results to the WT.

      Fig 4

      • Equivalent inputs (cell lysates) for the IPs should be included.

      Fig 5

      • Equivalent inputs (cell lysates) for the IPs should be included.

      Fig 6

      • A loading control should be included.
      • Blot using anti-HA to identify ERp44 should be included to substantiate claims.
      • How do the authors account for the huge difference in TMX5 associated complexes shown in Fig 6A compared to Fig 3A.
      • Inappropriate marking on the gel area.
      • Inconsistencies in protein standard labeling
      • It might be useful to demonstrate the colocalisation of ERp44 and ERp44C29S with Giantin and with TMX5 considering that ERp44 is known to cycle between the Golgi and ER.

      Significance

      This work provides an additional understanding on how the regulation of Erp44 trafficking might occur (and perhaps additional PDIs), and lead to the characterization of kinetic value that might explain better productive protein folding in the early secretory pathway. This represents a significant advance in the field and may in turn unveil uncharacterized pathophysiological functions in various diseases.

      This is a serious study well conducted and original by an expert in the field that desserves publication.

      Field of expertise: ER homeostasis control

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      Reply to the reviewers

      Reviewer #1 (Evidence, reproducibility and clarity (Required)): Summary: To explore the relationship between histone post-translational modifications (H3K4me3 and H3K27me3) and enhancer activation with gene expression during early embryonic development, the authors used a monolayer differentiation approach to convert mouse embryonic stem cells (ESCs) into Anterior Definitive Endoderm (ADE). They monitored differentiation stages using a dual reporter mESC line (B6), which has fluorescent reporters inserted at the Gsc (GFP) and Hhex (Redstar) loci. Their analyses indicate that the differentiating cells advanced through stages similar to those in the embryo, successfully converting into endoderm and ADE with high efficiency. This is elegant and well performed stem cell biology.

      Their subsequent genome-wide and nascent transcription analyses confirmed that the in vitro gene expression changes correlated with developmental stages and confirmed that transcriptional activation precedes mRNA accumulation. They then focussed on linking active enhancers and histone modifications (H3K4me3 and H3K27me3) were with gene expression dynamics. Finally, the performed PRC2 inhibition and showed that, while it enhanced differentiation efficiency, it also induced ectopic expression of non-lineage specific genes.

      Major comments: In terms of mechanistic advances, they propose that transcriptional up-regulation does not require prior loss of H3K27me3, which they show appears to lag behind gene activation, but critically, on a likely mixed population level. I am sceptical of their interpretation of their data because they are looking at heterogenous populations of cells. To explain, one could imagine a particular H3K27me3 coated gene that gets activated during differentiation. In a population of differentiating cells, while the major sub-population of cells could retain H3K27me3 on this particular gene when it is repressed, a minority sub-population of cells could have no H3K27me3 on the gene when it is actively transcribed. The ChIP and RNA-seq results in this mixed cell scenario would give the wrong impression that the gene is active while retaining H3K27me3, when in reality, it's much more likely that the gene is never expressed when its locus in enriched with the repressive H3K27me3 modification. Therefore, to support their claim, they would have to show that a particular gene is active when its locus is coated with H3K27me3. Personally, I don't feel this approach would be worth pursuing.

      They also report that inhibition of PRC2 using EZH2 inhibitor (EPZ6438) enhanced endoderm differentiation efficiency but led to ectopic expression of pluripotency and non-lineage genes. However, this is not surprising considering the established role of Polycomb proteins as repressors of lineage genes.

      Reviewer #1 (Significance (Required)): I feel that this is a solid and well conducted study in which the authors model early development in vitro. It should be of interest to researchers with an interest in more sophisticated in vitro differentiation systems, perhaps to knockout their gene of interest and study the consequences. However, I don't see any major mechanistic advances in this work.

      *>Author Response *

      *We agree with the point regarding the delayed loss of H3K27me3 relative to gene activation, and indeed this same point has been raised by reviewer 3 (see below). Our cell-population based data does not allow us to directly test if gene up-regulation in a small population of cells from TSSs lacking H3K27me3, accounts for the observed result. Furthermore, there are currently no robust methods to determine cell- or allele-specific expression simultaneously with ChIP/Cut and Run for chromatin marks. However, we provide the following additional evidence that strongly supports our conclusions. *

      • *

      Our FACs isolation strategy used to prepare cell populations for ChIP, microarray expression and 4sU-seq analysis is based on expression (or lack thereof) of a fluorescent GSC-GFP reporter. This means that every cell in the G+ populations express the Gsc fluorescent reporter, at least at the protein level, at the point of isolation. This is despite the presence of appreciable and invariant levels of H3K27me3 at the TSS of the Gsc gene in both G+ and G- populations at day 3 of differentiation. Comparable to our meta-analysis of all upregulated genes shown in the original manuscript (Figure 5 and S5), H3K27me3 levels are then subsequently reduced in the G+ relative to the G- populations at day 4. The transcriptional changes which correspond to the GSG-GFP reporter expression and associated ChIP-seq data are shown in the reviewer figure (Fig R1 A shown in revision plan). To further support our observations, we sought to rule out the possibility that the shift in H3K27me3 and transcription were from mutually exclusive gene sets, from nominal transcription levels or from sites with low level H3K27me3. To do this with a gene set of sufficient size to yield a robust result, we selected upregulated TSSs that had a greater than median value for both transcription (4sU-seq) and H3K27me3 (n=49 of 159 genes; Fig R1 B shown in revision plan). Meta-analysis of these genes showed that, as for all upregulated gene TSS (n=159), transcriptional activation occurred in the presence of substantial and invariant levels of H3K27me3 at day 3 followed by a subsequent reduction by day 4 of differentiation (Fig R1 C shown in revision plan). Importantly, many of these genes yielded high absolute 4sU-seq signal, comparable to that of Gsc, arguing against transcriptional activation being limited to a small subpopulation of cells.

      • *

      Reviewer #2 (Evidence, reproducibility and clarity (Required)): In this paper the authors profile gene expression, including active transcription, and histone modifications (k4 and k27me3) during a complex differentiation protocol from ES cells, which takes advantage of FACS sorting of appropriate fluorescent reporters. The data is of good quality and the experiments are well performed. The main conclusion, that the analyzed histone marks channel differentiation more than they directly allow/block it, is well supported by the data. The paper is interesting and will represent a good addition to an already extensive literature. I have however a few major concerns, described below:

      1/ K4me3 may show more changes than they interpret, at least over the +1 nucl. An alternative quantification to aggregate profiles should be used to more directly address the questions regarding the correlations between histone mods and gene expression.

      *>Author Response *

      *Whilst we state that H3K4me3 levels are somewhat invariant at differentially expressed genes relative to H3K27me3, quantification of individual TSS (+/- 500 bp) did show a direct correlation with gene expression (Figure 5 and S5). To further explore this in response to the reviewer’s comment we will quantify K4me3 signal at the +1 nucleosome to determine if this yields more substantial differences than that observed more broadly across TSSs. *

      2/ Related to the previous point, it appears clear in Fig.4 that the promoters of each gene expression cluster do not belong to a single chromatin configuration. I think it would be important to: 1/ cluster the genes based on promoter histone mods and interrogate gene expression and cluster allocation (basically the reverse to what is presented) 2/ order the genes in the heatmaps identically for K4me3 and K27me3 to more easily understand the respective chromatin composition per cluster

      >Author Response

      We thank the reviewer for these suggestions and will include these analyses in a revised manuscript.

      3/ Also, as it is apparent that not all promoters in every cluster are enriched for the studied marks, could the authors separately analyze these genes? What are they? Do they use alternative promoters?

      >Author Response

      *Indeed, this is the case. Whilst there is significant enrichment of H3K27me3 at the TSS of developmentally regulated genes, not all genes whose expression changes during the differentiation will be polycomb targets. We will further stratify these clusters as suggested and determine what distinguishes the subsets. If informative, this data will be included in a revised manuscript. *

      4/ The use of 4SU-seq to identify active enhancers is welcome; however, I have doubts it is working very efficiently: for instance, in the snapshots shown in Fig.2A, the very active Oct4 enhancers in ES cells are not apparent at all... More validation of the efficiency of the approach seems required.

      >Author Response

      The 4sU-seq data shown in Figure 2A was generated in samples isolated from day 3 and 4 of the ADE differentiation. It is therefore likely that the enhancers have been partly or wholly decommissioned at this point. Indeed, in a separate study we generated 4sU-seq data using the same protocol and conditions as presented here but in ES cells and differentiated NPCs (day 3 to 7) and indeed see transcription at Oct 4 enhancers in ESCs (arrowed in the screenshot shown in revision plan) which are extinguished upon differentiation to neural progenitor cells (NPCs); data from PMID: 31494034).

      5/ The effects of the EZH2 inhibitor are quite minor regarding the efficiency of the differentiation as analyzed by FACS, despite significant gene expression changes. To the knowledge of this referee, this is at odds with results obtained with Ezh2 ko ES cells that display defects in mesoderm and endoderm differentiation. I have issues reconciling these results (uncited PMID: 19026780). Either the authors perform more robust assays (inducible KOs) or they more directly explain the limitations of the study and the controversies with published work.

      >Author Response

      We agree that this result appears to be at odds with the findings in (PMID: 19026780*). This is likely due to the fact that we are acutely reducing H3K27me3 levels for a short period either during or immediately preceding the differentiation rather than removing PRC2 function genetically. This, likely provides a less pronounced defect on the ability to generate endodermal cells. However, we cannot address this without further experimentation which is beyond the scope of this study. We will more fully discuss the results in the context of this and other studies and discuss the limitations of the study in this regard. *

      Minor 1/ please add variance captured to PCA plots 2/ Fig1E add color scales to all heatmaps 3/ Fig4C,D are almost impossible to follow, please find a way to identify better the clusters/samples and make easier to correlate all the variables

      • *

      >Author Response

      *We will address all of these points in a revised manuscript. *

      Reviewer #2 (Significance (Required)):

      The paper is incremental in knowledge, and not by a big margin, as it is known already that histone mods rather channel than drive differentiation. Though, the authors do not clearly address inconsistencies with published work, especially regarding Ezh2 thought to be important to make endoderm. It is however a good addition to current knowledge, provided a better discussion of differences with published work is provided.

      >Author Response

      *As outlined above, we will address this with a more complete discussion about the distinction between the studies and what can and can’t be concluded from our approach. *

      * *

      • *

      Reviewer #3 (Evidence, reproducibility and clarity (Required)): This study investigates the role of chromatin-based regulation during cell fate specification. The authors use an ESC model of differentiation into anterior primitive streak and subsequently definitive endoderm, which they traced via a dual-reporter system that combines GSC-GFP and HHEX-RedStar. The authors mapped changes in (nascent) gene expression and histone modifications (H3K4me3/H3K27me3) at key timepoints and within different populations over six days of differentiation. Finally, the authors test the functional implications of H3K27me3 landscapes via PRC2 inhibition.

      The majority of data chart the descriptive changes in (epi)genomic and transcriptional dynamics coincident with cell differentiation. The use of nascent transcriptomics improves the temporal resolution of expression dynamics, and is an important strategy. By and large the data reinforce established paradigms. For example, that transcription is the dominant mechanism regulating mRNA levels, or that dynamic chromatin states changes occur and largely corelate of gene activity. They also identify putative enhancers with profiling data, albeit these are not validated, and confirm that PRC2 inhibition impacts cell fate processes - in this case promoting endodermal differentiation efficiency. Overall, the study is relatively well-performed and clearly written, with the omics profiling adding more datasets from in vitro cell types that can be difficult to characterise in vivo. Whilst the majority of the study may be considered incremental, the key finding is the authors conclusion that H3K27me3 is subordinate to gene activity rather than an instructive repressor. If borne out, this would mark an important observation with broad implications. However, in my view this conclusion is subject to many confounders and alternative interpretations, and the authors have not ruled out other explanations. Given the centrality of this to the novelty of the study, I would encourage further analysis/stratification of existing data, and potentially further experiments to provide more confidence in this key conclusion.

      Primary issue 1.) The authors show that at the earliest timepoint (d3), nascent gene activation of a handful of genes between G+ and G- populations is not associated with a FC loss of H3K27me3. From this the authors extrapolate their key conclusion that H3K27me3 is subordinate. Causality of chromatin modifications in gene regulation is critical to decipher, and therefore this is an important observation to confirm. Below I go through the possible confounders and issues with the conclusion at this point.

      (i) Single-cell penetrance. A possible (likely?) possibility is that gene activation initially occurs in a relatively small subset of cells at d3. Because these genes are expressed lowly prior to this, they will register as a significant upregulation in bulk analysis. However, in this scenario H3K27me3 would only be lost from a small fraction of cells, which would not be detectable against a backdrop of most cells retaining the mark. In short, the authors have not ruled out heterogeneity driving the effect. Given the different dynamic range of mRNA and chromatin marks, and that a small gain from nothing (RNA) is easier to detect than a small loss from a pre-marked state (chromatin), investigating this further is critical to draw the conclusions the authors have.

      (ii) Initial H3K27me3 levels. The plots in Fig 5 show the intersect FC of H3K27me3 and gene expression. Genes that activate at d3 show no loss of H3K27me3. However, it is important to characterise (and quantitate) whether these genes are significantly marked by H3K27me3 in the first place, which I could not find in the manuscript. Many/several of the genes may not be polycomb marked or may have low levels to begin with. This would obviously confound the analysis, since an absence/low K27 cannot be significantly lost and is unlikely to be functional. Thus, the DEG geneset should be further stratified into H3K27me3+ and K27me3- promoter groups/bins, with significance and conclusions based on the former only (e.g. boxplot in 5F).

      (iii) Sample size. The conclusions are based on a relatively small number of genes that upregulate between G+ and G- (n=55 in figure by my count, text mentions n=52). Irrespective of the other confounders above, this is quite a small subset to make the sweeping general conclusion that "loss of the repressive polycomb mark H3K27me3 is delayed relative to transcriptional activation" in the abstract. Indeed, the small number of DEG suggests the cell types being compared are similar and perhaps therefore have specific genomic features (this could be looked at) that drive .

      >Author Response

      *These are very good points and are also raised by reviewer 1 (see above). We have one example where we can definitively interrogate single cell protein expression, in our current data. Gsc (as monitored by GSC-GFP FACS and the bulk RNA analysis) meets the criteria of being robustly upregulated in all FACs sorted cells in the presence of high levels of H3K27me3 in the D3G+ population. We believe that the additional analysis (Figure R1A shown in revision plan) and the discussion above addresses the reviewer’s concerns about both the levels of expression and magnitude of H3K27me3. With respect to the third point, the numbers are low (although here I present data from the 4SU analysis with approximately three times more data points) however, the point here is not too say this happens in every instance of gene activation but more that it can happen and not just at a small subset of outlier genes. This is important, as the reviewer notes, in our understanding of how polycomb repression is relieved during development. We will also look to see if there are sequence characteristics/ motifs of these genes. In a revised manuscript we would include this data and further analysis as outlined above. The reviewer points out that the numbers vary a little between analyses. This arises due to the annotation of multiple TSSs per genes in some cases. This will be rectified throughout and made clearer in the legends. *

      Other comments: 2.) The authors show that promoter H3K4me3 corelates well with gene expression dynamics in their model. They conclude that "transcription itself is required for H3K4me3 deposition", or in other words is subordinate. This may well be the case but from their correlative data this cannot be inferred. Indeed, several recent and past papers have shown that H3K4me3 itself can directly modulate transcription, for example by triggering RNA II pause-release, by preventing epigenetic silencing and/or by recruiting the PIC. The authors could point out or discuss these alternative possibilities to provide a more balanced discourse.

      >Author Response

      We agree and this will be discussed more thoroughly and both possibilities put forward in the revised manuscript.

      3.) The labelling of some figures is unclear. In Fig 4C and 4D (right) it is impossible to tell what sample each of the lines represents. It is also not clear what the blue zone corresponds to in genome view plots (the whole gene?). Moreover, the replicate numbers are not shown in figure legends.


      >Author Response

      *We agree that the data presented in 4C and D is unclear. We will, as a minimum, collapse profiles into like populations (ESC / G- / G+ / G+H- / G+H+) which makes sense given the similarity of these populations across all analyses (see e.g. PCA analysis in Figure 1). We will also explore alternative ways of presenting the data to better highlight the dynamics and incorporate this with the changes suggested by reviewer 2. The blue shaded area represents the full extent of the key gene being discussed in the screen shot, this is mentioned in the legend but will be made clearer in a revised manuscript. Replication will also be added to the legend throughout (n=2 for ChIP-seq and n=3 for 4sU-seq). *

      4.) It would be nice to provide more discussion to reconcile the conclusions that H3K27me3 in endoderm differentiation is subordinate and the final figure showing inhibiting H3K27me3 has a significant effect on differentiation, since the latter is the functional assessment.

      >Author Response

      *We will build on the points already made that suggests that whilst K27me3 is a passive repressor that serves to act against sub-threshold activating cues, it is nonetheless a critical regulator of developmental fidelity. *

      Reviewer #3 (Significance (Required)): Overall, the study's strengths are in that it characterises epigenomic dynamics within a specific and relevant cell fate model. The nascent transcriptomics adds important resolution, and underpins the core conclusions. The weakness is that data is over-interpreted at this point, and other possibilities are not adequately tested. The conclusions should therefore either be scaled back (which reduces novelty) or further analysis and/or experiments should be performed to support the conclusion. If it proves correct, this would be a significant observation for the community,

      >Author Response

      In a revised manuscript, we will address the reviewer’s concerns with additional data and discussion as indicated above.

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      Referee #3

      Evidence, reproducibility and clarity

      This study investigates the role of chromatin-based regulation during cell fate specification. The authors use an ESC model of differentiation into anterior primitive streak and subsequently definitive endoderm, which they traced via a dual-reporter system that combines GSC-GFP and HHEX-RedStar. The authors mapped changes in (nascent) gene expression and histone modifications (H3K4me3/H3K27me3) at key timepoints and within different populations over six days of differentiation. Finally, the authors test the functional implications of H3K27me3 landscapes via PRC2 inhibition.

      The majority of data chart the descriptive changes in (epi)genomic and transcriptional dynamics coincident with cell differentiation. The use of nascent transcriptomics improves the temporal resolution of expression dynamics, and is an important strategy. By and large the data reinforce established paradigms. For example, that transcription is the dominant mechanism regulating mRNA levels, or that dynamic chromatin states changes occur and largely corelate of gene activity. They also identify putative enhancers with profiling data, albeit these are not validated, and confirm that PRC2 inhibition impacts cell fate processes - in this case promoting endodermal differentiation efficiency. Overall, the study is relatively well-performed and clearly written, with the omics profiling adding more datasets from in vitro cell types that can be difficult to characterise in vivo. Whilst the majority of the study may be considered incremental, the key finding is the authors conclusion that H3K27me3 is subordinate to gene activity rather than an instructive repressor. If borne out, this would mark an important observation with broad implications. However, in my view this conclusion is subject to many confounders and alternative interpretations, and the authors have not ruled out other explanations. Given the centrality of this to the novelty of the study, I would encourage further analysis/stratification of existing data, and potentially further experiments to provide more confidence in this key conclusion.

      Primary issue

      1.) The authors show that at the earliest timepoint (d3), nascent gene activation of a handful of genes between G+ and G- populations is not associated with a FC loss of H3K27me3. From this the authors extrapolate their key conclusion that H3K27me3 is subordinate. Causality of chromatin modifications in gene regulation is critical to decipher, and therefore this is an important observation to confirm. Below I go through the possible confounders and issues with the conclusion at this point.

      (i) Single-cell penetrance. A possible (likely?) possibility is that gene activation initially occurs in a relatively small subset of cells at d3. Because these genes are expressed lowly prior to this, they will register as a significant upregulation in bulk analysis. However, in this scenario H3K27me3 would only be lost from a small fraction of cells, which would not be detectable against a backdrop of most cells retaining the mark. In short, the authors have not ruled out heterogeneity driving the effect. Given the different dynamic range of mRNA and chromatin marks, and that a small gain from nothing (RNA) is easier to detect than a small loss from a pre-marked state (chromatin), investigating this further is critical to draw the conclusions the authors have.

      (ii) Initial H3K27me3 levels. The plots in Fig 5 show the intersect FC of H3K27me3 and gene expression. Genes that activate at d3 show no loss of H3K27me3. However, it is important to characterise (and quantitate) whether these genes are significantly marked by H3K27me3 in the first place, which I could not find in the manuscript. Many/several of the genes may not be polycomb marked or may have low levels to begin with. This would obviously confound the analysis, since an absence/low K27 cannot be significantly lost and is unlikely to be functional. Thus, the DEG geneset should be further stratified into H3K27me3+ and K27me3- promoter groups/bins, with significance and conclusions based on the former only (e.g. boxplot in 5F).

      (iii) Sample size. The conclusions are based on a relatively small number of genes that upregulate between G+ and G- (n=55 in figure by my count, text mentions n=52). Irrespective of the other confounders above, this is quite a small subset to make the sweeping general conclusion that "loss of the repressive polycomb mark H3K27me3 is delayed relative to transcriptional activation" in the abstract. Indeed, the small number of DEG suggests the cell types being compared are similar and perhaps therefore have specific genomic features (this could be looked at) that drive .

      Other comments:

      2.) The authors show that promoter H3K4me3 corelates well with gene expression dynamics in their model. They conclude that "transcription itself is required for H3K4me3 deposition", or in other words is subordinate. This may well be the case but from their correlative data this cannot be inferred. Indeed, several recent and past papers have shown that H3K4me3 itself can directly modulate transcription, for example by triggering RNA II pause-release, by preventing epigenetic silencing and/or by recruiting the PIC. The authors could point out or discuss these alternative possibilities to provide a more balanced discourse.

      3.) The labelling of some figures is unclear. In Fig 4C and 4D (right) it is impossible to tell what sample each of the lines represents. It is also not clear what the blue zone corresponds to in genome view plots (the whole gene?). Moreover, the replicate numbers are not shown in figure legends.

      4.) It would be nice to provide more discussion to reconcile the conclusions that H3K27me3 in endoderm differentiation is subordinate and the final figure showing inhibiting H3K27me3 has a significant effect on differentiation, since the latter is the functional assessment.

      Significance

      Overall, the study's strengths are in that it characterises epigenomic dynamics within a specific and relevant cell fate model. The nascent transcriptomics adds important resolution, and underpins the core conclusions. The weakness is that data is over-interpreted at this point, and other possibilities are not adequately tested. The conclusions should therefore either be scaled back (which reduces novelty) or further analysis and/or experiments should be performed to support the conclusion. If it proves correct, this would be a significant observation for the community,

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      Referee #2

      Evidence, reproducibility and clarity

      In this paper the authors profile gene expression, including active transcription, and histone modifications (k4 and k27me3) during a complex differentiation protocol from ES cells, which takes advantage of FACS sorting of appropriate fluorescent reporters. The data is of good quality and the experiments are well performed. The main conclusion, that the analyzed histone marks channel differentiation more than they directly allow/block it, is well supported by the data. The paper is interesting and will represent a good addition to an already extensive literature. I have however a few major concerns, described below:

      1. K4me3 may show more changes than they interpret, at least over the +1 nucl. An alternative quantification to aggregate profiles should be used to more directly address the questions regarding the correlations between histone mods and gene expression.
      2. Related to the previous point, it appears clear in Fig.4 that the promoters of each gene expression cluster do not belong to a single chromatin configuration. I think it would be important to:
        • cluster the genes based on promoter histone mods and interrogate gene expression and cluster allocation (basically the reverse to what is presented)
        • order the genes in the heatmaps identically for K4me3 and K27me3 to more easily understand the respective chromatin composition per cluster
      3. Also, as it is apparent that not all promoters in every cluster are enriched for the studied marks, could the authors separately analyze these genes? What are they? Do they use alternative promoters?
      4. The use of 4SU-seq to identify active enhancers is welcome; however, I have doubts it is working very efficiently: for instance, in the snapshots shown in Fig.2A, the very active Oct4 enhancers in ES cells are not apparent at all... More validation of the efficiency of the approach seems required.
      5. The effects of the EZH2 inhibitor are quite minor regarding the efficiency of the differentiation as analyzed by FACS, despite significant gene expression changes. To the knowledge of this referee, this is at odds with results obtained with Ezh2 ko ES cells that display defects in mesoderm and endoderm differentiation. I have issues reconciling these results (uncited PMID: 19026780). Either the authors perform more robust assays (inducible KOs) or they more directly explain the limitations of the study and the controversies with published work.

      Minor

      1. please add variance captured to PCA plots
      2. Fig1E add color scales to all heatmaps
      3. Fig4C,D are almost impossible to follow, please find a way to identify better the clusters/samples and make easier to correlate all the variables

      Significance

      The paper is incremental in knowledge, and not by a big margin, as it is known already that histone mods rather channel than drive differentiation. Though, the authors do not clearly address inconsistencies with published work, especially regarding Ezh2 thought to be important to make endoderm. It is however a good addition to current knowledge, provided a better discussion of differences with published work is provided.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      To explore the relationship between histone post-translational modifications (H3K4me3 and H3K27me3) and enhancer activation with gene expression during early embryonic development, the authors used a monolayer differentiation approach to convert mouse embryonic stem cells (ESCs) into Anterior Definitive Endoderm (ADE). They monitored differentiation stages using a dual reporter mESC line (B6), which has fluorescent reporters inserted at the Gsc (GFP) and Hhex (Redstar) loci. Their analyses indicate that the differentiating cells advanced through stages similar to those in the embryo, successfully converting into endoderm and ADE with high efficiency. This is elegant and well performed stem cell biology.

      Their subsequent genome-wide and nascent transcription analyses confirmed that the in vitro gene expression changes correlated with developmental stages and confirmed that transcriptional activation precedes mRNA accumulation. They then focussed on linking active enhancers and histone modifications (H3K4me3 and H3K27me3) were with gene expression dynamics. Finally, the performed PRC2 inhibition and showed that, while it enhanced differentiation efficiency, it also induced ectopic expression of non-lineage specific genes.

      Major comments:

      In terms of mechanistic advances, they propose that transcriptional up-regulation does not require prior loss of H3K27me3, which they show appears to lag behind gene activation, but critically, on a likely mixed population level. I am sceptical of their interpretation of their data because they are looking at heterogenous populations of cells. To explain, one could imagine a particular H3K27me3 coated gene that gets activated during differentiation. In a population of differentiating cells, while the major sub-population of cells could retain H3K27me3 on this particular gene when it is repressed, a minority sub-population of cells could have no H3K27me3 on the gene when it is actively transcribed. The ChIP and RNA-seq results in this mixed cell scenario would give the wrong impression that the gene is active while retaining H3K27me3, when in reality, it's much more likely that the gene is never expressed when its locus in enriched with the repressive H3K27me3 modification. Therefore, to support their claim, they would have to show that a particular gene is active when its locus is coated with H3K27me3. Personally, I don't feel this approach would be worth pursuing.

      They also report that inhibition of PRC2 using EZH2 inhibitor (EPZ6438) enhanced endoderm differentiation efficiency but led to ectopic expression of pluripotency and non-lineage genes. However, this is not surprising considering the established role of Polycomb proteins as repressors of lineage genes.

      Referee cross-commenting

      I see that Reviewer #3 has the same concern with over interpretation of data in places - most notably their (in my view not supported) suggestion that transcriptional up-regulation does not require prior loss of H3K27me3.

      Significance

      I feel that this is a solid and well conducted study in which the authors model early development in vitro. It should be of interest to researchers with an interest in more sophisticated in vitro differentiation systems, perhaps to knockout their gene of interest and study the consequences. However, I don't see any major mechanistic advances in this work.

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      Reply to the reviewers

      We thank the reviewers for taking the time to read and comprehensively evaluate our manuscript. We are pleased that, overall, they recognize the quality of our data and that it supports our conclusions. We are grateful for their comments, insights and advice and have revised the manuscript accordingly as described in the point-by-point response below. We believe that the revised manuscript is substantially improved by some experimental additions, additional replicates, improved analysis and increased clarity. Some key enhancements are as follows:

      Previously we had found increased expression of the WNT pathway following CHRDL2 treatment, using RNA seq. We have now demonstrated this experimentally using the cellular levels and localisation of β-catenin. Previously we had shown that overexpression of CHRDL2 increased resistance to common chemotherapy treatments, as well as irradiation in colorectal cell lines. We have now shown that cells surviving treatment show a further reduction SMAD1/5/8 phosphorylation indicating a selection for CHRLD2 high cells during the treatment. We have also demonstrated a decrease in chemotherapy sensitivity in intestinal organoids treated with secreted forms of CHRDL2.

      1. Point-by-point description of the revisions

      This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

      Reviewer #1

      __Evidence, reproducibility and clarity __

      Clarkson and Lewis present data suggesting that overexpression of Chordin like 2 (CHRDL2) can affect colorectal cancer cell responses to chemotherapy agents, possibly by modulating stem-cell like pathways. I have the following comments:

      1. Fig. 1J-it is standard to show the images of cell migration-this is important here, given the modest effect of CHRDL2 overexpression here.

      We have now included 3 replicate control and CHRDL2 overexpressing cell images in this figure panel to support the quantification in the graph.

      Fig. 2A-the very small error bars for most of the data on the curves suggests these are n=1 experiments with multiple technical replicates to generate the error bars. Please clarify. The legend says n=3 with ANOVA analysis but no significance detected. Please clarify.

      All experiments in this figure were done with 5 technical replicates per experiment, this was replicated at least three times to give n=3 biological replicates. The error bars represent the standard error of the mean of these 3 biological replicates as stated in the legend. Some data points showed very little data variation, hence the small error bars. Raw data is available if requested.

      1. Fig. 2B-given the overlapping error bars here, how can there be a pWe have removed this representation of the data as it combined many different experiments with variable cell types and chemotherapeutics and it was difficult to carry out meaningful statistics. An overview of the data can be better seen in table form as shown in the revised figure 2B.

      Fig. 2G-did the authors try to estimate the concentration of CHRDL2 in the conditioned medium? Which cell line was used to generate this CM?

      Conditioned media was harvested from the matching transgenic cell lines with inducible CHRDL2. eg RKO cells were treated with media collected from doxycycline induced transgenic RKO cells whereas CaCO2 cells were treated with media from CaCO2 cells. The concentration of doxycycline was represented by ++ for 10ug/ml, the same notation we have used for directly induced cells treated with 10ug/ml dox.

      We did not try to quantify the absolute concentration of CHRDL2 but we have shown the relative amount on a Western blot normalised with a ponceau stain (quantification now included in supplementary figure 1).

      We have clarified our description of this experiment, inserting the following statement, "Conditioned media was harvested from corresponding cell lines with the inducible CHRDL2 transgene and the parental control cells. Induction of CHRDL2 to generate conditioned media was carried out using the same concentration and duration of doxycycline treatment as the cells in figure 2A. "

      Fig. 5-what is the potential mechanism for gene expression changes in response to CHRDL2 overexpression? Is it all due to BMP inhibition? More mechanistic detail would be welcome here.

      We have suggested other pathways involved in these functional effects based on our RNA seq data but at the moment it is not possible to say whether any changes are independent of BMP signaling. CHRDL2 is relatively understudied and as yet there is not much literature supporting BMP independent actions of CHRDL2. However, we have added some discussion and reference to an article suggesting interactions between CHRLD2 and YAP (Wang et al., 2022) including the following statement on page 17: "While the changes in BMP and WNT signaling shown in our GSEA analysis suggest that the effects of CHRDL2 in our system work directly through inhibition of BMP, it is not possible to rule out that some pathways are affected by BMP independent actions of CHRLD2. Indeed, Wang et al, suggest that CHRDL2 can directly alter phosphorylation and activity of YAP in gastric cancer cell lines, which merits further exploration (Wang et al., 2022)"

      Significance

      Unclear whether genetically engineered inducible overexpression has any real physiological significance but we all use cell models so this is OK.

      Reviewer #2

      __Evidence, reproducibility and clarity __

      Summary: In the manuscript entitled "BMP antagonist CHRDL2 enhances the cancer stem-cell phenotype and increases chemotherapy resistance in Colorectal Cancer" the authors demonstrated that Chordin-like 2 (CHDRL2), a secreted BMP antagonist, promotes a chemo-resistant colorectal cancer stem cell phenotype through the inhibition of BMP signaling. The authors took advantage of both 2D engineered colorectal cancer (CRC) cells and healthy murine 3D organoid systems. Specifically, the authors showed a decreased proliferation rate and reduced clonogenic capability upon overexpression of CHRDL2 in established human colon cancer cell lines. Subsequently, they identified a chemo-resistant phenotype upon standard therapies (5FU, Oxaliplatin and Irinotecan) in CHDRL2 overexpressing cells by performing MTS assay. The authors showed that this chemo-resistant phenotype is associated with ATM and RAD21 activation, supporting an induction of DNA damage signaling pathway. Of note, the authors assessed that the exposure of 3D murine organoid to CHRDL2 resulted in a stem-like phenotype induction accompanied by a reduction of the differentiated counterpart. From RNA-seq data analysis emerged the upregulation of genes associated to stemness and DNA repair pathways in CHRDL2 overexpressing cells.

      Major comments: 1. In the first paragraph of the result section authors assessed that "Colorectal adenocarcinoma cell lines were deliberately chosen to encompass a range of CHRDL2 expression levels and genetic mutations", without showing qRT-PCR or WB data on the differential expression levels of CHRDL2 in a panel of immortalized CRC cell lines. Authors should include these data to better support their choice.

      *We have now included some qRT-PCR in supplementary figure 1 alongside a table of some of the key driver mutations in each cell line. Western blotting of these cells shows only a very low concentration of CHRDL2 protein. As shown in figure 1B in the control columns, no significant protein expression is observed in any line. *

      In Figure 1F, authors described a reduction of cell proliferation in CRC cell lines expressing high levels of CHRDL2 only under low glucose conditions. Why did the authors perform the assay under these conditions? They should better argue this aspect and validated the role of CHRDL2 in metabolism rewiring by performing additional in vitro assays.

      We have removed this aspect of the paper as it does not add significantly to our overall conclusions and we can clearly see the effects of CHRDL2 overexpression under standard growth conditions (Figure 1G).

      The authors should evaluate the role of CHRDL2 in promoting a stem-like phenotype in human colon cancer stem cells freshly isolated from patients and characterized.

      We would very much like to do experiments such as this but it is beyond the scope of this study and will be included in upcoming grant proposals.

      In order to confirm the data obtained on 3D murine organoids system obtained from normal Intestinal Stem Cells, authors should investigate the stemness induction, driven by CHRDL2, also in human intestinal organoids.

      Experiments using human intestinal organoids are currently planned and ethical approval applications and grant proposals are underway for future experiments of this nature.

      The authors should evaluate the oncogenic role of CHRDL2, through the maintenance of stemness, by performing orthotopic or subcutaneous experiments in vivo model.

      Similarly, this is not possible for this manuscript but is planned for the future alongside a transgenic mouse model of inducible CHRDL2 overexpression in the intestine.

      BMPs proteins are part of a very broad protein family. In the introduction section, authors should indicate the specific BMP protein on which CHRDL2 exerts its inhibitory function. Moreover, they should have assessed BMP protein levels in CACO2, LS180, COLO320 and RKO cell lines.

      We have clarified the interactions between CHRDL2 and specific BMPs in the introduction. We have not specifically assessed the BMP protein levels in our cells however we have now included an analysis of expression data from the Cancer Cell Line Encyclopedia in supplementary figure 1 C.

      In first panel, the authors should quantify the secreted levels of CHRDL2 in the media of overexpressing CHRDL2 cell lines.

      We have done this using the ponceau staining as a loading control and the results are displayed (supplementary figure 1).

      In Figure 2D the authors should use the appropriate controls and describe this with more details in results section.

      In this figure we have used Hoechst staining followed by FACs analysis to identify the cell cycle profile of our CHRDL2 treated cells. We have improved the description of this in the methods section. Appropriate controls for staining, both negative and positive, are used when setting up the analysis for this experiment. The cell cycle profile is calculated using the Novocyte in house software. We have now included the histogram plots in the main figure to clarify these data in figure 2D.

      In Figure 3A, the authors should have performed the assay by choosing IC50.

      *We attempted these experiments with the IC50 levels, however the high amount of cell death and frequency of apoptotic cells meant that clear images were difficult to obtain. We therefore reduced the concentrations and still had very measurable effects. *

      In Supplementary Fig. 4A-B. the results are unclear. The control cell lines are already chemo resistant.

      Again, we used IC25 levels of the drugs so that our cells were damaged but still live throughout the experiment. This has been explained on page 10.

      The authors should review and add statistical analysis in both main and supplementary figures.

      *We have now added additional details about statistical analysis throughout the figures, legend and main text, showing all significance levels as well as non-significance for each data set. * Minor comments: 1. The quality of immunofluorescence and WB images should be implemented, and in the immunofluorescence panels scale bars should be added.

      We have added or improved scale bars on each immunofluorescence image. Western blot images have been improved.

      In the graphical abstract authors reported that CHRDL2 overexpression increase WNT and EMT pathways, without performing any specific assay to demonstrate this. Authors should correct and graphically improve the graphical abstract.

      *This is a good point and we have now carried out Beta-catenin immunofluorescence as a measure of WNT signaling on both our cancer cell lines - showing an increase in nuclear beta-catenin (figure 1J and K), and our organoids - showing an increase in overall levels and cytoplasmic staining (Figure 4 F). In terms of EMT markers we have carried out immunofluorescence on IQGAP1 (Figure 1I). IQGAP1 is significantly upregulated in CHRDL2 cells, reflecting its role in reduced cell adhesion and increased migration. This correlates with our data showing increased cellular migration as well as the increase in EMT related transcription in our RNAseq data. *

      The term "significantly" in the discussion section is inappropriately referred to data showed in the histogram in Figure 1J. Moreover, in Figure 1Jthe authors should delete from the y-axis the term "corrected".

      We have changed significantly to substantially

      The term "significant" in discussion is inappropriately referred to BMI1 expression level if compared to the histogram in Figure 4G.

      We have changed significantly to "a trend to increase"

      In Figure 2C the authors should add the unit of measurement (fold over control) in the table.

      We have done this

      In Figure 4E the authors should add the figure legend reporting OLFM4 protein.

      We have done this

      The authors should include few sentences summarizing the findings at the end of each paragraph.

      We have added short summaries at the start or end of each section to improve the flow of the results section.

      Significance

      General assessment: Overall, the work is aimed to elucidate the role of CHRDL2 already considered a poor prognosis biomarker involved in the promotion of CRC (PMID: 28009989), in promoting stem-like properties. The authors elucidated new additional insights into the molecular mechanisms regulating stemness phenotype induced by the BMP antagonist CHRDL2 in CRC. The authors include in the study a large amount of data, which only partially support their hypothesis. However, this manuscript lacks organization and coherence, making it challenging to follow and read. Numerous concerns need to be addressed, along with some sentences to rephrase in the result and discussion sections.

      Advance: The manuscript reported some functional insights on the role of CHRDL2 in colorectal cancer, but additional data should be added to support authors 'conclusions.

      Audience: The manuscript is suggested for basic research scientists.

      __Reviewer #3 (Evidence, reproducibility and clarity (Required)):____ __ Summary BMP antagonist CHRDL2 enhances the cancer stem-cell phenotype and increases chemotherapy resistance in Colorectal Cancer Eloise Clarkson et al. The manuscript explored the function of CHRDL2, a BMP antagonist, on colorectal cancer (CRC). The authors found that CHRDL2 overexpression can enhance the survival of CRC cells during chemotherapy and irradiation treatment with elevated levels of stem-cell markers and reduced differentiation. Further RNA-seq analysis revealed that CHRDL2 increased the expression of stem-cell markers, WNT signaling and other well-established cancer-associated pathways. Overall, the manuscript is well-written and presented. I have some suggestions:

      Major points:

      1. The authors assert BMP antagonism was demonstrated by assessing levels of phosphorylated SMAD1/5 (Figure 1G). However, the immunoblotting assay only depicted P-SMAD 1/5 levels and B-ACTIN as internal control. It's suggested to include total-SMAD1/5 immunoblotting as an internal control to further support the claim of BMP antagonism.

      The reviewer is correct that this is the best control. Western blotting has now been performed with total SMAD1 protein expression used as an internal control and this is shown in Figure 1D and Supplementary figure 1F

      The authors argue that CHRDL2 overexpression reduced the proliferation of CRC cell lines, as evidenced by cell proliferation assays. However, from Figure 1E, the reduction in proliferation appears insignificant. It would be beneficial to perform one-way ANOVA tests on each time point for CHRDL2+ and CHRDL2++ with Control in Figure 1E to ascertain significance.

      *We now have repeated this experiment to reduce variability and have also provided two-way ANOVA analysis between Control and CHRDL2+ and Control and CHRDL2++. One-way ANOVA at timepoint 96hr also provided with details in the figure legend. *

      The findings indicating that overexpressing CHRDL2 can confer resistance to chemotherapy in CRC cells (Figure 2A-C) are noteworthy. To deepen the understanding of BMP signaling in cancer stemness and the molecular underpinning of CHRDL2 antagonism, additional western blot assays on P-SMAD1/5 with CHRDL2 overexpression and drug treatment are recommended.

      *Western blotting of P-SMAD1/5 upon cells treated with IC50 5FU has now been performed in figure 2C (in the same experiment as the revised panels in figure 1D). The data suggest that CHRDL2 overexpressing cells able to survive chemotherapy have higher levels of P-SMAD1/5 reduction compared to that of untreated cells, strongly suggesting that chemotherapy treatment acts to select the cells with the highest CHRDL2 expression. We thank reviewer 3 for this suggested experiment and have included further discussion on this on page 8. *

      The assertion that extrinsic CHRDL2 addition diminishes differentiation and enhances stem-cell numbers in an intestinal organoid model is intriguing. As BMP signaling inhibition contributes to intestinal cell stemness, incorporating additional layers for BMP antagonism of CHRDL2 on intestinal organoids through immunoblotting or real-time quantitative PCR for treated organoids would augment the conclusions.

      As stated in the response to reviewer 2, we have investigated Beta-catenin in our organoids following CHRDL2 treatment using immunofluorescence and find that the levels are increased with the staining shifting from the membrane to the cytoplasm and nucleus (Figure 4F).

      The authors claim CHRDL2 overexpression can decrease BMP signaling based on GSEA analysis (Figure 5E). However, the GSEA results did not demonstrate the downregulation of BMP signaling. Reanalysis of this GSEA analysis is warranted.

      *We agree with this point and have changed the description of this result since the gene set covers both positive and negative regulators of the BMP pathway. We cannot conclusively say from this RNAseq data set that BMP signaling is "downregulated", however since SMAD phosphorylation is increased and nuclear beta-catenin is increased, overall we suggest that the changes we see are likely to represent the effects of decreased BMP signaling along with increased WNT signaling. *

      Minor Points:

      6.Provide the threshold/cutoff values chosen for differential expressed genes (DEGs) in CHRDL2+ and CHRDL2++ RNA-seq compared with control cells. Explain the minimal overlap between CHRDL2 LOW and CHRDL2 HIGH DEGs. Consider presenting all DEGs in CHRDL2 LOW and CHRDL2 HIGH compared with control cells in one gene expression heatmap for better visualization.

      We have now provided the cutoff values for the DEGs in the legend for figure 5 (PThe minimal overlap of DEGs in the low and high expressing cells is an interesting point. We hypothesize that this may be related to the different effects of intermediate vs high levels of WNT signaling that occurs in colon cancer cells, frequently discussed in the literature as the "Just right hypothesis" (Lamlum et al. 1999, Albuquerque et al., 2002, Lewis et al., 2010). However, we haven't included this in the discussion as it merits further exploration. However, we have mainly focused on specific genes that are modified in both data sets, which are more likely to be the direct result of CHRDL2 modification. *

      After DEGs analysis, perform Gene Ontology (GO) analysis on these DEGs to further investigate possible gene functions rather than selectively discussing some genes, enhancing understanding of CHRDL2 functions in CRC cells.

      We have carried out this analysis using a variety of tools and have now included a Gene Ontology Panther analysis as supplementary figure 7. We have included a comment on this in the text on page 14 saying "Gene ontology analysis supports these findings with enrichment in biological processes such as cellular adhesion, apoptosis and differentiation. "

      Conduct similar experiments in both 2D culture and organoid systems, if feasible, to provide more comprehensive insights into CHRDL2's oncogenic roles in CRC tumor progression.

      *We have now performed chemotherapy treatment on our organoid systems, and have found that organoids with extrinsic CHRDL2 addition have a higher survival rate after chemotherapy compared to a control (Figure 4H and I). *

      Label significance (*, **, ***, and n.s.) for every CRC cell line treated with CHRDL2 in Figure 2D, 2F, 2J, 4G, 5D, and 5F.

      We have done this

      Label the antibodies with different colors used for immunofluorescence in the figure text in Figure 4E.

      We have done this

      * * Include replicate dots for the Control group in the bar plots in Figure 1F and 2B.

      We have done this

      * * Add scale bars in Figure 3A and correct similar issues in other figures if applicable.

      We have done this

      * *13.Correct grammar and punctuation mistakes throughout the manuscript. For example:

      We have done this and further proofread our revised manuscript

      Page 7: "As seen in Figure 1J, CHRDL2 overexpression significantly increased the number of migrated cells (P *We have now added additional details about statistical analysis throughout the figures, legend and main text, showing all significance levels as well as non-significance for each data set. * Reviewer #3 (Significance (Required)):

      The current study presents compelling evidence demonstrating that BMP signaling antagonist CHRDL2 enhances colon stem cell survival in colorectal cancer cell lines and organoid models. Further validation through CRC mouse models could offer invaluable insights into the clinical relevance and therapeutic implications of CHRDL2 in colorectal cancer.

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      Referee #3

      Evidence, reproducibility and clarity

      Summary

      BMP antagonist CHRDL2 enhances the cancer stem-cell phenotype and increases chemotherapy resistance in Colorectal Cancer Eloise Clarkson et al. The manuscript explored the function of CHRDL2, a BMP antagonist, on colorectal cancer (CRC). The authors found that CHRDL2 overexpression can enhance the survival of CRC cells during chemotherapy and irradiation treatment with elevated levels of stem-cell markers and reduced differentiation. Further RNA-seq analysis revealed that CHRDL2 increased the expression of stem-cell markers, WNT signaling and other well-established cancer-associated pathways. Overall, the manuscript is well-written and presented. I have some suggestions:

      Major points:

      1. The authors assert BMP antagonism was demonstrated by assessing levels of phosphorylated SMAD1/5 (Figure 1G). However, the immunoblotting assay only depicted P-SMAD 1/5 levels and B-ACTIN as internal control. It's suggested to include total-SMAD1/5 immunoblotting as an internal control to further support the claim of BMP antagonism.
      2. The authors argue that CHRDL2 overexpression reduced the proliferation of CRC cell lines, as evidenced by cell proliferation assays. However, from Figure 1E, the reduction in proliferation appears insignificant. It would be beneficial to perform one-way ANOVA tests on each time point for CHRDL2+ and CHRDL2++ with Control in Figure 1E to ascertain significance.
      3. The findings indicating that overexpressing CHRDL2 can confer resistance to chemotherapy in CRC cells (Figure 2A-C) are noteworthy. To deepen the understanding of BMP signaling in cancer stemness and the molecular underpinning of CHRDL2 antagonism, additional western blot assays on P-SMAD1/5 with CHRDL2 overexpression and drug treatment are recommended.
      4. The assertion that extrinsic CHRDL2 addition diminishes differentiation and enhances stem-cell numbers in an intestinal organoid model is intriguing. As BMP signaling inhibition contributes to intestinal cell stemness, incorporating additional layers for BMP antagonism of CHRDL2 on intestinal organoids through immunoblotting or real-time quantitative PCR for treated organoids would augment the conclusions.
      5. The authors claim CHRDL2 overexpression can decrease BMP signaling based on GSEA analysis (Figure 5E). However, the GSEA results did not demonstrate the downregulation of BMP signaling. Reanalysis of this GSEA analysis is warranted.

      Minor Points:

      6.Provide the threshold/cutoff values chosen for differential expressed genes (DEGs) in CHRDL2+ and CHRDL2++ RNA-seq compared with control cells. Explain the minimal overlap between CHRDL2 LOW and CHRDL2 HIGH DEGs. Consider presenting all DEGs in CHRDL2 LOW and CHRDL2 HIGH compared with control cells in one gene expression heatmap for better visualization. 7. After DEGs analysis, perform Gene Ontology (GO) analysis on these DEGs to further investigate possible gene functions rather than selectively discussing some genes, enhancing understanding of CHRDL2 functions in CRC cells. 8. Conduct similar experiments in both 2D culture and organoid systems, if feasible, to provide more comprehensive insights into CHRDL2's oncogenic roles in CRC tumor progression. 9. Label significance (, , **, and n.s.) for every CRC cell line treated with CHRDL2 in Figure 2D, 2F, 2J, 4G, 5D, and 5F. 10. Label the antibodies with different colors used for immunofluorescence in the figure text in Figure 4E. 11. Include replicate dots for the Control group in the bar plots in Figure 1F and 2B. 12. Add scale bars in Figure 3A and correct similar issues in other figures if applicable. 13.Correct grammar and punctuation mistakes throughout the manuscript. For example:

      Page 7: "As seen in Figure 1J, CHRDL2 overexpression significantly increased the number of migrated cells (P

      Page 7: "As seen in Figure 1J, CHRDL2 overexpression significantly increased the number of migrated cells (P

      Page 7: "As seen in Figure 1J, CHRDL2 overexpression significantly increased the number of migrated cells (P < 0.0449)," suggesting increased migratory ability, a hallmark of cancer stem cells."

      Page 8: "CHRDL2 overexpression resulted in an approximate twofold increase in IC50 values compared to control cells (P < 0.001)."

      Page 10: "As seen in Figure 4B, upon the" should be corrected to "Figure 4B."

      1. Specify the statistical methods or estimates used for determining statistical significance.

      Significance

      The current study presents compelling evidence demonstrating that BMP signaling antagonist CHRDL2 enhances colon stem cell survival in colorectal cancer cell lines and organoid models. Further validation through CRC mouse models could offer invaluable insights into the clinical relevance and therapeutic implications of CHRDL2 in colorectal cancer.

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

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      Referee #2

      Evidence, reproducibility and clarity

      Summary:

      In the manuscript entitled "BMP antagonist CHRDL2 enhances the cancer stem-cell phenotype and increases chemotherapy resistance in Colorectal Cancer" the authors demonstrated that Chordin-like 2 (CHDRL2), a secreted BMP antagonist, promotes a chemo-resistant colorectal cancer stem cell phenotype through the inhibition of BMP signaling. The authors took advantage of both 2D engineered colorectal cancer (CRC) cells and healthy murine 3D organoid systems. Specifically, the authors showed a decreased proliferation rate and reduced clonogenic capability upon overexpression of CHRDL2 in established human colon cancer cell lines. Subsequently, they identified a chemo-resistant phenotype upon standard therapies (5FU, Oxaliplatin and Irinotecan) in CHDRL2 overexpressing cells by performing MTS assay. The authors showed that this chemo-resistant phenotype is associated with ATM and RAD21 activation, supporting an induction of DNA damage signaling pathway. Of note, the authors assessed that the exposure of 3D murine organoid to CHRDL2 resulted in a stem-like phenotype induction accompanied by a reduction of the differentiated counterpart. From RNA-seq data analysis emerged the upregulation of genes associated to stemness and DNA repair pathways in CHRDL2 overexpressing cells.

      Major comments:

      1. In the first paragraph of the result section authors assessed that "Colorectal adenocarcinoma cell lines were deliberately chosen to encompass a range of CHRDL2 expression levels and genetic mutations", without showing qRT-PCR or WB data on the differential expression levels of CHRDL2 in a panel of immortalized CRC cell lines. Authors should include these data to better support their choice.
      2. In Figure 1F, authors described a reduction of cell proliferation in CRC cell lines expressing high levels of CHRDL2 only under low glucose conditions. Why did the authors perform the assay under these conditions? They should better argue this aspect and validated the role of CHRDL2 in metabolism rewiring by performing additional in vitro assays.
      3. The authors should evaluate the role of CHRDL2 in promoting a stem-like phenotype in human colon cancer stem cells freshly isolated from patients and characterized.
      4. In order to confirm the data obtained on 3D murine organoids system obtained from normal Intestinal Stem Cells, authors should investigate the stemness induction, driven by CHRDL2, also in human intestinal organoids.
      5. The authors should evaluate the oncogenic role of CHRDL2, through the maintenance of stemness, by performing orthotopic or subcutaneous experiments in vivo model.
      6. BMPs proteins are part of a very broad protein family. In the introduction section, authors should indicate the specific BMP protein on which CHRDL2 exerts its inhibitory function. Moreover, they should have assessed BMP protein levels in CACO2, LS180, COLO320 and RKO cell lines.
      7. In first panel, the authors should quantify the secreted levels of CHRDL2 in the media of overexpressing CHRDL2 cell lines.
      8. In Figure 2D the authors should use the appropriate controls and describe this with more details in results section.
      9. In Figure 3A, the authors should have performed the assay by choosing IC50.
      10. In Supplementary Fig. 4A-B. the results are unclear. The control cell lines are already chemoresistant.
      11. The authors should review and add statistical analysis in both main and supplementary figures.

      Minor comments:

      1. The quality of immunofluorescence and WB images should be implemented, and in the immunofluorescence panels scale bars should be added.
      2. In the graphical abstract authors reported that CHRDL2 overexpression increase WNT and EMT pathways, without performing any specific assay to demonstrate this. Authors should correct and graphically improve the graphical abstract.
      3. The term "significantly" in the discussion section is inappropriately referred to data showed in the histogram in Figure 1J. Moreover, in Figure 1Jthe authors should delete from the y-axis the term "corrected".
      4. The term "significant" in discussion is inappropriately referred to BMI1 expression level if compared to the histogram in Figure 4G.
      5. In Figure 2C the authors should add the unit of measurement (fold over control) in the table.
      6. In Figure 4E the authors should add the figure legend reporting OLFM4 protein.
      7. The authors should include few sentences summarizing the findings at the end of each paragraph.

      Significance

      General assessment:

      Overall, the work is aimed to elucidate the role of CHRDL2 already considered a poor prognosis biomarker involved in the promotion of CRC (PMID: 28009989), in promoting stem-like properties. The authors elucidated new additional insights into the molecular mechanisms regulating stemness phenotype induced by the BMP antagonist CHRDL2 in CRC. The authors include in the study a large amount of data, which only partially support their hypothesis. However, this manuscript lacks organization and coherence, making it challenging to follow and read. Numerous concerns need to be addressed, along with some sentences to rephrase in the result and discussion sections.

      Advance: The manuscript reported some functional insights on the role of CHRDL2 in colorectal cancer, but additional data should be added to support authors 'conclusions.

      Audience: The manuscript is suggested for basic research scientists.

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      Referee #1

      Evidence, reproducibility and clarity

      Clarkson and Lewis present data suggesting that overexpression of Chordin like 2 (CHRDL2) can affect colorectal cancer cell responses to chemotherapy agents, possibly by modulating stem-cell like pathways. I have the following comments:

      1. Fig. 1J-it is standard to show the images of cell migration-this is important here, given the modest effect of CHRDL2 overexpression here.
      2. Fig. 2A-the very small error bars for most of the data on the curves suggests these are n=1 experiments with multiple technical replicates to generate the error bars. Please clarify. The legend says n=3 with ANOVA analysis but no significance detected. Please clarify.
      3. Fig. 2B-given the overlapping error bars here, how can there be a p<0.01 between the groups?
      4. Fig. 2G-did the authors try to estimate the concentration of CHRDL2 in the conditioned medium? Which cell line was used to generate this CM?
      5. Fig. 5-what is the potential mechanism for gene expression changes in response to CHRDL2 overexpression? Is it all due to BMP inhibition? More mechanistic detail would be welcome here.

      Significance

      Unclear whether genetically engineered inducible overexpression has any real physiological significance but we all use cell models so this is OK.

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      Reply to the reviewers

      We would like to thank the reviewers for their overall positive assessment of our manuscript. We have used their constructive feedback to substantially improve our manuscript as described below.

      Reviewer #1

      Evidence, reproducibility and clarity

      This study by Reyes at al is a well conducted analysis of memory B cell dynamics of Plasmodium falciparum (Pf) -specific B cell populations over the course of reducing Pf prevalence in ten Ugandan adults. The data is presented well and the authors provide compelling evidence that 1. There is an overall loss of Ag specific B cells with reduction in exposure and 2. Different antigens (MSP1/AMA-1 vs CIDRa-1) generate different flavors of long lived responses. However, additional clarity to the reader should be provided on certain topics (listed below).

      Major comments: 1. While the premise of the study (reduced Pf transmission due to the use of indoor residual spraying (IRS)) is an important one, I think the authors must take into consideration that 9/10 subjects had at least one Pf positive episode between Time Points 1 and 2 (Figure 1). Also, it looks from Fig 1 that some samples were collected at a time of Pf positive test (green squares), while in Table S1 none of the subjects have a positive parasite status at TP1.

      We recognize that most individuals had detectable parasitemia before and after time point (TP) 1. In our manuscript, we therefore do not report the time between TP1 and TP2, because we agree that the length of this time interval is not relevant in our study methodology. We only mention the time between the last known P. falciparum infection and collection of blood at the second time point. We use the sample collected at TP1 only as a representative sample obtained during a time with high P. falciparum exposure and do not make any claims based on the time between TP1 and TP2. The occurrence of infections after sample collection at TP1 confirms that parasite transmission was still high at this time. We have added a schematic of the relative levels of parasite transmission to Figure 1 to emphasize this.

      With respect to infection status, none of the donors were blood smear positive at TP1. However, as mentioned in Table S1, parasites were detected in three individuals using the more sensitive LAMP assay. These three individuals are therefore marked as parasite positive in Figure 1. Table S1 has been modified to highlight the parasite status of these three individuals.

      1. Figure S1A: What is trBC? Figure S1B: What is Strep? Are the strep positive cells also CIDR-1 positive and were they gated out? Why is APC used for MZ-1 and one of the MSP1-AMA-1 tetramers? Do these stainings come from multiple panels?

      All abbreviations of B cell populations were defined in the figure legend (for example, trBC stands for transitional B cells). To facilitate the interpretation of Figure S1, we have now included the definitions of these abbreviations in the figure.

      Strep stands for streptavidin, which has now also been clarified in the figure. In our gating strategy, we used the term “strep” to denote cells that bound to both CIDRa1 and MSP1/AMA1 tetramers, which we interpreted as non-specific binding to streptavidin or other components of the antigen tetramers. Only the “non-strep” cells were used to gate on antigen-specific cells. We have added this clarification to the figure legend.

      In panel B, we accidentally used the term MZ (for merozoite) to describe tetramers of the merozoite antigens MSP1 / AMA1. These labels are interchangeable, but to avoid confusion, MZ-1 has been changed to MSP1 / AMA1.

      1. Figure 3A: how many cells does the umap plot represent? Were there a total of 3555 Ag specific B cells that were non-naive (Figure 3E)?

      It is correct that there were a total of 3,555 antigen-specific B cells used for the clustering shown in panel A. This information has been added to Figure 3A.

      1. Could the authors comment on why in Figure 3, Ig isotype expression was not considered for clustering? This would allow for characterization of DN sub populations/ clusters in addition to the CD21-CD27- ABCs? It looks like IgD expression was low across the clusters (Figure 3D). Was this the case for the cells considered in this analysis, or was it excluded? If it was truly low expressed, how were the assessments in Figure 2 made?

      From prior experience, we know that Ig isotype information tends to dominate in the clustering, which would result in major clusters based on IgM, IgD, IgG, and IgA expression, not on expression of other markers. This is illustrated in the example below. The UMAP on the left shows clusters in green and red that consist of IgG+ and IgA+ B cells, respectively. The UMAP on the right shows that switched memory (swM) B cells and DN B cells are found in both IgG and IgA clusters. Because we were mainly interested in identifying different subsets of B cells, irrespective of Ig isotype, we did not include Ig isotype in the clustering. We have clarified in the manuscript that Ig isotypes were excluded from the analysis to prevent these from dominating the clustering:

      “Unsupervised clustering was then performed based on expression of all markers, except for Ig isotypes to prevent these from dominating the clustering.”

      IgD expression among cell clusters shown in Figure 3 was low because only non-naïve B cells were included in the analyis. The majority of non-naïve cells are class-switched memory B cells and DN B cells, which by definition do not express IgD (see gating strategy in Figure S1A). Figure 2 shows all B cell populations, including naïve B cells and non-naïve B cell populations (unswitched memory, switched memory, and DN), that were gated based on IgD and CD27 expression.

      5.Are there differences in these designations / phenotypes of DN populations of atBCs vs CD21-CD27- atBCs?

      In the malaria field, atypical B cells are typically defined as CD21-CD27-. The definition of DN2 B cells comes from the autoimmunity field and is stricter: IgD-CD27-CD21-CD11c+ B cells. In our manuscript, we define atypical B cells in a stricter way than typically done in the malaria field, following published guidelines for the identification of B cell subsets (https://doi.org/10.3389/fimmu.2019.02458). Using these guidelines, atypical B cells and DN2 B cells are phenotypically identical. We have added a reference to these published guidelines in the Results section:

      “Following published guidelines for the identification of B cell populations (21), total CD19+ B cells were divided into naïve B cells (IgD+CD27-), unswitched memory B cells (IgD+CD27+), switched memory B cells (IgD-CD27+), and double negative B cells (IgD-CD27-).”

      1. Lines 258-259: In considering only switched MBCs, what clusters from Figure 3a were included? There seem to be 2588 sw MBCs (Table S3, Figure 4). Do the remaining cells (967 cells) come from clusters 2, 5 and 6 (and excludes the atBC clusters)

      This analysis did not use the clusters presented in Figure 3, but instead used switched memory B cells gated as shown in Figure S1A. The reason for this is that the clusters in Figure 3 were generated using antigen-specific B cells and cannot be reproduced using non-antigen-specific B cells. Thus, it is not possible to separate all other B cells into the same six clusters. The only way to compare expression of certain markers between antigen-specific and non-antigen specific switched memory B cells is to gate on these populations manually. We have now tried to clarify this in the manuscript as follows:

      “we determined the percentages of CD95+ cells and CD11c+ cells among antigen-specific switched memory B cells and the total population of switched memory B cells (gated manually as shown in Figure S1A).”

      Minor comments: 1. Line 178- 179: Was there a specific measure of rate of decline made for these cells?

      We did not calculate a rate of decline of antigen-specific B cells for several reasons: 1) the time between TP1 and TP2 is not the same for all people in the study, 2) the time between last exposure and TP2 is not the same for all people, and 3) the rate of decline is most likely not linear and cannot accurately be estimated with only two data points. We have changed the wording of this sentence such that we do not use the word “rate”:

      “we did not observe a difference in the percentage of B cells with specificity for merozoite antigens or variant surface antigens that were lost.”

      In addition, we included the percentage of reduction in size in the paragraph before this section:

      “we observed that both populations decreased in size by about 50%, although these differences were not statistically significant.”

      Significance

      General assessment: Strengths: The authors provide evidence that the dynamics of antigen specific cells in humans can vary with exposure and with the nature of the antigen. They have nicely discussed the potential causes for these differences (Discussion), although they should include the findings of Ambegaonkar et al that ABCs in malaria may be restricted to responding specifically to membrane bound antigens (PMCID: PMC7380957)

      As suggested by the reviewer, we have added a paragraph to the Discussion section to discuss the results reported by Ambegaonkar et al. and how the difference between soluble vs. membrane-bound antigens may have an effect on how these antigens are perceived by B cells:

      The difference between soluble and membrane-bound antigens may also have a direct effect on how these antigens are perceived by B cells. Atypical B cells have been shown to be restricted to recognition of membrane-bound antigens (41). The interaction of a B cell with membrane-associated antigen allows the formation of an immunological synapse. Inhibitory receptors expressed by atypical B cells are excluded from this synapse, resulting in B cell receptor signaling and differentiation towards antibody-secreting cells (41). This could explain why atypical B cell subset 1 that expresses the highest levels of the inhibitory receptor FcRL5 is enriched for recognition of the CIDRα1 domain of membrane-bound protein PfEMP1. It should however be noted that soluble antigen can also be presented effectively in membrane-context by conventional dendritic cells, follicular dendritic cells, and subcapsular macrophages in secondary lymphoid organs, especially when it is part of an immune complex (reviewed in (42)). This would provide a route for atypical B cells to also respond to soluble merozoite antigens, such as MSP1 and AMA1.

      Limitations: 1. Outlined above, and as the authors also mention, a small sample size and homogenous population. 2. The evidence for reduced transmission is not clear, and the negative parasite tests for donors shown in Table S1 do not match with Figure 1 data. 3. Lack of IgD expression across clusters (Figure 3D- the authors will need to clarify this point) would require re-analysis of Figure 2 data

      1. We have provided clarification in response to the points raised by the reviewer.

      2. We believe there is clear evidence for reduced transmission, from a median of almost 2 infections per person per year prior to the implementation of IRS to a median parasite-free period of 1.7 years prior to sample collection at TP2. To further emphasize this, we have summarized the number of P. falciparum infections among the ten individuals included in this study (now included in Table S3):

      year

      Pf infections

      comment

      2012

      20

      2013

      19

      TP1

      2014

      20

      TP1

      2015

      8

      Start IRS

      2016

      0

      TP2

      This reduced parasite exposure is reflected in a decrease in immune activation as presented in Figure 2. We have clarified that the data in Table S1 did indeed match those shown in Figure 1.

      1. We have clarified that IgD expression is low in the clusters presented in Figure 3 because naïve B cells were excluded from this analysis.

      Advances: This study highlights the importance of studying antigen specific B cells in humans in the context of natural infection and the use of high-parameter tools such as spectral flow cytometry in assessing a large quantity of data from limited clinical samples. These data are important to inform better vaccine design. Studies in inbred animals can be quite limited or different from human B cell responses.

      Audience: This study will be of interest to malariologists and B cell immunologists. Atypical B cells are relevant to many infectious diseases and auto immunity, while the dynamics of memory B cells in malaria all be relevant to those interested in vaccine design against blood stage antigens.


      Reviewer #2

      Evidence, reproducibility and clarity

      Summary: In this study, the authors compared long-lived total and antigen (ag)-specific B-cell levels in a cohort of 10 Ugandan malaria patient samples that were collected before and after local reduction of P. falciparum transmission (pre/post-IRS). The focus is on the novel comparison of the two most common malaria antigens: merozoite antigens (MSP1/AMA1) and variant surface antigens (CIDRα1). Using high-parameter spectral flow cytometry, they also characterized the phenotype of the different populations of cells. Their main findings include 1) a decrease in activated but maintenance of resting ag-specific B-cells in the post-IRS sample and 2) CD95 and CD11c, as the only differentially expressed markers between MSP1/AMA1-specific and CIDRα1-specific long-lived memory B cells. Their further phenotypic characterization suggests functional consequences with MSP1/AMA1-specific B-cells being poised for rapid antibody-secreting cell differentiation while CIDRα1-specific B cells were enriched among a subset of atypical B cells that seem poised for antigen presentation (CD86+CD11chi/ AtBC1). Their findings consolidate and further expand our knowledge of long-lived B-cell levels during P. falciparum malaria and report/compare (for the first time to my knowledge) a differential selection of long-lived B-cell levels between these 2 antigen specificities. Overall, the manuscript is straightforward and well-written and the authors did a good job explaining their methodology, findings, and interpretations. I believe the major gap missing in this study is the reconciliation of long-lived antigen-specific B-cell levels with the serum antigen-specific antibody levels of these patients against the same 2 antigens (MSP1/AMA1 and CIDRα1) in the experiments and the discussion. The antibody data would strengthen their main argument and is the main missing piece for characterizing more completely the long-lived antigen-specific humoral responses. Below are my suggestions that would help improve the manuscript:

      Major comments: 1. Serum Anti-Pf antibodies: Do the authors have access to the serum/plasma of these patients? It would be important to correlate the total and ag-specific B-cell populations with levels of serum IgG antibodies against those specific Pf antigens (MSP1/AMA1 and CIDRα1) and total IgG levels to strengthen their point about long-lived humoral responses.

      To our understanding, the rationale for such an analysis would be that if IgG levels correlated with the size of a certain B cell population, it would suggest that this B cell population is implicated in the production of IgG against a particular antigen. While a correlation between the percentage of memory B cells and IgG titers has been observed for antigens from several viruses and bacteria (1-4), other studies have reported the absence of such a correlation (4-7). Similarly, for P. falciparum antigens, a moderate correlation between memory B cell abundance and IgG titers has been observed for some merozoite antigens, but not for others (8, 9). The lack of a correlation between the magnitude of the memory B cell and the antibody response fits with the prevailing model that memory B cells and plasma cells are two independently controlled arms of the humoral immune system (10, 11). Given the lack of strong evidence that the levels of IgG titers and memory B cells are interconnected, we do not think this analysis will be informative.

      An alternative analysis would be to study the contribution of B cell subsets to the production of IgG after re-exposure, similar to a recent study that identified T-bet+ memory B cells as the main contributors to antibody responses following influenza virus vaccination (12). Unfortunately, we are unable to perform this analysis in this study population, because only four of the individuals included in this study (spanning calendar years 2012 – 2016) were recruited into a follow up cohort (calendar years 2017 – 2019), and none of these four people were infected during this later time frame.

      We have however added this future direction to the Discussion section:

      To determine the contribution of different memory B cell subsets to the recall response against P. falciparum, it would be interesting to analyze IgG responses upon re-infection. However, none of the individuals included in this study experienced a recorded P. falciparum infection post-IRS, preventing us from performing such an analysis.

      References

      1. Crotty et al., J Immunol (2003), https://doi.org/10.4049/jimmunol.171.10.4969
      2. Quinn et al., J Infect Dis (2004), https://doi.org/10.1086/423937
      3. Cohen et al., Cell Rep Med (2021), https://doi.org/10.1016/j.xcrm.2021.100354
      4. Amanna et al., New England J Med (2007), https://doi.org/10.1056/nejmoa066092
      5. Leyendeckers et al., Eur J Immunol (1999), https://doi.org/10.1002/(sici)1521-4141(199904)29:04%3C1406::aid-immu1406%3E3.0.co;2-p
      6. Nanan et al., Vaccine (2001), https://doi.org/10.1016/s0264-410x(01)00328-0
      7. Goel et al., Science Immunol (2021), https://doi.org/10.1126/sciimmunol.abi6950
      8. Rivera-Correa et al., eLife (2019), https://doi.org/10.7554/elife.48309
      9. Jahnmatz et al., Front Immunol (2021), https://doi.org/10.3389/fimmu.2020.619398
      10. Weisel et al., Immunity (2016), https://doi.org/10.1016/j.immuni.2015.12.004
      11. Shinnakasu et al., Nat Immunol (2016), https://doi.org/10.1038/ni.3460
      12. Nellore et al., Immunity (2023), https://doi.org/10.1016/j.immuni.2023.03.00
        1. Correlation between populations and initial parasite load: Are the levels between any of the populations at any time point correlated significantly in any way? If the statistical power/N allows it, please perform a correlation array between all populations using all samples both total and ag-specific and initial parasite load.

      We agree that this analysis could be very interesting. However, in most recorded infection cases, parasitemia was submicroscopic and parasite load was not reported. Information about parasite density in the blood prior to TP1 is available for only half of the individuals in this study. In these people, the last known parasite density was recorded between three months to two years prior to TP1. Given the small number of individuals for whom these data are available and the large variation in time between parasitemia and sampling, we do not have sufficient data to perform this analysis.

      1. Figure 2: Why were total and ag-specific plasmablasts/plasma cells not included in this figure? Please include to compare levels in these two time points.

      We did not include the levels of total and antigen-specific plasmablasts (PBs) in Figure 2 because the percentages of PBs are relatively low, and very few antigen-specific PBs were detected. We have now included the levels of total PBs in Figure 2A and the percentages of antigen-specific PBs in Supplementary Figure 2. The percentage of PBs among total B cells decreased by about 50% between TP1 and TP2, in line with a decrease in immune activation.

      1. Healthy baseline: The study is missing "healthy" controls as a reference. I presume this is because each patient is its uninfected control in the post-IRS sample. In methods, they mentioned they used two naïve-USA B-cells as technical controls. It would be important to include and maybe expand (to match age and gender)on that specific data from those controls as supplementary figures to support their findings:
      2. Show negative Tetramer staining for these samples (to understand the background).
      3. Levels of all the USA controls total B cell populations and compared to the pre/post-IRS samples to understand "baseline" or "non-endemic" control levels.
      1. We have included flow cytometry plots of tetramer staining for the non-P. falciparum exposed donors (pooled B cells from two US donors) to show the level of background for these probes. These plots are shown in Figure S1B.

      2. We have used data from P. falciparum-naive US donors (n = 7) that we generated for a prior study to show the average level of total B cell populations in Figure 2, and the percentage of switched memory B cells that express CD95, CD11c, T-bet, and FcRL5 in Figure 4.

      Minor comments: 1. In the gating strategy (S1), please include the percentage of each population of that representative example.

      We have added the percentages for all gated populations to Figure S1.

      1. For Figure 2, since not every panel has the same N, please include the N for each panel in the figure or a supplementary table.

      All panels in Figure 2 show data for all 10 individuals. However, since some data points are overlapping, it may appear that some panels show data from fewer individuals. Specifically, no antigen-specific DN1 cells were detected pre- and post-IRS for four individuals. These data points therefore overlap and are not visible. To avoid confusion, we had mentioned this in the legend to Figure 2 (see text in orange). We have tried to further clarify this by emphasizing in the figure legend that data from all 10 individuals are shown (see text in red):

      Figure 2: Abundance of total and antigen-specific B cell subsets in the circulation during high parasite transmission and in the absence of P. falciparum exposure. The percentage of B cell subsets among circulating B cells is shown for total B cells (A), MSP1/AMA1-specific B cells (B), and CIDRα1-specific B cells (C). For MSP1/AMA1-specific B cells and CIDRα1-specific B cells, the total percentage among all circulating B cells is also shown (right most graphs in each panel). All panels show data for all 10 individuals. In panels B and C, no antigen-specific DN1 cells were detected pre- and post-IRS for four individuals. These data points therefore overlap and are not clearly visible. Differences between groups were evaluated using a Wilcoxon matched-pairs signed-rank test. P values

      1. Please mention the history of past and chronic co-infections of these 10 patients. Particularly if they had any other active or recent infection when the sample was taken.

      Four individuals had active or recent infections in the three months prior to sample collection, with upper respiratory tract infections being the most common. This information has been included in Table S3, with a reference to these data in the Methods section. We have also included a link to ClinEpiDB where additional information about the cohort participants, including medical history, can be found.

      1. Discussion: further discussion with relevant literature on the following points is needed to consolidate cellular and antibody studies: a. Whether the presence of long-lived ag-specific B-cell responses correlates with sustained levels of IgG against Pf antigens. b. The different types of antibodies (protective/pathogenic) that these different B-cell populations have been reported to produce during malaria.

      a. We have added the following paragraph to the Discussion section:

      To determine how these different long-lived B cell subsets contribute to protection against P. falciparum infection, it would be important to analyze the connection between the cellular repertoire and plasma IgG. For P. falciparum antigens, a moderate correlation between memory B cell abundance and IgG titers has been observed for some merozoite antigens, but not for others (28, 44). This is in line with studies for other pathogens, that showed a correlation between the percentage of memory B cells and IgG titers for antigens from several viruses and bacteria (48-51), while other studies have reported the absence of such a correlation (51-54). The lack of a correlation between the magnitude of the memory B cell and the antibody response fits with the prevailing model that memory B cells and plasma cells are two independently controlled arms of the humoral immune system (55, 56). To determine the contribution of different memory B cell subsets to the recall response against P. falciparum, it would be interesting to analyze IgG responses upon re-infection. However, none of the individuals included in this study experienced a recorded P. falciparum infection post-IRS, preventing us from performing such an analysis.

      b. We have added additional discussion about the types of antigens recognized by atypical B cells to the Discussion section:

      Prior studies have shown that while atypical B cells harbor reactivity against P. falciparum antigens (9,18), they are also enriched for autoreactivity (43). Specifically, atypical B cells produce antibodies against the membrane lipid phosphatidylserine, which can induce the destruction of uninfected erythrocytes and contribute to anemia (44).

      Significance

      General assessment:

      Strengths: - Novelty in contrasting two different types of P. falciparum antigen responses at the B-cell level. - The use of tetramers is a cutting-edge technique to assess this question. - Analyses were thorough and found contrasting differences in antigen-specific B-cell populations (atypical vs classical) between these 2 antigens for the first time (to my knowledge). - Well-written manuscript with clear data, methodology, and conclusions

      Limitations: - Missing serum/plasma antibody data to support their claim about long-lived humoral responses and reconciliation of ag-specific B-cell levels and ag-specific antibody levels in experiments and discussion. - Limited N of 10 patients of the same gender (female), some population analyses had even fewer samples. - Missing baseline levels for non-endemic uninfected control for B-cell populations for comparison.

      • We have included a discussion about the correlation between plasma antibody and memory B cell responses in the Discussion section.

      • We have clarified that some data points overlap in Figure 2, giving the impression that data from fewer than 10 individuals were shown.

      • We have included baseline levels of 1) tetramer reactivity (Figure S1), 2) the size of B cell populations (Figure 2), and 3) expression of select markers (Figure 4).

      Advance: The study consolidates antigen-specific responses with the discovery of recently characterized populations (ex. atypical) and finds novel differences between two types of malaria antigen responses at the B-cell level and between specific populations responding differentially to these antigens. The findings are incremental (role of B-cell population in malaria-specific responses), conceptual (contrasting two types of B-cell antigen responses in the same infection), and clinical (finding significant differences in patients).

      Audience: This study will attract basic B-cell immunology scientists, infectious disease clinicians/scientists, vaccinologists, and both basic malaria immunology and clinical audiences.

      Reviewer expertise: Malaria, immunology, antibodies.

      __Reviewer #3 __

      Evidence, reproducibility and clarity: The authors analysed the antigen specificity and phenotypes of B cells during high P falciparum transmission and after a period of successful malaria control with IRS in Uganda. The gap between the two sampling time points is close to two years.

      They use antigen probes for MSP1/AMA1 and CIDRalpha1, two antigens expressed at different stages of P. falciparum life cycle-merozoites and infected red cells, respectively. While MSP1/AMA1 are involved in the parasite's invasion of red blood cells, CIDRalpha1 is a domain of PFEMP1, a large family of antigenically variant proteins that mediates the sequestration of infected red cells in small blood vessels.

      They found that the percentage of activated antigen-specific memory B cells declined with malaria control. However, detectable frequencies of antigen-specific memory B cells were retained after malaria control, which confirms earlier reports.

      However, they also demonstrate that the phenotypic characteristics of memory B cells are associated with antigen specificity. The retained MSP1/AMA1-specific B cells were mostly CD95+CD11c+ memory B cells and FcRL5-Tbet- atypical B cells. In contrast, the retained CIDRalpha1-specific B cells were enriched among a subpopulation of atypical B cells.

      These findings suggest differences exist in how the MSA1/AMA1 and CIDRalpha1 y are recognised and processed by the human immune system and how the immune response responds to them upon re-infection with P falciparum.

      Major issues affecting the conclusion: The findings and conclusions of this study, whilst positively exciting and informative, are based on the analyses of very few cells (at times). Even the authors themselves acknowledge this. I expect the authors to address this issue by toning down their reporting and conclusions (where appropriate). Ultimately, we need to have the confidence that these results are reproducible.

      We appreciate the reviewer’s concern about the numbers of antigen-specific cells included in our analyses, which is an inherent limitation of this approach. However, we would like to point out that most analyses included a substantial number of antigen-specific B cells:

      Figure 3D: 158 to 2,038 cells per group

      Figure 4: an average of 26 to 184 cells per donor

      Figure 5B: 55 to 508 cells per group

      Figure 5C: 10 to 334 cells per group*

      * The group with 10 cells is an outlier here. All other groups contain at least 104 cells. Because this one condition had such a small number of cells, we specifically mentioned this number in the text.

      The numbers of cells for analyses shown in Figures 3D and 5B were already included in the figures. All the other numbers were mentioned in Table S3. To further clarify the number of cells included in each analysis, we have added the number of cells to Figures 4 and 5C.

      To tone down our reporting, we have rephrased some of our conclusions, and now present our section headers in past tense to make these statements reflect our observation instead of a definitive conclusion. For example:

      Conclusion: “The loss of MSP1/AMA1-specific and CIDRα1-specific B cells in the circulation was similar, but the phenotype of long-lived MSP1/AMA1-specific and CIDRα1-specific B cells appeared to differ.”

      Section header: “Long-lived MSP1/AMA1-specific and CIDRα1-specific B cells differed in phenotype”

      Finally, in the Discussion section, we have added a statement to our paragraph describing the limitations of our study to stress the importance of reproducing our findings:

      All in all, it will be important to perform additional studies of the phenotype and functionality of long-lived B cells with specificity for P. falciparum antigens to reproduce and extend our findings.

      Minor comments: Figure 2D-I found this figure, and its presentation is unclear. Notably, using contour plots doesn't allow the reader to appreciate the density of the cells being presented.

      To facilitate the interpretation of this figure, we have changed the plot type to a contour plot with density color gradient, and added the number of cells shown in each plot. (Please note that this panel has been renumbered to C.)

      Figure 4 - label the y-axis.

      The y-axis was labeled with “%”, which we have expanded to “% of B cells expressing marker of interest”.

      __Significance: __The study design-as outlined-allowed for the analyses of the specificity and phenotypic characteristics of residual P falciparum-specific memory B cells after 1.7 years of little to no P falciparum exposure. The cell phenotyping methods presented are also appropriate. However, antigen-specific cells are rare in blood circulation, and as the authors themselves acknowledge in the discussion, some of the results are based on very few cells. This means we cannot be sure all the results presented are reproducible.

      Previous studies demonstrated that P falciparum memory B cells are maintained long after cessation of antigen exposure. However, few (if any) detailed antigen-specific and phenotypic analyses of the characteristics of P falciparum-specific memory B cells following a long period of no exposure exist. Thus, this study presents an incremental advance in our knowledge. In addition, the association of antigen specificity with cell phenotypes is a new concept in malaria immunology. The research presented will greatly interest infectious disease immunologists and vaccinologists.

      I am an infectious disease immunologist with substantial experience in malaria immunology.

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      Referee #3

      Evidence, reproducibility and clarity

      The authors analysed the antigen specificity and phenotypes of B cells during high P falciparum transmission and after a period of successful malaria control with IRS in Uganda. The gap between the two sampling time points is close to two years.

      They use antigen probes for MSP1/AMA1 and CIDRalpha1, two antigens expressed at different stages of P. falciparum life cycle-merozoites and infected red cells, respectively. While MSP1/AMA1 are involved in the parasite's invasion of red blood cells, CIDRalpha1 is a domain of PFEMP1, a large family of antigenically variant proteins that mediates the sequestration of infected red cells in small blood vessels.

      They found that the percentage of activated antigen-specific memory B cells declined with malaria control. However, detectable frequencies of antigen-specific memory B cells were retained after malaria control, which confirms earlier reports.

      However, they also demonstrate that the phenotypic characteristics of memory B cells are associated with antigen specificity. The retained MSP1/AMA1-specific B cells were mostly CD95+CD11c+ memory B cells and FcRL5-Tbet- atypical B cells. In contrast, the retained CIDRalpha1-specific B cells were enriched among a subpopulation of atypical B cells.

      These findings suggest differences exist in how the MSA1/AMA1 and CIDRalpha1 y are recognised and processed by the human immune system and how the immune response responds to them upon re-infection with P falciparum.

      Major issues affecting the conclusion:

      The findings and conclusions of this study, whilst positively exciting and informative, are based on the analyses of very few cells (at times). Even the authors themselves acknowledge this. I expect the authors to address this issue by toning down their reporting and conclusions (where appropriate). Ultimately, we need to have the confidence that these results are reproducible.

      Minor comments:

      Figure 2D-I found this figure, and its presentation is unclear. Notably, using contour plots doesn't allow the reader to appreciate the density of the cells being presented.

      Figure 4 - label the y-axis.

      Significance

      The study design-as outlined-allowed for the analyses of the specificity and phenotypic characteristics of residual P falciparum-specific memory B cells after 1.7 years of little to no P falciparum exposure. The cell phenotyping methods presented are also appropriate. However, antigen-specific cells are rare in blood circulation, and as the authors themselves acknowledge in the discussion, some of the results are based on very few cells. This means we cannot be sure all the results presented are reproducible.

      Previous studies demonstrated that P falciparum memory B cells are maintained long after cessation of antigen exposure. However, few (if any) detailed antigen-specific and phenotypic analyses of the characteristics of P falciparum-specific memory B cells following a long period of no exposure exist. Thus, this study presents an incremental advance in our knowledge. In addition, the association of antigen specificity with cell phenotypes is a new concept in malaria immunology. The research presented will greatly interest infectious disease immunologists and vaccinologists.

      I am an infectious disease immunologist with substantial experience in malaria immunology.

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

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      Referee #2

      Evidence, reproducibility and clarity

      Summary:

      In this study, the authors compared long-lived total and antigen (ag)-specific B-cell levels in a cohort of 10 Ugandan malaria patient samples that were collected before and after local reduction of P. falciparum transmission (pre/post-IRS). The focus is on the novel comparison of the two most common malaria antigens: merozoite antigens (MSP1/AMA1) and variant surface antigens (CIDRα1). Using high-parameter spectral flow cytometry, they also characterized the phenotype of the different populations of cells. Their main findings include 1) a decrease in activated but maintenance of resting ag-specific B-cells in the post-IRS sample and 2) CD95 and CD11c, as the only differentially expressed markers between MSP1/AMA1-specific and CIDRα1-specific long-lived memory B cells. Their further phenotypic characterization suggests functional consequences with MSP1/AMA1-specific B-cells being poised for rapid antibody-secreting cell differentiation while CIDRα1-specific B cells were enriched among a subset of atypical B cells that seem poised for antigen presentation (CD86+CD11chi/ AtBC1). Their findings consolidate and further expand our knowledge of long-lived B-cell levels during P. falciparum malaria and report/compare (for the first time to my knowledge) a differential selection of long-lived B-cell levels between these 2 antigen specificities. Overall, the manuscript is straightforward and well-written and the authors did a good job explaining their methodology, findings, and interpretations. I believe the major gap missing in this study is the reconciliation of long-lived antigen-specific B-cell levels with the serum antigen-specific antibody levels of these patients against the same 2 antigens (MSP1/AMA1 and CIDRα1) in the experiments and the discussion. The antibody data would strengthen their main argument and is the main missing piece for characterizing more completely the long-lived antigen-specific humoral responses. Below are my suggestions that would help improve the manuscript:

      Major comments:

      1. Serum Anti-Pf antibodies: Do the authors have access to the serum/plasma of these patients? It would be important to correlate the total and ag-specific B-cell populations with levels of serum IgG antibodies against those specific Pf antigens (MSP1/AMA1 and CIDRα1) and total IgG levels to strengthen their point about long-lived humoral responses.
      2. Correlation between populations and initial parasite load: Are the levels between any of the populations at any time point correlated significantly in any way? If the statistical power/N allows it, please perform a correlation array between all populations using all samples both total and ag-specific and initial parasite load.
      3. Figure 2: Why were total and ag-specific plasmablasts/plasma cells not included in this figure? Please include to compare levels in these two time points.
      4. Healthy baseline: The study is missing "healthy" controls as a reference. I presume this is because each patient is its uninfected control in the post-IRS sample. In methods, they mentioned they used two naïve-USA B-cells as technical controls. It would be important to include and maybe expand (to match age and gender)on that specific data from those controls as supplementary figures to support their findings:
      5. Show negative Tetramer staining for these samples (to understand the background).
      6. Levels of all the USA controls total B cell populations and compared to the pre/post-IRS samples to understand "baseline" or "non-endemic" control levels.

      Minor comments:

      1. In the gating strategy (S1), please include the percentage of each population of that representative example.
      2. For Figure 2, since not every panel has the same N, please include the N for each panel in the figure or a supplementary table.
      3. Please mention the history of past and chronic co-infections of these 10 patients. Particularly if they had any other active or recent infection when the sample was taken.
      4. Discussion: further discussion with relevant literature on the following points is needed to consolidate cellular and antibody studies: a. Whether the presence of long-lived ag-specific B-cell responses correlates with sustained levels of IgG against Pf antigens. b. The different types of antibodies (protective/pathogenic) that these different B-cell populations have been reported to produce during malaria.

      Significance

      General assessment:

      Strengths:

      • Novelty in contrasting two different types of P. falciparum antigen responses at the B-cell level.
      • The use of tetramers is a cutting-edge technique to assess this question.
      • Analyses were thorough and found contrasting differences in antigen-specific B-cell populations (atypical vs classical) between these 2 antigens for the first time (to my knowledge).
      • Well-written manuscript with clear data, methodology, and conclusions

      Limitations:

      • Missing serum/plasma antibody data to support their claim about long-lived humoral responses and reconciliation of ag-specific B-cell levels and ag-specific antibody levels in experiments and discussion.
      • Limited N of 10 patients of the same gender (female), some population analyses had even fewer samples.
      • Missing baseline levels for non-endemic uninfected control for B-cell populations for comparison.

      Advance:

      The study consolidates antigen-specific responses with the discovery of recently characterized populations (ex. atypical) and finds novel differences between two types of malaria antigen responses at the B-cell level and between specific populations responding differentially to these antigens. The findings are incremental (role of B-cell population in malaria-specific responses), conceptual (contrasting two types of B-cell antigen responses in the same infection), and clinical (finding significant differences in patients).

      Audience:

      This study will attract basic B-cell immunology scientists, infectious disease clinicians/scientists, vaccinologists, and both basic malaria immunology and clinical audiences.

      Reviewer expertise:

      Malaria, immunology, antibodies.

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

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      Referee #1

      Evidence, reproducibility and clarity

      This study by Reyes at al is a well conducted analysis of memory B cell dynamics of Plasmodium falciparum (Pf) -specific B cell populations over the course of reducing Pf prevalence in ten Ugandan adults. The data is presented well and the authors provide compelling evidence that 1. There is an overall loss of Ag specific B cells with reduction in exposure and 2. Different antigens (MSP1/AMA-1 vs CIDRa-1) generate different flavors of long lived responses. However, additional clarity to the reader should be provided on certain topics (listed below).

      Major comments:

      1. While the premise of the study (reduced Pf transmission due to the use of indoor residual spraying (IRS)) is an important one, I think the authors must take into consideration that 9/10 subjects had at least one Pf positive episode between Time Points 1 and 2 (Figure 1). Also, it looks from Fig 1 that some samples were collected at a time of Pf positive test (green squares), while in Table S1 none of the subjects have a positive parasite status at TP1.
      2. Figure S1A: What is trBC? Figure S1B: What is Strep? Are the strep positive cells also CIDR-1 positive and were they gated out? Why is APC used for MZ-1 and one of the MSP1-AMA-1 tetramers? Do these stainings come from multiple panels?
      3. Figure 3A: how many cells does the umap plot represent? Were there a total of 3555 Ag specific B cells that were non-naive (Figure 3E)?
      4. Could the authors comment on why in Figure 3, Ig isotype expression was not considered for clustering? This would allow for characterization of DN sub populations/ clusters in addition to the CD21-CD27- ABCs? It looks like IgD expression was low across the clusters (Figure 3D). Was this the case for the cells considered in this analysis, or was it excluded? If it was truly low expressed, how were the assessments in Figure 2 made?
      5. Are there differences in these designations / phenotypes of DN populations of atBCs vs CD21-CD27- atBCs?
      6. Lines 258-259: In considering only switched MBCs, what clusters from Figure 3a were included? There seem to be 2588 sw MBCs (Table S3, Figure 4). Do the remaining cells (967 cells) come from clusters 2, 5 and 6 (and excludes the atBC clusters)

      Minor comments:

      1. Line 178- 179: Was there a specfic measure of rate of decline made for these cells?

      Significance

      General assessment:

      Strengths: The authors provide evidence that the dynamics of antigen specific cells in humans can vary with exposure and with the nature of the antigen. They have nicely discussed the potential causes for these differences (Discussion), although they should include the findings of Ambegaonkar et al that ABCs in malaria may be restricted to responding specifically to membrane bound antigens (PMCID: PMC7380957)

      Limitations:

      1. Outlined above, and as the authors also mention, a small sample size and homogenous population.
      2. The evidence for reduced transmission is not clear, and the negative parasite tests for donors shown in Table S1 do not match with Figure 1 data.
      3. Lack of IgD expression across clusters (Figure 3D- the authors will need to clarify this point) would require re-analysis of Figure 2 data

      Advances: This study highlights the importance of studying antigen specific B cells in humans in the context of natural infection and the use of high-parameter tools such as spectral flow cytometry in assessing a large quantity of data from limited clinical samples. These data are important to inform better vaccine design. Studies in inbred animals can be quite limited or different from human B cell responses.

      Audience: This study will be of interest to malariologists and B cell immunologists. Atypical B cells are relevant to many infectious diseases and auto immunity, while the dynamics of memory B cells in malaria all be relevant to those interested in vaccine design against blood stage antigens.

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      Reply to the reviewers

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

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      Referee #3

      Evidence, reproducibility and clarity

      Summary

      The manuscript presents IGNITE (Inference of Gene Networks using Inverse kinetic Theory and Experiments), an unsupervised machine learning framework for constructing gene regulatory networks from single-cell RNA sequencing (scRNA-seq) data. IGNITE utilizes a kinetic inverse Ising model to infer gene interactions from binarized expression data and can predict genetic perturbation effects, such as those from knockout experiments. Although the application of inverse Ising models to network reconstruction is not entirely novel, IGNITE's specific implementation and its application to single-cell RNA sequencing data represent a new development. The method is tested on the transition from naive to formative states in murine pluripotent stem cells, a system the authors are highly knowledgeable about, and its performance is compared to state-of-the-art alternative methods.

      Major concerns

      My concern regards the generality of the method, particularly the entire pipeline presented, and the fairness of the performance comparison. These concerns can be easily addressed by the authors by better explaining their choices and their general applicability, and by toning down the conclusions about the comparison with existing inference methods.

      The pre-processing steps are extensive, and their rationale is not always clear, though the results heavily depend on this analysis. Several steps appear to involve arbitrary choices optimized for specific outcomes, potentially introducing biases. The authors should better explain the rationale behind their choices to mitigate these concerns.

      Specifically, part of the pipeline seems to be built to reproduce a specific expression pattern of 24 genes that some of the authors discovered in a previous paper. Although this prior knowledge could be useful and relevant in this specific system, it could limit the generality of the method. For example, the authors selected approximately 2000 genes based on prior knowledge and used a combination of t-SNE and UMAP for dimensionality reduction (although the two techniques have a similar goal). This specific combination seems to reproduce the pseudotime alignment the authors were expecting to find, but such prior information might not be available in general. Therefore, feature selection and the methods used to project data need more justification, especially if the goal is to create a general tool applicable across different biological systems.

      Analogously, the clustering seems manually adjusted to match known expression patterns of 24 relevant genes, rather than being the result of an optimized clustering method. Additionally, the clusters overlap with different time points, raising concerns about potential batch effects. These issues should be addressed to strengthen the validity of the method.

      The claims about the comparison with existing methods should be toned down. While the comparisons are useful and interesting, they might be biased due to the method's fine-tuning for the specific system studied. The claim that the model requires only scRNA-seq data is misleading, as strong prior biological knowledge was used to select, for example, the genes analyzed.

      Significance

      The manuscript is scientifically sound, clearly written, and deserves publication. The proposed method is quantitative, novel, theoretically grounded, and was tested in detail with appropriate null models and statistical methods. Moreover, IGNITE can be applied to various biological systems as the availability of scRNA-seq datasets is continuously growing. The paper will be of interest to a broad community of computational biologists and biology labs interested in gene regulation using scRNA-seq data.

      The limitation, in my opinion, is the method's (particularly the pre-processing pipeline) fine-tuning for the specific biological system tested. Testing IGNITE on another biological system without pre-selected pre-processing steps or detailed biological priors would be more convincing and make the paper's conclusions much stronger. The comparison with other methods also may be slightly biased due to this fine-tuning.

      My background is in statistical physics, with expertise in biological physics, specifically in mathematical modeling and data analysis in molecular biology.

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      Referee #2

      Evidence, reproducibility and clarity

      Corridori et al introduce IGNITE, a computational framework to infer gene regulatory networks (GRNs) from scRNA-seq data leveraging the kinetic Ising model, which can be used to simulate synthetic gene expression and perform in-silico knockout experiments. Other similar frameworks exist, but none combine these three aspects together. The authors have generated a scRNA-seq of murine ESCs differentiation which they use to compare their method with others. Specifically they show that they can infer known regulatory interactions, that they can generate similar data than the original and that it can potentially predict gene expression changes in transcription factor knock-out perturbations.

      Major comments:

      • Many of the authors' claims are backed by qualitative results and not properly quantified. In Fig2, authors qualitatively compare intra gene correlations between genes for the original data and their prediction. Instead of just visualizing they should compute and report the Spearman correlation between the original expression and the predicted one. The Fraction of Agreement is not a good metric to compare knockout predictions since it is completely dependent on the class imbalance of signs, for example if the selected genes are 75% positive and 25% negative, a naive predictor that only outputs positive predictions will still have a high score. Instead, the authors should quantify this with Spearman correlation or RMSE and compare across methods. In FigS4a-b the authors qualitatively claim that other methods could not predict the expected cell composition, which they should quantify and report the values across methods. When comparing against the ground truth network, the fraction of correctly inferred interactions is technically the same as precision but is ignoring recall. I suggest the authors compute precision, recall and a combined F1 score to compare the evaluated methods. Authors claim that the method is scalable to a larger number of genes but no data is provided, they should show how their method compares to others when using a different number of cells and number of genes at memory usage and running time.
      • The authors need to better describe which tests were performed when talking about significance, which thresholds and which corrections, if any, were employed.
      • To reduce the number of dimensions of scRNA-seq data the authors use t-SNE and then from the obtained result UMAP to project the data into a lower dimensional space. This is fundamentally wrong since distances are not well preserved in t-SNE. Instead the authors should first employ PCA and then UMAP. Additionally, the authors use UMAP distances in the Slingshot pseudotime calculation. Similar to t-SNE, UMAP distances have no real meaning and should only be used for visualization purposes. Instead, the authors should provide Slingshot the obtained PCA embeddings.
      • Dictys (PMID: 37537351) is a known GRN inference method that also can simulate gene expression but is missing in the benchmark, the authors should add it to the method comparison.
      • The current manuscript is not reproducible since it is missing the method's code, the code to reproduce the figures and the generated scRNA-seq data.
      • Authors claim that the method is scalable to a larger number of genes but no data is provided to back this claim. They should show how their method compares to others when using a different number of cells and number of genes.

      Minor points:

      • In the introduction, authors mention multimodal GRN inference methods but do not provide any references.
      • In Table 1, CellOracle is annotated as not being able to do multiple KO which is wrong. Additionally, the authors mention that IGNITE uses no prior knowledge which is not really true since it requires pseudotime ordering. The authors should add a column to Table 1 whether methods require pseudotime.
      • It is unclear what the dashed arrow of Fig1b means. Moreover, plotting gene expression values on top of UMAPs can be misleading, instead authors should plot the gene expression distributions binned by pseudotime.
      • The authors report a p-value of 1.04x10-171 which is below detection limit (see PMID: 30921532). Authors should change it to an interval such as p < 2.2×10-16.
      • To make CellOracle results easier to interpret and more comparable, authors should run it at the atlas level instead of at the cell type level, this way generating only one GRN. This can be achieved by assigning the same cluster label to all cells.
      • Experimental values in FigS3b seem to have been repeated and do not match the previous ones for IGNITE and SCODE.
      • It is unclear what the different circles mean in Fig5b.

      Significance

      This manuscript is an incremental and methodological work for specialized audiences. Its strengths are that the authors employ kinetic Ising model for GRN inference and that they provide a single framework capable of inferring, simulating and perturbing gene expression. The main limitations are that the claims should be better quantified and that the code and data need to be made accessible.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary

      Corridori and colleagues propose IGNITE, a novel method to recover Gene Regulatory Networks (GRN) from single cell RNA-sequencing (scRNA-seq) data. Their method solves the inverse Ising problem generating a cohort of candidate GRN optimising it to minimise the difference to the input expression matrix. Authors report the IGNITE is able to predict wild type data and simulate both single and multiple gene knockouts. Authors benchmark this method on a in-house data set of differentiating pluripotent stem cells (PSC). They focus on a small set of genes known to be involved in PSC differentiation into formative cells. Authors benchmark IGNITE against state of the art tools (SCODE, MaxEnt and CELLORACLE). They evaluate IGNITE ability to predict wild type gene expression by comparing their data with experimental data and with SCODE. They conclude the tool has generative capacity comparable with SCODE. They also evaluate IGNITE ability to recover known interactions with respect to other tools without finding it to significantly outperform them.

      Major comments

      • Are the key conclusions convincing?

      Conclusions appear convincing although model generalizability could be shown in a more thorough manner. For instance, analysing some other publicly available dataset could help demonstrate hyperparameters effects on GRN predictions and their robustness across different experiments. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

      Claims are well supported by data. - 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.

      I think the work would benefit from an additional benchmark on a different cellular system. This experiment would show how hyperparameters generalise across datasets and would provide potential users insights how to tweak them.

      Also, how does the model scale with the number of genes? A benchmark on computation time and resources required to infer GRN of growing size would be valuable in the adoption of this tool.

      In addition, I think the GRN comparison benchmark presented in section (3.4) would benefit from a quantitative discussion. Authors show inferred GRNs in Figure 4 and S5. For instance, measuring matrix similarity (when appropriate) would help understanding how predicted GRN compare. I understand authors attempt to do so by focusing on validated interactions and computing the fraction of correctly inferred interactions (FCI) but I think a measurement of the overall similarity (eg. Pearson correlation) would add on this.

      Another comment regards the dependency between Correlation Matrices Distance (CMD) and FCI, shown in Figure 5. I understand that IGNITE GRN that maximise FCI are not the same that minimise CMD. However, it looks like GRN that maximise FCI have higher value in terms of biological information. I wonder whether optimization for one or the other metric could be left to the end user as a tunable parameter.

      Authors should discuss why the expression of some genes does not follow the expected trends (Fig 1C vs Fig S1A). Out of the 24 genes they select for their analysis, at least four do not follow the expected trends: Sox2, according to literature, is a Naive gene, however, in Figure 1C its gene expression pattern is more similar to Formative late genes. Other genes with similar "unexpected" patterns are Zic3, Etv4 and Sall4.

      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.

      I think suggested experiments are doable as long as authors get publicly available data, i.e. the in-house dataset they generated for this study is enough to show applicability. For example datasets analysed in SCODE paper (https://doi.org/10.1093/bioinformatics/btx194) could be used as second benchmark. The point of applying the tool to another dataset is to show how it generalises across different biological systems, experiments and, potentially, sequencing technologies. - Are the data and the methods presented in such a way that they can be reproduced?

      The methods section is really clear. To enable reproducibility both raw scRNA-seq data, the IGNITE source code and code written to benchmark it should be released in the public domain in appropriate repositories (eg. ENA, GitHub, Binder etc). - Are the experiments adequately replicated and statistical analysis adequate?

      Yes.

      Minor comments

      • Specific experimental issues that are easily addressable.

      Related to the Sox2 expression pattern is the binarization shown in Figure 2D. How is it possible that Sox2 is always marked as active? Could the authors clarify how these outlier behaviours emerge and propose mitigation strategies, if any?

      In section 5.11.2 it is unclear if xi are in log scale or not. Since the model starts from binarized, log transformed expression values, should not generated ones be in the same scale as the input? - Are prior studies referenced appropriately?

      Yes, referencing is clear. - Are the text and figures clear and accurate?

      Yes, figures appear to be clear, readable and well documented both in captions and main text. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

      Section 3.3 could be improved by better describing experimental datasets. Only in the methods section it is clearly stated that experimental data for single KO experiments were retrieved from the literature.

      Check typesetting:

      • parenthesis missing in Eq. 1
      • Leftover $ in section 3.1
      • Parenthesis missing in Section 3.3
      • Misplaced comma in section 5.2.1

      Significance

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

      The paper presents a method to infer GRN from scRNA-seq data alone. Applications include GRN prediction and their perturbations. This paper represents a technical advance in the field as it is the first application of the inverse Ising problem GRN inference. - Place the work in the context of the existing literature (provide references, where appropriate).

      The paper itself presents the landscape of GRN inference tools using scRNA-seq data: SCODE, MaxEnt and CELLORACLE. More tools exist, for instance SCENIC (https://doi.org/10.1038/nmeth.4463) mainly relies on co-expression matrices. Other tools exist but require additional data types e.g. GRaNIE and GRaNPA (https://doi.org/10.15252/msb.202311627) leverage on physical interaction data (ATAC-seq, ChIP-seq). Similarly DeepFlyBrain uses deep neural networks to infer eGRN in Drosophila (https://doi.org/10.1038/s41586-021-04262-z). The value of tools like IGNITE and its competitors is that they do not require additional data types, which, in turn, helps in controlling experimental costs. - State what audience might be interested in and influenced by the reported findings.

      The paper might be of interest to biologists interested in regulation of gene expression. The tool might turn out to be useful in planning experimental work by guiding the choice of perturbations to introduce in experimental systems. - 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.

      I am a computational biologist.

      I have no sufficient expertise to evaluate the mathematical details of the method.

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      Reply to the reviewers

      REVIEWER 1

      Reviewer #1 Evidence, reproducibility and clarity: Nornes et al. have generated a cohort of arterial enhancers based on in silico analysis and validation with transgenic lines in both zebrafish and mice. They utilized publicly available datasets for chromatin marks, including ATAC-seq on endothelial cells either from cell culture or isolated from mice, as well as EP300 binding, H3K27Ac, and H3K4Me1. Focusing on eight arterial-expressed genes, they identified a putative enhancer region marked by at least one enhancer feature. After validating the activity of these enhancers in zebrafish and mice, the authors assessed the regulatory pathways upstream of these genes. Using ChIP-seq and Cut&Run for key endothelial transcription factors, they discovered that binding sites for SoXF and ETS factors are shared in arterial enhancers, whereas binding sites for Notch, MEF2, and Fox are present only in the subset of identified enhancers. Together this study provides an arterial enhancer atlas that allows further characterisation of regulatory network behind endothelial cell identity.

      __Reviewer #1 Major Comment 1: __The authors have assessed 15 enhancers for arterial-venous specificity, by assessing the expression in DA, ISV, cardinal and ventral veins at 2 dpf. Interestingly there is a clear difference in the expression patterns of these enhancers in the zebrafish axial vasculature, especially seen at the level of ISV. The co-localization of the enhancer expression in the endothelium was done using endothelial marks expressed in both venous and arterial EC (kdrl). To fully distinguish if the expression is venous or arterial endothelial compartment colocalization with Tg expressed in arterial (flt1) or venous (lyve1) EC would be informative.

      RESPONSE: We agree with the reviewer that a more detailed description of arterial-venous specificity of each enhancer could be included. In the original manuscript, the expression pattern of each enhancer within the vasculature was primarily assessed at 2 days post fertilization (dpf) in Fig 1-2. This identified arteries using direction of blood flow and available descriptive information, as arterial development in 2pdf zebrafish is very stereotypical and already well characterized.

      __REVISION (PLANNED): __The original Figure 3A includes a more detailed assessment of arterial-venous specificity at 3dpf for four arterial enhancers (Cxcr4+135, Cxcr4+151, Gja5-78 and Gja5-7, chosen as enhancers representing the four types of expression patterns seen). We will now extend this more detailed analysis to all arterial enhancer:GFP lines. This analysis uses kdrl-mCherry to mark the entire vasculature, comparative to the expression of the arterial enhancers (GFP). This allows us to clearly identify the intersegmental arteries (as opposed to intersegmental veins) by looking for direct connection to the dorsal aorta, and by assessing the direction of blood flow within these vessels. This analysis is done at 3dpf to give time for the intersegmental arteries to acquire identity and connect definitively with the dorsal aorta, and for the diminishment of any GFP expression originating from the initial sprouting from the dorsal aorta. By extending this analysis to the other arterial enhancer zebrafish lines shown in Figure 2, we will be able to more clearly classify the activity of each enhancer within different vascular beds. This information will also be recorded in a new Table better detailing the timing and specificity of activity of each enhancer.

      We chose not to use arterial or venous "marker lines" (e.g. Flt1:reporter or Lyve1:reporter) for the simple reason that these are also enhancer:GFP transgenes, and therefore are not necessarily definitive of the arterial or venous lineage per se (e.g. Flt1:GFP expression is controlled by the transcription factors binding the Flt1 enhancer in the same way that Cxcr4+135 and the others are, with the added caveat that the transcriptional regulation of the Flt1 and Lyve enhancers are not well defined). We felt that morphological determination based on direct connections and blood flow direction was therefore more accurate.

      __Reviewer #1 Major Comment 2: __In addition, it is striking that cxc4+135 drives the expression in nearly every ISV as cxcl12+269 only every other. Similarly, not all the enhancers are enriched in the DA to the same level. Is there biological significance to this? could authors discuss these results further? The pattern of expression of the unc5b-identified enhancer is also striking, does this reflect the known roles of unc5b in the vascular formation?

      __RESPONSE: __We agree, the diversity of enhancer expression patterns within the arterial compartment is notable, and really very interesting. The variations in enhancer expression pattern must be largely influenced by the transcription factor motifs within each enhancer, as these patterns were seen in both transient and stable transgenic zebrafish and therefore largely independent of chromatin integration location.

      __REVISION (PLANNED): __The extension of Figure 3A to all enhancer lines (see previous comment) will permit us to more clearly classify the activity of each arterial enhancer within different beds and at different time points. Currently there were no clear links between a particular transcription factor motif/binding and expression pattern, something that is discussed briefly in the original Results and Discussion sections. However, the expansion of Figure 3A to all enhancers, and the creation of a Table summarizing this more systematically will make the link (or lack of one) between expression patterns within the arterial tree and TF motifs easier to appreciate and discuss.

      __Reviewer #1 Major Comment 3: __The final part of the paper focuses on defining the presence of "deeply conserved" transcription factor binding sites (TFSB), defined as TFBS that are as conserved as the enhancer sequence surrounding them. In literature, the term 'deep conservation' refers to evolutionary conservation (genomic sequence preservation) in a wide range of species. Therefore, the additional classification presented by the authors based on the surrounding sequence is not clear. As, the KLF motifs in the Ece1in1, which is conserved between mouse and human, are defined as "deeply conserved". However, the FLK motif in the following enhancer, Flk1in10 (one line below), gets classified as non-deeply conserved, despite also being conserved between mouse and human. Thus, in the current form, there is a contradiction in the way the authors use the term 'deeply conserved' and the accepted meaning of this term. To avoid confusion, it would be important to revise this nomenclature.

      RESPONSE: We agree that this nomenclature should be revised. Our aim was to develop a standard approach to transcription factor motif analysis that could be applied to enhancers regardless of conservation levels and size, and easily replicated by others. Because not all functional transcription factor motifs within enhancers are necessarily conserved between species, we were careful to label both conserved and non-conserved motifs for each TF examined. Nonetheless, extra emphasis was placed on motifs with confirmatory TF binding evidence (e.g. ChIP-seq/CUT&RUN), and those conserved at the same depth as the surrounding sequence. This was because our previous work on endothelial enhancers clearly indicates that these motifs are far more likely to play a key role in regulation. However, the reviewer is correct to note that referring to such motifs as "deeply" conserved could be misinterpreted.

      REVISION (COMPLETED): We have altered our nomenclature. This is explained in the relevant Results sections: "Because the level of conservation of motifs can often be an indication of their importance to enhancer activity, we classified each motif into three categories: strongly conserved (motif conserved to the same depth of the surrounding sequence), weakly conserved (motif conserved in orthologous human enhancer but not to the same depth as the surrounding sequence) and not conserved (motif is not conserved within the orthologous human sequence)".

      Two enhancers (Unc5b-57 and Cdh1-1) were only conserved human-mouse, therefore each TF motif within these enhancers could be annotated as both weakly and strongly conserved. As the reviewer noted, this does create confusion. We have now adjusted Figure 5 to use a distinct shape for motifs for which no distinction between weak and strong motif can be made. This does not cover Ece1in1, which is conserved human-mouse-tenrec but was erroneously originally labelled human-mouse only. This error has been corrected.

      __Reviewer #1 Minor Comment 1: __Details on how the corresponding non-coding regions between mice and humans were established are missing, what alignment tool was used?

      RESPONSE AND REVISION (COMPLETED): This information has now been included in the relevant Results section: "Orthologous human enhancer sequences were identified for every enhancer using the Vertebrate Multiz Alignment & Conservation Track on the UCSC genome browser"

      __Reviewer #1 Minor Comment 2: __Not sufficient details are provided for the re-analysis of siRNA data. E.g., which clustering method was used? How the clusters were assigned to cell identities?

      RESPONSE AND REVISION (COMPLETED): The details regarding the re-analysis of scRNA data has been expanded in the Methods sections: "Publicly available E12 and E17.5 scRNA-seq data from EC isolated from BmxCreERT2;RosatdTomato lineage traced murine hearts54 was obtained from GEO (GSE214942) prior to processing FASTQ files with the 10X Genomics CellRanger pipeline (V7.0.0). RNA-seq reads were aligned to the mm10 genome reference downloaded from 10X Genomics with the addition of the TdTomato-WPRE sequence. Exclusion of low quality cells with either a UMI count >100,000, total gene count 10%) was performed using Scater55. Data normalisation was performed using the MultiBatchNormalisation method prior to merging of TdTomato positive and negative datasets from individual timepoints. The top 2000 most highly variable genes (excluding mitochondrial and ribosomal genes) in the merged datasets were identified using the Seurat FindVariableFeatures method and utilised to calculate principal component analysis (PCA). Normalised data was scaled using the ScaleData function. Cell clustering was performed using the standard unsupervised graph-based clustering method implemented within Seurat (V4)56. Clusters were visualised in two dimensions using UMAP based non-linear dimensional reduction following the standard Seurat (V4) workflow49. Identified clusters were assigned identities based on marker genes shown to be differentially expressed between populations previously identified in the original study47. Key markers include Npr3 (endocardial), Fabp4 (coronary vascular endothelial), and Nfatc1 (valvular endothelial). The E12.5 sinus venosus EC cluster was assigned based in Aplnr as previously described54. Arterial and venous EC clusters in the E17.5 datasets were annotated based on their enriched expression of Gja5 and Nr2f2, respectively."

      __Reviewer #1 Minor Comment 3: __Details about the first HOMER analysis (in the assessment of transcription factor motifs and binding patterns at arterial enhancers) seem to be missing from the methods section.

      RESPONSE AND REVISION (COMPLETED): This has been included in the methods: "Analysis of overrepresented motifs within our validated arterial enhancer cohort was performed with HOMER's findMotifsGenome tool using the full validated region of the arterial enhancers. The analysis used the hg38 masked genome and otherwise default settings for all other parameters including randomly selected background regions".

      __Reviewer #1 Minor Comment 4: __Pg 12: "For ETS, 23/23 arterial enhancers contained at least one conserved motif (all "deeply" conserved to the same depth as the surrounding enhancer, see S7)". Is it S8, where conservation is indicated?

      __ ____RESPONSE AND REVISION (COMPLETED):__ We have corrected this error in the text - no figure actually needed to be referenced here as the previous sentence contained the full list of relevant figures to this statement (Table 2 and Figures 5 and S9, previously called S8, are the places to see this information).

      __Reviewer #1 Minor Comment 5: __Figure 1 and 2 for non-zebrafish readers it would be useful to indicate in Figures 1 and 2 the non EC expression that can be observed in the embryos.

      RESPONSE AND REVISION (COMPLETED): In addition to arterial expression, a number of the enhancer:GFP transgenes also showed GFP expression within the neural tube. In addition, some transient transgenic embryos also showed ectopic expression in muscle fibres. These have now been indicated on the images in Figure 1 and 2.

      __Reviewer #1 Minor Comment 6: __Table S1: Please, indicate in the legend what the asterisk in the H DNAseI column stands for

      RESPONSE AND REVISION (COMPLETED): The asterisk indicates where DNaseI hypersensitivity is also seen in multiple non-EC lines. This explanation has been added to the legend.

      __Reviewer #1 Minor Comment 7: __Figure S8: The phrasing "conserved to animal" in Figure S8 is misleading. There is no difference in something being conserved to tenrec or manatee, as both are Afrotherians. Hence, the data show that both Efnb2-141 and Ephb4-2 were present in the common ancestor of Afrotherians and humans, namely the ancestor of all placentals. Instead, it would be good to indicate the phylogenetic group for which the presence of the enhancer can be inferred (in this case, Placentalia).

      __RESPONSE: __Whilst I appreciate the point, it is the exact sequence that is important here - obviously tenrec and manatee are similar species but still contain differences in nucleotide sequences. The information about conservation leads the reader to the exact species with which the comparison is being made. We tried to restrict this to just one species per phylogenetic group (e.g. tenrec, opossum, chicken, zebrafish) but occasionally this was not possible.

      Reviewer #1 Significance

      To date, a systematic approach to identifying the regulatory networks driving endothelial cell identity is missing. This study provides important datasets and validation of enhancers involved in arterial gene expression and the associated transcription factors. Although this is only the tip of the iceberg, this work represents a significant milestone in the systematic understanding of how arterial gene expression is regulated. Overall, this study offers a powerful resource for understanding arterial gene regulation and conducting genome-wide studies of arterial enhancers.

      __RESPONSE: __We thank the reviewer for these kind words. Whilst we agree this is only a very small snapshot of all the arterial enhancers involved in gene regulation, we would like to stress that not only is this a massive increase to what has been known previously, but is also deliberately focused on the genes used to define arterial identity during development and in the adult, therefore these enhancers by themselves form an extremely valuable dataset with which to study the key factors driving arterial differentiation and identity.

      __ __


      REVIEWER 2

      __Reviewer #2 Evidence, reproducibility and clarity: __In this work, Nornes and collaborators have described a cohort of arterial enhancers that drive gene expression in arteries and not in veins. The paper is very well written and it is very informative. The authors have used in silico models to identified the potential artery enhancers and then used different developmental in vivo systems, zebrafish and mice, to validate their findings. Finally, the authors have explored what transcription factors may be binding the identified enhancer sequences and thus, drive arterial gene expression. I would like to congratulate the authors for this work that it has been a pleasure to read and review.

      Reviewer #2 Major Comment 1: In their identification of enhancers, the authors consider a candidate every enhancer that has a putative mark in both mouse and human. Nevertheless, all the human data comes from in vitro analysis. Considering how much cell culture affects endothelial cell identity, inducing effects like EndoMT, would this have any effect on the enhancer selection? Would it be possible to search any human in vivo data? Would this allow for even stronger and more relevant sequences?

      __RESPONSE: __We agree that the use of human endothelial cells in culture raises some potential issues. However, we stress that the mouse EC enhancer marks, which played a key role in defining putative enhancers, come from in vivo analysis (E11 embryos, P6 retina and adult aorta), limiting the potential for significant impact from cell culture-induced issues. Whilst we would have enthusiastically incorporated human in vivo data had it been available, our approach was still indisputably successful at identifying arterial enriched/specific enhancers.

      We consider it unlikely that culture/identity-related problems with human cultured ECs led to a significant undercount of enhancers, in part because comparatively few regions with enhancer marks in mouse in vivo ECs were excluded due to the absence of human enhancer marks. In fact, Cxcr4, Cxcl12, and Gja5 were poorly transcribed in the human cell lines studied here and consequently only enhancer marks in mouse were used to define putative enhancers for these three genes (this is clearly stated in the Results section). If a similar rational had applied to the remaining five genes, only an additional six putative enhancers would have been tested (one for Gja4, two for Nrp1 and three for Unc5b). However, we felt it made sense to include analysis of human enhancer marks for these five genes, as all were expressed in the human ECs used (as indicated by H3K1Me3 and DNaseI hypersensitivity at promoter regions) and orthologous human enhancers were identified for all. Additionally, our retrospective analysis of previously described mammalian in vivo-validated EC enhancers (Table S1 in the original manuscription, including eight arterial enhancers) found that all 32 were marked by at least one enhancer mark in human samples (1/32 did not contain mouse enhancer marks). We also tested eleven regions that did not reach our putative enhancer threshold, including five with only mouse marks. None of these directed expression in transgenic analysis.

      Reviewer #2 Major Comment 2: The human data comes from vein endothelial or microvasculature endothelial cells. Specially because some of the enhancers identified by the authors drive also vein expression, could the authors discriminate whether this is due to the identification coming from vein cells. Is there available data from HAECs? Would this not be conceptually more correct that using vein endothelial cells data? This should be at least discussed in the paper.

      __RESPONSE AND REVISION (COMPLETED): __We have now included a comparison with enhancer marks from HAECs, telo-HAECs and HUAECs as a new Figure S5. The enhancer marks seen in these cells were very similar to those in the HUVEC and microvascular cells already surveyed. Had enhancer marks within HAECs/telo-HAEC/HUAECs been included as a human enhancer mark in our initial survey, it would have been unlikely to have altered our analysis, although we agree it would have made it more conceptually correct. We chose not to go back and engineer this into our original enhancer selection rational however as we felt it would be intellectually dishonest. A paragraph has been added to the Results section about this analysis.

      Reviewer #2 Major Comment 3: Although the authors use the mouse embryo to further validate their finding beyond the zebrafish, the expression are a bit different. While on the fish the enhancers label smaller vessels of arterial identity, in the mouse, only bigger arteries are marked. Is this defined by the time of the analysis?

      __RESPONSE: __This experiment was conducted to demonstrate that these enhancers were arterial enriched in both zebrafish and mouse transgenesis, and feel this is clearly shown by the current data. Whilst I do not really agree that the expression pattern is different (for example, the Gja5 enhancers are more restricted to the major arteries in both zebrafish and mouse, compared to the more widely expressed Efnb2-333), this is challenging to ascertain at a single time-point in a transient transgenic mouse assay. Whilst it would be potentially interesting to better assess the activity of these enhancers over time in mice, we consider this a lengthy experiment (multiple stable lines would need to be established and characterized for each enhancer) which would not add particular benefit to this paper.

      Reviewer #2 Major Comment 4: The analysis of the enhancers is only done during development. Is the activity of these enhancers maintained through live or only important for artery vs vein determination? Is the expression of the different enhancer reporters maintained into adulthood?

      RESPONSE AND REVISION (PLANNED): We agree this would be interesting to ascertain. We plan to examine the activity of enhancer:GFP activity in adult fish fins (which are accessible even without crossing into a casper background, which is beyond the timescale of this project) in the fully revised version of this paper. We have already conducted a feasibility study on four arterial enhancers:GFP lines (Gja5-7:GFP, Gja5-78:GFP, Gja4+40:GFP and Efnb2-333:GFP), which found that all four were still active, and arterial-specific, in the adult.

      Reviewer #2 Significance

      This is a very well done study with potential interest for vascular biologists, in particular to those interested in the determination between artery and veins in a context of development. It advances our knowledge on the field of vascular biology as it not only proposes potential enhancers but also goes on to validation of the enhancers. Nevertheless, it is important to note that some of this enhancers have been identified from in vitro human data. In vitro culture of endothelial cells affects their cellular identity and thus, this study may have underscored many potential enhancers.

      REVIEWER 3

      __Reviewer #3: Evidence, reproducibility and clarity: __This manuscript by Nornes et al analyzed multiple published databases and identified a group of putative enhancers for 8 selected non-Notch arterial genes in mouse and human ECs. These enhancers were cloned and screened in fish embryos to test their effect in driving GFP reporter expression, which narrowed down a cohort of enhancers for further testing of expression activities in mouse embryonic arteries. The authors then analyzed the sequences of these enhancers, and identified binding motifs of ETS, SOX-F, FOX and MEF2 family TFs and Notch transcription regulator RBPJ commonly present in closed proximity in these arterial enhancers, suggesting interaction between these TFs in determination of arterial identity.

      Reviewer #3 Major Comment : This study provides an enormous amount of bioinformatic data analysis and screening results in transgenic fish and mouse models, which led to the discovery of a group of arterial enhancers and TFs binding motifs essential in regulating arterial identity.

      Reviewer #3 Other Comments ____1: Choice of arterial genes is slightly biased. Acvrl1/Alk1 is not enriched in arterial ECs. Sema3G, which is highly expressed in arterial ECs, is missing. UNC5B is enriched in arterial ECs but also expressed by sprouting ECs (PMID: 38866944).

      __RESPONSE: __When we started this project, scRNA-seq datasets in the developing vasculature were less available. Consequently, we initially based our choice of genes on data from Raftrey et al., Circ Res 2021 (available earlier on bioRxiv), which was focused on mouse coronary arterial ECs at the timepoints that arteries differentiate. This found Acvrl1 to be arterial enriched (not a novel observation, many publications treat Acvrl1 as arterial specific or arterial-enriched) and did not list Sema3g. We also considered a wider dataset from mouse and human mid-gestation embryos when available (Hou et al., Cell Research 2022). However, it is important to note that we did not aim to investigate every arterial-enriched gene, rather to use these datasets to help identify loci associated with gene expression patterns which indicated a high likelihood of containing arterial enhancers active during arterial differentiation.

      Sc-RNAseq data from both Raftery et al., and Hou et al., indicated that arterial ECs are subdivided into two groups, reflecting maturity but also potentially slightly different developmental trajectories. The genes studied here were therefore selected to evenly cover both subgroups, with Acvrl1, Cxcl12, Gja5 and Nrp1 primarily restricted to the mature arterial EC subgroup, while Cxcr4, Efnb2, Gja4 and Unc5b were also expressed in the less mature/arterial plexus/pre-arterial EC subgroup. It is notable that genes within the latter subgroup are also associated with angiogenic/sprouting ECs (Dll4 also belongs to this subgroup), which likely indicates biological links between angiogenesis and arterial identity rather than a problem in gene choice and specificity.

      __REVISION (COMPLETED): __This is already discussed in the Results section (angiogenic expression of arterial genes is discussed within the MEF2 and RBPJ sections) and in the Discussion (paragraph 2, referring to different expression patterns within arterial ECs). However, we have now edited the relevant Results section to better explain gene selection: "It is therefore clear that a better understanding of the regulatory pathways directing arterial differentiation requires the identification and characterization of a larger number of arterial enhancers directing the expression of key arterial identity genes. To identify a cohort of such enhancers, we looked in the loci of eight non-Notch genes: Acvrl1(ALK1) Cxcr4, Cxcl12, Efnb2, Gja4(CX37), Gja5 (CX40), Nrp1 and Unc5b. Although not a definitive list of arterial identity genes, single cell transcriptomic analysis indicates these genes are all significantly enriched in arterial ECs4,20, and are commonly used to define arterial EC populations in mouse and human scRNAseq analysis4,5,20,54. Additionally, single-cell transcriptomic data indicates that arterial ECs can be divided into two subgroups4,20. The genes selected here are equally split between subgroups (Acvrl1, Cxcl12, Gja5 and Nrp1 from the mature arterial EC subgroup, Cxcr4, Efnb2, Gja4 and Unc5b from the less mature/arterial plexus/pre-arterial EC subgroup)4,20. We did not exclude genes also implicated in angiogenesis/expressed in sprouting ECs, as these genes formed that vast majority of those associated with the less mature EC subgroup".

      Reviewer #3 Other Comments ____2: Exclusion of Notch genes. Although the reason for choosing non-notch genes and excluding notch genes for screening is addressed in this paper, it would be interesting to examine how the arterial enhancers identified in this study are present in the Notch genes, especially Dll4 (enriched in arterial and sprouting ECs) and Jag1 (enriched in arterial ECs).

      __RESPONSE: __Previous work from our lab and others has already examined arterial enhancers for Notch pathway genes. We already included these enhancers in all our later analysis (Figure 5-6 and relevant supplemental figures), including analysis of TF motifs.

      Reviewer #3 Other Comments ____3: SoxF family TFs. Among the 3 members of SoxF TFs, only Sox17 and Sox7 were assessed. Though not specific, Sox18 is highly expressed in the arteries. On the contrary, Sox7 is highly expressed in the vein and shows weak expression in arterial ECs (PMID: 26630461).

      __RESPONSE AND REVISION (PLANNED): __We agree. We will include assessment of SOX18 binding in our final revised manuscript. An antibody for this analysis has been identified already.

      Reviewer #3 Other Comments ____4: Minor inaccuracy in Intro/paragraph 3: though sox17 is reported as indispensable for arterial specification (PMID: 24153254), losing a single SoxF factor does not seem to completely compromise the arterial program (PMID: 24153254, PMID: 26630461). A combined loss of Sox17/18, or Sox 7/17/18, seems to do the job (PMID: 26630461).

      __RESPONSE: __We have altered this section: "The evidence linking SOXF transcription factors to arterial differentiation is more extensive, with loss of either SOX17 (the SOXF factor most specific to arterial ECs) or SOX7 resulting in arterial defects21-24. Whilst losing a single SOXF factor does not entirely compromise the arterial program, arterial differentiation appears absent after compound Sox17;Sox18 and Sox7;Sox17;Sox18 deletion, although this occurs alongside significantly impaired angiogenesis and severe vascular hyperplasia21-24. PMID 24153254 is reference 23, PMID 26630461 is reference 24.

      Reviewer #3 Other Comments ____5: Fig.4 e14.5 mouse embryos. If the observation aims to assess the dorsal aorta, it would be better to use mouse embryos at mid-gestation (e9.5-10.5), when the paired DAs are formed with arterial identity but haven't been remodelled and fused as one single aorta. The morphological data in this figure would be better to show the colocalization of LacZ expression and an arterial marker (e.g. Sox17) using immulfluorescence staining instead of purely lacZ.

      RESPONSE: This experiment was primarily conducted to demonstrate that our enhancers were arterial enriched in both zebrafish and mouse transgenesis, and feel this is clearly shown with the e14.5 transgenic embryos originally shown. We chose e14.5 because it matched the timepoints used for the single cell transcriptomics first used to select the target arterial identity genes, and feel it is a good match to 2-3 dpf zebrafish in terms of arterial differentiation mechanisms. We agree that E9-10 would have also been an additional useful timepoint, but we do not have the resources to generate this data nor consider it essential for the conclusions of our work here.

      __REVISION (PLANNED): __We are unable to perform immunofluorescence in the e14.5 transgenic embryos due to the fixation and staining solutions used for X-gal staining (which was done by an external company and could not be altered), but agree additional information is needed to demonstrate arterial endothelial specificity. We will therefore expand the analysis of sectioned embryos (currently restricted to just the Efnb2-333:LacZ transgene) to all enhancers shown in Figure 4. This analysis has some limitations due to infiltration of the X-gal solution to deeper tissues, but is anticipated it will clearly show enhancer activity in arterial endothelial cells rather than venous ECs or smooth muscle cells.

      __Reviewer #3 (Significance (Required)): __This novel work establishes an important foundation for future understanding of how TFs may interact to determine arterial specification.

      Other revisions

      In addition to changes suggested by the reviewers, we also made one additional adjustment to the paper to include analysis of two additional putative enhancers (Efnb2-159 and Cxcr4+119). These were initially omitted in error yet both regions reach the standard of testable putative enhancers (noted in small changes to Figure S1 and Table S2). When tested in zebrafish transient transgenic embryos, Cxcr4+119 was inactive whilst Efnb2-159 was active in arterial endothelial cells. The relevant tables and figures have been adjusted to reflect these changes, the most significant of which are the inclusion of Efnb2-159 positive zebrafish in Figure 1 (and the necessity to create an additional supplemental Figure (S3) to accommodate the increased number of images), and analysis of Efnb2-159 transcription factor motifs/binding as part of Figure 5 and 6. No conclusions were altered by the inclusion of this additional data.

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      Referee #3

      Evidence, reproducibility and clarity

      This manuscript by Nornes et al analyzed multiple published databases and identified a group of putative enhancers for 8 selected non-Notch arterial genes in mouse and human ECs. These enhancers were cloned and screened in fish embryos to test their effect in driving GFP reporter expression, which narrowed down a cohort of enhancers for further testing of expression activities in mouse embryonic arteries. The authors then analyzed the sequences of these enhancers, and identified binding motifs of ETS, SOX-F, FOX and MEF2 family TFs and Notch transcription regulator RBPJ commonly present in closed proximity in these arterial enhancers, suggesting interaction between these TFs in determination of arterial identity.

      Major comments:

      This study provides an enormous amount of bioinformatic data analysis and screening results in transgenic fish and mouse models, which led to the discovery of a group of arterial enhancers and TFs binding motifs essential in regulating arterial identity.

      Other comments:

      1. Choice of arterial genes is slightly biased. Acvrl1/Alk1 is not enriched in arterial ECs. Sema3G, which is highly expressed in arterial ECs, is missing. UNC5B is enriched in arterial ECs but also expressed by sprouting ECs (PMID: 38866944).
      2. Exclusion of Notch genes. Although the reason for choosing non-notch genes and excluding notch genes for screening is addressed in this paper, it would be interesting to examine how the arterial enhancers identified in this study are present in the Notch genes, especially Dll4 (enriched in arterial and sprouting ECs) and Jag1 (enriched in arterial ECs).
      3. SoxF family TFs. Among the 3 members of SoxF TFs, only Sox17 and Sox7 were assessed. Though not specific, Sox18 is highly expressed in the arteries. On the contrary, Sox7 is highly expressed in the vein and shows weak expression in arterial ECs (PMID: 26630461). Minor inaccuracy in Intro/paragraph 3: though sox17 is reported as indispensable for arterial specification (PMID: 24153254), losing a single SoxF factor does not seem to completely compromise the arterial program (PMID: 24153254, PMID: 26630461). A combined loss of Sox17/18, or Sox 7/17/18, seems to do the job (PMID: 26630461).
      4. Fig.4 e14.5 mouse embryos. If the observation aims to assess the dorsal aorta, it would be better to use mouse embryos at mid-gestation (e9.5-10.5), when the paired DAs are formed with arterial identity but haven't been remodeled and fused as one single aorta. The morphological data in this figure would be better to show the colocalization of LacZ expression and an arterial marker (e.g. Sox17) using immulfluorescence staining instead of purely lacZ.

      Significance

      This novel work establishes an important foundation for future understanding of how TFs may interact to determine arterial specification.

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      Referee #2

      Evidence, reproducibility and clarity

      In this work, Nornes and collaborators have described a cohort of arterial enhancers that drive gene expression in arteries and not in veins. The paper is very well written and it is very informative. The authors have used in silico models to identified the potential artery enhancers and then used different developmental in vivo systems, zebrafish and mice, to validate their findings. Finally, the authors have explored what transcription factors may be binding the identified enhancer sequences and thus, drive arterial gene expression. I would like to congratulate the authors for this work that it has been a pleasure to read and review.

      Major comments:

      1. In their identification of enhancers, the authors consider a candidate every enhancer that has a putative mark in both mouse and human. Nevertheless, all the human data comes from in vitro analysis. Considering how much cell culture affects endothelial cell identity, inducing effects like EndoMT, would this have any effect on the enhancer selection? Would it be possible to search any human in vivo data? Would this allow for even stronger and more relevant sequences?
      2. The human data comes from vein endothelial or microvasculature endothelial cells. Specially because some of the enhancers identified by the authors drive also vein expression, could the authors discriminate whether this is due to the identification coming from vein cells. Is there available data from HAECs? Would this not be conceptually more correct that using vein endothelial cells data? This should be at least discussed in the paper.
      3. Although the authors use the mouse embryo to further validate their finding beyond the zebrafish, the expression are a bit different. While on the fish the enhancers label smaller vessels of arterial identity, in the mouse, only bigger arteries are marked. Is this defined by the time of the analysis?
      4. The analysis of the enhancers is only done during development. Is the activity of these enhancers maintained through live or only important for artery vs vein determination? Is the expression of the different enhancer reporters maintained into adulthood?

      Significance

      This is a very well done study with potential interest for vascular biologists, in particular to those interested in the determination between artery and veins in a context of development. It advances our knowledge on the field of vascular biology as it not only proposes potential enhancers but also goes on to validation of the enhancers. Nevertheless, it is important to note that some of this enhancers have been identified from in vitro human data. In vitro culture of endothelial cells affects their cellular identity and thus, this study may have underscored many potential enhancers.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      Nornes et al. have generated a cohort of arterial enhancers based on in silico analysis and validation with transgenic lines in both zebrafish and mice. They utilized publicly available datasets for chromatin marks, including ATAC-seq on endothelial cells either from cell culture or isolated from mice, as well as EP300 binding, H3K27Ac, and H3K4Me1. Focusing on eight arterial-expressed genes, they identified a putative enhancer region marked by at least one enhancer feature. After validating the activity of these enhancers in zebrafish and mice, the authors assessed the regulatory pathways upstream of these genes. Using ChIP-seq and Cut&Run for key endothelial transcription factors, they discovered that binding sites for SoXF and ETS factors are shared in arterial enhancers, whereas binding sites for Notch, MEF2, and Fox are present only in the subset of identified enhancers. Together this study provides an arterial enhancer atlas that allows further characterisation of regulatory network behind endothelial cell identity.

      Major comments:

      The authors have assessed 15 enhancers for arterial-venous specificity, by assessing the expression in DA, ISV, cardinal and ventral veins at 2 dpf. Interestingly there is a clear difference in the expression patterns of these enhancers in the zebrafish axial vasculature, especially seen at the level of ISV. The co-localization of the enhancer expression in the endothelium was done using endothelial marks expressed in both venous and arterial EC (kdrl). To fully distinguish if the expression is venous or arterial endothelial compartment colocalization with Tg expressed in arterial (flt1) or venous (lyve1) EC would be informative. In addition, it is striking that cxc4+135 drives the expression in nearly every ISV as cxcl12+269 only every other. Similarly, not all the enhancers are enriched in the DA to the same level. Is there biological significance to this? could authors discuss these results further? The pattern of expression of the unc5b-identified enhancer is also striking, does this reflect the known roles of unc5b in the vascular formation? The final part of the paper focuses on defining the presence of "deeply conserved" transcription factor binding sites (TFSB), defined as TFBS that are as conserved as the enhancer sequence surrounding them. In literature, the term 'deep conservation' refers to evolutionary conservation (genomic sequence preservation) in a wide range of species. Therefore, the additional classification presented by the authors based on the surrounding sequence is not clear. As, the KLF motifs in the Ece1in1, which is conserved between mouse and human, are defined as "deeply conserved". However, the FLK motif in the following enhancer, Flk1in10 (one line below), gets classified as non-deeply conserved, despite also being conserved between mouse and human. Thus, in the current form, there is a contradiction in the way the authors use the term 'deeply conserved' and the accepted meaning of this term. To avoid confusion, it would be important to revise this nomenclature.

      Minor:

      Details on how the corresponding non-coding regions between mice and humans were established are missing, what alignment tool was used?

      Not sufficient details are provided for the re-analysis of siRNA data. E.g., which clustering method was used? How the clusters were assigned to cell identities?

      Details about the first HOMER analysis (in the assessment of transcription factor motifs and binding patterns at arterial enhancers) seem to be missing from the methods section.

      Pg 12: "For ETS, 23/23 arterial enhancers contained at least one conserved motif (all "deeply" conserved to the same depth as the surrounding enhancer, see S7)". Is it S8, where conservation is indicated?

      Figure 1 and 2 for non-zebrafish readers it would be useful to indicate in Figures 1 and 2 the non EC expression that can be observed in the embryos.

      Table S1: Please, indicate in the legend what the asterisk in the H DNAseI column stands for

      Figure S8: The phrasing "conserved to animal" in Figure S8 is misleading. There is no difference in something being conserved to tenrec or manatee, as both are Afrotherians. Hence, the data show that both Efnb2-141 and Ephb4-2 were present in the common ancestor of Afrotherians and humans, namely the ancestor of all placentals. Instead, it would be good to indicate the phylogenetic group for which the presence of the enhancer can be inferred (in this case, Placentalia).

      Significance

      To date, a systematic approach to identifying the regulatory networks driving endothelial cell identity is missing. This study provides important datasets and validation of enhancers involved in arterial gene expression and the associated transcription factors. Although this is only the tip of the iceberg, this work represents a significant milestone in the systematic understanding of how arterial gene expression is regulated. Overall, this study offers a powerful resource for understanding arterial gene regulation and conducting genome-wide studies of arterial enhancers.

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      Reply to the reviewers

      REVIEWER 1

      Reviewer #1 Evidence, reproducibility and clarity: Nornes et al. have generated a cohort of arterial enhancers based on in silico analysis and validation with transgenic lines in both zebrafish and mice. They utilized publicly available datasets for chromatin marks, including ATAC-seq on endothelial cells either from cell culture or isolated from mice, as well as EP300 binding, H3K27Ac, and H3K4Me1. Focusing on eight arterial-expressed genes, they identified a putative enhancer region marked by at least one enhancer feature. After validating the activity of these enhancers in zebrafish and mice, the authors assessed the regulatory pathways upstream of these genes. Using ChIP-seq and Cut&Run for key endothelial transcription factors, they discovered that binding sites for SoXF and ETS factors are shared in arterial enhancers, whereas binding sites for Notch, MEF2, and Fox are present only in the subset of identified enhancers. Together this study provides an arterial enhancer atlas that allows further characterisation of regulatory network behind endothelial cell identity.

      __Reviewer #1 Major Comment 1: __The authors have assessed 15 enhancers for arterial-venous specificity, by assessing the expression in DA, ISV, cardinal and ventral veins at 2 dpf. Interestingly there is a clear difference in the expression patterns of these enhancers in the zebrafish axial vasculature, especially seen at the level of ISV. The co-localization of the enhancer expression in the endothelium was done using endothelial marks expressed in both venous and arterial EC (kdrl). To fully distinguish if the expression is venous or arterial endothelial compartment colocalization with Tg expressed in arterial (flt1) or venous (lyve1) EC would be informative.

      RESPONSE: We agree with the reviewer that a more detailed description of arterial-venous specificity of each enhancer could be included. In the original manuscript, the expression pattern of each enhancer within the vasculature was primarily assessed at 2 days post fertilization (dpf) in Fig 1-2. This identified arteries using direction of blood flow and available descriptive information, as arterial development in 2pdf zebrafish is very stereotypical and already well characterized.

      __REVISION (PLANNED): __The original Figure 3A includes a more detailed assessment of arterial-venous specificity at 3dpf for four arterial enhancers (Cxcr4+135, Cxcr4+151, Gja5-78 and Gja5-7, chosen as enhancers representing the four types of expression patterns seen). We will now extend this more detailed analysis to all arterial enhancer:GFP lines. This analysis uses kdrl-mCherry to mark the entire vasculature, comparative to the expression of the arterial enhancers (GFP). This allows us to clearly identify the intersegmental arteries (as opposed to intersegmental veins) by looking for direct connection to the dorsal aorta, and by assessing the direction of blood flow within these vessels. This analysis is done at 3dpf to give time for the intersegmental arteries to acquire identity and connect definitively with the dorsal aorta, and for the diminishment of any GFP expression originating from the initial sprouting from the dorsal aorta. By extending this analysis to the other arterial enhancer zebrafish lines shown in Figure 2, we will be able to more clearly classify the activity of each enhancer within different vascular beds. This information will also be recorded in a new Table better detailing the timing and specificity of activity of each enhancer.

      We chose not to use arterial or venous “marker lines” (e.g. Flt1:reporter or Lyve1:reporter) for the simple reason that these are also enhancer:GFP transgenes, and therefore are not necessarily definitive of the arterial or venous lineage per se (e.g. Flt1:GFP expression is controlled by the transcription factors binding the Flt1 enhancer in the same way that Cxcr4+135 and the others are, with the added caveat that the transcriptional regulation of the Flt1 and Lyve enhancers are not well defined). We felt that morphological determination based on direct connections and blood flow direction was therefore more accurate.

      __Reviewer #1 Major Comment 2: __In addition, it is striking that cxc4+135 drives the expression in nearly every ISV as cxcl12+269 only every other. Similarly, not all the enhancers are enriched in the DA to the same level. Is there biological significance to this? could authors discuss these results further? The pattern of expression of the unc5b-identified enhancer is also striking, does this reflect the known roles of unc5b in the vascular formation?

      __RESPONSE: __We agree, the diversity of enhancer expression patterns within the arterial compartment is notable, and really very interesting. The variations in enhancer expression pattern must be largely influenced by the transcription factor motifs within each enhancer, as these patterns were seen in both transient and stable transgenic zebrafish and therefore largely independent of chromatin integration location.

      __REVISION (PLANNED): __The extension of Figure 3A to all enhancer lines (see previous comment) will permit us to more clearly classify the activity of each arterial enhancer within different beds and at different time points. Currently there were no clear links between a particular transcription factor motif/binding and expression pattern, something that is discussed briefly in the original Results and Discussion sections. However, the expansion of Figure 3A to all enhancers, and the creation of a Table summarizing this more systematically will make the link (or lack of one) between expression patterns within the arterial tree and TF motifs easier to appreciate and discuss.

      __Reviewer #1 Major Comment 3: __The final part of the paper focuses on defining the presence of "deeply conserved" transcription factor binding sites (TFSB), defined as TFBS that are as conserved as the enhancer sequence surrounding them. In literature, the term 'deep conservation' refers to evolutionary conservation (genomic sequence preservation) in a wide range of species. Therefore, the additional classification presented by the authors based on the surrounding sequence is not clear. As, the KLF motifs in the Ece1in1, which is conserved between mouse and human, are defined as "deeply conserved". However, the FLK motif in the following enhancer, Flk1in10 (one line below), gets classified as non-deeply conserved, despite also being conserved between mouse and human. Thus, in the current form, there is a contradiction in the way the authors use the term 'deeply conserved' and the accepted meaning of this term. To avoid confusion, it would be important to revise this nomenclature.

      RESPONSE: We agree that this nomenclature should be revised. Our aim was to develop a standard approach to transcription factor motif analysis that could be applied to enhancers regardless of conservation levels and size, and easily replicated by others. Because not all functional transcription factor motifs within enhancers are necessarily conserved between species, we were careful to label both conserved and non-conserved motifs for each TF examined. Nonetheless, extra emphasis was placed on motifs with confirmatory TF binding evidence (e.g. ChIP-seq/CUT&RUN), and those conserved at the same depth as the surrounding sequence. This was because our previous work on endothelial enhancers clearly indicates that these motifs are far more likely to play a key role in regulation. However, the reviewer is correct to note that referring to such motifs as “deeply” conserved could be misinterpreted.

      REVISION (COMPLETED): We have altered our nomenclature. This is explained in the relevant Results sections: “Because the level of conservation of motifs can often be an indication of their importance to enhancer activity, we classified each motif into three categories: strongly conserved (motif conserved to the same depth of the surrounding sequence), weakly conserved (motif conserved in orthologous human enhancer but not to the same depth as the surrounding sequence) and not conserved (motif is not conserved within the orthologous human sequence)”.

      Two enhancers (Unc5b-57 and Cdh1-1) were only conserved human-mouse, therefore each TF motif within these enhancers could be annotated as both weakly and strongly conserved. As the reviewer noted, this does create confusion. We have now adjusted Figure 5 to use a distinct shape for motifs for which no distinction between weak and strong motif can be made. This does not cover Ece1in1, which is conserved human-mouse-tenrec but was erroneously originally labelled human-mouse only. This error has been corrected.

      __Reviewer #1 Minor Comment 1: __Details on how the corresponding non-coding regions between mice and humans were established are missing, what alignment tool was used?

      RESPONSE AND REVISION (COMPLETED): This information has now been included in the relevant Results section: “Orthologous human enhancer sequences were identified for every enhancer using the Vertebrate Multiz Alignment & Conservation Track on the UCSC genome browser”

      __Reviewer #1 Minor Comment 2: __Not sufficient details are provided for the re-analysis of siRNA data. E.g., which clustering method was used? How the clusters were assigned to cell identities?

      RESPONSE AND REVISION (COMPLETED): The details regarding the re-analysis of scRNA data has been expanded in the Methods sections: “Publicly available E12 and E17.5 scRNA-seq data from EC isolated from BmxCreERT2;RosatdTomato lineage traced murine hearts54 was obtained from GEO (GSE214942) prior to processing FASTQ files with the 10X Genomics CellRanger pipeline (V7.0.0). RNA-seq reads were aligned to the mm10 genome reference downloaded from 10X Genomics with the addition of the TdTomato-WPRE sequence. Exclusion of low quality cells with either a UMI count >100,000, total gene count 10%) was performed using Scater55. Data normalisation was performed using the MultiBatchNormalisation method prior to merging of TdTomato positive and negative datasets from individual timepoints. The top 2000 most highly variable genes (excluding mitochondrial and ribosomal genes) in the merged datasets were identified using the Seurat FindVariableFeatures method and utilised to calculate principal component analysis (PCA). Normalised data was scaled using the ScaleData function. Cell clustering was performed using the standard unsupervised graph-based clustering method implemented within Seurat (V4)56. Clusters were visualised in two dimensions using UMAP based non-linear dimensional reduction following the standard Seurat (V4) workflow49. Identified clusters were assigned identities based on marker genes shown to be differentially expressed between populations previously identified in the original study47. Key markers include Npr3 (endocardial), Fabp4 (coronary vascular endothelial), and Nfatc1 (valvular endothelial). The E12.5 sinus venosus EC cluster was assigned based in Aplnr as previously described54. Arterial and venous EC clusters in the E17.5 datasets were annotated based on their enriched expression of Gja5 and Nr2f2, respectively.”

      __Reviewer #1 Minor Comment 3: __Details about the first HOMER analysis (in the assessment of transcription factor motifs and binding patterns at arterial enhancers) seem to be missing from the methods section.

      RESPONSE AND REVISION (COMPLETED): This has been included in the methods: “Analysis of overrepresented motifs within our validated arterial enhancer cohort was performed with HOMER’s findMotifsGenome tool using the full validated region of the arterial enhancers. The analysis used the hg38 masked genome and otherwise default settings for all other parameters including randomly selected background regions”.

      __Reviewer #1 Minor Comment 4: __Pg 12: "For ETS, 23/23 arterial enhancers contained at least one conserved motif (all "deeply" conserved to the same depth as the surrounding enhancer, see S7)". Is it S8, where conservation is indicated?

      __ ____RESPONSE AND REVISION (COMPLETED):__ We have corrected this error in the text – no figure actually needed to be referenced here as the previous sentence contained the full list of relevant figures to this statement (Table 2 and Figures 5 and S9, previously called S8, are the places to see this information).

      __Reviewer #1 Minor Comment 5: __Figure 1 and 2 for non-zebrafish readers it would be useful to indicate in Figures 1 and 2 the non EC expression that can be observed in the embryos.

      RESPONSE AND REVISION (COMPLETED): In addition to arterial expression, a number of the enhancer:GFP transgenes also showed GFP expression within the neural tube. In addition, some transient transgenic embryos also showed ectopic expression in muscle fibres. These have now been indicated on the images in Figure 1 and 2.

      __Reviewer #1 Minor Comment 6: __Table S1: Please, indicate in the legend what the asterisk in the H DNAseI column stands for

      RESPONSE AND REVISION (COMPLETED): The asterisk indicates where DNaseI hypersensitivity is also seen in multiple non-EC lines. This explanation has been added to the legend.

      __Reviewer #1 Minor Comment 7: __Figure S8: The phrasing "conserved to animal" in Figure S8 is misleading. There is no difference in something being conserved to tenrec or manatee, as both are Afrotherians. Hence, the data show that both Efnb2-141 and Ephb4-2 were present in the common ancestor of Afrotherians and humans, namely the ancestor of all placentals. Instead, it would be good to indicate the phylogenetic group for which the presence of the enhancer can be inferred (in this case, Placentalia).

      __RESPONSE: __Whilst I appreciate the point, it is the exact sequence that is important here – obviously tenrec and manatee are similar species but still contain differences in nucleotide sequences. The information about conservation leads the reader to the exact species with which the comparison is being made. We tried to restrict this to just one species per phylogenetic group (e.g. tenrec, opossum, chicken, zebrafish) but occasionally this was not possible.

      Reviewer #1 Significance

      To date, a systematic approach to identifying the regulatory networks driving endothelial cell identity is missing. This study provides important datasets and validation of enhancers involved in arterial gene expression and the associated transcription factors. Although this is only the tip of the iceberg, this work represents a significant milestone in the systematic understanding of how arterial gene expression is regulated. Overall, this study offers a powerful resource for understanding arterial gene regulation and conducting genome-wide studies of arterial enhancers.

      __RESPONSE: __We thank the reviewer for these kind words. Whilst we agree this is only a very small snapshot of all the arterial enhancers involved in gene regulation, we would like to stress that not only is this a massive increase to what has been known previously, but is also deliberately focused on the genes used to define arterial identity during development and in the adult, therefore these enhancers by themselves form an extremely valuable dataset with which to study the key factors driving arterial differentiation and identity.

      __ __


      REVIEWER 2

      __Reviewer #2 Evidence, reproducibility and clarity: __In this work, Nornes and collaborators have described a cohort of arterial enhancers that drive gene expression in arteries and not in veins. The paper is very well written and it is very informative. The authors have used in silico models to identified the potential artery enhancers and then used different developmental in vivo systems, zebrafish and mice, to validate their findings. Finally, the authors have explored what transcription factors may be binding the identified enhancer sequences and thus, drive arterial gene expression. I would like to congratulate the authors for this work that it has been a pleasure to read and review.

      Reviewer #2 Major Comment 1: In their identification of enhancers, the authors consider a candidate every enhancer that has a putative mark in both mouse and human. Nevertheless, all the human data comes from in vitro analysis. Considering how much cell culture affects endothelial cell identity, inducing effects like EndoMT, would this have any effect on the enhancer selection? Would it be possible to search any human in vivo data? Would this allow for even stronger and more relevant sequences?

      __RESPONSE: __We agree that the use of human endothelial cells in culture raises some potential issues. However, we stress that the mouse EC enhancer marks, which played a key role in defining putative enhancers, come from in vivo analysis (E11 embryos, P6 retina and adult aorta), limiting the potential for significant impact from cell culture-induced issues. Whilst we would have enthusiastically incorporated human in vivo data had it been available, our approach was still indisputably successful at identifying arterial enriched/specific enhancers.

      We consider it unlikely that culture/identity-related problems with human cultured ECs led to a significant undercount of enhancers, in part because comparatively few regions with enhancer marks in mouse in vivo ECs were excluded due to the absence of human enhancer marks. In fact, Cxcr4, Cxcl12, and Gja5 were poorly transcribed in the human cell lines studied here and consequently only enhancer marks in mouse were used to define putative enhancers for these three genes (this is clearly stated in the Results section). If a similar rational had applied to the remaining five genes, only an additional six putative enhancers would have been tested (one for Gja4, two for Nrp1 and three for Unc5b). However, we felt it made sense to include analysis of human enhancer marks for these five genes, as all were expressed in the human ECs used (as indicated by H3K1Me3 and DNaseI hypersensitivity at promoter regions) and orthologous human enhancers were identified for all. Additionally, our retrospective analysis of previously described mammalian in vivo-validated EC enhancers (Table S1 in the original manuscription, including eight arterial enhancers) found that all 32 were marked by at least one enhancer mark in human samples (1/32 did not contain mouse enhancer marks). We also tested eleven regions that did not reach our putative enhancer threshold, including five with only mouse marks. None of these directed expression in transgenic analysis.

      Reviewer #2 Major Comment 2: The human data comes from vein endothelial or microvasculature endothelial cells. Specially because some of the enhancers identified by the authors drive also vein expression, could the authors discriminate whether this is due to the identification coming from vein cells. Is there available data from HAECs? Would this not be conceptually more correct that using vein endothelial cells data? This should be at least discussed in the paper.

      __RESPONSE AND REVISION (COMPLETED): __We have now included a comparison with enhancer marks from HAECs, telo-HAECs and HUAECs as a new Figure S5. The enhancer marks seen in these cells were very similar to those in the HUVEC and microvascular cells already surveyed. Had enhancer marks within HAECs/telo-HAEC/HUAECs been included as a human enhancer mark in our initial survey, it would have been unlikely to have altered our analysis, although we agree it would have made it more conceptually correct. We chose not to go back and engineer this into our original enhancer selection rational however as we felt it would be intellectually dishonest. A paragraph has been added to the Results section about this analysis.

      Reviewer #2 Major Comment 3: Although the authors use the mouse embryo to further validate their finding beyond the zebrafish, the expression are a bit different. While on the fish the enhancers label smaller vessels of arterial identity, in the mouse, only bigger arteries are marked. Is this defined by the time of the analysis?

      __RESPONSE: __This experiment was conducted to demonstrate that these enhancers were arterial enriched in both zebrafish and mouse transgenesis, and feel this is clearly shown by the current data. Whilst I do not really agree that the expression pattern is different (for example, the Gja5 enhancers are more restricted to the major arteries in both zebrafish and mouse, compared to the more widely expressed Efnb2-333), this is challenging to ascertain at a single time-point in a transient transgenic mouse assay. Whilst it would be potentially interesting to better assess the activity of these enhancers over time in mice, we consider this a lengthy experiment (multiple stable lines would need to be established and characterized for each enhancer) which would not add particular benefit to this paper.

      Reviewer #2 Major Comment 4: The analysis of the enhancers is only done during development. Is the activity of these enhancers maintained through live or only important for artery vs vein determination? Is the expression of the different enhancer reporters maintained into adulthood?

      RESPONSE AND REVISION (PLANNED): We agree this would be interesting to ascertain. We plan to examine the activity of enhancer:GFP activity in adult fish fins (which are accessible even without crossing into a casper background, which is beyond the timescale of this project) in the fully revised version of this paper. We have already conducted a feasibility study on four arterial enhancers:GFP lines (Gja5-7:GFP, Gja5-78:GFP, Gja4+40:GFP and Efnb2-333:GFP), which found that all four were still active, and arterial-specific, in the adult.

      Reviewer #2 Significance

      This is a very well done study with potential interest for vascular biologists, in particular to those interested in the determination between artery and veins in a context of development. It advances our knowledge on the field of vascular biology as it not only proposes potential enhancers but also goes on to validation of the enhancers. Nevertheless, it is important to note that some of this enhancers have been identified from in vitro human data. In vitro culture of endothelial cells affects their cellular identity and thus, this study may have underscored many potential enhancers.

      REVIEWER 3

      __Reviewer #3: Evidence, reproducibility and clarity: __This manuscript by Nornes et al analyzed multiple published databases and identified a group of putative enhancers for 8 selected non-Notch arterial genes in mouse and human ECs. These enhancers were cloned and screened in fish embryos to test their effect in driving GFP reporter expression, which narrowed down a cohort of enhancers for further testing of expression activities in mouse embryonic arteries. The authors then analyzed the sequences of these enhancers, and identified binding motifs of ETS, SOX-F, FOX and MEF2 family TFs and Notch transcription regulator RBPJ commonly present in closed proximity in these arterial enhancers, suggesting interaction between these TFs in determination of arterial identity.

      Reviewer #3 Major Comment : This study provides an enormous amount of bioinformatic data analysis and screening results in transgenic fish and mouse models, which led to the discovery of a group of arterial enhancers and TFs binding motifs essential in regulating arterial identity.

      Reviewer #3 Other Comments ____1: Choice of arterial genes is slightly biased. Acvrl1/Alk1 is not enriched in arterial ECs. Sema3G, which is highly expressed in arterial ECs, is missing. UNC5B is enriched in arterial ECs but also expressed by sprouting ECs (PMID: 38866944).

      __RESPONSE: __When we started this project, scRNA-seq datasets in the developing vasculature were less available. Consequently, we initially based our choice of genes on data from Raftrey et al., Circ Res 2021 (available earlier on bioRxiv), which was focused on mouse coronary arterial ECs at the timepoints that arteries differentiate. This found Acvrl1 to be arterial enriched (not a novel observation, many publications treat Acvrl1 as arterial specific or arterial-enriched) and did not list Sema3g. We also considered a wider dataset from mouse and human mid-gestation embryos when available (Hou et al., Cell Research 2022). However, it is important to note that we did not aim to investigate every arterial-enriched gene, rather to use these datasets to help identify loci associated with gene expression patterns which indicated a high likelihood of containing arterial enhancers active during arterial differentiation.

      Sc-RNAseq data from both Raftery et al., and Hou et al., indicated that arterial ECs are subdivided into two groups, reflecting maturity but also potentially slightly different developmental trajectories. The genes studied here were therefore selected to evenly cover both subgroups, with Acvrl1, Cxcl12, Gja5 and Nrp1 primarily restricted to the mature arterial EC subgroup, while Cxcr4, Efnb2, Gja4 and Unc5b were also expressed in the less mature/arterial plexus/pre-arterial EC subgroup. It is notable that genes within the latter subgroup are also associated with angiogenic/sprouting ECs (Dll4 also belongs to this subgroup), which likely indicates biological links between angiogenesis and arterial identity rather than a problem in gene choice and specificity.

      __REVISION (COMPLETED): __This is already discussed in the Results section (angiogenic expression of arterial genes is discussed within the MEF2 and RBPJ sections) and in the Discussion (paragraph 2, referring to different expression patterns within arterial ECs). However, we have now edited the relevant Results section to better explain gene selection: “It is therefore clear that a better understanding of the regulatory pathways directing arterial differentiation requires the identification and characterization of a larger number of arterial enhancers directing the expression of key arterial identity genes. To identify a cohort of such enhancers, we looked in the loci of eight non-Notch genes: Acvrl1(ALK1) Cxcr4, Cxcl12, Efnb2, Gja4(CX37), Gja5 (CX40), Nrp1 and Unc5b. Although not a definitive list of arterial identity genes, single cell transcriptomic analysis indicates these genes are all significantly enriched in arterial ECs4,20, and are commonly used to define arterial EC populations in mouse and human scRNAseq analysis4,5,20,54. Additionally, single-cell transcriptomic data indicates that arterial ECs can be divided into two subgroups4,20. The genes selected here are equally split between subgroups (Acvrl1, Cxcl12, Gja5 and Nrp1 from the mature arterial EC subgroup, Cxcr4, Efnb2, Gja4 and Unc5b from the less mature/arterial plexus/pre-arterial EC subgroup)4,20. We did not exclude genes also implicated in angiogenesis/expressed in sprouting ECs, as these genes formed that vast majority of those associated with the less mature EC subgroup”.

      Reviewer #3 Other Comments ____2: Exclusion of Notch genes. Although the reason for choosing non-notch genes and excluding notch genes for screening is addressed in this paper, it would be interesting to examine how the arterial enhancers identified in this study are present in the Notch genes, especially Dll4 (enriched in arterial and sprouting ECs) and Jag1 (enriched in arterial ECs).

      __RESPONSE: __Previous work from our lab and others has already examined arterial enhancers for Notch pathway genes. We already included these enhancers in all our later analysis (Figure 5-6 and relevant supplemental figures), including analysis of TF motifs.

      Reviewer #3 Other Comments ____3: SoxF family TFs. Among the 3 members of SoxF TFs, only Sox17 and Sox7 were assessed. Though not specific, Sox18 is highly expressed in the arteries. On the contrary, Sox7 is highly expressed in the vein and shows weak expression in arterial ECs (PMID: 26630461).

      __RESPONSE AND REVISION (PLANNED): __We agree. We will include assessment of SOX18 binding in our final revised manuscript. An antibody for this analysis has been identified already.

      Reviewer #3 Other Comments ____4: Minor inaccuracy in Intro/paragraph 3: though sox17 is reported as indispensable for arterial specification (PMID: 24153254), losing a single SoxF factor does not seem to completely compromise the arterial program (PMID: 24153254, PMID: 26630461). A combined loss of Sox17/18, or Sox 7/17/18, seems to do the job (PMID: 26630461).

      __RESPONSE: __We have altered this section: “The evidence linking SOXF transcription factors to arterial differentiation is more extensive, with loss of either SOX17 (the SOXF factor most specific to arterial ECs) or SOX7 resulting in arterial defects21–24. Whilst losing a single SOXF factor does not entirely compromise the arterial program, arterial differentiation appears absent after compound Sox17;Sox18 and Sox7;Sox17;Sox18 deletion, although this occurs alongside significantly impaired angiogenesis and severe vascular hyperplasia21–24. PMID 24153254 is reference 23, PMID 26630461 is reference 24.

      Reviewer #3 Other Comments ____5: Fig.4 e14.5 mouse embryos. If the observation aims to assess the dorsal aorta, it would be better to use mouse embryos at mid-gestation (e9.5-10.5), when the paired DAs are formed with arterial identity but haven't been remodelled and fused as one single aorta. The morphological data in this figure would be better to show the colocalization of LacZ expression and an arterial marker (e.g. Sox17) using immulfluorescence staining instead of purely lacZ.

      RESPONSE: This experiment was primarily conducted to demonstrate that our enhancers were arterial enriched in both zebrafish and mouse transgenesis, and feel this is clearly shown with the e14.5 transgenic embryos originally shown. We chose e14.5 because it matched the timepoints used for the single cell transcriptomics first used to select the target arterial identity genes, and feel it is a good match to 2-3 dpf zebrafish in terms of arterial differentiation mechanisms. We agree that E9-10 would have also been an additional useful timepoint, but we do not have the resources to generate this data nor consider it essential for the conclusions of our work here.

      __REVISION (PLANNED): __We are unable to perform immunofluorescence in the e14.5 transgenic embryos due to the fixation and staining solutions used for X-gal staining (which was done by an external company and could not be altered), but agree additional information is needed to demonstrate arterial endothelial specificity. We will therefore expand the analysis of sectioned embryos (currently restricted to just the Efnb2-333:LacZ transgene) to all enhancers shown in Figure 4. This analysis has some limitations due to infiltration of the X-gal solution to deeper tissues, but is anticipated it will clearly show enhancer activity in arterial endothelial cells rather than venous ECs or smooth muscle cells.

      __Reviewer #3 (Significance (Required)): __This novel work establishes an important foundation for future understanding of how TFs may interact to determine arterial specification.

      Other revisions

      In addition to changes suggested by the reviewers, we also made one additional adjustment to the paper to include analysis of two additional putative enhancers (Efnb2-159 and Cxcr4+119). These were initially omitted in error yet both regions reach the standard of testable putative enhancers (noted in small changes to Figure S1 and Table S2). When tested in zebrafish transient transgenic embryos, Cxcr4+119 was inactive whilst Efnb2-159 was active in arterial endothelial cells. The relevant tables and figures have been adjusted to reflect these changes, the most significant of which are the inclusion of Efnb2-159 positive zebrafish in Figure 1 (and the necessity to create an additional supplemental Figure (S3) to accommodate the increased number of images), and analysis of Efnb2-159 transcription factor motifs/binding as part of Figure 5 and 6. No conclusions were altered by the inclusion of this additional data.

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      Referee #3

      Evidence, reproducibility and clarity

      This manuscript by Nornes et al analyzed multiple published databases and identified a group of putative enhancers for 8 selected non-Notch arterial genes in mouse and human ECs. These enhancers were cloned and screened in fish embryos to test their effect in driving GFP reporter expression, which narrowed down a cohort of enhancers for further testing of expression activities in mouse embryonic arteries. The authors then analyzed the sequences of these enhancers, and identified binding motifs of ETS, SOX-F, FOX and MEF2 family TFs and Notch transcription regulator RBPJ commonly present in closed proximity in these arterial enhancers, suggesting interaction between these TFs in determination of arterial identity.

      Major comments:

      This study provides an enormous amount of bioinformatic data analysis and screening results in transgenic fish and mouse models, which led to the discovery of a group of arterial enhancers and TFs binding motifs essential in regulating arterial identity.

      Other comments:

      1. Choice of arterial genes is slightly biased. Acvrl1/Alk1 is not enriched in arterial ECs. Sema3G, which is highly expressed in arterial ECs, is missing. UNC5B is enriched in arterial ECs but also expressed by sprouting ECs (PMID: 38866944).
      2. Exclusion of Notch genes. Although the reason for choosing non-notch genes and excluding notch genes for screening is addressed in this paper, it would be interesting to examine how the arterial enhancers identified in this study are present in the Notch genes, especially Dll4 (enriched in arterial and sprouting ECs) and Jag1 (enriched in arterial ECs).
      3. SoxF family TFs. Among the 3 members of SoxF TFs, only Sox17 and Sox7 were assessed. Though not specific, Sox18 is highly expressed in the arteries. On the contrary, Sox7 is highly expressed in the vein and shows weak expression in arterial ECs (PMID: 26630461). Minor inaccuracy in Intro/paragraph 3: though sox17 is reported as indispensable for arterial specification (PMID: 24153254), losing a single SoxF factor does not seem to completely compromise the arterial program (PMID: 24153254, PMID: 26630461). A combined loss of Sox17/18, or Sox 7/17/18, seems to do the job (PMID: 26630461).
      4. Fig.4 e14.5 mouse embryos. If the observation aims to assess the dorsal aorta, it would be better to use mouse embryos at mid-gestation (e9.5-10.5), when the paired DAs are formed with arterial identity but haven't been remodeled and fused as one single aorta. The morphological data in this figure would be better to show the colocalization of LacZ expression and an arterial marker (e.g. Sox17) using immulfluorescence staining instead of purely lacZ.

      Significance

      This novel work establishes an important foundation for future understanding of how TFs may interact to determine arterial specification.

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      Referee #2

      Evidence, reproducibility and clarity

      In this work, Nornes and collaborators have described a cohort of arterial enhancers that drive gene expression in arteries and not in veins. The paper is very well written and it is very informative. The authors have used in silico models to identified the potential artery enhancers and then used different developmental in vivo systems, zebrafish and mice, to validate their findings. Finally, the authors have explored what transcription factors may be binding the identified enhancer sequences and thus, drive arterial gene expression. I would like to congratulate the authors for this work that it has been a pleasure to read and review.

      Major comments:

      1. In their identification of enhancers, the authors consider a candidate every enhancer that has a putative mark in both mouse and human. Nevertheless, all the human data comes from in vitro analysis. Considering how much cell culture affects endothelial cell identity, inducing effects like EndoMT, would this have any effect on the enhancer selection? Would it be possible to search any human in vivo data? Would this allow for even stronger and more relevant sequences?
      2. The human data comes from vein endothelial or microvasculature endothelial cells. Specially because some of the enhancers identified by the authors drive also vein expression, could the authors discriminate whether this is due to the identification coming from vein cells. Is there available data from HAECs? Would this not be conceptually more correct that using vein endothelial cells data? This should be at least discussed in the paper.
      3. Although the authors use the mouse embryo to further validate their finding beyond the zebrafish, the expression are a bit different. While on the fish the enhancers label smaller vessels of arterial identity, in the mouse, only bigger arteries are marked. Is this defined by the time of the analysis?
      4. The analysis of the enhancers is only done during development. Is the activity of these enhancers maintained through live or only important for artery vs vein determination? Is the expression of the different enhancer reporters maintained into adulthood?

      Significance

      This is a very well done study with potential interest for vascular biologists, in particular to those interested in the determination between artery and veins in a context of development. It advances our knowledge on the field of vascular biology as it not only proposes potential enhancers but also goes on to validation of the enhancers. Nevertheless, it is important to note that some of this enhancers have been identified from in vitro human data. In vitro culture of endothelial cells affects their cellular identity and thus, this study may have underscored many potential enhancers.

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

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      Nornes et al. have generated a cohort of arterial enhancers based on in silico analysis and validation with transgenic lines in both zebrafish and mice. They utilized publicly available datasets for chromatin marks, including ATAC-seq on endothelial cells either from cell culture or isolated from mice, as well as EP300 binding, H3K27Ac, and H3K4Me1. Focusing on eight arterial-expressed genes, they identified a putative enhancer region marked by at least one enhancer feature. After validating the activity of these enhancers in zebrafish and mice, the authors assessed the regulatory pathways upstream of these genes. Using ChIP-seq and Cut&Run for key endothelial transcription factors, they discovered that binding sites for SoXF and ETS factors are shared in arterial enhancers, whereas binding sites for Notch, MEF2, and Fox are present only in the subset of identified enhancers. Together this study provides an arterial enhancer atlas that allows further characterisation of regulatory network behind endothelial cell identity.

      Major comments:

      The authors have assessed 15 enhancers for arterial-venous specificity, by assessing the expression in DA, ISV, cardinal and ventral veins at 2 dpf. Interestingly there is a clear difference in the expression patterns of these enhancers in the zebrafish axial vasculature, especially seen at the level of ISV. The co-localization of the enhancer expression in the endothelium was done using endothelial marks expressed in both venous and arterial EC (kdrl). To fully distinguish if the expression is venous or arterial endothelial compartment colocalization with Tg expressed in arterial (flt1) or venous (lyve1) EC would be informative. In addition, it is striking that cxc4+135 drives the expression in nearly every ISV as cxcl12+269 only every other. Similarly, not all the enhancers are enriched in the DA to the same level. Is there biological significance to this? could authors discuss these results further? The pattern of expression of the unc5b-identified enhancer is also striking, does this reflect the known roles of unc5b in the vascular formation? The final part of the paper focuses on defining the presence of "deeply conserved" transcription factor binding sites (TFSB), defined as TFBS that are as conserved as the enhancer sequence surrounding them. In literature, the term 'deep conservation' refers to evolutionary conservation (genomic sequence preservation) in a wide range of species. Therefore, the additional classification presented by the authors based on the surrounding sequence is not clear. As, the KLF motifs in the Ece1in1, which is conserved between mouse and human, are defined as "deeply conserved". However, the FLK motif in the following enhancer, Flk1in10 (one line below), gets classified as non-deeply conserved, despite also being conserved between mouse and human. Thus, in the current form, there is a contradiction in the way the authors use the term 'deeply conserved' and the accepted meaning of this term. To avoid confusion, it would be important to revise this nomenclature.

      Minor:

      Details on how the corresponding non-coding regions between mice and humans were established are missing, what alignment tool was used?

      Not sufficient details are provided for the re-analysis of siRNA data. E.g., which clustering method was used? How the clusters were assigned to cell identities?

      Details about the first HOMER analysis (in the assessment of transcription factor motifs and binding patterns at arterial enhancers) seem to be missing from the methods section.

      Pg 12: "For ETS, 23/23 arterial enhancers contained at least one conserved motif (all "deeply" conserved to the same depth as the surrounding enhancer, see S7)". Is it S8, where conservation is indicated?

      Figure 1 and 2 for non-zebrafish readers it would be useful to indicate in Figures 1 and 2 the non EC expression that can be observed in the embryos.

      Table S1: Please, indicate in the legend what the asterisk in the H DNAseI column stands for

      Figure S8: The phrasing "conserved to animal" in Figure S8 is misleading. There is no difference in something being conserved to tenrec or manatee, as both are Afrotherians. Hence, the data show that both Efnb2-141 and Ephb4-2 were present in the common ancestor of Afrotherians and humans, namely the ancestor of all placentals. Instead, it would be good to indicate the phylogenetic group for which the presence of the enhancer can be inferred (in this case, Placentalia).

      Significance

      To date, a systematic approach to identifying the regulatory networks driving endothelial cell identity is missing. This study provides important datasets and validation of enhancers involved in arterial gene expression and the associated transcription factors. Although this is only the tip of the iceberg, this work represents a significant milestone in the systematic understanding of how arterial gene expression is regulated. Overall, this study offers a powerful resource for understanding arterial gene regulation and conducting genome-wide studies of arterial enhancers.

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      Reply to the reviewers

      We thank the reviewers for going through our manuscript and providing valuable feedback. We are grateful to all 3 reviewers for describing our findings as important and valuable, well-designed and robust, and of value to the Parkinson's and Crohn's disease communities studying LRRK2. Below we detail a point-by-point response to the reviewers.

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

      The paper by Dikovskaya and collaborators investigated the activitiy and expression of LRRK2 in different subtypes of splenic and intestinal immune cells, taking advantage of a novel GFP-Lrrk2 knockin mouse. Interestingly, they found that T-cell-released IL-4 stimulates Lrrk2 expression in B cells. I have a few comments and suggestions for the authors. 1) Figure 1C. LRRK2 KO cells display residual Rab10 phosphorylation. Do the authors have any idea of which kinase other than LRRK2 could be involved in this phosphorylation?

      As far as we are aware no other kinase is known to phosphorylate Rab10 at T73 in vivo. In vitro, recombinant Rab10 can be phosphorylated by MST3 at this site (Knebel A. et al, protocols.io https://dx.doi.org/10.17504/protocols.io.bvjxn4pn), but its relevance in vivo or in cells has not been shown. It is possible that the residual band recognised by anti-pT73 Rab10 ab in splenocytes is unspecific background, as it is mainly seen in LRRK2 KO spleen cells and not in other tissues. But to be certain that our assay assesses LRRK2-dependent Rab10 phosphorylation, we have always compared with the MLi-2 control.

      2) Since there are no good antibodies for IF/IHC as pointed by the authors, the GFP-Lrrk2 mouse gives the opportunity to check endogenous LRRK2 localization, i.e. in cells untreated or treated with IL-4 or other cytokines. Also, does endogenous GFP-LRRK2 accumulate into filaments/puncta upon MLi2 inhibition? The relocalization into filaments of inhibited LRRK2 has been observed in overexpression but not under endogenous expression. This analysis would be interesting also in light of the observed side effect of type-I inhibitors.

      We thank the reviewer for this suggestion. We will attempt a super-resolution microscopy using Airyscan with isolated B-cells treated with cytokine and/or LRRK2 inhibitor to address this question.

      3) Figure 5. The authors need to label more clearly the graphs referring to wt mice versus GFP-Lrrk2 KI mice.

      We have now labelled the panels referring to the WT mice only with "WT mice", to distinguish them from the other panels that incorporate data from both EGFP-Lrrk2 mice and their WT littermates used as a background.

      They should also replace GFP-LRRK2 with GFP-Lrrk2 since they edited the endogenous murine gene.

      Thank you, we have corrected it, and also the other mouse genotypes.

      4) In the material and methods MLi-2 administration in mice is indicated at 60 mg/kg for 2 hr whereas in suppl. figure 5 the indicated dose is 30 mg/kg. Please correct with the actual dose used.

      Thank you, we have corrected the mistake.

      5) The discovery of IL-4 as a Lrrk2 activator in B cells is a very interesting and novel finding. The authors could take advantage of the GFP tag to investigate LRRK2 interactome upon IL-4 stimulation (optional). Also, is the signaling downstream of IL-4 attenuated in Lrrk2 KO cells?

      We thank the reviewer for these interesting suggestions. The role of LRRK2 in IL-4 activated B-cells is currently under active research in the lab.

      Reviewer #1 (Significance (Required)):

      The manuscript is well designed and organized, and the experimental approaches are robust. These results are significant for the field as they add additional layers in the complex regulation and regulatory roles of LRRK2 in immunity, with implication for inflammatory disorders and Parkinson's disease.

      We thank the reviewer for their positive comments and for recognising our efforts to provide some clarity to a complex field.

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

      The authors present a flow cytometry methodology to assess LRRK2 expression and pathway markers in mouse models and explore LRRK2 in splenic and intestinal immune cells. This is a highly valuable study given the emerging understanding that LRRK2 pathway activity in peripheral tissues may be of crucial importance to Parkinson's disease and Crohn's disease. P8 : the authors state that their results indicate 'that the effects of LRRK2-R1441C mutation and inflammation on LRRK2 activity represent two different parallel pathways'. This seems like an overinterpretation as pathway suggests the presence of additional partners in the pathway while R1441C is a LRRK2 intrinsic modification. The results can equally be explained by synergistic effects between both activation mechanisms (mutant and inflammation).

      We agree with the reviewer, and have added this into the text. The sentence now reads "suggesting that the LRRK2-R1441C mutation and inflammation have different impacts on LRRK2 activity, either in parallel or in synergy."

      Methods and experiment descriptions in results : the authors appear to use the terms anti-CD3 stimulation and CD3 stimulation interchangeably, although it is not always clear in the text that these are synonymous. This should be clarified.

      We thank reviewer for pointing out this error on our part. We have made the necessary changes to always refer to the stimulation as anti-CD3.

      One major observation in this paper is that LRRK2 is not detected in gut epithelial cells as previously has been reported. It would be useful to comment on any differences between the presented protocol and the previous reports, in particular relating to the antigen retrieval step. In order to reinforce the finding, it would be useful to include in situ hybridization data that could further strengthen the observations of which cellular subtypes express LRRK2 and which do not. Indeed, while the KO control shows that there is an unacceptable high non-specific staining, it does not prove absence of expression. Also, can any conclusions be made about expression of LRRK2 in neural cells of the gut? This important information on LRRK2 detection in gut should be mentioned in the abstract and highlighted in the discussion.

      We thank the reviewer for pointing this out. In fact, we think the observation that LRRK2 is not detected in epithelial cells is so important that we have a separate manuscript exploring this point. Please see 1. Tasegian, A. et al.https://doi.org/10.1101/2024.03.07.582590 (2024). In this manuscript we have explored the expression of LRRK2 in human and murine intestinal epithelial cells using qPCR. Although we do not have in situ hybridization data, we believe that using both the EGFP-LRRK2 and the pRab10 flow cytometry, as well as qPCR and proteomics on selected cell types, corroborates our findings on the cell types that express LRRK2. We did not analyse LRRK2 expression in the neural cells of the gut, as the focus was on the immune cells, however we hope that others will use the tools developed here to explore this further.

      The authors mention in the discussion that they 'show for the first time that eosinophils also express active LRRK2 at levels comparable to B-cells and DCs.' The relevance of this finding should be further developed. Why is this important?

      We thank the reviewer for this point. We don't know how LRRK2 is important in these cells. However, as the role of LRRK2 in eosinophils and neutrophils has not yet been explored and both cell types play important roles in IBD, we think it is important to point out. We have now added a sentence to the discussion highlighting the importance of eosinophils in IBD. "Since eosinophils have recently been implicated as key player in intestinal defense and colitis(Gurtner et al, 2022), it will be interesting to evaluate LRRK2 functions in these cells."

      In the isolation of lamina propria cells, what efforts were made to characterize the degree of purification of the lamina propria cells compared to cells of other gut wall layers such as epithelium, muscularis mucosa, or deeper layers? Please specify.

      Isolation of lamina propria cells is a very well-established process (LeFrancois and Lycke, 'Isolation of Mouse Small Intestinal Intraepithelial Lymphocytes, Peyer's Patch, and Lamina Propria Cells.' Curr. Protocols in Immunology 2001), where we extensively wash off the epithelial layer before digesting the tissue for the LP. After the digestion the muscle and wall of the gut are still intact, so we do not get any contamination with other deeper layers. The subsets of cells we find in the LP are in line with isolations from other labs.

      Minor comments Figure 5G, for the graphs indicating LRRK2 activity and LRRK2 phosphorylation, the specific measures should be specified in the graph titles to avoid any ambiguity (pT73-Rab10, pS935-LRRK2).

      We have added the specifications to the new version of the figure.

      Suppl figure 1 : please specify the figure label and abbreviation AF568 in the legend. Suppl figure 2 : please specify the figure label and abbreviation anti-rb in the legend

      Thank you, we added the abbreviations to the legends. The Figure labels for both figures have been already included at the top of figure legends.

      Reviewer #2 (Significance (Required)):

      The authors present a flow cytometry methodology to assess LRRK2 expression and pathway markers in mouse models and explore LRRK2 in splenic and intestinal immune cells. This is a highly valuable study given the emerging understanding that LRRK2 pathway activity in peripheral tissues may be of crucial importance to Parkinson's disease and Crohn's disease.

      We thank the reviewer for recognising the value of this study.

      Reviewer #3

      Evidence, reproducibility and clarity

      The paper describes a set of experiments to analyse LRRK2 activity in tissues and despite it has very important findings and technical developments is largely descriptive. It does look like a collection of experiments more than a defined hypothesis and experiments to address that.

      We thank the reviewer for recognising the importance of our findings and the technical developments. We agree that the paper's focus is to describe where LRRK2 is expressed in immune cells, and in which cells is it active or activated after inflammation in a hypothesis-free unbiased manner. We believe this is important data to share as a resource for the wider LRRK2 community and we will submit the manuscript as a Resource.

      The flow cytometry assay of the first part is a great technical challenge and represents the establishment of a potentially very useful tool for the field. It would have been important to test other organs, either as controls or for example because of their relevance e.g. lungs. This first part is disconnected from the second part below.

      We thank the reviewer for pointing out that the pRab10 assay would be useful to apply to other organs too. Since we are interested in the role of LRRK2 in IBD, we had focused on applying the pRab10 assay on intestinal tissue, with spleens also analysed as major lymphoid organ and a source of immune cells that can translocate to the gut in inflammation. We hope that the publication of this method would allow other researchers to analyse other tissues in the future.

      The authors generated a new mouse KI mouse expressing EGFP-LRRK2 and show data the levels of LRRK2 expression are reduced in tissues at different degrees and established a flow cytometry assay to measure LRRK2 expression by monitoring the GFP signal. Interestingly they found that expression does not correlate with activity (as measured by phospho-Rabs). I suggest taking this part out as it breaks the flow of the paper. If data using this mouse is included, then microscopy should be included to complement the flow cytometry data. I understand the mice were used later with the anti-CD3 treatment, but it is very confusing that some experiments are done with EGFP-LRRK2 mice and others not. It does look in general like the mice do not behave as wild types and this is an important caveat. Without microscopy of the tissues or even cells (Figure 4) is hard to conclude much about these experiments.

      We thank the reviewer for this point and would like to explain. It is true that in Suppl Figure 5, we show reduction of LRRK2 signal in the EGFP-Lrrk2-KI mice. However, based on immunoblotting, a significant reduction in EGFP-LRRK2 expression levels was seen only in the brain, but not in the tissues we analysed, that is the spleen and the intestine. Further, we have shown clearly using proteomics (Fig. 3D and 5E), that the GFP signal in immune cells correlates very well with the WT LRRK2 expression. Therefore, we think that the GFP signal in these mice reflects WT LRRK2 expression pattern. Further, despite the limitations of reduced kinase activity that we thoroughly describe, we think this model is very useful since no antibodies work to stain for LRRK2 in mice. We therefore respectfully disagree with this reviewer that the EGFP-LRRK2 data should be taken out, as it has proven to be an invaluable tool to measure and track changes in endogenous LRRK2 expression. Moreover, we think the fact that LRRK2 expression does not correlate with levels of activity, that is, LRRK2 is more active in some immune cells than in others, is a very important finding that evidences the cell-specific regulation of LRRK2 activity beyond its expression level.

      We tried but failed to visualize the EGFP-LRRK2 signal using fluorescence microscopy in the tissue. This is most likely due to the low expression of LRRK2 (proteomics data suggests that even neutrophils express less than 9000 copies), confounded further by the high background autofluorescence in tissues, especially in the gut. We now explain the lack of tissue images from the EGFP-LRRK2 mice in the text. However, we can visualize the EGFP-LRRK2 in B cells, and we will provide these images in a revised version of the manuscript.

      We have also added the following paragraph to the discussion:

      "We complemented the pRab10 assay with the development of the EGFP-Lrrk2-KI reporter mouse. Although the reporter was initially designed as a fluorescent tracker for imaging LRRK2 localisation in cells and tissues, the low expression of LRRK2, combined with high and variable autofluorescence in tissues precluded its use for microscopy. Even in neutrophils, which express highest level of LRRK2 among immune cells, there are less than 9000 copies of LRRK2 per cell (Sollberger et al, 2024), making it difficult to identify localization. However, the EGFP signal was sufficient for flow cytometry-based measurements, where background autofluorescence of each cell type was taken into account and subtracted."

      Then the authors show that LRRK2 expression and activity is different in different cell types and depends on inflammation. The anti-CD3 strategy to induce inflammation is very different from physiological inflammation such as sepsis and LPS stimulation, so experiments with other stimuli could be important here to contribute to the message of inflammatory trigger of LRRK2 activation and decoupling of cell type.

      We thank the reviewer for this suggestion. We used the anti-CD3 model as it also causes intestinal inflammation, and mimics T-cell cytokine storms that happens in many diseases. However, for the revisions we will also test another model of inflammation as suggested, such as LPS stimulation, to measure how inflammation affects LRRK2 expression and activity.

      The IL-4 data is intriguing but too preliminary. The lack of strong effect of IFN-gamma is expected as the promoter of LRRK2 in mice and humans is different and human cells responds much better with regards to LRRK2 expression after IFN-gamma stimulation.

      We are confused by what the reviewer means by saying the IL-4 data is preliminary. We have shown by flow cytometry, immunoblotting, qPCR and proteomics that IL-4 induced LRRK2 expression in B-cells. So we are uncertain as to how else this can be shown. As to the effect of IFNγ on LRRK2 expression, it may indeed be that human cells respond better than murine cells. Importantly, the IL-4 ability to induce LRRK2 in B-cells is a novel and important finding, regardless of the effects of IFNγ.

      Reviewer #3 (Significance (Required))

      The paper describes a set of experiments to analyse LRRK2 activity in tissues and despite it has very important findings and technical developments is largely descriptive. It does look like a collection of experiments more than a defined hypothesis and experiments to address that.

    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

      The authors present a flow cytometry methodology to asses LRRK2 epxression and pathway markers in mouse models and explore LRRK2 in splenic and intestinal immune cells. This is a highly valuable study given the emerging understanding that LRRK2 pathway activity in peripheral tissues may be of crucial importance to Parkinson's disease and Crohn's disease.

      P8 : the authors state that their results indicate 'that the effects of LRRK2-R1441C mutation and inflammation on LRRK2 activity represent two different parallel pathways'. This seems like an overinterpretation as pathway suggests the presence of additional partners in the pathway while R1441C is a LRRK2 intrinsic modification. The results can equally be explained by synergistic effects between both activation mechanisms (mutant and inflammation).

      Methods and experiment descriptions in results : the authors appear to use the terms anti-CD3 stimulation and CD3 stimulation interchangeably, although it is not always clear in the text that these are synonymous. This should be clarified.

      One major observation in this paper is that LRRK2 is not detected in gut epithelial cells as previously has been reported. It would be useful to comment on any differences between the presented protocol and the previous reports, in particular relating to the antigen retrieval step. In order to reinforce the finding, it would be useful to include in situ hybridization data that could further strengthen the observations of which cellular subtypes express LRRK2 and which do not. Indeed, while the KO control shows that there is an unacceptable high non-specific staining, it does not prove absence of expression. Also, can any conclusions be made about expression of LRRK2 in neural cells of the gut? This important information on LRRK2 detection in gut should be mentioned in the abstract and highlighted in the discussion. The authors mention in the discussion that they 'show for the first time that eosinophils also express active LRRK2 at levels comparable to B-cells and DCs.' The relevance of this finding should be further developed. Why is this important ?

      In the isolation of lamina propria cells, what efforts were made to characterize the degree of purification of the lamina propria cells compared to cells of other gut wall layers such as epithelium, muscularis mucosa, or deeper layers? Please specify.

      Minor comments

      Figure 5G, for the graphs indicating LRRK2 activity and LRRK2 phosphorylation, the specific measures should be specified in the graph titles to avoid any ambiguity (pT73-Rab10, pS935-LRRK2).

      Suppl figure 1 : please specify the figure label and abbreviation AF568 in the legend.

      Suppl figure 2 : please specify the figure label and abbreviation anti-rb in the legend

      Significance

      The authors present a flow cytometry methodology to asses LRRK2 epxression and pathway markers in mouse models and explore LRRK2 in splenic and intestinal immune cells. This is a highly valuable study given the emerging understanding that LRRK2 pathway activity in peripheral tissues may be of crucial importance to Parkinson's disease and Crohn's disease.

    3. 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 paper by Dikovskaya and collaborators investigated the activitiy and expression of LRRK2 in different subtypes of splenic and intestinal immune cells, taking advantage of a novel GFP-Lrrk2 knockin mouse. Interestingly, they found that T-cell-released IL-4 stimulates Lrrk2 expression in B cells.

      I have a few comments and suggestions for the authors.

      1. Figure 1C. LRRK2 KO cells display residual Rab10 phosphorylation. Do the authors have any idea of which kinase other than LRRK2 could be involved in this phosphorylation?
      2. Since there are no good antibodies for IF/IHC as pointed by the authors, the GFP-Lrrk2 mouse gives the opportunity to check endogenous LRRK2 localization, i.e. in cells untreated or treated with IL-4 or other cytokines. Also, does endogenous GFP-LRRK2 accumulate into filaments/puncta upon MLi2 inhibition? The relocalizaiton into filaments of inhibited LRRK2 has been observed in overexpression but not under endogenous expression. This analysis would be interesting also in light of the observed side effect of type-I inhibitors.
      3. Figure 5. The authors need to label more clearly the graphs referring to wt mice versus GFP-Lrrk2 KI mice. They should also replace GFP-LRRK2 with GFP-Lrrk2 since they edited the endogenous murine gene.
      4. In the material and methods MLi-2 administration in mice is indicated at 60 mg/kg for 2 hr whereas in suppl. figure 5 the indicated dose is 30 mg/kg. Please correct with the actual dose used.
      5. The discovery of IL-4 as a Lrrk2 activator in B cells is a very interesting and novel finding. The authors could take advantage of the GFP tag to investigate LRRK2 interactome upon IL-4 stimulation (optional). Also, is the signaling downstream of IL-4 attenuated in Lrrk2 KO cells?

      Significance

      The manuscript is well designed and organized, and the experimental approaches are robust. These results are significant for the field as they add additional layers in the complex regulation and regulatory roles of LRRK2 in immunity, with implication for inflammatory disorders and Parkinson's disease.

    4. 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 paper describes a set of experiments to analyse LRRK2 activity in tissues and despite it has very important findings and technical developments is largely descriptive. It does look like a collection of experiments more than a defined hypothesis and experiments to address that.

      The flow cytometry assay of the first part is a great technical challenge and represents the establishment of a potentially very useful tool for the field. It would have been important to test other organs, either as controls or for example because of their relevance e.g. lungs. This first part is disconnected from the second part below.

      The authors generated a new mouse KI mouse expressing EGFP-LRRK2 and show data the levels of LRRK2 expression are reduced in tissues at different degrees and established a flow cytometry assay to measure LRRK2 expression by monitoring the GFP sugnal. Interestengly they found that expression does not correlate with activity (as measured by phospho-Rabs). I suggest taking this part out as it breaks the flow of the paper. If data using this mouse is included, then microscopy should be included to complement the flow cytometry data. I understand the mice were used later with the anti-CD3 treatment, but it is very confusing that some experiments are done with EGFP-LRRK2 mice and others not. It does look in general like the mice do not behave as wild types and this is an important caveat. Without microscopy of the tissues or even cells (Figure 4) is hard to conclude much about these experiments.

      Then the authors show that LRRK2 expression and activity is different in different cell types and depends on inflammation. The anti-CD3 strategy to induce inflammation is very different from physiological inflammation such as sepsis and LPS stimulation, so experiments with other stimuli could be important here to contribute to the message of inflammatory trigger of LRRK2 activation and decoupling of cell type.

      The IL-4 data is intriguing but too preliminary. The lack of strong effect of IFN-gamma is expected as the promoter of LRRK2 in mice and humans is different and human cells responds much better with regards to LRRK2 expression after IFN-gamma stimulation.

      Significance

      The paper describes a set of experiments to analyse LRRK2 activity in tissues and despite it has very important findings and technical developments is largely descriptive. It does look like a collection of experiments more than a defined hypothesis and experiments to address that.

    1. 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:

      In this work, Anandi et al. propose an ex vivo model that can be used to recapitulate the in vivo structure of the tumor microenvironment, which allows the observation of morphological and functional changes in tumor cells in a 3D context. Due to the ability of cancer cells to induce hypoxic condition within the TME, authors propose this model to tackle the study of metastasis initiation in vitro. The proposed system successfully displays an ischemic gradient with cells accessing nutrients at different rates, similarly to what happens in solid tumors in vivo. Moreover, in line with the literature, tumor cell migration and invasiveness were promoted by hypoxic conditions. Authors also show that the system could be used to study cell-cell interaction, as co-cultures of macrophages and cancer cells were successfully cultured in the system and studied in the context of tumor hypoxia.

      The study proposed is interesting and timely, as cancer cell invasion remains an important area of tumor biology that needs further exploration. The methodology is well explained and proposed in a linear flow. However, the work could benefit from some improvement and changes, as well as from additional experiments. On an important note, authors do not properly refer to the current literature, as several studies on 3D culture systems/chambers have already been studied and developed to investigate the tumor microenvironment, but they are not cited nor referred to in the manuscript. Authors should refer to such literature and explain how this system is different and adds to it.

      Major comments:

      1. Authors propose this method to study the TME in 3D. When culturing cells with different ECM (Collagen vs. matrigel+collagen I) authors should take into consideration the effect of these materials on different cell types. It is known how collagen and matrigel can differently influence the polarization and phenotype of stromal cells (particularly in regards of fibroblasts - major components of solid cancers - e.g., PMID 21029367), therefore these points should be addressed at least in the discussion.

      We completely agree with the reviewer so we added this point (and reference) to our manuscript's introduction (lines 45-46) and discussion (lines 442-445).

      1. In addition to the previous comment, matrigel and collagen are also known to alter cancer cell phenotype (e.g., PMID 21029367) and this point should be taken into account.

      We completely agree with the reviewer so we added this point (and reference) to our discussion in the main text (lines 442-445).

      1. The need for novel 3D systems to study different aspects of the TME in vitro/ex vivo are certainly needed, however they are not inexistent. Authors should address this in the text, as the current literature already started to propose 3D models (including models involving matrigel/collagen in combination with other materials). 3D chambers (of different materials, and with different aims) are being used and designed and can be found in the literature. These works are not cited in the current study at all. For instance, Anguiano 2017; Cavo et al. 2018; Anguiano et al., 2020; Sodek et al. 2008, etc.

      We agree so we have now added those references to the main text (line 56-57).

      1. Even though the focus is on hypoxia and the achievement of an ischemic gradient in the chamber to allow resemblance of an in vivo tumor, the authors write in line 123 (and also in other parts of the text) that: "these results show that consumer cells in the 3MIC form ischemic gradients that can influence the local metabolic microenvironment experienced by neighboring tumor spheroids". The addition of the use of the PMDS membrane partly supports the claim, however it would be interesting to check whether this is indeed true, by measuring for example the levels of certain metabolites (e.g., glucose, glutamine, glutamate, lactate, aspartate) reached with the system, or pH levels, etc., in presence or absence of the hypoxic gradient/consumer cells.

      This is an insightful question and defining the exact composition of this complex ischemic microenvironment is a major ambition of our lab, so we completely agree with the reviewer's comment. However, as the 3MIC was designed specifically for microscopy, measuring specific metabolites it is unfortunately outside its capabilities.

      Having said that, and following the spirit of the reviewer's comments, we used microscopy to measure additional signs of metabolic stress. Specifically, we used fluorescent probes to detect changes in intracellular pH (pHrodo, Molecular Probes) and in Redox status (CellROX, Molecular Probes) and glucose (2-NBDG - a fluorescent D-glucose analog). As we explain below, we found exciting results from our pH measurements which led us to additional functional experiments. We are very excited about these new results, and we thank the reviewer for encouraging these experiments. These new results also provide evidence that other parameters in ischemia - and not just hypoxia - change along the 3MIC and can have an impact on tumor cells.

      1. When looking at the references presented in the manuscript, authors quote too many review articles, rather than scientific articles. Given the extremely wide literature on cancer metastasis, more of these works should be quoted in this context. For example: in the introduction - text lines 27-38 - only 4 references are research articles, out of 14 references presented in that paragraph.

      The reviewer is correct in pointing this out. Our intention was to use reviews on topics that are well established where citing primary research could be unfair to other contributions. But again, we agree with the reviewer, so we replaced reviews with primary research articles in multiple locations along the manuscript.

      1. As authors showed successfully how macrophages and cancer cells can interact in the chamber, recapitulating cell interactions in an in vivo context, it would be very interesting to see whether different consumer cells would induce similar or different changes to the spheroids and the ischemic gradient (for instance using stromal cells or non-tumor cell lines as consumers, instead of cancer cells only), as we know how tumors are a multitude of cell subsets, each contributing to nutrient production, oxygen consumption, etc.

      This is a great point. We thought about that very same point and conducted several experiments to test the combinatorial effects of different consumer cells. In broad terms, we did not observe major differences when using different consumer cells. However, we agree that this system may provide compelling opportunities to test the effect of different cell types on each other. Still, for consistency and ease, we conducted most of our experiments using the same cells in both consumers and in spheroids.

      In the resubmitted version, we added an experiment where we looked at the sprouting of SVEC endothelial cells using the same cells or Lung KPs as consumers (Fig. S6A).

      Minor comments:

      1. Studying the early metastatic development/seeding remains a timely quest, however authors should refer to several new studies in which various mouse models are used to study metastasis from different points of view (e.g., PMID 25822788; PMID 36991128; PMID 25171411; PMID 25633981; PMID 34632412; PMID 35921474; etc). Or line 41, three reviews are quoted (refs 27-29), whilst there are several works that could be quoted on metabolism in solid tumors also in the context of metastasis (e.g., PMID 36522548; PMID: 26719539, PMID 34303764). This comment applies to the rest of the text.

      We thank the reviewer for their help in processing this vast literature. We were aware of most of those works but some were new to us so thanks again! We have now added these references.

      1. The order of the references is not properly presented. In the introduction, the first reference is n. 4 (text line 22), instead of it being reference 1. Moreover, the subsequent literature ref. is number 12 and not number 2. Please revise the order of the references, and position them within the bibliography from first cited to last cited in the text.

      We apologize for this confusion. We have now revised all the references and we hope they are correctly formatted and numbered. The origin of this confusion may have been that we had references in the abstract thus their numbering started there rather than from the introduction. To avoid further confusions, we removed all references from the abstract.

      1. Lines 98-104. It would be helpful to the reader to define here what these consumer cells are. Even though it is explained in the methods that the consumer cells are cancer cells, it is important to make it clear in the text, as it could be misleading at times.

      We agree with the reviewer although we did not mean to be misleading. As mentioned above, we chose to use the same cells for both: consumers and spheroids and we have now added a new figure to illustrate this point (Fig S6A). Following the advice, we are also including additional text to make the message clearer (lines 107-109).

      1. The English grammar and spelling should be revised in some parts, as well as typos and missing words throughout the text (e.g., Line 38, the word "interraction" is misspelled and should be corrected with "interaction". Line 49, the first sentence seems incomplete. Lines 68-69 should be revised as the sentences do not flow well together, probably due to a missing word. In line 77 it should be "presents". Line 341 should be "cannot be explained").

      We apologize for these typos and mistakes. We have tried our best to avoid these type of errors in the new manuscript version.

      Referees cross-commenting

      I find the comments from the other reviewers to be in line with one another as well as with my general assessment. The major and comments of all reviewers should be addressed. The minor comments should be taken into account as well, as they would render the text and the figures more precise. I suggest that 3-6 months to complete the revision process is an appropriate time frame for the authors.

      Finally, I strongly encourage the authors to add in the discussion the points and questions raised by all reviewers, as well as to improve the bibliography in terms of organisation, linearity, and state of the art.

      Significance:

      General assessment:

      The work by Anandi et al. offers an additional tool to tackle the issue of studying the tumor microenvironment, in a 3D culture system.

      The authors show a model that can be used to study tumor hypoxia in 3D, offering the possibility to study the TME in a more in vivo-like manner without turning to mice models. The development of new tools to study the TME avoiding the excessive use of animals is definitely a timely quest. In addition, the system has the potential to be applied to tackle different biological questions, as the methodology is well explained and could be suitable to many other fields of cancer biology (e.g., drug resistance or uptake). The work is overall presented in a clear way and the methodology is explained thoroughly and it has the potential to be a useful tool for the study of cancer hypoxia.

      However, authors should address how their method could differently impact other cells when applied to other systems. As one major claim is the potential use of this methodology to study the TME, it should be taken into consideration how stromal cells are strongly affected by the ECM, and how certain settings or features of the system may impact such cell populations. In addition, the work does not properly refer to the current state of the art. As other studies started to propose 3D systems for the study of TME and cell-cell interactions - besides organoids - the authors should cite these works and frame their own study in a more appropriate context, pointing out differences with the current 3D chambers available, the advantages of one vs the other, and so on.

      Advance: the study adds to the current literature as the study of tumor hypoxia in 3D remains a complicated issue. The interesting co-culture settings with macrophages suggests potential uses of this model to study cell-cell interactions.

      Audience: the study is very methodological and offers a tool that could be used by cancer biologists - and maybe by other biology fields.

      Reviewer #2

      Evidence, reproducibility and clarity:

      Summary

      Anandi and colleagues present a manuscript describing a nice assay for exploring the progressive effect of metabolic depletion of the nutrients and oxygen on the invasion of cancer cells. This builds upon and extends a device that they previously described - MEMIC - and now enables 3D analysis of small numbers of cells. The key to their method is the inclusion of a layer of consumer cells that deplete oxygen and nutrients. Using this tool, they demonstrate that depleted environments promote invasive behavior and lower cell-cell adhesion. This is related to the nutrient-deprived and hypoxic environments found in the center of many tumors. Cellular Potts Modelling is used to explore ideas around the cooperation between reduced cell-cell adhesion and increase ECM adhesion in promoting invasion. Overall, this is a well-constructed manuscript that will be of interest to cell biologists and cancer biologists.

      Major comments

      I realize this work is submitted to review commons and this complicates the recommendation regarding publication. My view is that the 'more prestigious' journals would require greater mechanistic insight, but that the work could find a suitable place in other members of the review commons stable. My comments are divided into those essential for any journal and those that might be journal dependent.

      We hope that the mechanistic experiments added to our new manuscript version will appeal the reviewer and merit publication in any of the review commons journals.

      Essential regardless of journal

      1. Many of the figures lack information about the number of spheroids analyzed and from how many biological repeats they are derived.

      We have now added this information to all our experiments. This information can be found in the figures and on the figure legends.

      1. The authors need to provide citations for their assertion that only gases can cross the PDMS, but not other small metabolites. They should also comment on whether the build-up of CO2 might be relevant.

      We have now added the original reference where they describe PDMS's properties (Cox and Dunn, 1986).

      The point raised about CO2 is very interesting, but we do not expect a buildup of this gas. When using PDMS, CO2 would not accumulate as PDMS membranes are permeable to gases - including CO2. When using glass covers, the lack of oxygen should minimize CO2 production as hypoxic cells will not be able to conduct oxidative phosphorylation and produce lactic acid instead.

      1. The data on the directionality of migration when consumers are present are not significant and doesn't warrant the speculation in lines 186-189.

      Following the reviewer's advice we have removed this speculation.

      1. The ECM degradation in Figure 3 should be quantified.

      We agree. We added additional quantifications for the gelatin degradation assay. We also highlight the quantification we already had of the ECM degradation assessed via DQ collagen. Those data can be found in the new figures 4 and S4, respectively.

      1. Do the authors have evidence that the hypoxia-exposed cells are more adhesive to ECM. This is central to their Potts model and I could not locate the supporting experimental data. If not, then the Potts model should include matrix proteolysis, which they do have data about.

      Again, this is a very insightful observation, and we completely understand this confusion. We think that this may part of the inherent challenge of trying to condense biological problems into analogies or "metaphors" when using physical/mathematical models.

      The algorithm in a Cellular Potts model (CPM) tries to minimize the energy of the system (the entire group of cells/ECM that we are modelling). This global energy reduction is achieved by minimizing local energies in the cell-cell and cell-ECM interactions. The way the algorithm executes this minimization, is by always (probability p=1) accepting a configuration that decrease the energy while restricting the configurations that lead to higher energies (with a probability of p = e-DHT) where DH is the difference between the current and previous energy.

      So, the only thing the model is really doing is to increase the likelihood that cells are in a more "comfortable" environment - i.e. that the energy from the interactions with their neighboring cells and ECM is as low as possible. For example, if cell 1 and cell 2 adhere strongly but not to cell 3, in a CPM this is modelled as a low DH between cell 1 and 2 and a higher DH with cell 3. Conversely, when people model cells better at "invading" into a new "territory" they choose a lower energy between that cell type and that type of substratum.

      In other words, our CPM does not "care" whether ischemic cells invade the ECM because they create space through increased proteolysis or because they are more adherent to the ECM. These two scenarios are the same in a CPM and it is consistent with previous CPM models of similar scenarios (e.g.: PMID: 18835895, 33933478, 26436883, 23596570).

      We have now reworded the description of the model on the main text, and we added an illustration hoping to make this aspect of the model clearer (Fig. S4F).

      1. Is the down-regulation of E-cadherin transcriptional - i.e. is the mRNA level reduced?

      This is a great question. After the reviewer posed this question, we looked at out data and we concluded E-cad's downregulation is transcriptional. Assessing local mRNA levels in the 3MIC is challenging. However, our E-Cad reporter (pHAGE-E-cadherin-RFP, addgene #79603) is a red fluorescent protein driven by the CDH1 (E-Cad) reporter. RFP levels decrease with ischemia indicating that this regulation occurs at the promoter/transcriptional level. We now added this point to the revised manuscript (lines 259-261). We thank the reviewer for this insight!

      1. The title of figure 6 is misleading. The authors do not demonstrate chemoresistance in terms of cell survival or cell proliferation, which is how the term is normally used. The authors should measure cell number, proliferation, and cell viability. The data presented in the Supplementary Figure are inadequate with no quantification. The FUCCI reporter cells would be a good tool for this. Also, why use 150nM paclitaxel when the IC50 is 817nM? This seems bizarre. Lastly, there is a typo in the figure that suggest 150mM drug was used.

      We apologize if these experiments caused confusion. Our intention was to look at the anti-migratory effects of Taxol-related drugs. As such, we first determined the concentrations at which the drug was lethal to our cells (this is the LD50 of ~800nM). Then, we tested if lower concentrations - which we knew where not lethal - would affect cell migration, protrusions, etc. Hence the 30-150nM range we used in our experiments.

      We have now completely rewritten this section hoping that our approach is now clearer. We have also changed the title of the section and the figure legend to clarify that we are studying the effects of Taxol as anti-motility drug rather than its effects on cell survival and proliferation (now Fig. 7). Finally, we have now fixed the 150mM/150nM typo in the figure legend.

      Journal dependent

      1. The authors have not excluded that either changes in nutrients, or even a pro-invasive factor, produced by consumer cells are necessary for the increased invasion. They have only shown that they are not sufficient. The authors should perform a series of experiments comparing hypoxic conditions with normal media and normoxic conditions with nutrient depleted/condition media by prior culturing of KP cancer cells.

      This is a great point. We actually do not want or propose to exclude this possibility. So, we have now added text to clarify this issue (lines 431-435).

      In fact, we would be thrilled if there is a pro-invasive factor. If that would be the case, our results indicate this factor is only effective under ischemia. Because the same consumer cells do not have an effect on the same type of tumor spheroids under well-nurtured environments. In addition, our new pH measurements and perturbations experiments agree with this reviewer's intuition about additional factors being key in the increased invasion (see new Figure 2). We are very excited about these new results, and we hope this reviewer will be excited too.

      1. What is the oxygen sensor for increased invasion? PHD1-3 would be a good place to start looking. Is the PHD2-HIF axis important? Do VHL mutant cells still show responses to the consumer cells?

      Following the reviewer's feedback, we generated isogenic HIF1A KO cell lines to study whether HIF1A was directly needed in the invasion of tumor spheroids within the 3MIC. We complemented these loss-of-function experiments with For HIF1A gain-of-function using pharmacological interventions that stabilize HIF1A under normal oxygen levels (CoCl2 and DMOG).

      As shown in the new figure 2, these experiments mirrored our hypoxia experiments: HIF1A activity was not sufficient but it was required to drive the invasion of ischemic spheroids. We think that these new results are particularly interesting when taken together with our new pH-perturbation experiments. Briefly, our new experiments results show that in addition to the requirement of hypoxia/HIF1A, media acidity also has a strong effect on spheroid invasion. More excitingly, a drop in pH is sufficient to dramatically increase invasion - even in control well-nurtured spheroids. We think that the effects of pH and hypoxia are linked. HIF1A activation and hypoxia the increase glycolysis and thus lactic acid secretion. We speculate that this glycolytic switch is where hypoxia is important, but it is not sufficient because under well-perfused conditions (e.g. healthy tissue or large culture media volume) lactic acid levels may not buildup enough to significantly lower the extracellular pH. In contrast, under poor perfused conditions (3MIC and solid tumors) or if we flood cell cultures with lactic acid, the media's pH drops dramatically (Fig. 2).

      1. If they include both spheroids of endothelial cells and cancer cells, will the resulting protrusions in hypoxia grow towards each other? Would macrophages enhance this process?

      We agree with the reviewer this is an interesting question and we have anecdotally observed this effect. In the manuscript, we used these chimeric endothelial/tumor spheroids rather than separate ones (Fig. 6E). We do not find strong evidence that their protrusions grew towards each other, but this is something that we would like to explore in the future with more detail.

      Significance:

      The main advance is technical, as many previous studies have related hypoxia to increased cancer cell invasion, which the authors correctly acknowledge and cite. It is scholarly study, which will be of interest to many readers, and the method reported is likely to be adopted by several groups.

      Reviewer #3

      Evidence, reproducibility and clarity:

      In this work, Anandi et al., developed a cell culture system to live image the initial transformation of cells in deprivation of oxygen and nutrients in a 3D context. Using this system, 3MIC, they were able to create oxygen and nutrient gradients to simulate ischemic conditions that arise deep within tumors and that typically precede metastasis. With the 3MIC system they validated that ischemia triggers cell migration and invasion of tumor cells. In addition, 3MIC also allowed them to study the interaction of tumor spheroids with stromal cells such as macrophages and endothelial cells. Interestingly, the authors showed that co-culturing tumor spheroids with stromal cells increased the pro-metastatic features induced by ischemia conditions. Lastly, using 3MIC allowed the authors to discern that a poor paclitaxel response in ischemic-like cells is driven by intrinsic cellular resistance rather than due to lower drug concentration.

      Overall, the work is very well-written, and the results are consisting, convincing and support the conclusions. The methods are clear and complete and allow the reproducibility of the experiments. The experiments are adequately replicated and statistical analyses are well described. However, I have few suggestions to improve the impact of the manuscript:

      1. The authors conclude that 3MIC results in the accumulation of lactic acid and nutrient deprivation in an increasing manner when moving far from the opening site. Is there a way to actually show this? So far, the authors employ a hypoxia sensor only. A sensor for internal pH or other method for nutrient deprivation would help to support the conclusion and further validate the model.

      This is an excellent point. Following the reviewer's feedback, we tested additional sensors including for extra- and intra-cellular pH. As mentioned above, we observed dramatic changes in extracellular pH levels. We followed up these observations with a series of experiments that showed a key functional role for media acidification in driving invasion (Figure 2).

      1. According to figure S3E, the main cell line used by the authors is already quite mesenchymal. It would be good to know if the results showed here are consistent in cells with a more basal epithelial phenotype. Do epithelial cells need stronger ischemic conditions to undergo phenotypic changes?

      This is a great catch. To explore this further, we run a Western Blot analysis to compare epithelial and mesenchymal markers expressed by the main cells we used here (Lung KPs) and to compare them to levels in a stereotypical epithelial (MCF-7) and a mesenchymal (MDA-MB-231) cell line (new Fig. S4D). As the reviewer correctly points out, we do see that E-Cad and Vimentin are co-expressed in KP cells.

      So far, our observations in a range of cell lines are a consistent decrease in E-Cad levels with no significant effects in vimentin levels - regardless of the basal levels of this protein.

      Interestingly, a recent study[1] demonstrated in triple-negative breast cancer models, that an EMT hybrid phenotype - including the presence of Vimentin - is required for metastasis. A compelling hypothesis then is that ischemia in the tumor microenvironment may favor these hybrid phenotypes. We briefly discuss this topic in the revised version of this manuscript.

      1. The number of replicates should be included in each figure legend and not only in the methods section. From data presented it is not clearly stated what do points mean in boxplots (e.g, Fig1H, 2B,G...). How many cells/spheroids did the authors count in each experiment?

      We have now added this information to all our experiments. This information can be found in the figures and on the figure legends.

      1. Figure 3B is not mentioned in the main text.

      We apologize for this error, and we thank the reviewer for catching this issue, which have now corrected.

      1. Line 295: "In the absence of macrophages, clusters of endothelial cells remained mostly rounded, even in the presence of consumer cells and regardless of their location along the ischemic gradient (Fig. 5A; Video S6)." However, in Video S6, both images show endothelial cells co-cultured with macrophages. I consider that Video S6 should be not referenced here.

      The reviewer is correct so have removed that reference.

      1. References style should be homogeneous (e.g, in Ref 13 appears "Nature Reviews Cancer" whereas in Ref 14 "Nat Rev Cancer"). Also, in Ref 25, the journal is missing.

      We apologize for this oversight, and we have not tried to be more consistent in our references.

      1. In plots where distance to open chamber site is not especify (e.g. 6B), at what distance were the data recorded? Please, indicate in the figure legend.

      We have now added this information to our figures.

      1. In the experiment showed in Fig 4, the sorting strategy would include stromal cells such as fibroblasts and endothelial cells in the GFP- population (as only CD45+ cells are removed). These cells will likely also grow in the 3MIC system and have an effect in migration. Can the authors rule out this confounding effect?

      The reviewer is correct. We still think that the possibility of fibroblast contamination is low. First, the fluorescence of HRE-GFP cells under normoxic, is still higher than the autofluorescence of cells not expressing this constructs (such as fibroblasts). This is quite normal as most sensors/reporter have some leakage and thus there is a small amount of transcription. Second, intradermal and subcutaneous tumors are quite poor in fibroblasts. In fact, to study the role of fibroblasts in these tumors, they are usually co-injected with tumor cells (PMID: 20138012). Third, in the process of tumor dissociation and in vitroestablishment, non-transformed cells tend to die more. Since these are more technical points, we moved the cell sorting details to the material and methods section.

      1. In Fig 5C the panel of proximal + macrophages is missing

      We apologize for this mistake, and we have corrected in the new version of the manuscript.

      1. In Fig. 5, Linifanib is used to study the effect of blocking VEGF. Linifanib can also interact with RTKs and PDGF. This fact should be acknowledged.

      We agree with this point. Following the reviewer's advice, we now acknowledged the potential off-target effects of these inhibitors (lines 354-355).

      Significance

      This is a very interesting work with the development of a simple and cost-effective system that allows to continuously monitor biological processes in 3D cultures under nutrient-modified conditions. In general, these data would be broadly interesting to cancer community in general, as 3MIC is a very versatile system, where several aspects can be studied and precisely discerned.

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      Referee #3

      Evidence, reproducibility and clarity

      In this work, Anandi et al., developed a cell culture system to live image the initial transformation of cells in deprivation of oxygen and nutrients in a 3D context. Using this system, 3MIC, they were able to create oxygen and nutrient gradients to simulate ischemic conditions that arise deep within tumors and that typically precede metastasis. With the 3MIC system they validated that ischemia triggers cell migration and invasion of tumor cells. In addition, 3MIC also allowed them to study the interaction of tumor spheroids with stromal cells such as macrophages and endothelial cells. Interestingly, the authors showed that co-culturing tumor spheroids with stromal cells increased the pro-metastatic features induced by ischemia conditions. Lastly, using 3MIC allowed the authors to discern that a poor paclitaxel response in ischemic-like cells is driven by intrinsic cellular resistance rather than due to lower drug concentration.

      Overall, the work is very well-written, and the results are consisting, convincing and support the conclusions. The methods are clear and complete and allow the reproducibility of the experiments. The experiments are adequately replicated and statistical analyses are well described. However, I have few suggestions to improve the impact of the manuscript:

      1. The authors conclude that 3MIC results in the accumulation of lactic acid and nutrient deprivation in an increasing manner when moving far from the opening site. Is there a way to actually show this? So far, the authors employ a hypoxia sensor only. A sensor for internal pH or other method for nutrient deprivation would help to support the conclusion and further validate the model.
      2. According to figure S3E, the main cell line used by the authors is already quite mesenchymal. It would be good to know if the results showed here are consistent in cells with a more basal epithelial phenotype. Do epithelial cells need stronger ischemic conditions to undergo phenotypic changes?
      3. The number of replicates should be included in each figure legend and not only in the methods section. From data presented it is not clearly stated what do points mean in boxplots (e.g, Fig1H, 2B,G...). How many cells/spheroids did the authors count in each experiment?
      4. Figure 3B is not mentioned in the main text.
      5. Line 295: "In the absence of macrophages, clusters of endothelial cells remained mostly rounded, even in the presence of consumer cells and regardless of their location along the ischemic gradient (Fig. 5A; Video S6)." However, in Video S6, both images show endothelial cells co-cultured with macrophages. I consider that Video S6 should be not referenced here.
      6. References style should be homogeneous (e.g, in Ref 13 appears "Nature Reviews Cancer" whereas in Ref 14 "Nat Rev Cancer"). Also, in Ref 25, the journal is missing.
      7. In plots where distance to open chamber site is not especify (e.g. 6B), at what distance were the data recorded? Please, indicate in the figure legend.
      8. In the experiment showed in Fig 4, the sorting strategy would include stromal cells such as fibroblasts and endothelial cells in the GFP- population (as only CD45+ cells are removed). These cells will likely also grow in the 3MIC system and have an effect in migration. Can the authors rule out this confounding effect?
      9. In Fig 5C the panel of proximal + macrophages is missing
      10. In Fig. 5, Linifanib is used to study the effect of blocking VEGF. Linifanib can also interact with RTKs and PDGF. This fact should be acknowledged.

      Significance

      This is a very interesting work with the development of a simple and cost-effective system that allows to continuously monitor biological processes in 3D cultures under nutrient-modified conditions. In general, these data would be broadly interesting to cancer community in general, as 3MIC is a very versatile system, where several aspects can be studied and precisely discerned.

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

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      Referee #2

      Evidence, reproducibility and clarity

      Summary

      Anandi and colleagues present a manuscript describing a nice assay for exploring the progressive effect of metabolic depletion of the nutrients and oxygen on the invasion of cancer cells. This builds upon and extends a device that they previously described - MEMIC - and now enables 3D analysis of small numbers of cells. The key to their method is the inclusion of a layer of consumer cells that deplete oxygen and nutrients. Using this tool, they demonstrate that depleted environments promote invasive behavior and lower cell-cell adhesion. This is related to the nutrient-deprived and hypoxic environments found in the center of many tumors. Cellular Potts Modelling is used to explore ideas around the cooperation between reduced cell-cell adhesion and increase ECM adhesion in promoting invasion. Overall, this is a well-constructed manuscript that will be of interest to cell biologists and cancer biologists.

      Major comments

      I realize this work is submitted to review commons and this complicates the recommendation regarding publication. My view is that the 'more prestigious' journals would require greater mechanistic insight, but that the work could find a suitable place in other members of the review commons stable. My comments are divided into those essential for any journal and those that might be journal dependent. Essential regardless of journal

      • Many of the figures lack information about the number of spheroids analyzed and from how many biological repeats they are derived.
      • The authors need to provide citations for their assertion that only gases can cross the PDMS, but not other small metabolites. They should also comment on whether the build-up of CO2 might be relevant.
      • The data on the directionality of migration when consumers are present are not significant and doesn't warrant the speculation in lines 186-189.
      • The ECM degradation in Figure 3 should be quantified.
      • Do the authors have evidence that the hypoxia-exposed cells are more adhesive to ECM. This is central to their Potts model and I could not locate the supporting experimental data. If not, then the Potts model should include matrix proteolysis, which they do have data about.
      • Is the down-regulation of E-cadherin transcriptional - i.e. is the mRNA level reduced?
      • The title of figure 6 is misleading. The authors do not demonstrate chemoresistance in terms of cell survival or cell proliferation, which is how the term is normally used. The authors should measure cell number, proliferation, and cell viability. The data presented in the Supplementary Figure are inadequate with no quantification. The FUCCI reporter cells would be a good tool for this. Also, why use 150nM paclitaxel when the IC50 is 817nM? This seems bizarre. Lastly, there is a typo in the figure that suggest 150mM drug was used.

      Journal dependent

      • The authors have not excluded that either changes in nutrients, or even a pro-invasive factor, produced by consumer cells are necessary for the increased invasion. They have only shown that they are not sufficient. The authors should perform a series of experiments comparing hypoxic conditions with normal media and normoxic conditions with nutrient depleted/condition media by prior culturing of KP cancer cells.
      • What is the oxygen sensor for increased invasion? PHD1-3 would be a good place to start looking. Is the PHD2-HIF axis important? Do VHL mutant cells still show responses to the consumer cells?
      • If they include both spheroids of endothelial cells and cancer cells, will the resulting protrusions in hypoxia grow towards each other? Would macrophages enhance this process?

      Significance

      The main advance is technical, as many previous studies have related hypoxia to increased cancer cell invasion, which the authors correctly acknowledge and cite. It is scholarly study, which will be of interest to many readers, and the method reported is likely to be adopted by several groups.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary

      In this work, Anandi et al. propose an ex vivo model that can be used to recapitulate the in vivo structure of the tumor microenvironment, which allows the observation of morphological and functional changes in tumor cells in a 3D context. Due to the ability of cancer cells to induce hypoxic condition within the TME, authors propose this model to tackle the study of metastasis initiation in vitro. The proposed system successfully displays an ischemic gradient with cells accessing nutrients at different rates, similarly to what happens in solid tumors in vivo. Moreover, in line with the literature, tumor cell migration and invasiveness were promoted by hypoxic conditions. Authors also show that the system could be used to study cell-cell interaction, as co-cultures of macrophages and cancer cells were successfully cultured in the system and studied in the context of tumor hypoxia. The study proposed is interesting and timely, as cancer cell invasion remains an important area of tumor biology that needs further exploration. The methodology is well explained and proposed in a linear flow. However, the work could benefit from some improvement and changes, as well as from additional experiments. On an important note, authors do not properly refer to the current literature, as several studies on 3D culture systems/chambers have already been studied and developed to investigate the tumor microenvironment, but they are not cited nor referred to in the manuscript. Authors should refer to such literature and explain how this system is different and adds to it.

      Major comments:

      • Authors propose this method to study the TME in 3D. When culturing cells with different ECM (Collagen vs. matrigel+collagenI) authors should take into consideration the effect of these materials on different cell types. It is known how collagen and matrigel can differently influence the polarization and phenotype of stromal cells (particularly in regards of fibroblasts - major components of solid cancers - e.g., PMID 21029367), therefore these points should be addressed at least in the discussion.
      • In addition to the previous comment, matrigel and collagen are also known to alter cancer cell phenotype (e.g., PMID 21029367) and this point should be taken into account.
      • The need for novel 3D systems to study different aspects of the TME in vitro/ex vivo are certainly needed, however they are not inexistent. Authors should address this in the text, as the current literature already started to propose 3D models (including models involving matrigel/collagen in combination with other materials). 3D chambers (of different materials, and with different aims) are being used and designed and can be found in the literature. These works are not cited in the current study at all. For instance, Anguiano 2017; Cavo et al. 2018; Anguiano et al., 2020; Sodek et al. 2008, etc.
      • Even though the focus is on hypoxia and the achievement of an ischemic gradient in the chamber to allow resemblance of an in vivo tumor, the authors write in line 123 (and also in other parts of the text) that: "these results show that consumer cells in the 3MIC form ischemic gradients that can influence the local metabolic microenvironment experienced by neighboring tumor spheroids". The addition of the use of the PMDS membrane partly supports the claim, however it would be interesting to check whether this is indeed true, by measuring for example the levels of certain metabolites (e.g., glucose, glutamine, glutamate, lactate, aspartate) reached with the system, or pH levels, etc., in presence or absence of the hypoxic gradient/consumer cells.
      • When looking at the references presented in the manuscript, authors quote too many review articles, rather than scientific articles. Given the extremely wide literature on cancer metastasis, more of these works should be quoted in this context. For example: in the introduction - text lines 27-38 - only 4 references are research articles, out of 14 references presented in that paragraph.
      • As authors showed successfully how macrophages and cancer cells can interact in the chamber, recapitulating cell interactions in an in vivo context, it would be very interesting to see whether different consumer cells would induce similar or different changes to the spheroids and the ischemic gradient (for instance using stromal cells or non-tumor cell lines as consumers, instead of cancer cells only), as we know how tumors are a multitude of cell subsets, each contributing to nutrient production, oxygen consumption, etc.

      Minor comments:

      • Studying the early metastatic development/seeding remains a timely quest, however authors should refer to several new studies in which various mouse models are used to study metastasis from different points of view (e.g., PMID 25822788; PMID 36991128; PMID 25171411; PMID 25633981; PMID 34632412; PMID 35921474; etc). Or line 41, three reviews are quoted (refs 27-29), whilst there are several works that could be quoted on metabolism in solid tumors also in the context of metastasis (e.g., PMID 36522548; PMID: 26719539, PMID 34303764). This comment applies to the rest of the text.
      • The order of the references is not properly presented. In the introduction, the first reference is n. 4 (text line 22), instead of it being reference 1. Moreover, the subsequent literature ref. is number 12 and not number 2. Please revise the order of the references, and position them within the bibliography from first cited to last cited in the text.
      • Lines 98-104. It would be helpful to the reader to define here what these consumer cells are. Even though it is explained in the methods that the consumer cells are cancer cells, it is important to make it clear in the text, as it could be misleading at times.
      • The English grammar and spelling should be revised in some parts, as well as typos and missing words throughout the text (e.g., Line 38, the word "interraction" is misspelled and should be corrected with "interaction". Line 49, the first sentence seems incomplete. Lines 68-69 should be revised as the sentences do not flow well together, probably due to a missing word. In line 77 it should be "presents". Line 341 should be "cannot be explained").

      Referees cross-commenting

      I find the comments from the other reviewers to be in line with one another as well as with my general assessment. The major and comments of all reviewers should be addressed. The minor comments should be taken into account as well, as they would render the text and the figures more precise. I suggest that 3-6 months to complete the revision process is an appropriate time frame for the authors. Finally, I strongly encourage the authors to add in the discussion the points and questions raised by all reviewers, as well as to improve the bibliography in terms of organisation, linearity, and state of the art.

      Significance

      General assessment:

      The work by Anandi et al. offers an additional tool to tackle the issue of studying the tumor microenvironment, in a 3D culture system. The authors show a model that can be used to study tumor hypoxia in 3D, offering the possibility to study the TME in a more in vivo-like manner without turning to mice models. The development of new tools to study the TME avoiding the excessive use of animals is definitely a timely quest. In addition, the system has the potential to be applied to tackle different biological questions, as the methodology is well explained and could be suitable to many other fields of cancer biology (e.g., drug resistance or uptake). The work is overall presented in a clear way and the methodology is explained thoroughly and it has the potential to be a useful tool for the study of cancer hypoxia.

      However, authors should address how their method could differently impact other cells when applied to other systems. As one major claim is the potential use of this methodology to study the TME, it should be taken into consideration how stromal cells are strongly affected by the ECM, and how certain settings or features of the system may impact such cell populations. In addition, the work does not properly refer to the current state of the art. As other studies started to propose 3D systems for the study of TME and cell-cell interactions - besides organoids - the authors should cite these works and frame their own study in a more appropriate context, pointing out differences with the current 3D chambers available, the advantages of one vs the other, and so on.

      Advance: the study adds to the current literature as the study of tumor hypoxia in 3D remains a complicated issue. The interesting co-culture settings with macrophages suggests potential uses of this model to study cell-cell interactions.

      Audience: the study is very methodological and offers a tool that could be used by cancer biologists - and maybe by other biology fields.

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      Reply to the reviewers

      We would first like to thank the reviewers for their careful reading and thoughtful feedback.

      We have substantially revised the manuscript and included additional experimental evidence on O-GlcNAc and OGT/OGA protein levels in the placenta of embryos bearing the OGT-Y851A hypomorphic mutation.

      Overall, we believe our improved manuscript provides compelling evidence that the glycosyltransferase activity of OGT, and thus the O-GlcNAc modification itself, plays a sexually dimorphic function in placental development and the developmental repression of retrotransposons in the developing embryo.

      We have addressed each of the reviewers' comments below. The original comments (C) are in italic, our responses (R) in Roman font.

      Reviewer #1

      Evidence, reproducibility and clarity

      C1: Formichetti at el. developed mice with OGT catalytic dead mutations and then studied their function during early embryogenesis. Not surprisingly, dramatic reduction in OGT activity failed to produce embryos; however, mild reduction in OGT did produce animals. The authors then use the T931 animals that have a mild reduction in activity to further characterize the function in the early embryo. Not surprisingly, male mice showed changes in gene expression, implantation sub-lethality, and an uptick in loss of retrotransposon silencing. The authors also show that an even milder reduction in OGT activity (Y851A) effects male placenta function and chromatin remodeling. Finally, the authors make a less stable OGT transgene within the mouse and again found embryogenesis issues in the males and alterations in numerous gene families including mTOR signaling and p53 function. All in all, this is an interesting study that track functions of OGT in early embryonic development. The studies are well-controlled and rigorous.

      R1: We thank the reviewer for their clear understanding and their appreciation of the rigor and impact of this work.

      Significance

      C2: This is a good study and novel. Not only is it of interest to reproductive biologist, but it echos themes found in O-GlcNAc biology.

      R1: We are pleased that the reviewer underlined the novelty of the study and its impact across fields.

      Reviewer #2

      Evidence, reproducibility and clarity

      Comments to authors

      C3: To investigate the function of OGT at specific developmental stages, the authors perturbed OGT's function in vivo by creating a murine allelic series featuring four single amino acid substitutions that variably reduced OGT's catalytic activity. The goal was to identify the direct effect of O-GlcNAcylation, using a sophisticated collection of genetic mutants to evaluate in vivo the role of this modification at early stages of development. Overall, the severity of embryonic lethality correlated with the extent of catalytic impairment of OGT, demonstrating that the O-GlcNAc modification is essential for early development.The study represents a substantial advance in our understanding of OGT and O-GlcNAcylation in mammalian development. The creation of novel murine models and inducible systems is an important contribution, providing powerful tools for future research in this field. The insights into the role of OGT's catalytic activity and its involvement in epigenetic regulation during embryonic development are noteworthy, opening new avenues for research.

      R3: We thank the reviewer for their insightful comments. We are grateful for the supporting statements. Please find below detailed response to all your comments.

      However, there are a few considerations and concerns:

      Major:

      C4: 1. An assumption of the study is that different mutations cause different levels of O-GlcNAcylation rather than alterations in substrate specificity. It might be important to test, at least in cultured cells, that the different mutations do not change the preference of OGT to modify certain proteins rather than others, which can provide alternative explanations for their findings.

      R4: Thanks for asking this question, it helped us to better explain the rationale behind the choice of the Ogt amino-acid substitutions.

      This is a critical point that we carefully considered in the design of the single amino-acid substitutions. Two lines of evidence support that the precise mutations created impact the catalytic rate without modifying the substrate specificity:

      First, as explained in the text, the choice of the single amino-acid substitutions was driven by previous structural and enzymology knowledge. The impact of the four point mutations selected on OGT protein stability and on the Michaelis-Menten kinetic values had previously been determined experimentally (Fig. 1A legend and Martinez-Fleites, C. et al. Nature Structure Molecular Biology 2008; https://doi.org/10.1038/nsmb.1443).

      There is a second important rationale that we added in the revised manuscript: the four point mutations selected are all located in the catalytic domain (specifically, H568A in the N-Cat domain and Y851A, T931A and Q849A in the C-Cat domain), while the substrate recognition is operated via two other domains namely the intervening domain (Int-D) https://doi.org/10.1038/s41589-023-01422-2) and the tetratricopeptide Repeat (TPR) superhelix (10.1021/jacs.7b13546; https://doi.org/10.1073/pnas.2303690120). Therefore, for both these reasons, it is extremely unlikely that these mutations could influence the substrate specificity.

      C5.1: 2. In Fig 1D and 1H, the thresholds to define a gene or TE as differentially expressed are not strong. According to the figure legends, "any" change in terms of log2Fc was considered as DE and colored. I think the figures should illustrate better that the changes are subtle, by for example adding a dotted line (at least) in the value 0.5 of the y-axis. These subtle transcriptional changes should be reflected better in certain paragraphs where the expression of TEs are presented/and discussed as a hallmark of the absence of O-GlcNAcylation in the OGT-mutants. The same happens with Suppl Fig 3C (changes are very minor). {. Applying a stronger threshold, among the upregulated genes, only Xist will be significantly overexpressed. If a gentle threshold needs to be applied to this data, authors should at least justify the reasons behind doing so. Same for Fig2D.

      R5.1: The reviewer means Figure 2D for MA plot of gene expression and Figure 2H for retrotransposons expression. These figures now include a dash line to indicate Log2FC = 0.5 (as all MA plots).

      The text is explicit on the subtle changes in transcription, it reads "with 2/3 of the genes downregulated and 90% of the significant changes below 1 log__2__FC"; "most of the Ogt__T931del/Y embryos showed a low magnitude upregulation of retrotransposons".

      The revised text states "Notably, most of the OgtT931__del/Y embryos showed a low magnitude (log2FC < 1) upregulation of retrotransposons".

      We expand on this topic in the next response (R5.2) noting that changes in gene expression upon O-GlcNAc perturbation in different systems were previously characterized as subtle and widespread. We suggest that this phenotype may arise from the scarcely understood pleiotropic function of O-GlcNAc in fine-tuning gene expression; this phenotype could have a biological significance.

      C5.2: If a gentle threshold needs to be applied to this data, authors should at least justify the reasons behind doing so. Same for Fig2D.

      R5.2: Previous studies in different systems reported that O-GlcNAc perturbation causes a widespread change in gene expression of low magnitude (https://doi.org/10.1101/2024.01.22.576677, https://www.pnas.org/doi/10.1073/pnas.2218332120). We use the same thresholds as a recent functional Ogt study in ES cells to call differentially expressed genes, specifically: p<0.05 (Wald test), any FC (Li et al. PNAS 2023, https://www.pnas.org/doi/10.1073/pnas.2218332120). The p value threshold is standard; the absence of FC threshold is dictated by the insufficient knowledge of the significance of the low magnitude changes observed across many transcripts.

      C6: 3. In Figure 2B, the T931del allele was recovered in the blastocyst population with a very high frequency, even higher than the male WT group (T931del: 10; WT: 3). This observation suggests that the T931del allele did not significantly affect blastocyst survival. Further clarification or additional experiments might be necessary to understand the implications of this finding on early developmental stages.

      R6: This is only a hint as the numbers of blastocysts recovered were too small to perform statistics on Mendelian distribution. Thus, more experiments are needed to perform these statistical tests. These experiments are onerous because the low frequency of germline transmission is incompatible with maintaining this mutation by breeding heterozygous animals. Because of this, a new mouse line needs to be created by CRISPR-HDR targeting in the zygote in order to compute statistics on Mandelian ratios. Importantly, this question - does T931del affect blastocyst survival? - is peripheral, and the results of these experiments would not affect our conclusions in any way.

      C7: 4. Similarly, in Figure 2G, there is an apparent higher expression of TE expression in the T931A/Y embryos group than in the T931del/Y group, which combined with the higher frequency of blastocyst generated in this latest group it may indicate a deeper molecular consequence after the deletion of the T931. A comparison of the transcriptome between these two cell lines help to address this possibility. Also, the authors should compare the O-GlcNAc levels of WT, T931A, and T931del mutant blastocysts by immunostaining, similar to what was done in Figure S5F.

      R7: We agree that a direct comparison between the two mutations of the T931 residue would be interesting; however, this comment is very difficult to address experimentally for the reasons outlined below:

      Firstly, it is not possible to perform a statistical comparison of the transcriptome T931A/Y VS. T931del/Y with the data generated because the number of hemizygous T931A/Y (n=2) is too small. Hence, it cannot be ruled out that the seemingly milder retrotransposon reactivation in one of the T931A/Y embryos could have occurred by chance.

      Secondly, considering the low magnitude effect on gene expression changes upon O-GlcNAc genetic perturbation, to statistically assess the penetrance of the molecular phenotype and perform the differential expression analysis, numerous (>>3) hemizygous blastocysts of each genotype would be needed. Because females heterozygous for the T931 mutations transmit the mutant allele at very low frequency, these experiments require numerous de novo CRISPR injection sessions.

      Thirdly, for the immunostaining of O-GlcNAc to be semi-quantitative, a large number of hemizygous blastocysts for each genotype would be required (note that in Figure S5F, 29 morulae per condition were imaged), thus requiring numerous CRISPR injection experiments as discussed above. Moreover, O-GlcNAc changes could be subtler than what expected based on the strong reduction of OGT activity, since as a compensatory mechanism Ogt expression is upregulated in the Ogt__T931A/del blastocysts (Fig. S2D), making a quantification even more challenging despite a high number of stained embryos.

      In sum, these in vivo experiments are difficult and require sacrificing many animals (about 20 females per CRISPR injection experiment). Because the results would bring refinement to the study but would not change our conclusions, we suggest that the cost/benefit is too high.

      C8: 5. In Boulard et al. 2019 O-GlcNAcylation was shown to be sufficient to modulate expression of DNA methylation-dependent TEs. It would be interesting to know (or at least discuss) if the changes in TE expression observed in OGT-mutant embryos in this study involve changes in DNA methylation. Ideally, some DNA methylation measurement optimized for low input numbers of cells would be useful.

      R8: Thank you for making the link with our previous study. In the PNAS paper, we report that targeted removal of O-GlcNAc at proteins bound to specific TEs (e.g. IAPez) causes their full-blown reactivation without detectable changes in DNA methylation, thus suggesting a role of the O-GlcNAc modification for the silencing of methylated TEs downstream or independent of DNA methylation. We agree that it would be informative to quantify DNA methylation in the T931-mutant blastocysts to test if the in vitro result is the same in vivo, but this would require performing onerous microinjection sessions as explained above.

      C9: 6. The data related with the OGT-degron system in MEs seem disconnected with the rest of the manuscript. While the developmental models (blastocyst, etc) elegantly assess the contribution of O-GlcNAcylation to the control of cell survival and gene expression through the use of different OGT mutants, the degron system is a system of graded depletion that unfortunately was only possible to be used in MEFs (instead of embryos). Thus, the results obtained with the degron system in MEFs are difficult to intersect with the data from the use of OGT-mutants in embryos. Even though there are obvious interesting questions that one may want to know about this OGT degron MEF system, none of them would demonstrate a direct role for O-GlcNAcylation in cellular function, the major point addressed in the developmental system. Using the degron system in embryonic stem cells might have provided a more parallel comparison. The authors should discuss this point in more detail and either use ESC instead of MEFs or provide a stronger justification for the use of MEFs over ESC.

      R9: We thank the reviewer for their clear understanding of the system. The choice of primary MEF as an in vitro model was imposed by technical limitations we encountered during the study. We fully agree that ES cells is the model of choice for preimplantation embryos; thus we initially derived ES cells and obtained only one male clone bearing the AID degron system. Upon auxin addition to the culture media, OGT's level remained unchanged in ES cells. Thus, the ES cells model was not usable. To test the AID degron in a different cell type, we then derived MEFs and showed its effectiveness (Figures 4C and S4C-E), which also allowed to collect functional data on OGT's cellular function (Figures 4D-F). We took the comment on board and clarified the rationale of studying MEFs in the revised manuscript. We agree that it remains to be verified that the OGT-dependent pathways uncovered in MEFs are relevant in the preimplantation embryo. Despite this caveat, we feel the mouse model for endogenous OGT-degron, as well as the negative results in vivo and conclusions in MEFs should be shared with the community, which could take advantage of our results to refine the system.

      Minor:C10: 7. In Fig 2C the color and shape codes are confusing to understand - there are some colors/shapes that are not represented in the PCA plot. The same in Fig 3H, where in the PCA plot there are pink triangles that do not match with the code legends.

      R10: We apologize for the confusion with the legends of Figures 2C and 3H, that we have made unambiguous in the revised version (as well as Figures S2B,C and S3C).

      C11: 8. In the figure legends of Figures 2D, 2E, 2F, and 2H, the notation should be corrected from "OgtT931A/Y" to "OgtT931del/Y".

      R11: This has been corrected; many thanks for bringing it to our attention.

      Significance

      C12: To investigate the function of OGT at specific developmental stages, the authors perturbed OGT's function in vivo by creating a murine allelic series featuring four single amino acid substitutions that variably reduced OGT's catalytic activity. The goal was to identify the direct effect of O-GlcNAcylation, using a sophisticated collection of genetic mutants to evaluate in vivo the role of this modification at early stages of development. Overall, the severity of embryonic lethality correlated with the extent of catalytic impairment of OGT, demonstrating that the O-GlcNAc modification is essential for early development.

      R12: We thank the reviewer for their clear understanding of our work and their appreciation of the biological importance of the findings.

      Reviewer #3

      Evidence, reproducibility and clarity

      C13: This is a conceptually interesting paper that attempts to leverage the knowledge of OGT catalysis to begin to dissect OGT function. The evidence is presented I a straightforward fashion and is in general well documented. The breeding strategies are well informed and the paper draws heavily on previous work carried out in the mouse.

      R13: We greatly appreciate the overall supporting review. However, we fail to understand what they mean with "the paper draws heavily on previous work carried out in the mouse". This comment may stem from a misunderstanding because this work is not based on any previously published study. Specifically, neither the seven murine alleles presented and analyzed nor the single embryo-transcriptomic data sets on which our conclusions are based have been published elsewhere.

      To put this work into context, before our study there were two seminal studies published two decades ago that reported the essential role of Ogt for mouse development, but no molecular profiling was performed (10.1073/pnas.100471497, 10.1128/mcb.24.4.1680-1690.2004). The two Ogt loss-of-function alleles studied in these papers were deemed as not suitable for interrogating molecular phenotypes because they caused cell death that confounds molecular profiling and embryonic lethality at implantation, thus preventing study of the sexually-dimorphic role of Ogt placenta. To overcome this long-standing problem, we created new seven murine alleles, which allowed us to tease apart molecular phenotypes at key stages of mouse embryonic development, focusing on the blastocyst and the placenta.

      Significance

      C14: The paper describes tools which will help dissect the many potential roles of O-GlcNAc addition in early development. As it stands, this is a descriptive manuscript that will lead to hypothesis generation and testing and this should not be undervalued. The biological reagents produced and characterized will be of general interest to the field. Most of the findings presented represented a verification of existing ideas in the field but this is not meant as a criticism since part of the motivation for the approach was to generate a reproducible system for analyzing the biological phenomena.

      R14: We thank the reviewer for their appreciation of the importance of experimentally testing ideas shared in the field without direct evidence.

      However, we must respectfully disagree with the qualification of "descriptive manuscript". This qualification may stem from the particularly difficult challenge to accessing the molecular details on how the O-GlcNAc modification exerts the biological functions we report. We are fully cognizant of the limitations of the study that we discussed in the discussion section and in R20.2. However, we feel that the adjective "descriptive" is not a fair qualification because we provide numerous novel functional evidence. Specifically, we introduce two novel orthogonal in vivo perturbations for endogenous Ogt that allowed us to interrogate for the first time its function in the developing mouse embryo. These perturbations allow us to draw causative conclusions (not descriptive) on the essential role of the O-GlcNAc modification itself for preimplantation development, its sexually-dimorphic role in the placenta and its requirement in vivo for the stable repression of retrotransposons.

      C15: There are perhaps some bioinformatic shortcuts taken that may need to be corrected upon thorough review. These do not lessen the overall impact of the contribution.

      R15: All the code written for the bioinformatic analyses performed in this study is publicly available: https://github.com/boulardlab/Ogt_mouse_models_Formichetti2024. The reviewer needs to specify which bioinformatic analysis they suggest could be improved.

      Reviewer #4 (Evidence, reproducibility and clarity (Required)):

      Summary

      C16: O-GlcNAcylation is the fundamental post-translational modification of numerous nuclear and cytosolic proteins. OGT is the sole enzyme catalyzing O-GlcNAc addition onto the proteins. The essentiality of OGT for early development and cellular viability has been established by using OGT-KO mice and cell lines. However, it remains to be elucidated whether the catalytic activity of OGT is required for the early development, and if the catalytic activity of OGT is required what are the functions of OGT or O-GlcNAcylation in early development due to a lack of appropriate mouse models. To overcome the technical difficulty of manipulating the levels of O-GlcNAcylation in early embryos, Formichetti et al. created the series of four mouse models (OgtY851A, OgtT931A, OgtQ849N, and OgtH568A) with different OGT activity by introducing single amino acid substitution in the catalytic domain. By analyzing the inheritance of the hypomorphic OGT alleles and the lethality of mouse embryos, they discovered OGT activity is a critical factor for early development. Subsequently, RNA-seq analyses with two mouse models showing the maternal inheritance of the hypomorphic OGT alleles indicated that sever hypo-OGT activity altered transcription and silencing of retrotransposon in preimplantation development while mild reduction of OGT's activity affected placental development in a sexually dimorphic manner rather than preimplantation development. Furthermore, to study the function of OGT at specific developmental stages, they developed a mouse model bearing endogenously AID-tagged OGT for acute degradation of OGT. Although the degron system wasn't efficient in preimplantation embryos, they discovered quick transcriptional changes upon OGT deletion in MEFs. The quality of the manuscript is good because the question to be solved was appropriately set, the approach was well designed, and their findings were interesting, although their writing was sometimes hard to understand as I raised in my following comments. Nevertheless, there are several points to be fixed before being published.

      R16: We thank the reviewer for their clear understanding of our work and their appreciation of the biological importance of the findings. Your comprehensive review of the manuscript and the questions you raised were extremely helpful in improving the manuscript and fully addressing its limitations. Below, we respond to comments in full, have revised the manuscript to improve clarity and have included novel results.

      Major Comments

      C17: 1. Although the authors showed in vitro activity of each mutant of OGT used in this manuscript by referencing the previous literature, they never showed the levels of global O-GlcNAcylation (and OGT itself) in their established mouse embryos. Although it could be impossible to determine O-GlcNAc levels in OgtQ849N and OgtH568A embryos because of the lack of germline transmission and founder line, respectively, they could do that in OgtY851A and OgtT931A embryos. Given that Y851A and T931A mutants had similar VMAX/KM with different VMAX, it is possible that their activity is comparable or Y851A has even lower activity in vivo depending on the concentration of UDP-GlcNAc in embryos. Therefore, it is critical to assess whether in vivo OGT activity is correlated with that in vitro as expected to conclude that severity of sub-Mendelian inheritance is proportional to the reduction of activity of OGT in vivo. Moreover, since the authors developed the elegant system to deplete OGT, the activity of Q849N and H568A mutant OGT can be examined at least in cells by expressing them in MEFs with OGT-degron system. Thus, I propose determination of global O-GlcNAc levels compensated by OGT levels by western blotting in OgtY851A, and OgtT931A embryos or MEFs with the OGT degron system re-expressing the individual four mutant OGTs. If the protein amount is insufficient for western blotting in the embryos because of the sizes of the earlier stages of embryos, I believe the author could address this by utilizing immunofluorescence as shown in Figure S5.

      R17: We fully agree that this is an important point that requires revision. The only mutation for which the level of O-GlcNAc and OGT can be assessed by western blot in vivo is Y851A, the other mutations resulting in embryonic lethality before the blastocyst stage.

      We have included in the revised manuscript western blot analyses of protein expression for OGT, OGA and O-GlcNAc levels in the placenta of the OgtY851A mutants (new Figures 3C,D). The new data show that OGT is upregulated at the protein level in homozygous females, in good agreement with our transcriptomic analysis. Furthermore, O-GlcNAc levels were slightly reduced in homozygous and hemizygous placentae thus showing the impact of the point mutation on global O-GlcNAc levels in the placentae. Moreover, the analysis of OGA protein level unexpectedly revealed the enrichment of a previously uncharacterized OGA fast migrating isoform in hemizygous and homozygous placentae.

      We agree that it would be informative to compare O-GlcNAc levels in OgtT931A versus OgtY851A embryos. A comparison implies performing the experiment at the same developmental stage, which has to be the blastocyst stage or prior because T931A/Y embryos die around implantation. The blastocyst being made of approximately 140 cells, it would require to pool many single blastocysts to obtain the necessary protein input for western blot. We are not aware of another study performing western blot with pooled blastocysts. An additional great challenge for this experiment is the necessity to genotype and sex the blastocysts before pooling. Thus, the feasibility of this experiment is uncertain.

      As an alternative, the reviewer suggests measuring O-GlcNAc levels in the degron MEFs after introduction of OGT transgenes bearing the mutation studied. This experiment would not be conclusive because of residual O-GlcNAc after OGT degradation (Figure S4E). Furthermore, the O-GlcNAc proteome is dynamic during development (as shown in the developing brain by Liu et al. https://doi.org/10.1371/journal.pone.0043724), therefore the MEFs results would have limited value to explain our results in the early embryo.

      In sum, available technologies to quantify O-GlcNAc (e.g. western bot, mass spectrometry) are inadequate for low input samples as the early embryo. However, our series of hypomorphic alleles backed up with in vitro enzymology measurements brings indirect evidence to this question. Specifically, the qualitative correlation between the measured OGT activity in vitro and the developmental phenotype indicates that the resulting relative levels of O-GlcNAc are consistent with in vitro measurements.

      C18.1 : 2. I didn't understand why the authors couldn't find any founder lines of the OgtH568A mutant. Was that because mosaic mice with OgtH568A mutation are lethal?

      R18.1: To answer to this question, it is important to recall two key features of the biological system:

      1) The mutation H568A was reported to disrupt the glycosyltransferase activity completely (10.1038/nsmb.1443). Hence, OGT-H588A is catalytic dead.

      2) We performed the CRISPR-HDR targeting in the 1-cell embryo.

      Based on these premises, the absence of F0 with the OgtH568A mutation (0/31) suggests that introducing this mutation causes embryonic lethality in both males and females. This hypothesis is consistent with the previously reported lethality around implementation of Ogt-null alleles (10.1128/mcb.24.4.1680-1690.2004). It is possible that the sgRNA is very efficient and results in homozygous mutations in all female zygotes injected (as we have not obtained heterozygous females bearing these mutations). High efficiency of the targeted mutagenesis in the zygote results in mutants where all or the majority of cells bear the mutation (no or low mosaicism). The high number of microinjections performed (416 embryos over the 3 injection sessions) allows us to make these claims.

      C18.2 : Also, I believe there was no explanation why the OgtQ849N allele showed no maternal inheritance. Was that because Q849N possesses enough activity for sustaining mosaic embryos, but not oocytes? The authors should better explain these points in the manuscript text.

      R18.2: Thanks for this comment, we agree that this maternal effect phenotype demands further explanation.

      The phenotype observed suggests two possibilities: either that the oocyte cannot maturate or that the cleavage-stage embryo cannot develop with the resulting lower levels of O-GlcNAc. The cleavage-stage embryo does not transcribe a catalytically active OGT before the 8-cell stage and thus relies on the OGT protein inherited from the oocyte until this stage (https://doi.org/10.1101/2024.01.22.576677).

      Thank you for this comment, we added this interpretation of the result in the text:<br /> "The lack of maternal transmission of the Q849N allele from seemingly mosaic founder females is likely explained by the reliance of the cleavage stage embryo onto the oocyte payload of OGT and O-GlcNAc modified proteins. Specifically, Ogt's exons encoding for the catalytic domains are not detectable before the 8-cell stage, while OGT full-length protein is present and thus maternally inherited (Formichetti et al, 2024)."

      C19: 3. The authors serendipitously found a T931del-allele in the "WT" allele of the OgtT931A line, and suggested that T931del had milder activity loss, although the lethality of embryos was greatly mitigated. Nevertheless, transcriptome analyses in male blastocysts revealed that 120 genes' expression was changed in T931del/Y males. This raised the question about which mutant OGT has higher activity, Y851A or T931del. I think comparing the activity of Y851A and T931del mutants in MEFs with OGT-degron system is important to confirm the proportional relationship between activity and phenotypic severity.

      R19: We agree that it is a limitation that the effect of the T931del mutation on OGT activity has not been biochemically characterized. However, the important point here is that our assessment of phenotypic severity based on maternal inheritance of the mutant allele and embryonic lethality is based on the point mutations for which the catalytic activity has been determined, namely Y851A, T931A, Q849N and H568A, but not T931del.

      We studied the serendipitously discovered T931del mutation to obtain transcriptional insights in the blastocyst. Because the deleted residue T931 is key for the binding to the donor substrate, we can reasonably assume that this mutation affects the catalytic activity, albeit to an undetermined level.

      Hence, our conclusions regarding the requirement of O-GlcNAcylation for development are unaffected by the lack of biochemical knowledge on T931del.

      C20.1: 4. Regarding transcriptomes of T931del/Y, the authors found the upregulation of proteasomal activity and stress granules along with the downregulation of amino acid metabolism, mitochondrial respiration, and so on. To validate the results, the authors should perform qPCR on several up- or down-regulated genes.

      R20.1 : We agree that, in principle, qPCR validation is suitable. However, this validation experiment is particularly expensive in this case because of the requirement of numerous CRISPR zygote pronuclear injection sessions.

      The conclusions of the RNA-seq analysis are strongly supported by a high number of biological replicates (n=10). This high number of biological replicates was essential to obtain sufficient statistical power to quantify with a high level of confidence transcriptional changes of low magnitudes (below 2-fold change, see R5.1 and R5.2).

      Therefore, the qPCR validation experiment would require to repeat the CRISPR zygote pronuclear injection sessions with the same high number of animals. This represents a major investment in experimental work and the sacrificing of about 40 animals. Importantly, the RNA-seq results presented are authoritative because of a high number of biological replicates and high number of sequencing reads per sample. Thus, we argue that qPCR validation is not essential and thus the high cost of this experiment is difficult to justify.

      C20.2: In addition, according to Figure S2E, the authors pointed out that at least for genes upregulated in OgtT931A embryos, the changes were not explained by a developmentally delayed transcriptome, suggesting that upregulation of these genes was the cause of developmental delay. Therefore, I strongly encourage them to discuss in the manuscript text how up-regulated genes could contribute to developmental delay.

      R20.2: Throughout the manuscript, we have been cautious to avoid establishing causal relationships between the differentially expressed genes uncovered and the developmental phenotypes (e.g. delayed development). There are two main obstacles which we believe prevent us from establishing causality with the data available. Firstly, it is not possible to disentangle differentially expressed genes and developmental delay (in other words, we have no way to tell which is the cause and which is the consequence). Secondly, O-GlcNAc modifies over 5000 proteins and the developing embryo is a particularly dynamic system; thus we cannot know whether the differentially expressed promoters are direct targets of O-GlcNAc modified proteins (or alternatively secondary effect of another molecular alteration, for example of the proteome). We discuss this limitation of the study in the discussion section.

      C21: 5. Regarding the transcriptome in OgtY851A mice, Y851A/Y male mice had huge transcriptomic differences, while Y851A/Y851A female mice barely had any. Although it seems to agree with the number of Ogt alleles, I wonder whether other X-linked genes expressed higher in female placenta as shown in Figure 3C could attenuate the effects of decreased OGT activity. I don't think this possibility can be excluded, unless the authors further decrease OGT activity in Y851A/Y851A female placenta and obtain the similar results as for male placenta. Or if they compared the levels of global O-GlcNAcylation between Y851A/Y and Y851A/Y851A mouse placentas and discovered they had similar levels of O-GlcNAcylation, then the authors could conclude that the number of Ogt alleles was not the reason of sexual-dimorphism. The authors should determine the levels of O-GlcNAcylation in Y851A/Y and Y851A/Y851A mouse placentas and/or at least discuss the above possibilities in the manuscript text.

      R21: Thank you for the thoughtful feedback. We agree that the most likely explanation for the higher sensitivity of males placenta as compared to females to OGT reduced activity is the difference in Ogt copy number, especially because Ogt escapes X-chromosome inactivation in the placenta (new Figure S3A).

      Western blot quantification of global O-GlcNAc levels was now performed (new Figures 3C,D). We measured similar level of O-GlcNAc in Y851A/Y and Y851A/Y851A placentas (lowered than WT males in both cases), but we cannot exclude that the WB does not have the dynamic range required to detect a subtle difference. In fact, female homozygous were expected to have an intermediate level between WT males and hemizygous males, and the difference between the two male genotypes (also considering sample-to-sample variability) is already small when quantified from the blot (new Figure 3D). It is possible that a X-linked modifier attenuates the impact of hypo-O_GlcNAcylation in female mutant placenta in the case of identical O-GlcNAc levels in homozygous females and hemizygous males. Thank you for the idea that we included in the revised manuscript:

      "Of note, the lower sensitivity of the homozygous females' transcriptome to Ogt disruption (Fig. 3F,I and S3B) seems difficult to reconcile with their lower O-GlcNAc level comparable (lower) O-GlcNAc level to the hemizygous males (Fig. 3C). It is possible that the western blot technique is not sensitive enough to detect subtle differences in O-GlcNAcylation. An alternative hypothesis, if O-GlcNAc levels were truly identical between Y851A/Y and Y851A/Y851A, could be the existence of a modifier in female that could be a XCI-escapee."

      C22: 6. In terms of the transcriptome in OgtY851A mice, similar to comment 4, the authors should confirm their transcriptomics data shown as Figure 3D by qPCR. In addition, the authors should describe the potential mechanisms by which the differentiation of precursor cells of LaTPs and JZPs were disrupted. Were master regulators of the differentiation known to be O-GlcNAcylated and loss of O-GlcNAcylation perturbed the function?

      R22: As for the whole embryo discussed in R20.2, we also interpret cautiously the gene expression phenotype observed in the placenta. Specifically, we state in the manuscript that it could either be caused by an impact of lower O-GlcNAcylation on placental differentiation or by a general delay in placentation or in the development of the embryo as a whole. The hypothesis of a general delay (of the whole embryo and/or of placental formation specifically) is supported by the downregulation of essentially all markers of more differentiated cell types and the upregulation of the precursor marker. We favor this hypothesis because it is consistent with what observed with the T931 mutants and also with the enzymatic removal of O-GlcNAc in the zygote (Formichetti et al., 2024 BioRxiv). Because of the thousands of O-GlcNAcylated proteins present in the cell, it is impossible to know which is the responsible molecular mechanism, which could even start at much earlier stages.

      Minor Comments

      C23: 1. Regarding DFP461-463 mutant, I couldn't understand the point of this figure because the results had no difference, and the meaning of the mutation was quite different from the others. Thus, the figure was awkward and a little confusing to me. If the authors still want to include the figures, I would suggest that they should reorganize the position of the figure (maybe after figure 3 is better to show you had tried to investigate the effects of nuclear localization of OGT on the changes of transcriptomes) and add some results. Since WT OGT seems to be localized mainly in the cytosol at steady state (Figure S1B and S1C), the effect of mutation on its nuclear localization should not be obvious. Therefore, it is difficult to conclude the mutation had no effect on the nuclear localization unless the ratio of nuclear and cytosol localization is quantified. Also, I wonder whether the O-GlcNAc levels of nuclear and cytosolic proteins in the mutant cells were comparable to those in WT cells. If this is the case, the results would also support the authors' conclusion.

      R23: We took the comments on board and made it clearer that the rationale for the DFP461-463 mutant was an attempt to separate OGT's nuclear and cytosolic functions. We fully agree that these results are peripheral, and thus we presented these results in Supplementary Figure 1 (not in the main figure).

      The biochemical evidence presented in Fig S1C shows that the genetic substitution of DFP to AAA on endogenous OGT has no detectable impact on its nuclear localization in primary MEFs. This result is far more authoritative than the evidence provided by Seo et al. 2016 (doi: 10.1038/srep34614), which is based on the overexpression of OGT transgenes in HeLa cells. Importantly, Seo et al. 2016 did not assess the impact of their mutations on endogenous OGT.

      We believe that the negative results we obtained with the DFP461-463 mouse model shall be extremely valuable for the field. Firstly, science can move forward only if both negative and positive results are shared. In this specific case, we found that mutation of endogenous OGT in MEFs yielded to a different result than previously reported overexpression of the same mutant construct in HeLa cells. Secondly, we want to make the Ogt-NLS- mouse model available for further investigations.

      C24: 2. Since OGT or O-GlcNAcylation regulates chromatin status, the authors analyzed the gene expression profiles of retrotransposons in T931del/Y or T931A/Y mice. Is it possible to investigate if the release of gene silencing is also seen in non-retrotransposon genes? I assumed retrotransposons might be a well-established system to analyze gene silencing status, however, if the authors could find similar effects on genes other than retrotransposons, that would be highly valuable.

      R24: This is an interesting idea. This notion refers to the activation of promoters that are normally epigenetically repressed (e.g. silent despite the presence of all trans-active factors required for their expression). Epigenetically repressed promoters include retrotransposons, imprinted genes and germline specific genes that are normally expressed in germ cells and maintained in a repressed state in somatic cells (10.1038/s41580-019-0159-6). Testing of mono-allelic expression of imprinted genes required F1-hybrid. Thus, we assessed whether well-studied germline specific genes could be realized from silencing in T931del/Y or T931A/Y blastocyst and found no evidence for it (see dot plot below). The unbiased transcriptomic analysis presented in the manuscript shows that the product of upregulated genes are enriched in mRNA processing (Figure 2E), but these genes are not normally epigenetically repressed. Thus, contrary to retrotransposons, the role of O-GlcNAc at cellular gene promoters appears not to be linked to epigenetic silencing. This could be explained by the many different protein substrates for O-GlcNAc.

      C25: 3. OgtY851A mice with milder OGT activity loss didn't exhibit impaired preimplantation development, but did display postimplantation development such as placental development, suggesting that O-GlcNAcylation of proteins required for preimplantation and postimplantation development relies on different degrees of OGT activity. I wonder whether global O-GlcNAc levels in embryos in preimplantation and postimplantation developmental stages are different or not. This might include both the pattern of blotting and intensities. The results would give the authors an explanation why the dependency on OGT activity was different in two developmental stages. Can the authors provide data? If not, then the authors should at least describe hypotheses in the manuscript to address these questions.

      R25: We recently reported that the subcellular patterns of O-GlcNAc are highly dynamic during preimplantation development (Formichetti et al. 2024, BioRxiv). The most striking O-GlcNAc remodeling we observed is the enrichment of nuclear O-GlcNAc as compared to cytoplasmic O-GlcNAc that is concomitant to embryonic genome activation (Formichetti et al. 2024, BioRxiv). We quantified the ratio of the nuclear/cytoplasmic signal by immunofluorescence, but absolute quantification is not possible with this method. Due to the limited number of cells of the preimplantation embryo, this analysis cannot be performed by western blot. Hence, there is no appropriate method to quantitatively compare O-GlcNAc levels between preimplantation and postimplantation embryos.

      C26: 4. The authors' AID-degron system elegantly worked in MEFs but was inefficient in preimplantation embryos. I wonder if this was because of the high expression of the shorter isoform of OGT detected as OGTp78 in the author's western blot. Is it possible to examine this possibility in the embryos? Either way, the authors should describe a potential explanation for why the efficiency in the embryos was low. In addition, the authors should describe why they inserted the AID tag only into the longest OGT isoform.

      R26: This is a good point. The smallest isoform OGTp78 bears the catalytic domain and thus can partially compensate for the degradation of OGTp110. Note that the level of OGTp78 is low and does not increase upon OGTp110 degradation; thus a compensation can only be partial (Figures S4A and S4D). Alternative hypotheses for the ineffectiveness of the degron system in ex vivo grown embryos include: i) the expression level of OsTIR that may be too low in the early embryo (Rosa26 promoter not being activated at EGA), ii) a possible steric hindrance of the N-ter AID tag in these cells, iii) the lower concentration of Auxin imposed by toxicity on the embryo is likely suboptimal. Testing these possibilities is very difficult in preimplantation embryos.

      It is unclear how the OGTp78 isoform is produced; it was hypothesized to originate from an alternative transcription start site (https://doi.org/10.1007/s00335-001-2108-9). We initially attempted to target both isoforms by inserting the AID tag at the C-terminus, but we were unsuccessful in producing this mouse model. It is possible that the C-terminus that is near the catalytic site cannot tolerate the AID knock-in.

      C27: 5. In Figure S1C, is the band detected right below OGTp78 in nuclei fractions non-specific or do both bands correspond to OGTp78 ?

      R27: To answer this question, a knockout control would be needed. OGTp78 being not targeted by our AID-degron, we cannot test the specificity of these bands using our perturbation tool kit.

      C28: 6. Figure 1D top row third column: hemizgous -> hemizygous

      R28: Many thanks; the embarrassing typo has been corrected.

      C29: 7. Figure 1D second row third column: hemyzygous -> hemizygous

      R29: Thanks for bringing this other typo to our attention, it is now corrected.

      Reviewer #4 (Significance (Required)):

      General assessment: strengths and limitations

      C30: Strength: This manuscript elegantly revealed the requirement of OGT in mammalian development by taking advantage knock-in mouse models with different OGT activity. In addition, the manuscript provided the interesting and important transcriptomics data in both pre- and post-implantation embryos of OGT mutant mice. These data sets could explain detailed mechanisms how OGT or O-GlcNAcylation regulates mammalian development in the future. Furthermore, development of AID-tagged OGT system would be a useful tool for other researchers studying OGT function.

      Limitation: Although they found interesting changes in terms transcriptomes in developing mice with different OGT activity, they lack the data showing how these changes caused the observed phenotypes. In other words, there are less mechanistic insights behind the developmental problems seen in mice with different OGT activity.

      In addition, although I agree the question about whether OGT activity itself is crucial for the early development of mammals has not been completely solved for a long time, I assume people thought OGT activity is actually important for the mammalian development thorough the observation of OGT-linked congenital disorders of glycosylation.

      Therefore, I would say the novelty of the manuscript is a little less impactful. Furthermore, although AID-tagged OGT system revealed fundamental questions regarding the transcriptional changes upon acute depletion of OGT in cellular levels, the system was inefficient in mouse embryos. So, they showed nothing about developmental-stage specific requirements of OGT.

      Advance: The manuscript can fill a current gap regarding requirement of OGT in mammalian development. Also, the manuscript developed a series of mutant mice with different OGT activity and an AID-tagged OGT mouse line. These mice provide technical advances.

      Audience: The manuscript will be interested in researchers in specific fields such as glycobiology, developmental biology, and clinical fields.

      Describe your expertise: Biochemistry, Glycobiology, Cell biology

      R30: We are thankful for the constructive and supportive review.

      We fully agree with the limitations of the study and discussed them in the manuscript. Our in vivo approach revealed the most phenotypically relevant transcriptional phenotypes resulting from OGT catalytic impairment during embryonic development. We make the mouse models created for this study available to the community to facilitate follow-up studies aiming at exploring the underlying molecular details.

      As pointed out in the comments, the requirement of OGT glycosyltransferase activity for mammalian development was widely assumed by the field, but this belief was without direct experimental evidence. This study provides the first in vivo evidence for this important conclusion.

      Conclusion: The reviewers' comments were tremendously useful to improving the clarity of the manuscript and adding important new in vivo evidence. We note that none of the reviewers provided any reason to doubt our important conclusions:

      • The demonstration that the enzymatic activity of Ogt, thus the O-GlcNAc modification itself, is essential for preimplantation development.
      • The finding that a mild reduction of OGT's activity is sufficient to perturb the silencing of multiple families of retrotransposons in the growing embryo.
      • The indication, from transcriptomes of hypo-O-GlcNAcylated embryos, of a developmental retardation upon a mild O-GlcNAc perturbation.

      • The discovery that OGT's rapid depletion in vitro downregulates basal cellular function, including translation. This result provides mechanistic support to the embryonic growth delay resulting from decreasing O-GlcNAc in vivo.

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      Referee #4

      Evidence, reproducibility and clarity

      Summary

      O-GlcNAcylation is the fundamental post-translational modification of numerous nuclear and cytosolic proteins. OGT is the sole enzyme catalyzing O-GlcNAc addition onto the proteins. The essentiality of OGT for early development and cellular viability has been established by using OGT-KO mice and cell lines. However, it remains to be elucidated whether the catalytic activity of OGT is required for the early development, and if the catalytic activity of OGT is required what are the functions of OGT or O-GlcNAcylation in early development due to a lack of appropriate mouse models. To overcome the technical difficulty of manipulating the levels of O-GlcNAcylation in early embryos, Formichetti et al. created the series of four mouse models (OgtY851A, OgtT931A, OgtQ849N, and OgtH568A) with different OGT activity by introducing single amino acid substitution in the catalytic domain. By analyzing the inheritance of the hypomorphic OGT alleles and the lethality of mouse embryos, they discovered OGT activity is a critical factor for early development. Subsequently, RNA-seq analyses with two mouse models showing the maternal inheritance of the hypomorphic OGT alleles indicated that sever hypo-OGT activity altered transcription and silencing of retrotransposon in preimplantation development while mild reduction of OGT's activity affected placental development in a sexually dimorphic manner rather than preimplantation development. Furthermore, to study the function of OGT at specific developmental stages, they developed a mouse model bearing endogenously AID-tagged OGT for acute degradation of OGT. Although the degron system wasn't efficient in preimplantation embryos, they discovered quick transcriptional changes upon OGT deletion in MEFs. The quality of the manuscript is good because the question to be solved was appropriately set, the approach was well designed, and their findings were interesting, although their writing was sometimes hard to understand as I raised in my following comments. Nevertheless, there are several points to be fixed before being published.

      Major Comments

      1. Although the authors showed in vitro activity of each mutant of OGT used in this manuscript by referencing the previous literature, they never showed the levels of global O-GlcNAcylation (and OGT itself) in their established mouse embryos. Although it could be impossible to determine O-GlcNAc levels in OgtQ849N and OgtH568A embryos because of the lack of germline transmission and founder line, respectively, they could do that in OgtY851A and OgtT931A embryos. Given that Y851A and T931A mutants had similar VMAX/KM with different VMAX, it is possible that their activity is comparable or Y851A has even lower activity in vivo depending on the concentration of UDP-GlcNAc in embryos. Therefore, it is critical to assess whether in vivo OGT activity is correlated with that in vitro as expected to conclude that severity of sub-Mendelian inheritance is proportional to the reduction of activity of OGT in vivo. Moreover, since the authors developed the elegant system to deplete OGT, the activity of Q849N and H568A mutant OGT can be examined at least in cells by expressing them in MEFs with OGT-degron system. Thus, I propose determination of global O-GlcNAc levels compensated by OGT levels by western blotting in OgtY851A, and OgtT931A embryos or MEFs with the OGT degron system re-expressing the individual four mutant OGTs. If the protein amount is insufficient for western blotting in the embryos because of the sizes of the earlier stages of embryos, I believe the author could address this by utilizing immunofluorescence as shown in Figure S5.
      2. I didn't understand why the authors couldn't find any founder lines of the OgtH568A mutant. Was that because mosaic mice with OgtH568A mutation are lethal? Also, I believe there was no explanation why the OgtQ849N allele showed no maternal inheritance. Was that because Q849N possesses enough activity for sustaining mosaic embryos, but not oocytes? The authors should better explain these points in the manuscript text.
      3. The authors serendipitously found a T931del-allele in the "WT" allele of the OgtT931A line, and suggested that T931del had milder activity loss, although the lethality of embryos was greatly mitigated. Nevertheless, transcriptome analyses in male blastocysts revealed that 120 genes' expression was changed in T931del/Y males. This raised the question about which mutant OGT has higher activity, Y851A or T931del. I think comparing the activity of Y851A and T931del mutants in MEFs with OGT-degron system is important to confirm the proportional relationship between activity and phenotypic severity.
      4. Regarding transcriptomes of T931del/Y, the authors found the upregulation of proteasomal activity and stress granules along with the downregulation of amino acid metabolism, mitochondrial respiration, and so on. To validate the results, the authors should perform qPCR on several up- or down-regulated genes. In addition, according to Figure S2E, the authors pointed out that at least for genes upregulated in OgtT931A embryos, the changes were not explained by a developmentally delayed transcriptome, suggesting that upregulation of these genes was the cause of developmental delay. Therefore, I strongly encourage them to discuss in the manuscript text how up-regulated genes could contribute to developmental delay.
      5. Regarding the transcriptome in OgtY851A mice, Y851A/Y male mice had huge transcriptomic differences, while Y851A/Y851A female mice barely had any. Although it seems to agree with the number of Ogt alleles, I wonder whether other X-linked genes expressed higher in female placenta as shown in Figure 3C could attenuate the effects of decreased OGT activity. I don't think this possibility can be excluded, unless the authors further decrease OGT activity in Y851A/Y851A female placenta and obtain the similar results as for male placenta. Or if they compared the levels of global O-GlcNAcylation between Y851A/Y and Y851A/Y851A mouse placentas and discovered they had similar levels of O-GlcNAcylation, then the authors could conclude that the number of Ogt alleles was not the reason of sexual-dimorphism. The authors should determine the levels of O-GlcNAcylation in Y851A/Y and Y851A/Y851A mouse placentas and/or at least discuss the above possibilities in the manuscript text.
      6. In terms of the transcriptome in OgtY851A mice, similar to comment 4, the authors should confirm their transcriptomics data shown as Figure 3D by qPCR. In addition, the authors should describe the potential mechanisms by which the differentiation of precursor cells of LaTPs and JZPs were disrupted. Were master regulators of the differentiation known to be O-GlcNAcylated and loss of O-GlcNAcylation perturbed the function?

      Minor Comments

      1. Regarding DFP461-463 mutant, I couldn't understand the point of this figure because the results had no difference, and the meaning of the mutation was quite different from the others. Thus, the figure was awkward and a little confusing to me. If the authors still want to include the figures, I would suggest that they should reorganize the position of the figure (maybe after figure 3 is better to show you had tried to investigate the effects of nuclear localization of OGT on the changes of transcriptomes) and add some results. Since WT OGT seems to be localized mainly in the cytosol at steady state (Figure S1B and S1C), the effect of mutation on its nuclear localization should not be obvious. Therefore, it is difficult to conclude the mutation had no effect on the nuclear localization unless the ratio of nuclear and cytosol localization is quantified. Also, I wonder whether the O-GlcNAc levels of nuclear and cytosolic proteins in the mutant cells were comparable to those in WT cells. If this is the case, the results would also support the authors' conclusion.
      2. Since OGT or O-GlcNAcylation regulates chromatin status, the authors analyzed the gene expression profiles of retrotransposons in T931del/Y or T931A/Y mice. Is it possible to investigate if the release of gene silencing is also seen in non-retrotransposon genes? I assumed retrotransposons might be a well-established system to analyze gene silencing status, however, if the authors could find similar effects on genes other than retrotransposons, that would be highly valuable.
      3. OgtY851A mice with milder OGT activity loss didn't exhibit impaired preimplantation development, but did display postimplantation development such as placental development, suggesting that O-GlcNAcylation of proteins required for preimplantation and postimplantation development relies on different degrees of OGT activity. I wonder whether global O-GlcNAc levels in embryos in preimplantation and postimplantation developmental stages are different or not. This might include both the pattern of blotting and intensities. The results would give the authors an explanation why the dependency on OGT activity was different in two developmental stages. Can the authors provide data? If not, then the authors should at least describe hypotheses in the manuscript to address these questions.
      4. The authors' AID-degron system elegantly worked in MEFs but was inefficient in preimplantation embryos. I wonder if this was because of the high expression of the shorter isoform of OGT detected as OGTp78 in the author's western blot. Is it possible to examine this possibility in the embryos? Either way, the authors should describe a potential explanation for why the efficiency in the embryos was low. In addition, the authors should describe why they inserted the AID tag only into the longest OGT isoform.
      5. In Figure S1C, is the band detected right below OGTp78 in nuclei fractions non-specific or do both bands correspond to OGTp78 ?
      6. Figure 1D top row third column: hemizgous -> hemizygous
      7. Figure 1D second row third column: hemyzygous -> hemizygous

      Significance

      General assessment: strengths and limitations

      Strength: This manuscript elegantly revealed the requirement of OGT in mammalian development by taking advantage knock-in mouse models with different OGT activity. In addition, the manuscript provided the interesting and important transcriptomics data in both pre- and post-implantation embryos of OGT mutant mice. These data sets could explain detailed mechanisms how OGT or O-GlcNAcylation regulates mammalian development in the future. Furthermore, development of AID-tagged OGT system would be a useful tool for other researchers studying OGT function.

      Limitation: Although they found interesting changes in terms transcriptomes in developing mice with different OGT activity, they lack the data showing how these changes caused the observed phenotypes. In other words, there are less mechanistic insights behind the developmental problems seen in mice with different OGT activity. In addition, although I agree the question about whether OGT activity itself is crucial for the early development of mammals has not been completely solved for a long time, I assume people thought OGT activity is actually important for the mammalian development thorough the observation of OGT-linked congenital disorders of glycosylation. Therefore, I would say the novelty of the manuscript is a little less impactful. Furthermore, although AID-tagged OGT system revealed fundamental questions regarding the transcriptional changes upon acute depletion of OGT in cellular levels, the system was inefficient in mouse embryos. So, they showed nothing about developmental-stage specific requirements of OGT.

      Advance: The manuscript can fill a current gap regarding requirement of OGT in mammalian development. Also, the manuscript developed a series of mutant mice with different OGT activity and an AID-tagged OGT mouse line. These mice provide technical advances.

      Audience: The manuscript will be interested in researchers in specific fields such as glycobiology, developmental biology, and clinical fields.

      Describe your expertise: Biochemistry, Glycobiology, Cell biology

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      Referee #3

      Evidence, reproducibility and clarity

      This is a conceptually interesting paper that attempts to leverage the knowledge of OGT catalysis to begin to dissect OGT function. The evidence is presented I a straightforward fashion and is in general well documented. The breeding strategies are well informed and the paper draws heavily on previous work carried out in the mouse.

      Significance

      The paper describes tools which will help dissect the many potential roles of O-GlcNAc addition in early development. As it stands, this is a descriptive manuscript that will lead to hypothesis generation and testing and this should not be undervalued. The biological reagents produced and characterized will be of general interest to the field. Most of the findings presented represented a verification of existing ideas in the field but this is not meant as a criticism since part of the motivation for the approach was to generate a reproducible system for analyzing the biological phenomena.

      There are perhaps some bioinformatic shortcuts taken that may need to be corrected upon thorough review. These do not lessen the overall impact of the contribution.

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      Referee #2

      Evidence, reproducibility and clarity

      Comments to authors

      To investigate the function of OGT at specific developmental stages, the authors perturbed OGT's function in vivo by creating a murine allelic series featuring four single amino acid substitutions that variably reduced OGT's catalytic activity. The goal was to identify the direct effect of O-GlcNAcylation, using a sophisticated collection of genetic mutants to evaluate in vivo the role of this modification at early stages of development. Overall, the severity of embryonic lethality correlated with the extent of catalytic impairment of OGT, demonstrating that the O-GlcNAc modification is essential for early development.<br /> The study represents a substantial advance in our understanding of OGT and O-GlcNAcylation in mammalian development. The creation of novel murine models and inducible systems is an important contribution, providing powerful tools for future research in this field. The insights into the role of OGT's catalytic activity and its involvement in epigenetic regulation during embryonic development are noteworthy, opening new avenues for research. However, there are a few considerations and concerns:

      Major:

      1. An assumption of the study is that different mutations cause different levels of O-GlcNAcylation rather than alterations in substrate specificity. It might be important to test, at least in cultured cells, that the different mutations do not change the preference of OGT to modify certain proteins rather than others, which can provide alternative explanations for their findings.
      2. In Fig 1D and 1H, the thresholds to define a gene or TE as differentially expressed are not strong. According to the figure legends, "any" change in terms of log2Fc was considered as DE and colored. I think the figures should illustrate better that the changes are subtle, by for example adding a dotted line (at least) in the value 0.5 of the y-axis. These subtle transcriptional changes should be reflected better in certain paragraphs where the expression of TEs are presented/and discussed as a hallmark of the absence of O-GlcNAcylation in the OGT-mutants. The same happens with Suppl Fig 3C (changes are very minor). Similarly, in Fig2C, the changes in gene expression are lower than log2FC 1 (which represent the double in absolute expression). Applying a stronger threshold, among the upregulated genes, only Xist will be significantly overexpressed. If a gentle threshold needs to be applied to this data, authors should at least justify the reasons behind doing so. Same for Fig2D.
      3. In Figure 2B, the T931del allele was recovered in the blastocyst population with a very high frequency, even higher than the male WT group (T931del: 10; WT: 3). This observation suggests that the T931del allele did not significantly affect blastocyst survival. Further clarification or additional experiments might be necessary to understand the implications of this finding on early developmental stages.
      4. Similarly, in Figure 2G, there is an apparent higher expression of TE expression in the T931A/Y embryos group than in the T931del/Y group, which combined with the higher frequency of blastocyst generated in this latest group it may indicate a deeper molecular consequence after the deletion of the T931. A comparison of the transcriptome between these two cell lines help to address this possibility. Also, the authors should compare the O-GlcNAc levels of WT, T931A, and T931del mutant blastocysts by immunostaining, similar to what was done in Figure S5F.
      5. In Boulard et al. 2019 O-GlcNAcylation was shown to be sufficient to modulate expression of DNA methylation-dependent TEs. It would be interesting to know (or at least discuss) if the changes in TE expression observed in OGT-mutant embryos in this study involve changes in DNA methylation. Ideally, some DNA methylation measurement optimized for low input numbers of cells would be useful.
      6. The data related with the OGT-degron system in MEs seem disconnected with the rest of the manuscript. While the developmental models (blastocyst, etc) elegantly assess the contribution of O-GlcNAcylation to the control of cell survival and gene expression through the use of different OGT mutants, the degron system is a system of graded depletion that unfortunately was only possible to be used in MEFs (instead of embryos). Thus, the results obtained with the degron system in MEFs are difficult to intersect with the data from the use of OGT-mutants in embryos. Even though there are obvious interesting questions that one may want to know about this OGT degron MEF system, none of them would demonstrate a direct role for O-GlcNAcylation in cellular function, the major point addressed in the developmental system. Using the degron system in embryonic stem cells might have provided a more parallel comparison. The authors should discuss this point in more detail and either use ESC instead of MEFs or provide a stronger justification for the use of MEFs over ESC.

      Minor:

      1. In Fig 2C the color and shape codes are confusing to understand - there are some colors/shapes that are not represented in the PCA plot. The same in Fig 3H, where in the PCA plot there are pink triangles that do not match with the code legends.
      2. In the figure legends of Figures 2D, 2E, 2F, and 2H, the notation should be corrected from "OgtT931A/Y" to "OgtT931del/Y".

      Significance

      To investigate the function of OGT at specific developmental stages, the authors perturbed OGT's function in vivo by creating a murine allelic series featuring four single amino acid substitutions that variably reduced OGT's catalytic activity. The goal was to identify the direct effect of O-GlcNAcylation, using a sophisticated collection of genetic mutants to evaluate in vivo the role of this modification at early stages of development. Overall, the severity of embryonic lethality correlated with the extent of catalytic impairment of OGT, demonstrating that the O-GlcNAc modification is essential for early development.

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      Referee #1

      Evidence, reproducibility and clarity

      Formichetti at el. developed mice with OGT catalytic dead mutations and then studied their function during early embryogenesis. Not surprisingly, dramatic reduction in OGT activity failed to produce embryos; however, mild reduction in OGT did produce animals. The authors then use the T931 animals that have a mild reduction in activity to further characterize the function in the early embryo. Not surprisingly, male mice showed changes in gene expression, implantation sub-lethality, and an uptick in loss of retrotransposon silencing. The authors also show that an even milder reduction in OGT activity (Y851A) effects male placenta function and chromatin remodeling. Finally, the authors make a less stable OGT transgene within the mouse and again found embryogenesis issues in the males and alterations in numerous gene families including mTOR signaling and p53 function. All in all, this is an interesting study that track functions of OGT in early embryonic development. The studies are well-controlled and rigorous.

      Significance

      This is a good study and novel. Not only is it of interest to reproductive biologist, but it echos themes found in O-GlcNAc biology.

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      Reply to the reviewers

      Point-to-point answer to reviewers comments

      Reviewer #1

      Evidence, reproducibility and clarity

      *Summary: *

      *The study by Cottignies-Calamarte et al. describes that AMP-activated protein kinase (AMPK) regulates cell energy balance by suppressing energy-consuming pathways like lipid and protein synthesis and promoting nutrient availability through autophagy. These pathways contribute to SARS-CoV-2 infection by hijacking autophagy and accumulating lipid droplets for viral replication. The antiviral activity of MK-8722, a direct pan-AMPK allosteric activator, was evaluated in vitro. MK-8722 effectively inhibited Alpha and Omicron SARS-CoV-2 variants in Vero76 and human bronchial epithelial Calu-3 cells at micromolar concentrations. This inhibition restored autophagic flux, degrading newly synthesized viral proteins, and reduced lipid metabolism, affecting viral factories. Additionally, MK-8722 treatment increased the type I interferon (IFN-I) response. Post-infection treatment with MK-8722 efficiently suppressed viral replication and restored the IFN-I response without altering the SARS-CoV-2-specific CD8+ T cell response elicited by Spike vaccination. The authors concluded that, MK-8722 acts as an effective antiviral against SARS-CoV-2 infection, even when applied post-exposure, suggesting potential for preclinical tests to inhibit viral replication and alleviate patient symptoms. *

      __Major comments: __

        • Are the key conclusions convincing?** Partially. See comments below! *

      - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

      From my perspective, the title "Direct pharmacological AMPK activation inhibits mucosal SARS-CoV-2 infection by reducing lipid metabolism, restoring autophagy flux and the type I IFN response" is a clear overstatement. In no way can the authors make statements about the autophagic flux, as it simply was not measured. The study would greatly benefit from conducting an autophagy/autophagic flux assay. See specific comments below!

      Answer: As suggested by the author, we have now investigated the autophagic flux by staining the cells for LC3b expression and colocalization with the lysosomal marker LAMP1. Results are shown in the new Fig4.D and E and detailed in the results section to read lines 468-475 page 23-24:

      “To assess directly the impact of MK-8722 on the autophagic flux, Calu3 cells were infected by SARS-CoV-2 without and with MK-8722 (5uM), double labelled with LC3b and LAMP1, and co-localisation of the two marker quantified (Fig.4D). MK-8722 treatment, compared with no treatment, increased LC3b colocalization in the LAMP1 compartment as shown by the increase in MOCs in treated versus non treated infected cells (LAMP1 signal in LC3b signal 0.078±0.014 vs 0.01±0.006, Mann-Whitney pand lines 480-481 page 24:

      “This result indicates that MK-8722 restores the autophagic flux to address viral components to the lysosome, where they are degraded.”

      - 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.

      See below specific comments regarding cell line consistency and autophagy measurements.

      - 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.

      This question depends on various factors such as access to relevant biosafety labs, availability of required reagents, etc. In my estimation, experiments involving WT viruses and autophagy measurements could be conducted within 3-4 months. The proposed experiments with the delta-N-SARS-CoV-2 mutants, of course, depend on access to such viruses. Overall, I believe all experiments could be completed within 6 months. The costs of those assays are not very high.

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

      In the present study, a total of 3 cell lines and human PBMCs were utilized for various experiments. Please indicate why each cellular model was chosen and highlight the differences between these models considering what is known for SARS-CoV-2 infection and autophagy! Furthermore, the study would greatly benefit if the key findings were consistently demonstrated in a single cell line.

      Answer: We agree with the reviewer that three cell lines and PBMC from patients were used but it was necessary for the experimental design of our experiments as detailed below.

      In Figures 1 and 2, experiments use both Vero76 and Calu3 cells for the following reasons. We first used the simian Vero76 cells in order to validate the inhibitory effect of MK-8722 in widely a used cell line in virology, but which lacks the interferon response. This lack of the IFN response renders Vero cells a poor model for the pathophysiology of SARS-CoV-2. We therefore then used the IFN-competent human lung Calu-3 cell line as a more relevant cell model.

      In Figures 3 both cells were again and western blots show a similar pattern of activation downstream AMPK after activation by MK-8722 and similar antiviral activity of MK-8722 in Vero76 and Calu3 cells. In Figure.4, we then mostly focused on deciphering the antiviral mechanism of MK-8722 and therefore focused on Calu3, which is more relevant from a pathophysiological point of view.

      In Figure 5, we then investigated the T-cell response and therefore used primary human, namely PBMC/purified CD8 T-cells from healthy donors. As the reviewer knows, T-cell activation is restricted by HLA-TCR interaction, or in other words, only matched HLA cells can activate CD8 T-cells. As HLA-A2 is the main HLA expressed in human and only a HLA-A2 antibody is available on the market, for these experiments we used only CD8 T cells from HLA-A2 patients and had to find an additional HLA-A2-expressing epithelial cell susceptible to SARS-CoV-2 infection. It is the case of Caco2 cells, which are HLA-A2+ susceptible to infection and competent for IFN responses. We could not use simian Vero cells that are IFN-deficient and do not express human MHC, nor Calu3 cells being HLA-A2 negative. Altogether, in experiments in Figure 5 addressing HLA-A2 restricted antigen presentation, the use of Caco-2 cells was appropriate in contrast to that of Vero or Calu3.

      Furthermore, for sake of clarification, we have now added the following p. 19 lines 390-392:

      “The trends in modification of all markers by MK-8722 treatment by being conserved between cell lines indicates a common antiviral mechanism. We therefore focused our study on Calu-3 cells since they are more relevant to SARS-CoV-2 infection.”

      The authors conclude that selective activation of AMPK has a pro-autophagic effect which in turn leads to a reduced SARS-CoV-2 replication. I would generally agree with this statement, but throughout the entire manuscript, no real autophagy assays are shown. This should definitely be rectified. It is important to demonstrate that (1) MK-8722 is capable of increasing autophagy and particularly autophagic flux in the cell models used, (2) that in the cell models employed, SARS-CoV-2 infection leads to modulation of autophagy, and (3) that SARS-CoV-2 infected cells, when co-treated with MK-8722, lead to a re-established autophagy. The autophagy assays should be performed according to the expert-curated guidelines by Klionsky et al. This is extremely important so that the results can be compared with the now vast number of existing autophagy-SARS-CoV-2 studies.

      We fully agree with the reviewer that it was important for our study to formally address the impact of MK-8722 on the autophagic flux. Following reviewer recommendation and reading of the guidelines for autophagy study, we therefore have evaluated whether MK-8722 affected localization of LC3b, which is essential for autophagosome biogenesis/maturation and also functions as an adaptor protein for selective autophagy, in lysosomal compartment (labelled, by LAMP1). Therefore we labelled cells infected in the presence or absence of MK-8722 for LC3b expression and colocalization with the lysosomal marker LAMP1. Results are shown in the new Fig4.D, E. Please see our above answer (p1) for results description. These results indicate that MK-8722 restored the autophagic flux that had been interrupted by SARS-CoV-2 infection in Calu3 cells.

      - Are the experiments adequately replicated and statistical analysis adequate?

      Minor comments:

      - Specific experimental issues that are easily addressable.

      Typo: Line 288: It should be "MK-8722" instead of "MK-7288".

      In general, a space between value and unit is not consistently used.

      Please indicate always the phosphosite of substrate proteins when phosphorylation is described. E.g. line 288 and throughout the manuscript: regarding ACC phosphorylation.

      Answer: We apologize for these typos, which have now been corrected in the revised MS.

      • Are prior studies referenced appropriately?

      See comment below. Fundmental work that describes the virus-autophagy relationship, such as the work by the Beth Levine lab would be important to add. Also the work bei Konstantin Sparrer and colleagues is important and leads to the current work presented here.

      Answer: Konstantin Sparrer’s work is already cited as by ref 17. However, as suggested by the reviewer, the work by the Beth Livine lab has now been added in the revised MS in p29-30 lines 610-613, to read:

      .“Convergence of Beclin-Atg14 and P62 activation could stimulated the selective clearance of viral components, in a process called virophagy64–66. We thus propose that AMPK pharmacological activation induce virophagy and is responsible, at least partially, for its antiviral effect.”

      - Are the text and figures clear and accurate?

      Introduction: In general, for some of the statements claimed in the introduction, which is in sum nicely written, informative and well structured, citations are required. For example - line 59 "...autophagy is sequentially activated and inhibited."

      Answer: Citation has been added, namely: Koepke 2021 Autophagy ref 17

      Lines 59-65. In the introduction, the interaction between autophagy and SARS-CoV-2 is primarily described in a one-sided manner. There are now several studies demonstrating that both inhibition of autophagy and also induction of autophagy in context of coronaviral infection. Both aspects should be illuminated and introduced here.

      Answer: The reviewer points towards a crucial point of autophagy during ß-coronaviruses infection. Indeed, we fully agree that the autophagy is both inhibited and activated, at different levels, by different proteins as exemplified by, Sparrer’s group (ref 17). As we have mentioned in the initial version of our MS: “Throughout the SARS-CoV-2 viral cycle, autophagy is sequentially activated and inhibited 17–20”. As it may have not been clear enough, we have reformulated this paragraph as follows to read line 68-75 p5:

      “Throughout the SARS-CoV-2 viral cycle, autophagy is sequentially activated and inhibited 17–20. Indeed, autophagy is initiated by the early expressed nsp6, resulting in the formation of autophagosomes that are essential for the establishment of viral factories 17,21 and subsequent viral proteins expression 17,21. In turn, viral proteins OFR3a and ORF7a expressed at a latter time post-infection, prevent the fusion between autophagosomes and lysosomes, thereby blocking completion of autophagy, as evidenced by increased LC3-B expression, activation of the ULK1 kinase and increase in the autophagy cargo receptor sequestosome-1/p62. Overall, this disruption of autophagy protects newly formed virus from degradation in the LAMP1+ lysosome 19,22–25”

      Discussion: The selectivity of the compound should be discussed.

      Answer: Manuscript have been revised as follows to discuss both specificity in regards of AMPK and tissue accessibility:

      • lines 557-560, p27: “We show here that the blockade of AMPK activation upon infection can be reversed by MK-8722, the pharmacological allosteric pan-activator of AMPK, which blocks infection at a µM concentration, in agreement with the predicted role of AMPK activity on SARS-CoV-2 infection48 and with MK-8722 action on infection by other viruses49”

      • Line 576-581, p28: “In contrast, MK-8722, as systemic drug, may reach these tissues with minimal side effects, as a daily treatment in diabetic Non-human primates (NHPs) with MK-8722 (10 mg/kg) for a month induced only a limited and reversible cardiac hypertrophy 36”

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

      The presentation of the data is understandable. For reader with a less mechanistic background it would be helpful to present a schematic figure like a graphical abstract.

      Answer: As suggested by the reviewer, we have now introduced a graphical abstract in the revised MS.

      SECTION B – Significance

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

      • Even though there is now a plethora of studies on autophagy and SARS-CoV-2, this study is important and of great interest to a broad readership. Not only virologists, immunologists, and autophagy researchers will eagerly anticipate this study, but especially researchers focusing on pharmacology around AMPK and autophagy will recognize the importance of the data presented here.*

      Answer: We thank the reviewer for this positive appreciation of our work.

      - Place the work in the context of the existing literature (provide references, where appropriate).

      The work builds upon a variety of studies on the interplay between coronaviruses and the mechanism of autophagy. Foundational contributions to this research stem from groundbreaking preliminary work conducted in the laboratories of Gassen and Müller (Gassen et al. 2019 and Gassen et al. 2021), as well as general virus-autophagy studies from the laboratory of Beth Levine. Additionally, recent work by Konstantin Sparrer and colleagues would be important to cite, as it underscores the insights gained in this manuscript.

      Answer: As suggested and previously mentioned, these references have now been added to the discussion p27 lines 557-560: “We show here that the blockade of AMPK activation upon infection can be reversed by MK-8722, the pharmacological allosteric pan-activator of AMPK, which blocks infection at a µM concentration, in agreement with the predicted role of AMPK activity on SARS-CoV-2 infection48 and with MK-8722 action on infection by other viruses49”.

      In addition, Gassen et al. 2019 is already cited as ref 18

      - State what audience might be interested in and influenced by the reported findings. See comment above!__ __

      Reviewer #2

      Evidence, reproducibility and clarity

      In the current manuscript, Cottignes-Calamarte et al. have shown tha pharmacological activation of AMPK can be a strategy for overcoming SARS-CoV-2 infection induced reprogramming of host degradation pathways and innate immune response, without hindering the efficacy of spike expression from vaccine agents. Though the suggestion of selective activity of MK-8722 in degrading viral proteins in infection but not the ectopic spike peptides expression is interesting, the evaluation of the mechanism and providing therapeutic index for the drug will overall improve the study.

      • Majorly, I have these suggestions;*

        • The manuscript did not clarify the mechanism clearly but correlated the reduction in viral proteins and their association to LAMP1 as the mechanisim of activity of MK-8722. In this way, the authors did not separate whether the reduction in SARS-CoV-2 infection could lead to the potentiation of these effects. There is mentioning of potential mechanism of the drug by inhibiting the activity of SARS-CoV-2 proteins that reduce the autophagic flux without directly showing this. SARS-CoV-2 Orf3a is a known inhibitor of autophagosome maturation and hence the authors should directly probe the activity of MK-8722 in overcoming the suppression of autophagic flux in cells by ectopically expressing Orf3a.* Answer: We fully agree with the reviewer that our work correlated the reduction in viral proteins and their association to LAMP1 to explain the mechanism of MK-8722 activity and did not focus on particular viral protein(s) that could induced autophagic flux.

      Indeed, our approach has been to describe the MK-8722 antiviral activity against full primary SARS-CoV-2 viruses (not ectopically expressed viral proteins or recombinant viruses) in a pathologically relevant cell model including primary CD8+ T cells to mimic at best the initial steps of SARS-CoV-2 infection. Although the ectopical expression of Orf3a is recognized as a potent tool to study the principle of autophagy in the guidelines of autophagy measurement methods, when applied to infection, this ectopical expression of Orf3a will modify the endogenous level of Orf3a (as compared to infection level) and probably affect by itself the autophagy kinetics. To address the question of autophagic flux as suggested by the reviewer, we therefore preferred to use another recommended technique from the guidelines of autophagy measurement methods directly applicable to infected cells. We now evaluated the colocalization of LC3b with LAMP1 during treatment and infection of Calu-3 cells by primary viruses as now described in figure 4.D and E and discussed lines 468-475 pages 23-24 :

      “To assess directly the impact of MK-8722 on the autophagic flux, Calu3 cells were infected by SARS-CoV-2 without and with MK-8722 (5uM), double labelled with LC3b and LAMP1, and co-localisation of the two marker quantified (Fig.4D, E). MK-8722 treatment, compared with no treatment, increased LC3b colocalization in the LAMP1 compartment as shown by the increase in MOCs in treated versus non treated infected cells (LAMP1 signal in LC3b signal 0.078±0.014 vs 0.01±0.006, Mann-Whitney p * As the authors propose MK-8722 as a preclinical candidate, they should present therapeutic measures and indexes. All across the data presented, there was no mentioning or measurement of drug toxicity for extended uses up to 36h pi.*

      Answer: Our study aimed to describe the antiviral activity of MK-8722 in a cellular model mimicking only the initial steps of infection up to 3 dpi. Complementary experiments were conducted as required and show that treatment with MK-8722 up to 10mM did not result in an increase in cell death at any time post treatment as shown in the new Fig S2I and corresponding description in line 328-332 p17, which read__: __

      __“__Furthermore, we also investigated MK-8722 toxicity at 4h, 24h and 96h (Fig. S2I) and found that the drug was not toxic up to 10mM. The 50% toxicity dose was calculated to be 57mM at 96h in Calu3 cells. This allows us to determine a therapeutic index of 76 against the SARS-CoV-2 Alpha variant and 36 against the Omicron variant, thus, placing MK-8722 as an attractive antiviral candidate.”

      • Also, it was not clarified if the drug reduced the replication or exclusively worked by restoration of autophagic flux. For the earlier, the authors can consider two assays, i.e., a direct assay of looking into the replicon of SARS-CoV-2 (Bigotti et al 2024; PMID 38387750), or looking at earlier time points of infection (up to 8h pi; Twu et al. 2021; PMID 34788596) with intracellular sgRNA specific RNA probes.In this regards, 24h or 32h (Fig 1F-G) is too long to only measure single-round of infection.*

      Answer: We thank the reviewer for this interesting question. The drug likely acts on both steps. Concerning replication, as shown in figure 1 GH at 24 and 32hrs, there is a block in replication but not in virus entry into the cell, since there is no difference in viral N cellular content after 1hr chase. Concerning the autophagic flux, the new Fig4 D and E shows that MK-8722 restores the autophagic flux in infected cells, which had been interrupted by the infection in the absence of the drug.

      The viral cycle of ß-coronaviruses is highly dependent on hijacking cellular autophagy and lipid biosynthesis, which are both necessary for the assembly of DMV, essential for viral replication. Since MK-8722 treatment reduces cellular lipid content and increases autophagic flux, the use of viral replicons deficient in structural proteins or early post-infection timepoints will most likely show a decrease in viral genome replication under the effect of MK-8722 due to the inability of the replicons to establish such favourable environments (indicated in the corresponding Fig3A, B and C). However, the effect of MK-8722 on the replicon system will not distinguish between whether MK-8722 affects the viral replication complex and whether it is unable to induce viral factory formation.

      • Are the viral components degraded by restored lysosomal activity include replicase or replication organelle components? This needs to be shown with intracellular nsp3/nsp4 levels in infection or ectopic expression.*

      Answer: The reviewer raises a question highly relevant to the biology of coronaviruses, which we have addressed in Figure 4. Indeed, the Replication-Transcription Complex (RTC) is a multifactorial complex, in which N protein bound to the viral RNA is believed to help recruiting RdRp (Cong 2020 J Virol 10.1128/jvi.01925-19, Scherer 2022 Sci Adv DOI: 10.1126/sciadv.abl4895). The increased colocalisation of in N staining in LAMP-1+ compartments observed after MK-8722 treatment indicates that MK-8722 addresses RTC to the lysosomes and therefore our results indicate that replication-transcription organelles could be degraded in lysosomes.

      • Previous studies suggested the decrease in AMPK phospharhorylation in SARS-CoV-2 infection What is inconsistent to previous studies should be commented by the authors. Eg, why is AMPK suppression not see in SARS-CoV- 2 inefction as reported before (Parthasarathy et al 2023; PMID 36417940)*

      Answer: We agree with the reviewer and had already mentioned in the discussion that SARS-CoV-2 infection can have different outcome on AMPK activation as reported in ref 45 and 46 in the original version. Indeed, Gassen and colleagues reports that activation of AMPK and resulting phosphorylation are decreased in cells infected by SARS-CoV-2, as shown in (Ref 18), whereas Parthasarathy reports an increase in AMPK phosphorylation which is clear only at 96 h p.i. (Ref 47). Interestingly in this later study at earlier time point (24hr p.i.), authors report a tendency of AMPK phosphorylation to decrease although not in a statistically significant manner but for only n=3. In our present study, no statistically significant differences were found in AMPK phosphorylation although a small increase tendency is observed. Furthermore, cells used in all these studies differ: Gassen et al. used Vero-FM cells whereas Parthasarathy et al. used intestinal Caco2 cells, and in our study Vero 76 and lung Calu3 cells. Thus the differences reported on the effect of SARS-CoV-2 infection on AMPK activation are likely due to a question of kinetics and/or cellular background. Of note, the level of AMPK phosphorylation observed after SARS-CoV-2 infection is not to compare with the AMPK phosphoryalton induced by drug activation such as MK-8722.

      This heterogenity in AMPK activation during SARS-CoV-2 infection might contribute to the various effect of AMPK activator as antiviral reported in the literature. Indeed, as mentioned p27 lines 560-563 “metformin, a drug approved by FDA since 1994, and the adenosine analogue AICAR that activates AMPK indirectly can inhibit replication of SARS-CoV-2 as well as Flaviviruses, but at a concentrations of 10 and 1 mM, respectively 35,47 ”. The reported discrepancy on the antiviral effect of AMPK activation might rely then on an activation threshold, as 10mM metformin and 1mM AICAR blocks infection, while 25__m__M AICAR does not (ref 18, 47). This later concentration was not evaluated in Gassen et al. on AMPK activation. Furthermore; the time frame evaluated in each study is different and could also be a confusing factor. Finally, as shown by Myers and colleagues (Myers 2017, Science ref 36), MK-8722 activates AMPK more efficiently than AICAR, most probably due to its direct activation of AMPK. We believe that direct AMPK activation by MK-8722 and the higher activation level of AMPK is responsible for the antiviral effect reported in our study.

      As suggested by the reviewer, we have now clarified this section in the revised MS to read p27-28, lines 557-568:

      “We show here that the blockade of AMPK activation upon infection can be reversed by MK-8722, the pharmacological allosteric pan-activator of AMPK, which, at a µM concentration, blocks infection, in agreement with the predicted role of AMPK activity on SARS-CoV-2 infection48 and with MK-8722 action on infection by other viruses49” .In line, metformin, a drug approved by FDA since 1994, and the adenosine analogue AICAR that activates AMPK indirectly can inhibit replication of SARS-CoV-2 as well as Flaviviruses, but at concentrations of 10 and 1 mM, respectively 35,47. These AMPK-sensitive viruses replicate all in viral factories, disturbing lipid synthesis and escaping autophagy 50,51. AMPK activation by metformin at high concentration (10mM) inhibits SARS-CoV-2 replication in vitro 47. However, AMPK activation with 5-amino-imidazolecarboxamide riboside (AICAR), a non-metabolised analogue of AMP able to activate AMPK, used at 25mM is unable to inhibit SARS-CoV-2 infection 18 while at 1mM has been proven to reduce by 10-fold viral production 47, suggesting that AMPK needs to reach an activation threshold to inhibit viral replication. “

      • *

      • Although AMPK activation is shown to be antiviral for SARS-CoV-2 before, e.g., with Metformin (Parthasarathy et al 2023; PMID 36417940), the role of AMPK-related kinases are shown to be pro-viral (e.g., NUAK2; Prasad et al. 2023; PMID 37421942). The authors should discuss these points to provide the reader a context in this sub-field.*

      Answer: As suggested by the reviewer, we have now included in the discussion the following p28 lines 568-571:

      “Conversely, NUAK2, an AMPK-related kinase, was reported to stimulate viral replication in A549 and Calu3 cells50. Altogether our results, in agreement with the literature, indicate that AMPK-dependent antiviral activity is restricted to AMPK-members only, confirming their distance with AMPK-related kinases such as NUAK2 53”

      Minor

        • Was there an increase of lipid droplets in SARS-CoV-2 infected cells to non-infected condition? It is not mentioned here.* Answer: Yes indeed, lipid droplets content was increased in Infected non treated cells as indicated in Figure Suppl. 4B (p21 lines 409-411) and as stated in the Result section as follows:

      ” Infection increased the overall Nile Red staining by 40±10% compared to non-infected cells (Fig. S4B, ANOVA: p * There are several typos and grammatical errors.*

      Answer: We have now carefully checked the text for typographical and grammatical errors, which have been corrected.

      There is no Fig S2I but is mentioend in the legend.

      Answer: We apologize for this mistake in labelling figure S2 panel and have corrected their labelling as follows:

      “____G-H: __ACE2 expression and viability were evaluated in Vero76 cells after 24h or in Calu-3 cells after 4days of MK-8722 continuous treatment (1 µM or 5 µM respectively) by flow cytometry. ACE2 expression is expressed as MFI (__G) and viability as frequency of cells non-stained by the amine-reactive dye Viobility (H). n=3 independent experiments. “

      • Fig 4A - degradation is not shown, only association.*

      Answer: We agree with the reviewer and have modified the text accordingly to read p37 lines 873-874:

      Figure 4: MK-8722 treatment increases the ____autophagic flux directing viral components ____to ____lysosomes and restores type I interferon response.”


      • Line 333 - there is no 3d pi post exposure treatment with MK-8722 in Fig 1l.*

      Answer: We meant that treatment initiated at 1dpi lasted until harvest at 3dpi. This is clarified now to read, p18 line 351

      “Post-exposure treatment at 1dpi and until harvest at 3dpi, …”

      Significance

      General assessment*: *

      Strengths and limitations: The study provides evidence supporting previous results that the activation AMPK can be harnessed as a strategy to combat SARS-CoV2- infection. Whereas the results suggesting that this is targeted in infection by restoration of autopahgic flux and hence is selective is interesting, but the authors did not directly investigated the SARS-CoV-2 protein that is implicated in this effect. The study also does not discuss the context of AMPK and related kinases in discussion.*

      *

      Advance -* The study makes a pre-clinical advance, and has potential to make it fundamentally or conceptually sound. *

      Audience - Virologists and Clinicians.

      Expertise - SARS-CoV-2 infection biology, Cell biology an Molecular virology__ __

      __Reviewer #3 __

      Evidence, reproducibility and clarity (Required):

      • Summary.** The authors address a topic of great importance to the development of antivirals, particularly in light of the possibility of future pandemics due to hitherto understudied viruses: the evaluation of interfering with host pathways (host-directed antivirals), potentially leading to compounds that can be used against a broad spectrum of viruses which require the same host cell functions for their life cycle. The authors studied the effects of activating AMPK with a small molecule (MK-8722) on various aspects of infectivity of SARS-CoV-2. They find that the compound indeed markedly reduced viral infectivity in two cell lines (Vero and Calu3), which correlated with the ability of the compound to activate signaling downstream of AMPK and was associated with increased lysosomal genesis/function and reduced density of "lipid viral factories". *

      • *

      General assessment. The study provides important proof of concept in reductionist cellular models, which may lead to pharmacologically more conclusive in vivo studies later on. It is limited by the use of cell lines, instead of primary human cells, for viral infectivity. The caption "MK-8722 restores the IFN I pathway" is an overstatement, as the observed increase in ISG expression is quite modest.

      Answer: We agree with the reviewer that we did not use primary cells in our study, which was designed to evaluate the antiviral activity of MK-8722 in a simple epithelial cell model still relevant for the pathophysiology. However, we believe that MK-8722 antiviral effect we observed in the present study will be conserved using primary cells given the breadth of cell lines we used such as Vero, pulmonary Calu-3 and intestinal Caco2 cells. Furthermore, concerning the magnitude of the IFN I response we report, we remind the reviewer that Calu-3 cells are infected with an MOI of 0.05, which does not result in 100% cells infected after 24h. Consequently, the IFN-I response as limited to the sole infected cells in a limited amount in this setup and thus, bulk RT-qPCR of Type I IFN and targeted ISG mRNA is expected to remain modest.

      In future studies, as suggested by the reviewer, we plan to include few ALI culture treated primary cells. We have clarified this limitation of our study in the Discussion p. 31 line 636-638 to read:

      “The antiviral effect of AMPK activation in primary lung reconstruction and preclinical models such as hamster remains to be tested.”

      __ Significance (Required): __

      Taken as an early proof-of-concept study, the findings are quite important to investigators aiming to develop host-directed antivirals. However, the overall interest and impact of the manuscript would greatly benefit from verifying key findings in a primary cell model. Also, checking at least one other viral species (the authors mention flaviviruses) would be helpful to test how broadly applicable the current compound (or others to be developed in the future) would be as host-directed antivirals.

      Answer: We thank the reviewer for the positive evaluation of our work. We fully agree with the reviewer in that preparedness is the key to fighting future pandemics. However to our knowledge, the literature about Flaviviruses is already stating that AMPK activation by metformin is an antiviral strategy with regards to its lipid metabolism normalization and autophagy activation (Farfan-Morales 2021 Sci Rep doi: 10.1038/s41598-021-87707-9. Ref 50). Furthermore in a previous review, we discussed the role of AMPK activation on viral infection that could be either pro- or antiviral depending on the viral family and even within a viral family such as HSV-1 which first inhibits AMPK in early infection while activating AMPK in the latter stage (Moreira, D. et al. Curr Drug Targets 17, 942–953 (2016), ref 34). Hence, adding more viruses to our study will not add novelty to the study, even though the molecule is much stronger compared to metformin.

      • *
    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. The authors address a topic of great importance to the development of antivirals, particularly in light of the possibility of future pandemics due to hitherto understudied viruses: the evaluation of interfering with host pathways (host-directed antivirals), potentially leading to compounds that can be used against a broad spectrum of viruses which require the same host cell functions for their life cycle. The authors studied the effects of activating AMPK with a small molecule (MK-8722) on various aspects of infectivity of SARS-CoV-2. They find that the compound indeed markedly reduced viral infectivity in two cell lines (Vero and Calu3), which correlated with the ability of the compound to activate signaling downstream of AMPK and was associated with increased lysosomal genesis/function and reduced density of "lipid viral factories".

      General assessment. The study provides important proof of concept in reductionist cellular models, which may lead to pharmacologically more conclusive in vivo studies later on. It is limited by the use of cell lines, instead of primary human cells, for viral infectivity. The caption "MK-8722 restores the IFN I pathway" is an overstatement, as the observed increase in ISG expression is quite modest.

      Significance

      Taken as an early proof-of-concept study, the findings are quite important to investigators aiming to develop host-directed antivirals. However, the overall interest and impact of the manuscript would greatly benefit from verifying key findings in a primary cell model. Also, checking at least one other viral species (the authors mention flaviviruses) would be helpful to test how broadly applicable the current compound (or others to be developed in the future) would be as host-directed antivirals.

    3. 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, Cottignes-Calamarte et al. have shown tha pharmacological activation of AMPK can be a strategy for overcoming SARS-CoV-2 infection induced reprogramming of host degradation pathways and innate immune response, without hindering the efficacy of spike expression from vaccine agents. Though the suggestion of selective activity of MK-8722 in degrading viral proteins in infection but not the ectopic spike peptides expression is interesting, the evaluation of the mechanism and providing therapeutic index for the drug will overall improve the study.

      Majorly, I have these suggestions;

      1. The manuscript did not clarify the mechanism clearly but correlated the reduction in viral proteins and their association to LAMP1 as the mechanisim of activity of MK-8722. In this way, the authors did not separate whether the reduction in SARS-CoV-2 infection could lead to the potentiation of these effects. There is mentioning of potential mechanism of the drug by inhibiting the activity of SARS-CoV-2 proteins that reduce the autophagic flux without directly showing this. SARS-CoV-2 Orf3a is a known inhibitor of autophagosome maturation and hence the authors should directly probe the activity of MK-8722 in overcoming the suppression of autophagic flux in cells by ectopically expressing Orf3a.
      2. As the authors propose MK-8722 as a preclinical candidate, they should present therapeutic measures and indexes. All across the data presented, there was no mentioning or measurement of drug toxicity for extended uses up to 36h pi.
      3. Also, it was not clarified if the drug reduced the replication or exclusively worked by restoration of autophagic flux. For the earlier, the authors can consider two assays, i.e., a direct assay of looking into the replicon of SARS-CoV-2 (Bigotti et al 2024; PMID 38387750), or looking at earlier time points of infection (up to 8h pi; Twu et al. 2021; PMID 34788596) with intracellular sgRNA specific RNA probes.In this regards, 24h or 32h (Fig 1F-G) is too long to only measure single-round of infection.
      4. Are the viral components degraded by restored lysosomal activity include replicase or replication organelle components? This needs to be shown with intracellular nsp3/nsp4 levels in infection or ectopic expression.
      5. Previous studies suggested the decrease in AMPK phospharhorylation in SARS-CoV-2 infection What is inconsistent to previous studies should be commented by the authors. Eg, why is AMPK suppression not see in SARS-CoV- 2 inefction as reported before (Parthasarathy et al 2023; PMID 36417940)
      6. Although AMPK activation is shown to be antiviral for SARS-CoV-2 before, e.g., with Metformin (Parthasarathy et al 2023; PMID 36417940), the role of AMPK-related kinases are shown to be pro-viral (e.g., NUAK2; Prasad et al. 2023; PMID 37421942). The authors should discuss these points to provide the reader a context in this sub-field.

      Minor

      1. Was there an increase of lipid droplets in SARS-CoV-2 infected cells to non-infected condition? It is not mentioned here.
      2. There are several typos and grammatical errors.
      3. There is no Fig S2I but is mentioend in the legend.
      4. Fig 4A - degradation is not shown, only association.
      5. Line 333 - there is no 3d pi post exposure treatment with MK-8722 in Fig 1l.

      Significance

      General assessment

      Strengths and limitations: The study provides evidence supporting previous results that the activation AMPK can be harnessed as a strategy to combat SARS-CoV2- infection. Whereas the results suggesting that this is targeted in infection by restoration of autopahgic flux and hence is selective is interesting, but the authors did not directly investigated the SARS-CoV-2 protein that is implicated in this effect. The study also does not discuss the context of AMPK and related kinases in discussion.

      Advance - The study makes a pre-clinical advance, and has potential to make it fundamentally or conceptually sound.

      Audience - Virologists and Clinicians.

      Expertise - SARS-CoV-2 infection biology, Cell biology an Molecular virology

    4. 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:

      Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

      The study by Cottignies-Calamarte et al. describes that AMP-activated protein kinase (AMPK) regulates cell energy balance by suppressing energy-consuming pathways like lipid and protein synthesis and promoting nutrient availability through autophagy. These pathways contribute to SARS-CoV-2 infection by hijacking autophagy and accumulating lipid droplets for viral replication. The antiviral activity of MK-8722, a direct pan-AMPK allosteric activator, was evaluated in vitro. MK-8722 effectively inhibited Alpha and Omicron SARS-CoV-2 variants in Vero76 and human bronchial epithelial Calu-3 cells at micromolar concentrations. This inhibition restored autophagic flux, degrading newly synthesized viral proteins, and reduced lipid metabolism, affecting viral factories. Additionally, MK-8722 treatment increased the type I interferon (IFN-I) response. Post-infection treatment with MK-8722 efficiently suppressed viral replication and restored the IFN-I response without altering the SARS-CoV-2-specific CD8+ T cell response elicited by Spike vaccination. The authors concluded that, MK-8722 acts as an effective antiviral against SARS-CoV-2 infection, even when applied post-exposure, suggesting potential for preclinical tests to inhibit viral replication and alleviate patient symptoms.

      Major comments:

      • Are the key conclusions convincing?

      Partially. See comments below! - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

      From my perspective, the title "Direct pharmacological AMPK activation inhibits mucosal SARS-CoV-2 infection by reducing lipid metabolism, restoring autophagy flux and the type I IFN response" is a clear overstatement. In no way can the authors make statements about the autophagic flux, as it simply was not measured. The study would greatly benefit from conducting an autophagy/autophagic flux assay. See specific comments below! - 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.

      See below specific comments regarding cell line consistency and autophagy measurements. - 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.

      This question depends on various factors such as access to relevant biosafety labs, availability of required reagents, etc. In my estimation, experiments involving WT viruses and autophagy measurements could be conducted within 3-4 months. The proposed experiments with the delta-N-SARS-CoV-2 mutants, of course, depend on access to such viruses. Overall, I believe all experiments could be completed within 6 months. The costs of those assays are not very high. - Are the data and the methods presented in such a way that they can be reproduced?

      In the present study, a total of 3 cell lines and human PBMCs were utilized for various experiments. Please indicate why each cellular model was chosen and highlight the differences between these models considering what is known for SARS-CoV-2 infection and autophagy! Furthermore, the study would greatly benefit if the key findings were consistently demonstrated in a single cell line.

      The authors conclude that selective activation of AMPK has a pro-autophagic effect which in turn leads to a reduced SARS-CoV-2 replication. I would generally agree with this statement, but throughout the entire manuscript, no real autophagy assays are shown. This should definitely be rectified. It is important to demonstrate that (1) MK-8722 is capable of increasing autophagy and particularly autophagic flux in the cell models used, (2) that in the cell models employed, SARS-CoV-2 infection leads to modulation of autophagy, and (3) that SARS-CoV-2 infected cells, when co-treated with MK-8722, lead to a re-established autophagy. The autophagy assays should be performed according to the expert-curated guidelines by Klionsky et al. This is extremely important so that the results can be compared with the now vast number of existing autophagy-SARS-CoV-2 studies. - Are the experiments adequately replicated and statistical analysis adequate?

      Minor comments: - Specific experimental issues that are easily addressable.

      Typo: Line 288: It should be "MK-8722" instead of "MK-7288". In general, a space between value and unit is not consistently used. Please indicate always the phosphosite of substrate proteins when phosphorylation is described. E.g. line 288 and throughout the manuscript: regarding ACC phosphorylation. - Are prior studies referenced appropriately?

      See comment below. Fundmental work that describes the virus-autophagy relationship, such as the work by the Beth Levine lab would be important to add. Also the work bei Konstantin Sparrer and colleagues is important and leads to the current work presented here. - Are the text and figures clear and accurate?

      Introduction:

      In general, for some of the statements claimed in the introduction, which is in sum nicely written, informative and well structured, citations are required. For example - line 59 "...autophagy is sequentially activated and inhibited." Lines 59-65. In the introduction, the interaction between autophagy and SARS-CoV-2 is primarily described in a one-sided manner. There are now several studies demonstrating that both inhibition of autophagy and also induction of autophagy in context of coronaviral infection. Both aspects should be illuminated and introduced here.

      Discussion: The selectivity of the compound should be discussed. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

      The presentation of the data is understandable. For reader with a less mechanistic background it would be helpful to present a schematic figure like a graphical abstract.

      Significance

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

      Even though there is now a plethora of studies on autophagy and SARS-CoV-2, this study is important and of great interest to a broad readership. Not only virologists, immunologists, and autophagy researchers will eagerly anticipate this study, but especially researchers focusing on pharmacology around AMPK and autophagy will recognize the importance of the data presented here. - Place the work in the context of the existing literature (provide references, where appropriate).

      The work builds upon a variety of studies on the interplay between coronaviruses and the mechanism of autophagy. Foundational contributions to this research stem from groundbreaking preliminary work conducted in the laboratories of Gassen and Müller (Gassen et al. 2019 and Gassen et al. 2021), as well as general virus-autophagy studies from the laboratory of Beth Levine. Additionally, recent work by Konstantin Sparrer and colleagues would be important to cite, as it underscores the insights gained in this manuscript. - State what audience might be interested in and influenced by the reported findings.

      See comment above! - 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.

      My expertise is limited to the mechanistic aspects of autophagy, metabolism, and signaling cascades related to autophagy and endosomal-exosomal mechanisms. In some studies, I have been able to investigate the interplay between CoV and autophagy in collaborations with coronavirus experts. I can only provide a superficial assessment of the purely virological (methodological) aspects of the present study.

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      Reply to the reviewers

      Answers to reviewers


      Reviewer #1

      Sagia et al. present a manuscript using A. nidulans as model to study different transport routes of membrane proteins from the ER to the plasma membrane. They showed in earlier work that apparently at least two different transport routes exist, one involving the classical ER-ERES-ERGIC-Golgi route, one bypassing the Golgi. Unpolarized membrane proteins use the former, apically sorted membrane proteins the latter route. The study here confirms their earlier findings, uses a better model (co-expression of representatives for both routes in the same cell) and provides additional mechanistic insights about the roles of rabs, SNARES and other important proteins of the secretory pathway. The study is thoroughly done, figures are of high quality, data and methods well described and adequately replicated.

      Thank you for your positive comments

      I do have, however, a number of comments that could help to improve the manuscript.

      -I suggest using the term polarized or apical rather than polar. Polar alone to me refers more to physico-chemical properties like water-solubility.

      Amended in most parts of the revised text.

      -introduction and discussion: I don’t think the literature about unconventional secretion bypassing the Golgi is complete, for example studies about TMED10 like Zhang, M. et al. Cell 181, 637-652 e615 (2020) or Zhang et al. Elife 4 (2015) are missing, there might be others. Is UapA a leader-less cargo that could be inserted via TMED10 translocation?

      Thank you for letting us know, we have missed these articles. More references on UPS are now added, including the Zhang et all publications. UapA, as all transporters, is a multispan transmembrane protein with no leader peptide. In fact, we have checked the role of p24 family proteins (homologous to TMED10) in UapA trafficking. The knock-out of key p24 proteins does not affect UapA sorting to the PM (please consider this as confidential unpublished results)

      -Fig. 1C. Can these intracellular structures be characterized in more detail?

      As explained briefly to the handling editor above, and following the reviewer’s suggestion, we performed new experiments to better characterize the identity of the cargo-labeled fluorescent puncta. To do so, we used co-expression of a standard ERES marker, Sec16, in cells expressing either UapA or SynA, tagged with different fluorescent tags. More specifically, we constructed and analyzed strains co-expressing UapA-GFP/Sec16-mCherry or GFP-SynA/mCherry-Sec16 in the sec31ts genetic background, which allows synchronization and better analysis of ER exit, as described in our text. The new findings appear as Figure 5C __in the revised manuscript. Notice that sec16-mCherry introduced in the native sec16 locus by standard knock-in reverse genetics of A. nidulans (see Materials and methods) does not affect Aspergillus growth or secretion. Experiments depicted in __5C show that both cargoes, UapA and SynA, co-localize significantly (PCC ≈ 0.6), with Sec16, suggesting that most of these puncta are indeed ERES structures. Given that the puncta marked with UapA or SynA are clearly distinct (see Figures 1C,2A, 3A, 5B), this new experiment strongly suggests that there are indeed two distinct ERES, one populated mostly by UapA and the other by SynA. Notice, as we already outline in our response to the editor above, a three-colored approach using Sec16-BFP (or Sec13-BFP) for showing directly the existence of these two populations of cargo-specific ERES in the same cell failed as the BFP signal was problematic for colocalization studies.

      Where is the Golgi localized in A. nidulans, is it decentralized like in yeast?

      Yes, as in S. cerevisiae, A. nidulans Golgi cisternae are individually scattered throughout the cytoplasm, also similarly to other filamentous fungi. Notice that in A. nidulans Golgi structures are moderately polarized (Pantazopoulou and Penalva 2009).

      Is the UapA at the time points shown in Fig. 1C in some sub-PM structures? To me the distribution at or near the PM is more punctate than in the steady state image shown in 1B

      The punctuate appearance of PM transporters at the periphery of fungal cells is a common theme when these do not reach high, steady-state, levels of accumulation. In fact, several transporters mark specific subdomains of the PM, more evident before achieving their steady-state levels. For example, in yeast several amino acid and nucleobase transporters mark punctuate structures that colocalize with eisosomes markers (caveolin-like PM subdomains), while the proton pump ATPase Pma1 marks distinct punctuate domains. Similarly, UapA and other solute transporters mark punctuate structures before reaching their state-state accumulation in the PM. Figure 1C shows the de novo synthesis of cargoes after 100 min of transcription, while Figure 1B depicts the steady-state localization of UapA and SynA after 4h. In the latter case, the PM is ‘saturated’ with UapA molecules and thus the fluorescent signal of distinct puncta ‘fuses’, creating continuous fluorescent labeling. Notice also that in several cases, in our work, we have also performed UapA transport assays, which provide a direct tool to test and confirm the presence of UapA in the PM (see Figures 4D or 6C).

      -Fig. 3A. To me it looks like there is actually a lot of colocalization of UapA and SynA, especially at or near the PM, where there is quite some white, punctate staining. The green fluorescence is just much stronger, overlaying the violet. Can you show separate channels and explain?

      We think the reviewer means Figure 2A, which compares UapA and SynA (Figure 3A compares UapA with Golgi markers). If so, we have quantitatively estimated and performed statistical analysis (PCC) which indicates that this, visually apparent colocalization, is not significant (right panel in Figure 2A). Notice also that we cannot totally exclude very minimal colocalization of UapA and SynA signals as both cargoes mark very proximal early secretory domains (i.e., ERES or ERGIC), especially in fungal cells. Anyhow, in the revised Figure 2 we also added a panel depicting separate channels, as the reviewer asks.

      -Fig. 3: In my opinion the statement that UapA "is probably sorted from an early secretory compartment, ultimately bypassing the need for Golgi maturation" is too strong at that point. You say for both UapA and SynA you don’t get significant colocalization with early Golgi/ERGIC marker, then you cannot conclude that one takes the conventional route via early-late Golgi and the other does not. What you can say is that UapA is apparently not going through late Golgi.

      The reviewer is in principle correct. However, significant colocalization with the late Golgi marker, as SynA shows, strongly suggests that this cargo has passed via the early Golgi compartment. The fact we failed to detect significant colocalization of any cargo tested with early Golgi/ERGIC markers (e.g., SedV) is very probably due to very rapid passage of cargoes from these compartments, which conventional widefield or confocal microscopy cannot detect. To achieve this, ultra-fast fluorescent microcopy, as Lattice Light Sheet Microscopy (LLSM), should be used. In fact, we are currently initiating these studies, which will appear in the near future elsewhere.

      -Fig. 4C: UapA does not seem to accumulate in the ER in the Sec24 and 13 mutants but in punctate structures. This for me is unexpected, any explanations? Can you characterize that punctate staining?

      This is an interesting observation. Notice that UapA is a large homodimeric protein (e.g., 28 transmembrane domains) that oligomerizes further upon translocation into the ER membrane. Repression of Sec24, and to a less extent of Sec13, leads to inability to exit the ER properly. Consequently, this will lead to UapA overaccumulation in the ER, which might in turn lead to ER stress and turnover, reflected in UapA aggregates. In line with this, we have previously shown that specific mutants of UapA unable to exit the ER are indeed degraded by selective autophagy (Evangelinos et al., 2016). In contrast to UapA, SynA partitions in the entire ER without forming aggregates when sec24 or sec13 are repressed. This might be due to the fact that is a single-pass, much smaller, membrane protein compared to UapA and one that is not known to form oligomers. Thus, its overaccumulation in the ER might not lead to aggregation, allowing it to diffuse laterally in the membrane of the ER. A note on this is included in the Figure legend of the revised manuscript.

      -Fig. 6D: You state that BFA "has only a very modest effect on UapA translocation to the PM". To me the PM (or very near PM) staining of UapA looks very different in the PFA treated cells, more uneven/punctate. Is there an explanation for that?

      Our explanation is the following. When BFA is added, conventional secretion is blocked and Golgi collapses. We believe that this might have a moderate indirect effect also on cargoes bypassing the late Golgi/TGN, as UapA (i.e., lower levels of UapA present in the PM). This is based on the fact that UapA, in addition to conventional cargoes, requires the Q-SNARE complex SsoA/Sec9 to translocate to the PM. SsoA, being a membrane protein cargo itself, also needs to traffic to the PM. Interestingly, we have previously obtained evidence suggesting that SsoA traffics to the PM by both conventional and a Golgi-bypass routes (Dimou et al 2020). Thus, UapA translocation to the PM might indeed be partially impeded or delayed due to repression of proteins, such as SsoA (and probably Sec9), needed for its final integration into the PM bilayer. Importantly, in line with an indirect effect of BFA on the levels of UapA localized in the PM, notice that, unlike SynA, UapA was never trapped in brefeldin bodies (i.e., Golgi aggregates).

      Reviewer #1 (Significance):

      One strength of the study is the use of a model organism, A. nidulans, not cell cultures. Also, the use of both reporters, UapA and SynA, in the same cell is an advantage over previous studies using different lines and different promotors. Limitation of the study might be that it remains unclear to what extend the basic mechanism (UapA and SynA are transported to PM in different carrier and via different routes) can be generalized to other polarized (apically?) membrane proteins versus non-polarized membrane proteins in A. nidulans and whether a similar mechanism exists in other organisms. Some of the basic findings of the study are not new but were published by the same group. However, as the authors point out, the current study uses improved assays and extends their previous studies, advancing our understanding of the mechanistics of transport in the conventional secretory pathway and novel alternative routes. The study will be of interest for basic researchers in the trafficking field. My own expertise is transport through the secretory pathway in mammalian cells, many years ago more post-Golgi, now mostly ER-Golgi and ER itself.

      We thank the reviewer for his positive comments.

      __Reviewer #2 __

      __ __The idea that transmembrane proteins of the plasma membrane move from the ER to the Golgi and then to the cell surface is firmly entrenched, and the mechanisms and components of this secretory pathway have been extensively characterized. Secretory vesicles are often delivered from the Golgi to sites of polarized growth. This paper builds on previous work by the same group to provide evidence that in Aspergillus nidulans, some non-polarly localized plasma membrane proteins follow a very different pathway, which bypasses components of the conventional secretory machinery such as SNAREs that have been implicated in secretion as well as the exocyst. In particular, they systematically compare the trafficking of the SNARE SynA, which follows the conventional secretory pathway, with that of the purine transporter UapA, which apparently does not. The two proteins were co-expressed in the same cells using the same promoter. A variety of genetic and microscopy methods are used to support the conclusion that UapA reaches the plasma membrane by a route distinct from that followed by SynA.

      In my view, the authors present a convincing case. The individual experimental results are sometimes ambiguous, but the combined results favor the conclusion that UapA follows a novel pathway to the plasma membrane. I have only a few relatively minor comments.

      Thank you for your positive comments

      1. In the Introduction and elsewhere: to my knowledge, there is no clear evidence that AP-1-containing clathrin-coated vesicles carry cargoes from the Golgi to the plasma membrane. On the contrary, as recently reported by Robinson (https://pubmed.ncbi.nlm.nih.gov/38578286/), AP-1-containing vesicles likely mediate retrograde traffic in the late secretory pathway.

      Thank you for this comment and the relative reference. We are aware that AP-1 is likely to also mediate retrograde traffic in the late secretory pathway or/and intra-Golgi recycling, as also reported by the group of Benjamin Glick. Thus, in the revised version we added a short comment on this plus relative references. Along this line, our previous work has shown that transcriptional repression of AP-1 arrests the polar localization of several apical markers in A. nidulans and we reported that this might be due to an effect on both anterograde and retrograde trafficking. Please see “Secretory Vesicle Polar Sorting, Endosome Recycling and Cytoskeleton Organization Require the AP-1 Complex in Aspergillus nidulans”. Martzoukou O, Diallinas G, Amillis S. Genetics. 2018 Aug;209(4):1121-1138. Overall, the fact that AP-1 was found absolutely dispensable for UapA trafficking, further strengthens our conclusion that UapA bypasses the Golgi.

      1. In Figure 2, is there any known significance to the presence of UapA in "cytoplasmic oscillating thread structures decorated by pearl-like foci as well as a very faint vesicular/tubular network"?

      At present we cannot answer this question. In order to understand what these structures represent and answer what is their role, we will need to employ super-resolution and ultra-fast microscopy and additional markers, which we envision to do. We suspect that they might be tubular networks, but this extends beyond the present work.

      1. SynA is related to S. cerevisiae Snc1/2, which are known to be present in late Golgi compartments due to repeated rounds of endocytosis to the Golgi and exocytosis to the plasma membrane. The SynA shown here to colocalize with PHosbp is probably present in a similar recycling loop rather than being en route to the plasma membrane for the first time. Therefore, the differential colocalization of UapA and SynA with PHosbp does not by itself provide "strong evidence that the two cargoes studied traffic via different routes" as stated in the text but might instead indicate that only SynA undergoes frequent endocytosis. The text should be amended accordingly.

      The reviewer is in principle correct. However, given that colocalization of SynA and PHosbp occurred all over the cytoplasm of hyphae and not only at the apical region, and because we record colocalization of cargoes before their steady-state accumulation to the PM, thus at a stage where recycling must be minimal, the recorded colocalization should reflect anterograde transport rather than recycling. We added this reasoning it the revised text.

      1. A missing piece of the story is a test of whether the puncta visualized for the two cargoes in Figure 5B are indeed distinct populations of COPII-containing ER exit sites. The relevant experiment would involve co-labeling of the cargoes together with a COPII marker. Three-color labeling would presumably be needed.

      This point was also raised by reviewer 1 (and review 3) and thus performed new experiments to better characterize the identity of the cargo-labeled fluorescent puncta. To do so, we used co-expression of a standard ERES marker, Sec16, in cells expressing either UapA or SynA, tagged with different fluorescent tags. More specifically, we constructed and analyzed strains co-expressing UapA-GFP/Sec16-mCherry or GFP-SynA/Sec16-mCherry in the sec31ts genetic background, which allows synchronization and better analysis of ER exit, as described in our text. The new findings appear as Figure 5C __in the revised manuscript. Notice that sec16-mCherry introduced in the native sec16 locus by standard knock-in reverse genetics of A. nidulans (see Materials and methods) does not affect Aspergillus growth or secretion. Experiments depicted in __5C show that both cargoes, UapA and SynA, co-localize significantly (PCC ≈ 0.6), with Sec16, suggesting that most of these puncta are indeed ERES structures. Given that the puncta marked with UapA or SynA are clearly distinct (see Figures 1C,2A, 3A, 5B), this new experiment strongly suggests that there are indeed two distinct ERES, one populated mostly by UapA and the other by SynA. Notice, as we already outline in our response to the editor above, a three-colored approach using Sec16-BFP (or Sec13-BFP) for showing directly the existence of these two populations of cargo-specific ERES in the same cell failed as the BFP signal was problematic for colocalization studies.

      Reviewer #2 (Significance):

      This study provides compelling evidence that in the fungus Aspergillus nidulans, some transmembrane transporter proteins reach the plasma membrane by a pathway that bypasses much of the conventional machinery associated with the Golgi apparatus and secretory vesicles. Although previous publications pointed toward a similar conclusion, the present work tackles the problem in a more rigorous and systematic way. These findings are important for cell biologists who study membrane traffic, it remains to be determined how prevalent this type of non-canonical secretion might be in other organisms.

      We thank the reviewer for his positive comments

      Reviewer #3

      The manuscript by Sagia et al compares the trafficking of a polarized (SynA) with a non-polarized (UapA) transmembrane protein. In agreement with previous work of the same lab, they find that UapA reaches the plasma membrane through a Golgi-bypass route, which they characterize to some extent. Overall, the data are of good quality and the story is interesting and timely. Understanding trafficking routes that bypass the Golgi is highly interesting. Nevertheless, there are several points of criticism that I have and below is a list where I combine major and minor points together:

      Thank you for your positive comments

      Major Comments:

      1- Is it possible that the polarized phenotype of SynA is caused by selective removal, i.e. SynA is delivered to the entire plasma membrane, but endocytosed rapidly from all areas except the tip of the hyphae. This would also result in a polarized distribution.

      This is in principle possible, but here this is not the case. SynA is polarized due to rapid local endocytosis and immediate recycling at the subapical region, known as the subapical collar. Please see:

      Taheri-Talesh N, Horio T, Araujo-Bazán L, Dou X, Espeso EA, Peñalva MA, Osmani SA, Oakley BR. The tip growth apparatus of Aspergillus nidulans. Mol Biol Cell. 2008 Apr;19(4):1439-49. doi: 10.1091/mbc.e07-05-0464.

      Hernández-González M, Bravo-Plaza I, Pinar M, de Los Ríos V, Arst HN Jr, Peñalva MA. Endocytic recycling via the TGN underlies the polarized hyphal mode of life. PLoS Genet. 2018;14(4):e1007291. Published 2018 Apr 2. doi:10.1371/journal.pgen.1007291

      This applies to all apical markers; they remain polarized by continuous local recycling after the diffuse laterally to the subapical collar.

      2- The authors describe the distribution of SynA and UapA in cells deficient of various COPII/ERES proteins. However, these data are not shown, and it is not clear how they were quantified. It would be important to add quantitative data here.

      Quantitative data are included in Figure 4C, displaying the percentages of cells with UapA either retained in the ER or reaching the PM for each background deficient in a COPII protein. Repression of SarA and Sec31 resulted in UapA retention in the ER in all analyzed cells (100%). However, repression of Sec12, Sec24, or Sec13 had a differential effect across the cell population, with UapA reaching the PM in some cells, while remaining trapped in the ER in others. To quantify these data and determine which cargo localization pattern prevails, we measured the number of cells in each category and represented them as percentages. A similar approach was used to examine the role of Golgi proteins in the trafficking of UapA and SynA (Figure 6).

      3- on page 8, the authors discuss the discrepancy regarding the role of Sec13. They offer as an explanation that the previous studies have been performed in strains that separately expressed the two cargoes. However, I am unable to see why and how this would be a valid explanation.

      Given that Sec13 has a variable/partial effect on UapA, we have previously been biased towards images that showed an effect on localization, as expected, and considered that the lack of an effect might have been due to inefficient repression in a fraction of cells. In our new system, we were able to directly compare UapA to SynA and find out that while SynA was always affected under our conditions, the effect of UapA was still variable. Thus, the partial effect of Sec13 on UapA is physiologically valid and not a matter of insufficient repression in a fraction of cells. This shows the importance of our new improved system where we follow the synchronous expression of two cargoes in the same cells.

      4- Why is the effect of Sec24 depletion so much stronger than of Sec12 depletion? Sec12 is the GEF for SarA, without which Sec24 should not be recruited to ERES. The explanation that low amounts of Sec12 are still present and sufficient to carry out the role of this protein. What is the evidence for that?

      Sec24 is the principal receptor of cargoes responsible for their recruitment to ERES. Sec12 is the catalytic effector for SarA required for the initiation of COPII vesicle formation. The question of the reviewer is thus logical.

      However, Sec12 is indeed present at extremely very low levels when expressed from its native promoter under the condition of our experiment (minimal media). This is supported by our recent proteomic analysis, performed under similar conditions, which failed to detect the Sec12 protein, unlike all other COPII components (see Dimou et al., 2021, doi; 10.3390/jof7070560), but also by cellular studies of the group of M.A. Peñalva, who failed to detect Sec12 tagged with GFP (Bravo-Plaza et al., 2019, doi: 10.1016/j.bbamcr.2019.118551). Additionally, in yeast, immune detection of Sec12 has been possible only in cells harboring sec12 on a multicopy plasmid, suggesting its low abundance in wild-type cells (Nakano et al., 1988, doi:10.1083/jcb.107.3.851).

      Given that repression of sec12 transcription via the thiAp promoter still allows 68% of cells to secrete normally both SynA and UapA, while 32% of cells are blocked in the trafficking of both cargoes, suggests that in most cells either SarA can catalyze the exchange of GDP for GTP without Sec12, maybe through a cryptic guanine nucleotide exchange factor (GEF), or that very small amounts of Sec12 remaining after repression are sufficient for significant SarA activation. Whichever scenario is true, Sec12, similarly to SarA, is not critical for distinguishing Golgi-dependent from Golgi-independent routes, as both cargoes are affected similarly. In the revised text we added a not on this issue.

      5- In Figure 5, it would help readers who are not so familiar with Aspergillus organelle morphology to explain the figure a bit better. This might appear trivial for experts, but anyone from outside this field is slightly lost.

      In the revised manuscript we added a figure panel depicting a schematic representation of A. nidulans key secretory compartments.

      6- The authors write that not seeing UapA in Golgi membranes is evidence that it does not pass through this organelle. However, when they write that SynA is never seen in cis-Golgi elements, they do not conclude that SynA bypasses the cis-Golgi.

      The fact that SynA, unlike UapA, colocalized significantly with late-Golgi/TGN and follows conventional secretion in general, strongly suggests that SynA also passes from the early-Golgi. Cargo traffic through the Golgi is mediated by cisternal maturation, where an individual cisterna gradually changes its nature from an earlier to a later one, while the cargo remains inside. UapA, unlike SynA, never colocalized with any Golgi marker used and was not affected by BFA. We agree with the reviewer that we did not have direct proof for passage of UapA or SynA from the early-Golgi in the wt background, which allows for the alternative, but rather unlikely hypothesis, that none of the two cargos is sorted to the early Golgi and that SynA traffics directly to late-Golgi/TGN. Our inability to detect sorting of any cargo to the early-Golgi is seemingly due to ultra-fast passage of cargoes from very early secretory compartments, such as ERGIC/early-Golgi. In fact, we have obtained evidence of this using Lattice Light Sheet microscopy (results in progress, to appear elsewhere).

      7- Figure 5C: the authors claim that the CopA and ArfA affects trafficking of UapA and SynA from ER to plasma membrane and assign CopA and ArfA as regulators for anterograde trafficking. I think this interpretation is not justified by the data. Depletion of CopA and ArfA will affect the Golgi apparatus in structure and function. The more straight-forward interpretation is that repression of the COPI machinery results in a defect in Golgi exit and therefore retention in pre-Golgi compartments (including the ER and maybe the ERGIC should it exist in Aspergillus). The same is true for BFA treatment where there are also negative effects on ER export, which are rather indirect consequences of alterations of Golgi function and integrity. Likewise, the interpretation of the papers by Weigel et al and Shomron et al is not correct. It is more likely that COPI is recruited to the growing ERES-derived tubule (or ERGIC) to recycle proteins back to the ER. This is not necessarily a proof that COPI regulates anterograde trafficking

      This is a highly debatable issue which our work cannot address. However, we amended the text accordingly.

      8- Figure 6: The images look like in Figure 5, yet here you don't call them ER-associated.

      The two images are not alike. In Figure 5 upon activation of Sec31 (permissive temperature) we detect mostly punctual structures resembling ERES, whereas at the nonpermissive temperature we detect a membranous network typical of the ER. Upon repression of CopA we also detect punctual structures similar to ERES. In Figure 6, we mostly detect an effect on SynA. Repression of early secretory steps (SedV, GeaA) lead to collapse of SynA in the entire ER network. Repression at later stages of Golgi maturation and post-Golgi secretion (RabO, HypB, RabE, AP-1) lead to the appearance of punctual structures, most probably Golgi aggregates.

      9- Figure 6D: How long was the BFA treatment. I am surprised that the pool of SynA preexisting at the plasma membrane seems to also be sensitive to BFA.

      Cells were grown overnight under repressed conditions for both UapA and SynA. After 12-14h cells were shifted to derepressed conditions using fructose as carbon source. BFA was added after 90min of cargo derepression, while both cargoes were still in cytoplasmic structures so there was not preexisting SynA or UapA at the PM (see also Figure 1C). Subcellular localization of both cargoes was studied for 60min after BFA treatment.

      10- This might be beyond the scope of this study, but as far as I know UapA is not N-glycosylated. Would the introduction of an N-glycosylation site shift it towards the Golgi-based route?

      Thank you for this suggestion. We have performed this experiment, adding a glycosylation site on UapA, based on the glycosylation sites found in tis mammalians homologues. We did not detect any effect on UapA trafficking route or its activity. As the reviewer recognizes this goes beyond the scope of this study and thus, we did not include it the manuscript. Differential cargo glycosylation is however an important issue to be studied systemically in respect to different trafficking routes, and we envision to investigate it systematically.

      Minor Comments

      1- This might be just a personal preference, but I think that the term polar is misleading, because it implies something about the polarity of the amino acids. I think "polarized" might be the more common term. Anyway, this is just a minor point and just a suggestion from my side.

      Amended in the revised text.

      2- The paper by the Saraste lab should be mentioned and discussed (PMID: 16421253), which I think is very relevant to the current story.

      We thank the reviewer for pointing out this important publication. In that case, the Rab1 GTPase defined a pathway connecting a pre-Golgi intermediate compartment with the PM in mammalians nerve cells. Thus, the Saraste lab publication is indeed along the lines of findings supporting that Golgi-independent unconventional cargo trafficking routes initiate at very early secretory compartments. Notice, however, that RabO, the A. nidulans homologue of Rab1, which in their case was essential for direct cargo sorting from the ERES/ERGIC to the PM, in or system, was dispensable for Golgi bypass. The Saraste lab article is now mentioned and discussed.

      3- Having worked with ERES for over two decades, I find it strange to see it written ERes. I see no reason why ER exit sites in Aspergillus should be abbreviated differently from all other types of cells (yeast, drosophila, worms, mammals). I think that the entire acronym should be capitalized.

      Amended in the text

      4- When discussing the data about the partial effect of Sec13, it would be good to refer to a previous paper by the Stephens lab that showed that silencing Sec13/31 results in a defect in trafficking of collagen, but not of VSVG (PMID: 18713835).

      We thank the reviewer for also pointing out the publication of the Stephens lab, now mentioned in the revised text. Noticeably, in that case silencing of both Sec13 and Sec31 has no effect on the trafficking of specific cargoes, whereas in our case Sec31 is still absolutely needed for both conventional and Golgi-independent secretion of SynA and UapA, respectively.

      Reviewer #3 (Significance):

      Overall, the data are of good quality and the story is interesting and timely. Understanding trafficking routes that bypass the Golgi is highly interesting. The main weakness is the lack of mechanistic understanding of the Golgi-bypass pathway. In addition, the study is limited to two proteins as representatives of polarized vs. non-polarized proteins. The main target audience for this paper are scientists working in the area of secretion and trafficking in the secretory pathway.

      We thank the reviewer for his positive comments.

      We are aware that the mechanistic details of Golgi bypass are missing and this is our next goal, dissecting those via various approaches genetic and biochemical approaches and employment of super resolution and ultra-fast microscopy.

      __Reviewer #4 __

      In this study, Sagia et al investigate the trafficking of different secretory cargo in Aspergillus nidulans under conditions that repress expression of transport factors or block stages in membrane trafficking. The primary approach is to conduct dual live-cell imaging of GFP-tagged UapA (plasma membrane localized purine transporter) and SynA (plasma membrane R-SNARE) after their simultaneous derepression to monitor trafficking routes. In germlings, both secretory proteins are detected in non-overlapping intracellular compartments and puncta after 60-90 min of derepression. After 4-6 hrs, SynA localizes to hyphal tips whereas UapA localizes to non-polar regions of the PM. Colocalization studies do not show UapA overlap with Golgi markers (SedV, PH-OSBP) during its biogenesis whereas SynA displays significant co-localization. Repression of COPII and COPI components generally block transport of both cargos to the PM and cause accumulation in ER compartments, although there are some differential effects on UapA and SynA localization. Finally, repression of other transport factors (ER-Golgi SNAREs, Golgi transport factors, and exocytic machinery) had differential effects on UapA and SynA localization over time with UapA reaching the plasma membrane in many instances and SynA accumulating in intracellular compartments.

      Based on these observations, the authors conclude that UapA and SynA follow distinct trafficking routes to the plasma membrane where SynA uses a canonical SNARE-dependent secretory pathway route and UapA follows a non-canonical route that may bypass Golgi compartments. The study is extensive and supports the model that biogenesis of SynA and UapA follow distinct processes. However, there are some complexities that may limit interpretation. First, the cargo studied are targeted to the ER differently. UapA is a multispanning transmembrane protein that is likely dependent on the Sec61 translocon for co-translational membrane insertion and will involve ER chaperones and quality control machinery for its biogenesis. SynA will depend on the tail-anchored machinery (GET/TRC pathway) for insertion into the ER and is processed by cytosolic factors/chaperones. Therefore, the sites of ER insertion and the rates of biogenesis of these cargoes will be different. In addition, the repression of trafficking machinery used in this study appears to be variable and may exert partial blocks on intracellular transport stages. Regardless, the study clearly documents that SynA and UapA follow distinct biogenesis and transport processes when co-expressed in cells under experimentally controlled conditions.

      Thank you for your positive comments.

      To our knowledge there is no evidence suggesting that SynA translocates via a tail-anchored machinery (GET/TRC pathway) and not through the translocase. Despite this, we agree with the reviewer that translocation to the ER, as well as exit from it, might be cargo-dependent, especially when it concerns proteins with very different size, structures and oligomerization. Thus, the rate of biogenesis of UapA and SynA is probably quite different. However, this still does not dismiss our basic conclusion that the two cargoes follow distinct routes to traffic to the PM. The ‘problem’ of variable transcriptional repression of some trafficking-related proteins is solved by comparing the relative effect on the two cargoes in the same cells, and this is in fact the advantage of our new system. Importantly, notice that we took care to use conditions of repression where SynA trafficking by the conventional path was totally abolished and compared it to UapA.

      1. It was not clear if the translation, ER insertion and folding of UapA and SynA are fully synchronous. Is it possible that the rate of UapA synthesis and transport to the plasma membrane is substantially faster than for SynA? The imposition of transport blocks could trap SynA and not UapA if this cargo was at later transport stages.

      As already discussed above translation, ER insertion and folding of UapA and SynA might indeed by different. This might somehow affect the trafficking path followed, but this issue is beyond the scope of this work. Notice, however, that the transcription of both cargoes is kept fully repressed during establishment of repression of secretion. Only when repression and blocking of secretion is established (12-14 h germination), as verified by Western blot analysis, we derepress the transcription of UapA and SynA, expressed from the same promoter, and follow their dynamic subcellular localization. Hence, this system ensures that both cargoes start from the earliest transport stage, the ER, upon imposition of transport blocks.

      1. In repressing transport factors (e.g., SarA, Sec12, Sec24, Sec13, SedV, RabE), it is clear that under thiamine repressing conditions these cells do not grow or have greatly reduced growth rates. However, it was not clear if proteins are depleted to the same extent in cells after repression for 12-14 hr or 16-22 hr. as mentioned in the methods. Indeed, in some cases depleted cells display different cargo localization patterns, for example 67% of cells show normal localization of UapA and SynA after sec12 repression and 33% show ER accumulation of both cargoes. There is differential localization of UapA and SynA in many cases where transport factors are repressed, but this could be due to partial inhibition and not complete blocks. It would be helpful to clearly indicate the time points and conditions in each of the figure legends as in points 3-5 below.

      In the revised manuscript we did our best to clearly indicate the time points and conditions in each of the figure legends. Differential localization of UapA and SynA in many cases where trafficking factors are repressed is indeed an interesting outcome. Inefficient repression was dismissed based on the lack of colony growth (see relative growth tests of SarA, Sec24, Sec13, Sec31, SedV, GeaA, RabO, RabE, Ykt6, Sft1, SsoA and Sec9), but also by western blots (e.g., Sec24, Sec13, Sec31 or Sec9 shown in the present manuscript, or other trafficking proteins studied previously. Martzoukou et al., 2018; Dimou et al., 2020). Repression of Sec12 and HypB, and to lower degree AP-1, allowed formation of small and/or compact colonies, but even in these cases relative protein levels could not be detected in western blots, guaranteeing efficient repression.

      1. In Fig 4A immunoblot, HA-tagged proteins are not detected after thiamine repression. Please state the time of thiamine repression used before protein extraction and blot. Is this for the same length of time as for cells shown in panel 4C? It would also be helpful to state the time of cargo derepression before capturing images in 4C. The methods section mentions 12-14 hr or 16-22 hr of growth, presumably with thiamine in the culture, and then 1-8 hr or 60 min to 4 hr of cargo derepression before imaging. Please specify.

      The time of thiamine repression before protein extraction was 16-18h. The same repression time was used for experiments shown in Figures 4C and 6C (ER/COPII and Golgi/post-Golgi repression respectively). More specifically, for microscopy experiments cells were grown in the presence of glucose and thiamine for 12-14h (repressed UapA/SynA and thiAp expressed gene). After this time, cells were shifted to fructose and thiamine for 4h (derepression of UapA/SynA and repression of thiAp expressed gene). In both cases (protein extraction and microscopy experiments) the total time of thiamine repression was 16-18h.

      1. For the thiA-copA and thiA-arfA repression experiments (Fig 5C), the methods section states that thiamine was not added ab initio in the culture, but after an 8 h time window without thiamine at the start of spore incubation. This is interpreted to mean that repression was for a shorter period to time than the 12-14 hr overnight growth. However, the figure legend states that De novo synthesis of cargos takes place after full repression of CopA and ArfA is achieved (>16 hr). Please clarify.

      We think that the review was confused with repression of cargo synthesis (via alcAp+glucose) versus repression of trafficking proteins (via thiAp+thiamine). Please see Materials and methods. We clarify our protocol also here:

      For the thiAp-copA and thiAp-arfA repression experiments addition of thiamine ab initio in the culture leads to total arrest of spore germination and germling formation. Thus, we added an 8-hour time window without thiamine to allow conidiospores to germinate until the stage of young germlings, under conditions where cargo expression via the alcAp was repressed by glucose. Subsequently, thiamine was added in the media (16-18 h) to repress CopA and ArfA, while cargo expression remained glucose-repressed. The transcriptional repression of the cargoes UapA and SynA was maintained for a longer period (24-26 h) compared to other repression experiments, but longer times of repression of cargoes do not make any difference, as full repression is achieved already at 12 h. De novo cargo trafficking was followed next day by eliciting depression, via a shift to fructose media, while still maintaining thiamine to repress CopA or ArfA.

      1. In Fig 6D, BFA treatment is shown to trap SynA in Golgi aggregates while UapA still reaches the plasma membrane. Please state the time of BFA treatment before collecting these images. Do longer treatments with BFA before cargo derepression cause accumulation of UapA in intracellular compartments?

      As mentioned above (response to Reviewer’s #3 comment 9) cells were grown overnight under repressed conditions for both UapA and SynA. After 12-14h cells were shifted to derepressed conditions using fructose as carbon source. BFA was added after 90min of cargo derepression, while both cargoes were still in cytoplasmic structures so there was not preexisting SynA or UapA at the PM (see also Figure 1C). We have not noticed any different effect on UapA trafficking after a max of 1h of BFA treatment.

      1. A minor point, but on page 21 the methods state that "cells were shifted down to the permissive temperature (25 C), to restore the secretory block...". Suggest changing to "to reverse the secretory block..."

      Modified accordingly

      Reviewer #4 (Significance):

      This manuscript nicely builds on a developing line of investigation in the Aspergillus nidulans model that specific plasma membrane proteins are efficiently delivered to the cell surface in a pathway that is distinct from the canonical secretory pathway. Previous work from this lab has suggested that a subpopulation of COPII carriers can bypass the Golgi for delivery of specific cargo to the plasma membrane. The current study uses dual expression of UapA-GFP and mCherry-SynA to provide further support for this model. Molecular definition of a direct ER to PM transport pathway for secretory cargo would be a significant advance to a broad audience. This study provides additional depth and support that such a pathway exists but does not define how COPII vesicles or related intermediates are transported to the PM.

      Again, thank you for your positive comments.

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      Referee #4

      Evidence, reproducibility and clarity

      In this study, Sagia et al investigate the trafficking of different secretory cargo in Aspergillus nidulans under conditions that repress expression of transport factors or block stages in membrane trafficking. The primary approach is to conduct dual live-cell imaging of GFP-tagged UapA (plasma membrane localized purine transporter) and SynA (plasma membrane R-SNARE) after their simultaneous derepression to monitor trafficking routes. In germlings, both secretory proteins are detected in non-overlapping intracellular compartments and puncta after 60-90 min of derepression. After 4-6 hrs, SynA localizes to hyphal tips whereas UapA localizes to non-polar regions of the PM. Colocalization studies do not show UapA overlap with Golgi markers (SedV, PH-OSBP) during its biogenesis whereas SynA displays significant co-localization. Repression of COPII and COPI components generally block transport of both cargos to the PM and cause accumulation in ER compartments, although there are some differential effects on UapA and SynA localization. Finally, repression of other transport factors (ER-Golgi SNAREs, Golgi transport factors, and exocytic machinery) had differential effects on UapA and SynA localization over time with UapA reaching the plasma membrane in many instances and SynA accumulating in intracellular compartments.

      Based on these observations, the authors conclude that UapA and SynA follow distinct trafficking routes to the plasma membrane where SynA uses a canonical SNARE-dependent secretory pathway route and UapA follows a non-canonical route that may bypass Golgi compartments. The study is extensive and supports the model that biogenesis of SynA and UapA follow distinct processes. However, there are some complexities that may limit interpretation. First, the cargo studied are targeted to the ER differently. UapA is a multispanning transmembrane protein that is likely dependent on the Sec61 translocon for co-translational membrane insertion and will involve ER chaperones and quality control machinery for its biogenesis. SynA will depend on the tail-anchored machinery (GET/TRC pathway) for insertion into the ER and is processed by cytosolic factors/chaperones. Therefore, the sites of ER insertion and the rates of biogenesis of these cargo will be different. In addition, the repression of trafficking machinery used in this study appear to be variable and may exert partial blocks on intracellular transport stages. Regardless, the study clearly documents that SynA and UapA follow distinct biogenesis and transport processes when co-expressed in cells under experimentally controlled conditions.

      1. It was not clear if the translation, ER insertion and folding of UapA and SynA are fully synchronous. Is it possible that the rate of UapA synthesis and transport to the plasma membrane is substantially faster than for SynA? The imposition of transport blocks could trap SynA and not UapA if this cargo was at later transport stages.
      2. In repressing transport factors (e.g. sarA, sec12, sec24, sec13, sedV, rabE), it is clear that under thiamine repressing conditions these cells do not grow or have greatly reduced growth rates. However, it was not clear if proteins are depleted to the same extent in cells after repression for 12-14 hr or 16-22 hr as mentioned in the methods. Indeed, in some cases depleted cells display different cargo localization patterns, for example 67% of cells show normal localization of UapA and SynA after sec12 repression and 33% show ER accumulation of both cargo. There is differential localization of UapA and SynA in many cases where transport factors are repressed, but this could be due to partial inhibition and not complete blocks. It would be helpful to clearly indicate the time points and conditions in each of the figure legends as in points 3-5 below.
      3. In Fig 4A immunoblot, HA-tagged proteins are not detected after thiamine repression. Please state the time of thiamine repression used before protein extraction and blot. Is this for the same length of time as for cells shown in panel 4C? It would also be helpful to state the time of cargo derepression before capturing images in 4C. The methods section mentions 12-14 hr or 16-22 hr of growth, presumably with thiamine in the culture, and then 1-8 hr or 60 min to 4 hr of cargo derepression before imaging. Please specify.
      4. For the thiA-copA and thiA-arfA repression experiments (Fig 5C), the methods section states that thiamine was not added ab initio in the culture, but after an 8 h time window without thiamine at the start of spore incubation. This is interpreted to mean that repression was for a shorter period to time than the 12-14 hr overnight growth. However, the figure legend states that De novo synthesis of cargos takes place after full repression of CopA and ArfA is achieved (>16 hr). Please clarify.
      5. In Fig 6D, BFA treatment is shown to trap SynA in Golgi aggregates while UapA still reaches the plasma membrane. Please state the time of BFA treatment before collecting these images. Do longer treatments with BFA before cargo derepression cause accumulation of UapA in intracellular compartments?
      6. A minor point, but on page 21 the methods state that "cells were shifted down to the permissive temperature (25 C), to restore the secretory block...". Suggest changing to "to reverse the secretory block..."

      Significance

      This manuscript nicely builds on a developing line of investigation in the Aspergillus nidulans model that specific plasma membrane proteins are efficiently delivered to the cell surface in a pathway that is distinct from the canonical secretory pathway. Previous work from this lab has suggested that a subpopulation of COPII carriers can bypass the Golgi for delivery of specific cargo to the plasma membrane. The current study uses dual expression of UapA-GFP and mCherry-SynA to provide further support for this model.

      Molecular definition of a direct ER to PM transport pathway for secretory cargo would be a significant advance to a broad audience. This study provides additional depth and support that such a pathway exists but does not define how COPII vesicles or related intermediates are transported to the PM.

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      Referee #3

      Evidence, reproducibility and clarity

      The manuscript by Sagia et al compares the trafficking of a polarized (SynA) with a non-polarized (UapA) transmembrane protein. In agreement with previous work of the same lab, they find that UapA reaches the plasma membrane through a Golgi-bypass route, which they characterize to some extent. Overall, the data are of good quality and the story is interesting and timely. Understanding trafficking routes that bypass the Golgi is highly interesting. Nevertheless, there are several points of criticism that I have and below is a list where I combine major and minor points together:

      Major Comments:

      1. Is it possible that the polarized phenotype of SynA is caused by selective removal, i.e. SynA is delivered to the entire plasma membrane, but endocytosed rapidly from all areas except the tip of the hyphae. This would also result in a polarized distribution.
      2. The authors describe the distribution of SynA and UapA in cells deficient of various COPII/ERES proteins. However, these data are not shown, and it is not clear how they were quantified. It would be important to add quantitative data here.
      3. on page 8, the authors discuss the discrepancy regarding the role of Sec13. They offer as an explanation that the previous studies have been performed in strains that separately expressed the two cargoes. However, I am unable to see why and how this would be a valid explanation.
      4. Why is the effect of Sec24 depletion so much stronger than of Sec12 depletion? Sec12 is the GEF for SarA, without which Sec24 should not be recruited to ERES. The explanation that low amounts of Sec12 are still present and sufficient to carry out the role of this protein. What is the evidence for that?
      5. In Figure 5, it would help readers who are not so familiar with Aspergillus organelle morphology to explain the figure a bit better. This might appear trivial for experts, but anyone from outside this field is slightly lost.
      6. The authors write that not seeing UapA in Golgi membranes is evidence that it does not pass through this organelle. However, when they write that SynA is never seen in cis-Golgi elements, they do not conclude that SynA bypasses the cis-Golgi.
      7. Figure 5C: the authors claim that the CopA and ArfA affects trafficking of UapA and SynA from ER to plasma membrane and assign copA and ArfA as regulators fo anterograde trafficking. I think this interpretation is not justified by the data. Depletion of CopA and ArfA will affect the Golgi apparatus in structure and function. The more straight-forward interpretation is that repression of the COPI machinery results in a defect in Golgi exit and therefore retention in pre-Golgi compartments (including the ER and maybe the ERGIC should it exist in Aspergillus). The same is true for BFA treatment where there are also negative effects on ER export, which are rather indirect consequences of alterations of Golgi function and integrity. Likewise, the interpretation of the papers by Weigel et al and Shomron et al is not correct. It is more likely that COPI is recruited to the growing ERES-derived tubule (or ERGIC) to recycle proteins back to the ER. This is not necessarily a proof that COPI regulates anterograde trafficking
      8. Figure 6: The images look like in Figure 5, yet here you don't call them ER-associated.
      9. Figure 6D: How long was the BFA treatment. I am surprised that the pool of SynA preexisting at the plasma membrane seems to also be sensitive to BFA.
      10. This might be beyond the scope of this study, but as far as I know UapA is not N-glycosylated. Would the introduction of an N-glycosylation site shift it towards the Golgi-based route?

      Minor Comments

      1. This might be just a personal preference, but I think that the term polar is misleading, because it implies something about the polarity of the amino acids. I think "polarized" might be the more common term. Anyway, this is just a minor point and just a suggestion from my side.
      2. The paper by the Saraste lab should be mentioned and discussed (PMID: 16421253), which I think is very relevant to the current story.
      3. Having worked with ERES for over two decades, I find it strange to see it written ERes. I see no reason why ER exit sites in Aspergillus should be abbreviated differently from all other types of cells (yeast, drosophila, worms, mammals). I think that the entire acronym should be capitalized.
      4. When discussing the data about the partial effect of Sec13, it would be good to refer to a previous paper by the Stephens lab that showed that silencing Sec13/31 results in a defect in trafficking of collagen, but not of VSVG (PMID: 18713835)

      Significance

      Overall, the data are of good quality and the story is interesting and timely. Understanding trafficking routes that bypass the Golgi is highly interesting. The main weakness is the lack of mechanistic understanding of the Golgi-bypass pathway. In addition, the study is limited to two proteins as representatives of polarized vs. non-polarized proteins. The main target audience for this paper are scientists working in the area of secretion and trafficking in the secretory pathway.

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      Referee #2

      Evidence, reproducibility and clarity

      The idea that transmembrane proteins of the plasma membrane move from the ER to the Golgi and then to the cell surface is firmly entrenched, and the mechanisms and components of this secretory pathway have been extensively characterized. Secretory vesicles are often delivered from the Golgi to sites of polarized growth. This paper builds on previous work by the same group to provide evidence that in Aspergillus nidulans, some non-polarly localized plasma membrane proteins follow a very different pathway, which bypasses components of the conventional secretory machinery such as SNAREs that have been implicated in secretion as well as the exocyst. In particular, they systematically compare the trafficking of the SNARE SynA, which follows the conventional secretory pathway, with that of the purine transporter UapA, which apparently does not. The two proteins were co-expressed in the same cells using the same promoter. A variety of genetic and microscopy methods are used to support the conclusion that UapA reaches the plasma membrane by a route distinct from that followed by SynA.

      In my view, the authors present a convincing case. The individual experimental results are sometimes ambiguous, but the combined results favor the conclusion that UapA follows a novel pathway to the plasma membrane. I have only a few relatively minor comments.

      1. In the Introduction and elsewhere: to my knowledge, there is no clear evidence that AP-1-containing clathrin-coated vesicles carry cargoes from the Golgi to the plasma membrane. On the contrary, as recently reported by Robinson (https://pubmed.ncbi.nlm.nih.gov/38578286/), AP-1-containing vesicles likely mediate retrograde traffic in the late secretory pathway.
      2. In Figure 2, is there any known significance to the presence of UapA in "cytoplasmic oscillating thread structures decorated by pearl-like foci as well as a very faint vesicular/tubular network"?
      3. SynA is related to S. cerevisiae Snc1/2, which are known to be present in late Golgi compartments due to repeated rounds of endocytosis to the Golgi and exocytosis to the plasma membrane. The SynA shown here to colocalize with PH-osbp is probably present in a similar recycling loop rather than being en route to the plasma membrane for the first time. Therefore, the differential colocalization of UapA and SynA with PH-osbp does not by itself provide "strong evidence that the two cargoes studied traffic via different routes" as stated in the text, but might instead indicate that only SynA undergoes frequent endocytosis. The text should be amended accordingly.
      4. A missing piece of the story is a test of whether the puncta visualized for the two cargoes in Figure 5B are indeed distinct populations of COPII-containing ER exit sites. The relevant experiment would involve co-labeling of the cargoes together with a COPII marker. Three-color labeling would presumably be needed.

      Significance

      This study provides compelling evidence that in the fungus Aspergillus nidulans, some transmembrane transporter proteins reach the plasma membrane by a pathway that bypasses much of the conventional machinery associated with the Golgi apparatus and secretory vesicles. Although previous publications pointed toward a similar conclusion, the present work tackles the problem in a more rigorous and systematic way. These findings are important for cell biologists who study membrane traffic, although it remains to be determined how prevalent this type of non-canonical secretion might be in other organisms.

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      Referee #1

      Evidence, reproducibility and clarity

      Sagia et al. present a manuscript using A. nidulans as model to study different transport routes of membrane proteins from the ER to the plasma membrane. They showed in earlier work that apparently at least two different transport routes exist, one involving the classical ER-ERES-ERGIC-Golgi route, one bypassing the Golgi. Unpolarized membrane proteins use the former, apically sorted membrane proteins the latter route. The study here confirms their earlier findings, uses a better model (co-expression of representatives for both routes in the same cell) and provides additional mechanistic insights about the roles of rabs, SNARES and other important proteins of the secretory pathway. The study is thoroughly done, figures are of high quality, data and methods well described and adequately replicated.

      I do have, however, a number of comments that could help to improve the manuscript.

      • I suggest to use the term polarized or apical rather than polar. Polar alone to me refers more to physico-chemical properties like water-solubility.
      • introduction and discussion: I don´t think the literature about unconventional secretion bypassing the Golgi is complete, for example studies about TMED10 like Zhang, M. et al. Cell 181, 637-652 e615 (2020) or Zhang et al. Elife 4 (2015) are missing, there might be others. Is UapA a leader-less cargo that could be inserted via TMED10 translocation?
      • Fig. 1C. Can these intracellular structures be characterized in more detail? Where is the Golgi localized in A. nidulans, is it decentralized like in yeast? Is the UapA at the time points shown in Fig. 1C in some sub-PM structures? To me the distribution at or near the PM is more punctate than in the steady state image shown in 1B.
      • Fig. 3A. To me it looks like there is actually a lot of colocalization of UapA and SynA, especially at or near the PM, where there is quite some white, punctate staining. The green fluorescence is just much stronger, overlaying the violet. Can you show separate channels and explain?
      • Fig. 3: In my opinion the statement that UapA "is probably sorted from an early secretory compartment, ultimately bypassing the need for Golgi maturation" is too strong at that point. You say for both UapA and SynA you don´t get significant colocalization with early Golgi/ERGIC marker, then you cannot conclude that one takes the conventional route via early-late Golgi and the other does not. What you can say is that UapA is apparently not going through late Golgi.
      • Fig. 4C: UapA does not seem to accumulate in the ER in the Sec24 and 13 mutants but in punctate structures. This for me is unexpected, any explanations? Can you characterize that punctate staining?
      • Fig. 6D: You state that BFA "has only a very modest effect on UaPA translocation to the PM". To me the PM (or very near PM) staining of UaPA looks very different in the PFA treated cells, more uneven/punctate. Is there an explanation for that?

      Significance

      One strength of the study is the use of a model organism, A. nidulans, not cell cultures. Also the use of both reporters, UapA and SynA, in the same cell is an advantage over previous studies using different lines and different promotors. Limitation of the study might be that it remains unclear to what extend the basic mechanism (UapA and SynA are transported to PM in different carrier and via different routes) can be generalized to other polarized (apically?) membrane proteins versus non-polarized membrane proteins in A. nidulans and whether a similar mechanism exists in other organisms.

      Some of the basic findings of the study are not new but were published by the same group. However, as the authors point out, the current study uses improved assays and extends their previous studies, advancing our understanding of the mechanistics of transport in the conventional secretory pathway and novel alternative routes. The study will be of interest for basic researchers in the trafficking field.

      My own expertise is transport through the secretory pathway in mammalian cells, many years ago more post-Golgi, now mostly ER-Golgi and ER itself.

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      Reply to the reviewers

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

      Summary: MIC26 is a subunit of the 'mitochondrial contact site and cristae organizing system' (MICOS) complex required for crista junction (CJ) formation and was functionally linked to diabetes and modulation of lipid metabolism. In order to understand the role of MIC26 in metabolism, the authors generated MIC26-KO HepG2 cells and investigated the pathways regulated by MIC26 under normo- and hyper-glycemic culture conditions. They employed a multi-omics approach that include transcriptomics, proteomics, targeted metabolomics, and functional assays to document the changes in mRNAs, proteins, and metabolites as a result of MIC26 deletion. Through bioinformatic analyses, they showed that the function of MIC26 is critical in various pathways regulating fatty acid synthesis, oxidation, cholesterol metabolism, and glycolysis. Interestingly, they found an entirely antagonistic effect of lipogenesis in MIC26-KO cells compared to WT cells depending on the glucose concentration of the culture media. In addition, they showed that MIC26 deletion led to a major metabolic rewiring of glutamine utilization as well as oxidative phosphorylation.

      Major comments: 1) This is basically a descriptive study that document the transcriptomic, proteomic, and metabolic consequences of lacking MIC26 in normal or high glucose environment. It is data rich but insight poor. The connections between MIC26 as a subunit of MICOS complex and all those metabolic pathways are so tenuous that it is hard to see what to follow up after.

      __Response: __We respectfully differ from the reviewer’s opinion that the manuscript is data rich and insight poor. Our study provides significant insights by demonstrating how MIC26, strategically residing in the mitochondrial inner membrane (IM), regulates major cellular pathways.

      MIC26 operates in a dual manner:

      A) Depending on the nutritional status, normoglycemia or hyperglycemia, MIC26 regulates the glycolysis, lipid, cholesterol metabolism and TCA cycle intermediates in an antagonistic manner. B) Independent of the nutritional status, it regulates glutamine and OXPHOS metabolism.

      In addition, based on the suggestions by Reviewer #2, we have tested whether other proteins of MICOS (MIC27 and MIC19) present in two different sub-complexes regulate important metabolic pathways. Using the experimental results achieved (See reply to comments from Reviewer #2), we conclude that MIC26 plays a unique role as metabolic regulator in the IM and this study is therefore important to the general field of metabolism.

      2) In the Results section (page 5, line 114-123), the description of the Western blot (WB) analysis appears inconsistent with several blot images of Fig. 1A, which makes the result unconvincing. The authors should select appropriate representative WB images, assuming they have them, to support their claim.

      Response: Thank you for the suggestion. Firstly, we have performed additional experiments in this regard, and included the relevant quantification. Secondly, we have replaced some WBs which depict the appropriate quantification.

      Further, we also modified the relevant lines in the manuscript stating that ‘Mitochondrial apolipoproteins, MIC26, MIC27, and MIC25 are increased in cells exposed to hyperglycemia’ and not only MIC26 as stated before.

      Minor comments:

      3) As the functional role of MIC26 in metabolism is the primary focus, the authors should present the results in the figures in the order of WT-N, MIC26KO-N, WT-H, MIC26KO-H for easier comparison.

      Response: We understand the reasoning to interchange the two conditions. However, such an endeavour will involve cropping images of WBs, BN-PAGE and Clear native PAGE to better represent the corresponding quantification. This will also involve modifying all figures (data-sets and functional assays) in the whole manuscript. Overall, considering that the benefits of interchanging the order, of the WT-Hyperglycemia and MIC26 KO-Normoglycemia, are relatively minor, we have decided to stick to the original representation of the figures.

      Reviewer #1 (Significance (Required)):

      Mitochondria play important roles in metabolism and metabolic disorders. This study generated large amount of data relating to the role of a mitochondrial protein MIC26 in metabolism. Mutations in MIC26 have been associated with mitochondrial myopathy, lactic acidosis, and cognition defects (Beninca et al. 2021) and a lethal progeria-like condition (Peifer-Weib et al. 2023). There is also a connection between MIC26 and metabolic disorders. The results of this study will be of interest to researchers in the fields of mitochondrial diseases and metabolic disorders. My field of expertise is mitochondrial disease, proteomics, lipidomics, phospholipid biochemistry.

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

      Summary

      This study determines the role of MIC26, a mitochondrial component of the MICOS complex, in influencing cellular metabolic status. Using a variety of multiomic profiling techniques, as well as functional assays such as Seahorse-based respirometry, the authors propose that MIC26 regulates a variety of metabolic processes, including lipid and cholesterol homeostasis, glycolysis, fatty acid oxidation, fatty acid synthesis, TCA cycle homeostasis, glutamine metabolism, and general mitochondrial bioenergetics via OxPhos activity and supercomplex formation. The data were generated in MIC26 knockout HepG2 hepatocellular carcinoma cells grown in two nutrient conditions: high glucose (which they term "hyperglycemia") and low glucose (which they term "normoglycemia") DMEM. While the data support the authors' conclusion that loss of MIC26 causes braod metabolic changes across these conditions, the authors do not distinguish whether MIC26 knockout affects metabolism due to its canonical role in MICOS, or whether it acts as "a metabolic rheostat" to directly regulate central cellular fuel pathways, as is claimed in the title of this manuscript. Given the breadth of metabolic alterations seen in the MIC26 KO cells, it seems likely that at least a subset of these changes are indirect, rather than that MIC26 plays a direct regulatory role in the eight distinct metabolic pathways outlined above. Thus, while the data generally support the conclusion that expression of MIC26 is important for metabolic homeostasis, the mechanism(s) by which MIC26 influences cellular metabolism remains unclear and should be further addressed.

      Major Comments

      1) The authors infer that MIC26 influences cellular metabolism by referencing a handful of papers on MIC26 transcript differences in select metabolic models, metabolic alterations seen in a MIC26 transgenic/overexpression mouse model, or metabolic effects seen due to MIC26 tissue specific KO models. They thus hypothesize that "MIC26 has an unidentified regulatory role under nutrient-enriched conditions" (line 88). They support this observation by showing that MIC26 is increased in high glucose DMEM relative to low glucose DMEM in Figure 1. However, the authors claim, in both the figure legend title as well as the results section header, that "MIC26 is selectively increased in cells exposed to hyperglycemia" (lines 103-4), when their data demonstrate that this is not true. Figure 1B shows that MIC27, MIC26, and MIC25 increase in high glucose relative to low glucose conditions, indicating that MIC26 is not selectively increased, but rather that multiple subunits of MICOS are increased under nutrient-enriched conditions.

      Response: We agree to the reviewer’s comment and have now replaced the title in the results section in the manuscript accordingly - ‘Mitochondrial apolipoproteins, MIC26, MIC27, and MIC25 are increased in cells exposed to hyperglycemia’ and not only MIC26 as stated before. Further, in order to strengthen the WB data from Fig 1A & B, we also increased the number of experiments and updated the Fig 1B and also some WBs in Fig 1A to better represent the quantification.

      2) This does not suggest that MIC26 does not have an important role in maintaining metabolism under such nutrient conditions, but rather supports a model in which MICOS itself dynamically responds to altered nutrient conditions in cell culture. Interestingly, other MICOS subunits do not change in abundance (e.g., MIC19 and MIC60), which have previously been associated with a separate MICOS subcomplex than MIC26 in yeast (PMID: 33053165). These data may suggest that the nutrient responsive behavior of MIC26 may be due to its assembly within this specific MICOS subcomplex, rather than an independent "unidentified regulatory role under nutrient-enriched conditions".

      To test this, the authors should repeat a subset of functional assays (perhaps the Seahorse metabolic assays) in other MICOS deletion cell lines, including one that dynamically changes in expression in a similar manner to MIC26 (e.g., MIC27 KO or MIC25 KO) and one that does not dynamically change in expression in high glucose conditions (e.g., MIC60 or MIC13). In these sets of experiments the authors will be able to distinguish three possibilities:

      Model 1: if MICOS in general affects metabolic pathways, similar results will be seen for all MICOS subunit KOS.

      Model 2: if the MIC26-specific subcomplex is dynamically regulated to influence cellular metabolism, KO of MIC26 and other subunits of this subcomplex should show similar results, but KO of subunits of the non-dynamic subcomplex (e.g., MIC60) would not show similar phenotypes.

      Model 3: If only MIC26 KO, but not other MICOS subunits, show metabolic phenotypes, this would support a MICOS-independent role for MIC26 in influencing cellular metabolism.

      Importantly, any of these models are interesting, and testing these models does not invalidate any of the phenotypes presented in the manuscript. Rather, these experiments would assist the reader in understanding the underlying mechanism by which MIC26 loss causes cellular metabolic defects. Furthermore, it is worth stating that performing all experiments with multiple other MICOS cell lines is beyond the scope of the manuscript, but testing effects in select (preferably functional) assays, such as the glycolysis stress test (Fig 3E), FAO Seahorse (Fig 3H-J) glutamine oxidation (Fig 6B), and general stress test (Fig 7E) would be appropriate. Other more defined and easily achievable experiments could also be used to support these claims (e.g., western blots probing for levels of key metabolic regulators).

      __Response: __We appreciate the balanced comments of the reviewer who has carefully read and appreciated our manuscript. We also appreciate the constructive criticism of the reviewer who suggested various possible models considering the MIC26 role.

      In this endeavour, we have performed the following extensive experiments:

      1. Generated MIC19 KOs in HepG2 cells. We had already generated MIC27 KOs during the course of a previous publication (Lubeck et al, 2023) and used them for this publication (Fig S4). WB analyses was performed using the MIC27 KO and MIC19 KO cells.
      2. Measured glycolysis function using the glycolysis stress test in MIC27 and MIC19 KOs (Fig S5).
      3. Analysed lipid metabolism by imaging and extensively quantifying LD number and BODIPY fluorescence intensities in MIC27 and MIC19 KO cells (Fig S6).
      4. Measured glutamine oxidation using Mito Flex fuel tests in MIC27 and MIC19 KOs (Fig S10F).
      5. Analysed general mitochondrial respiration by using mito stress kit in MIC27 and MIC19 KOs (Fig S11-E-H). We provide a summary of the above results:

      #

      Metabolic Pathway

      Experiment

      MIC26____ KO

      MIC27____ KO

      MIC19____ KO

      1

      Glycolysis

      Glycolysis stress kit

      Glycolytic reserve increased

      Glycolytic reserve unchanged

      Glycolytic reserve unchanged

      2A

      Lipid Metabolism

      LD number

      General increase

      No consistent increase in treatment with and without palmitate in normoglycemia and hyperglycemia

      No consistent increase in treatment with and without palmitate in normoglycemia and hyperglycemia

      2B

      Lipid Metabolism

      LD (BODIPY) intensities

      Presence of antagonistic regulation of LD content

      Presence of antagonistic regulation of LD content

      Absence of antagonistic regulation of LD content

      3

      Glutamine oxidation

      Mito flex fuel test

      No dependency

      Dependent

      Dependent

      4

      Steady-state respiration

      Mito stress test

      Basal respiration increased

      Basal respiration unchanged

      Basal respiration unchanged

      5

      Steady-state respiration

      Mito stress test

      SRC decreased in normoglycemia

      SRC unchanged

      SRC unchanged

      Taking the above summary, we investigated three possibilities considering the role of MIC26:

      1. General role of MICOS – whether deletion of any MICOS protein leads to similar phenotype as MIC26 deletion

      2. Specific role of MIC26/27/10 subcomplex – whether deletion of any other protein in the MIC26-subcomplex like MIC27 leads to similar results, accompanied by dissimilar results in KOs of any protein belonging to the other MICOS subcomplex (MI19/MIC25/MIC60) and whose protein levels were not changed upon hyperglycemia treatment (MIC19 or MIC60 KOs).

      3. MICOS-independent role of MIC26. Considering the various metabolic pathways analysed, we conclude that MIC26 has a MICOS-independent role in regulating major cellular pathways.

      Minor Comments 1. The multiomics data as presented in Figure 2 is difficult to interpret. This is mainly driven by the fact that there are mulitpe comparisons that should be communicated (KO v WT, normoglycemia v hyperglycemia, upregulated v. downregulated), but only select enrichment values are shown (e.g., normoglycemia upregulated in 2C and hyperglycemia downregulated in 2D). It took me a long time as a reader to understand what I was looking at because only select analyses are presented. What pathways are upregulated in hyperglycemia in MIC26 KO v. WT?

      __Response: __Thank you for pointing this out. We have now represented all the four conditions regarding enrichment analysis as suggested. The antagonistic metabolic regulation is only observed in MIC26 KO cells cultured in normoglycemia (upregulated) when compared to MIC26 KOs cells cultured in hyperglycemia (downregulated). When MIC26 KOs cultured in hyperglycemia (upregulated) were compared with MIC26 KOs cultured in normoglycemia (downregulated), there were also few pathways which showed an antagonistic regulation, but not directly involved with metabolism, relating to apoptosis etc. Hence, we did not focus on these pathways in the current manuscript.

      The Treemaps have been shifted to Fig S1. All four Treemaps have been represented instead of the two shown before. In the process, the previous proteomics Fig S1B and S1C depicting antagonism in different pathways have been excluded.

      2. Figure 3 would be stronger if expression from all glycolytic proteins were shown instead of only a subset. If the authors are making the claim that MIC26 KO increases glycolytic flux via protein-level upregulation of glycolysis, this could be substantiated at a pathway level. These data could be included in supplemental data if they are difficult to fit into the figure.

      __Response: __Thank you. We have now included the data of proteins regulating glycolysis as a new figure (Fig S3C). MIC26 KO cells cultured in normoglycemia had increased levels of aldolase (ALDOA & ALDOC), phosphoglycerate kinase (PGK1) and pyruvate kinase (PKM & PKLR) when compared to control cells. We have included this data in the manuscript.

      3. In Figure 4H-J - the raw data for the Seahorse traces should be shown, and OCR should be reported in pmol/min rather than relative percentages so as to help the reader more critically evaluate the data.

      __Response: __For the FAO assays, we treat the cells with palmitate or mock (BSA serving as control). The histograms (Fig 4H-J) are represented as such because we normalised the oxygen consumption after palmitate treatment with oxygen consumption of mock-treated cells. We understand the reviewer’s concern and have now included the absolute values of oxygen consumption of FAO assay in an excel sheet (Supplementary Table S5). In addition, we have also included the absolute values for mito stress test and glycolysis assays where the oxygen consumption has been normalised to WT-normoglycemia condition (Supplementary Table S5). The original oxygen consumption curves for glycolysis stress kit (Fig 3E, S5A) and mito stress kits (Fig 7E, S11E) are shown as figures.

      4. The majority of the plots are shown with 4 comparisons, but statistical comparisons are often only provided for a subset of comparisons. It is unclear whether statistics were compared across all comparisons and the non-annotated comparisons are not significant, or whether those calculations were not performed. Defining this in the figure, or, better, annotating all relevant comparisons on each graph with "ns" for not significant, would assist the reader with interpreting the data.

      __Response: __Thanks for pointing this out. After comparing all meaningful conditions (except WT-N to MIC26 KO-H and WT-H to MIC26 KO-N), only those that were significant were represented using asterisks. We have now mentioned this information in the respective figure legends. We avoided using ‘non-significant (ns)’ in the figure as it would make some figures very crowded as seen from some of our trials.

      Reviewer #2 (Significance (Required)):

      This study broadly profiles the metabolic defects associated with loss of the MICOS subunit MIC26 in hepatocellular carcinoma cells in variable nutrient conditions (e.g., high glucose and low glucose). As a reviewer with expertise in multiomic profiling of metabolic models, I found the breadth of pathways studied in this manuscript to be impressive. Furthermore, the authors use a variety of techniques, including multiomic profiling, isotopic flux analysis, and functional Seahorse assays to support their conclusions. The study provides a comprehensive analysis of metabolic changes associated with MIC26, and is thus an important advance in profiling how loss of MIC26 (or MICOS in general; see below) affects cellular metabolism in the context of dynamic nutrient changes. However, the claim that "MIC26 is a metabolic rheostat regulating central cellular fuel pathways", as is proposed in the title of the manuscript, is unsubstantiated, as the authors do not test whether loss of MIC26 specifically influences cellular metabolism independent of its role in MICOS. This paper would be significantly strengthened if a subset of functional assays across metabolic pathways were repeated with other MICOS KO cell lines to delineate whether these metabolic effects are direct or indirect.

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

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      Referee #2

      Evidence, reproducibility and clarity

      Summary

      This study determines the role of MIC26, a mitochondrial component of the MICOS complex, in influencing cellular metabolic status. Using a variety of multiomic profiling techniques, as well as functional assays such as Seahorse-based respirometry, the authors propose that MIC26 regulates a variety of metabolic processes, including lipid and cholesterol homeostasis, glycolysis, fatty acid oxidation, fatty acid synthesis, TCA cycle homeostasis, glutamine metabolism, and general mitochondrial bioenergetics via OxPhos activity and supercomplex formation. The data were generated in MIC26 knockout HepG2 hepatocellular carcinoma cells grown in two nutrient conditions: high glucose (which they term "hyperglycemia") and low glucose (which they term "normoglycemia") DMEM. While the data support the authors' conclusion that loss of MIC26 causes braod metabolic changes across these conditions, the authors do not distinguish whether MIC26 knockout affects metabolism due to its canonical role in MICOS, or whether it acts as "a metabolic rheostat" to directly regulate central cellular fuel pathways, as is claimed in the title of this manuscript. Given the breadth of metabolic alterations seen in the MIC26 KO cells, it seems likely that at least a subset of these changes are indirect, rather than that MIC26 plays a direct regulatory role in the eight distinct metabolic pathways outlined above. Thus, while the data generally support the conclusion that expression of MIC26 is important for metabolic homeostasis, the mechanism(s) by which MIC26 influences cellular metabolism remains unclear and should be further addressed.

      Major Comments

      1. The authors infer that MIC26 influences cellular metabolism by referencing a handful of papers on MIC26 transcript differences in select metabolic models, metabolic alterations seen in a MIC26 transgenic/overexpression mouse model, or metabolic effects seen due to MIC26 tissue specific KO models. They thus hypothesize that "MIC26 has an unidentified regulatory role under nutrient-enriched conditions" (line 88). They support this observation by showing that MIC26 is increased in high glucose DMEM relative to low glucose DMEM in Figure 1. However, the authors claim, in both the figure legend title as well as the results section header, that "MIC26 is selectively increased in cells exposed to hyperglycemia" (lines 103-4), when their data demonstrate that this is not true. Figure 1B shows that MIC27, MIC26, and MIC25 increase in high glucose relative to low glucose conditions, indicating that MIC26 is not selectively increased, but rather that multiple subunits of MICOS are increased under nutrient-enriched conditions. This does not suggest that MIC26 does not have an important role in maintaining metabolism under such nutrient conditions, but rather supports a model in which MICOS itself dynamically responds to altered nutrient conditions in cell culture. Interestingly, other MICOS subunits do not change in abundance (e.g., MIC19 and MIC60), which have previously been associated with a separate MICOS subcomplex than MIC26 in yeast (PMID: 33053165). These data may suggest that the nutrient responsive behavior of MIC26 may be due to its assembly within this specific MICOS subcomplex, rather than an independent "unidentified regulatory role under nutrient-enriched conditions".

      To test this, the authors should repeat a subset of functional assays (perhaps the Seahorse metabolic assays) in other MICOS deletion cell lines, including one that dynamically changes in expression in a similar manner to MIC26 (e.g., MIC27 KO or MIC25 KO) and one that does not dynamically change in expression in high glucose conditions (e.g., MIC60 or MIC13). In these sets of experiments the authors will be able to distinguish three possibilities:

      Model 1: if MICOS in general affects metabolic pathways, similar results will be seen for all MICOS subunit KOS.

      Model 2: if the MIC26-specific subcomplex is dynamically regulated to influence cellular metabolism, KO of MIC26 and other subunits of this subcomplex should show similar results, but KO of subunits of the non-dynamic subcomplex (e.g., MIC60) would not show similar phenotypes.

      Model 3: If only MIC26 KO, but not other MICOS subunits, show metabolic phenotypes, this would support a MICOS-independent role for MIC26 in influencing cellular metabolism.

      Importantly, any of these models are interesting, and testing these models does not invalidate any of the phenotypes presented in the manuscript. Rather, these experiments would assist the reader in understanding the underlying mechanism by which MIC26 loss causes cellular metabolic defects. Furthermore, it is worth stating that performing all experiments with multiple other MICOS cell lines is beyond the scope of the manuscript, but testing effects in select (preferably functional) assays, such as the glycolysis stress test (Fig 3E), FAO Seahorse (Fig 3H-J) glutamine oxidation (Fig 6B), and general stress test (Fig 7E) would be appropriate. Other more defined and easily achievable experiments could also be used to support these claims (e.g., western blots probing for levels of key metabolic regulators).

      Minor Comments

      1. The multiomics data as presented in Figure 2 is difficult to interpret. This is mainly driven by the fact that there are mulitpe comparisons that should be communicated (KO v WT, normoglycemia v hyperglycemia, upregulated v. downregulated), but only select enrichment values are shown (e.g., normoglycemia upregulated in 2C and hyperglycemia downregulated in 2D). It took me a long time as a reader to understand what I was looking at because only select analyses are presented. What pathways are upregulated in hyperglycemia in MIC26 KO v. WT?
      2. Figure 3 would be stronger if expression from all glycolytic proteins were shown instead of only a subset. If the authors are making the claim that MIC26 KO increases glycolytic flux via protein-level upregulation of glycolysis, this could be substantiated at a pathway level. These data could be included in supplemental data if they are difficult to fit into the figure.
      3. In Figure 4H-J - the raw data for the Seahorse traces should be shown, and OCR should be reported in pmol/min rather than relative percentages so as to help the reader more critically evaluate the data.
      4. The majority of the plots are shown with 4 comparisons, but statistical comparisons are often only provided for a subset of comparisons. It is unclear whether statistics were compared across all comparisons and the non-annotated comparisons are not significant, or whether those calculations were not performed. Defining this in the figure, or, better, annotating all relevant comparisons on each graph with "ns" for not significant, would assist the reader with interpreting the data.

      Significance

      This study broadly profiles the metabolic defects associated with loss of the MICOS subunit MIC26 in hepatocellular carcinoma cells in variable nutrient conditions (e.g., high glucose and low glucose). As a reviewer with expertise in multiomic profiling of metabolic models, I found the breadth of pathways studied in this manuscript to be impressive. Furthermore, the authors use a variety of techniques, including multiomic profiling, isotopic flux analysis, and functional Seahorse assays to support their conclusions. The study provides a comprehensive analysis of metabolic changes associated with MIC26, and is thus an important advance in profiling how loss of MIC26 (or MICOS in general; see below) affects cellular metabolism in the context of dynamic nutrient changes. However, the claim that "MIC26 is a metabolic rheostat regulating central cellular fuel pathways", as is proposed in the title of the manuscript, is unsubstantiated, as the authors do not test whether loss of MIC26 specifically influences cellular metabolism independent of its role in MICOS. This paper would be significantly strengthened if a subset of functional assays across metabolic pathways were repeated with other MICOS KO cell lines to delineate whether these metabolic effects are direct or indirect.

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

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      MIC26 is a subunit of the 'mitochondrial contact site and cristae organizing system' (MICOS) complex required for crista junction (CJ) formation and was functionally linked to diabetes and modulation of lipid metabolism. In order to understand the role of MIC26 in metabolism, the authors generated MIC26-KO HepG2 cells and investigated the pathways regulated by MIC26 under normo- and hyper-glycemic culture conditions. They employed a multi-omics approach that include transcriptomics, proteomics, targeted metabolomics, and functional assays to document the changes in mRNAs, proteins, and metabolites as a result of MIC26 deletion. Through bioinformatic analyses, they showed that the function of MIC26 is critical in various pathways regulating fatty acid synthesis, oxidation, cholesterol metabolism, and glycolysis. Interestingly, they found an entirely antagonistic effect of lipogenesis in MIC26-KO cells compared to WT cells depending on the glucose concentration of the culture media. In addition, they showed that MIC26 deletion led to a major metabolic rewiring of glutamine utilization as well as oxidative phosphorylation.

      Major comments:

      This is basically a descriptive study that document the transcriptomic, proteomic, and metabolic consequences of lacking MIC26 in normal or high glucose environment. It is data rich but insight poor. The connections between MIC26 as a subunit of MICOS complex and all those metabolic pathways are so tenuous that it is hard to see what to follow up after.

      In the Results section (page 5, line 114-123), the description of the Western blot (WB) analysis appears inconsistent with several blot images of Fig. 1A, which makes the result unconvincing. The authors should select appropriate representative WB images, assuming they have them, to support their claim.

      Minor comments:

      As the functional role of MIC26 in metabolism is the primary focus, the authors should present the results in the figures in the order of WT-N, MIC26KO-N, WT-H, MIC26KO-H for easier comparison.

      Significance

      Mitochondria play important roles in metabolism and metabolic disorders. This study generated large amount of data relating to the role of a mitochondrial protein MIC26 in metabolism. Mutations in MIC26 have been associated with mitochondrial myopathy, lactic acidosis, and cognition defects (Beninca et al. 2021) and a lethal progeria-like condition (Peifer-Weib et al. 2023). There is also a connection between MIC26 and metabolic disorders. The results of this study will be of interest to researchers in the fields of mitochodrial diseases and metabolic disorders.

      My field of expertise is mitochondrial disease, proteomics, lipidomics, phospholipid biochemistry.

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      Reply to the reviewers

      Rebuttal_ Preprint- #RC-2023-02144

      First of all we would like to thank the three reviewers for their constructive and positive comments and suggestions, and the time spent in reviewing our manuscript. Their suggestions and comments had contributed to improve our manuscript. We feel the manuscript is much strengthened by this revision.

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

      __Summary:____ __The manuscript by Dabsan et al builds on earlier work of the Igbaria lab, who showed that ER-luminal chaperones can be refluxed into the cytosol (ERCYS) during ER stress, which constitutes a pro-survival pathway potentially used by cancer cells. In the current work, they extent these observations and a role for DNAJB12&14 in ERCYS. The work is interesting and the topic is novel and of great relevance for the proteostasis community. I have a number of technical comments:

      We thank the reviewer for his/her positive comments on our manuscript.


      __Major and minor comments: __

      1- In the description of Figure 2, statistics is only show to compare untreated condition with those treated with Tg or Tm, but no comparison between condition and different proteins. As such, the statement made by the authors "...DNAJB14-silenced cells were only affected in AGR2 but not in DNAJB11 or HYOU1 cytosolic accumulation" cannot be made.

      Answer: We totally agree with the reviewer#1. The aim of this figure is to show that during ER stress, a subset of ER proteins are refluxed to the cytosol. This is happening in cells expressing DNAJB12 and DNAJB14. We are not comparing the identity of the expelled proteins between DNAJB12-KD cells and DNAJB14-KD cells, This is not the scoop of this paper as such the statement was removed.

      2- Figure S2C: D11 seems to increase in the cytosolic fraction after Tm and Tg treatment. However, this is not reflected in the text. The membrane fraction also increases in the DKO. Is the increase of D11 in both cytosol and membrane and indication for a transcriptional induction of this protein by Tm/Tg? Again, the authors are not reflecting on this in their text.

      Answer: We performed qPCR experiments in control, DNAJB12-KD, DNAJB14-KD and in the DNAJB12/DNAJB14 double knock down cells (in both A549 and PC3 cells) to follow the mRNA levels of DNAJB11. As shown in (Figure S2F-S2N), there is no increase in the mRNA levels of DNAJB11, AGR2 or HYOU1 in the different cells in normal (unstressed conditions). Upon ER stress with tunicamycin or thapsigargin there is a little increase in the mRNA levels of HYOU1 and AGR2 but not in DNAJB11 mRNA levels. On the other hand, we also performed western blot analysis and we did not detect any difference between the different knockdown cells when we analyzed the levels of DNAJB11 compared to GAPDH. Those data are now added as (Figure S2F-S2N).

      We must note that although AGR2 and HYOU1 are induced at the mRNA as a result of ER stress, the data with the overexpression of DNAJB12 and DNAJB14 are important as control experiments because when DNAJB12 is overexpressed it doesn’t inducing the ER stress (Figure S3C-S3D). In those conditions there is an increase of the cytosolic accumulation of AGR2, HYOU1 and DNAJB11 despite that there was no induction of AGR2, HYOU1 or DNAJB11 (Figure 3C and Figure 3E, Figure S3, Figure 4, and Figure S4) . Those results argue against the idea that the reflux is a result of protein induction and an increase in the total proteins levels.

      3- Figure 2D: Only p21 is quantified. phospho-p53 and p53 levels are not quantified.


      Answer: We added the quantification of phospho-p53 and the p53 levels to (Figure 2E-G). Additional blots of the P21, phosphor-p53 and p53 now added to FigureS2O.

      4- Figure 2D: There appears to be a labelling error

      Answer: Yes, the labelling error was corrected.

      5- Are there conditions where DNAJB12 would be higher?

      Answer: In some cancer types there is a higher DNAJB12, DNAJB14 and SGTA expression levels that are associated with poor prognosis and reduced survival (New Figure S6E-M). The following were added to the manuscript: “Finally, we tested the effect of DNAJB12, DNAJB14, and SGTA expression levels on the survival of cancer patients. A high copy number of DNAJB12 is an unfavorable marker in colorectal cancer and in head and neck cancer because it is associated with poor prognosis in those patients (Figure S6E). A high copy number of DNAJB12, DNAJB14, and SGTA is associated with poor prognosis in many other cancer types, including colon adenocarcinoma (COAD), acute myeloid leukemia (LAML), adrenocortical carcinoma (ACC), mesothelioma (MESO), and Pheochromocytoma and paraganglioma (PCPG) (Figure S6F-M). In uveal melanoma (UVM), a high copy number of the three tested genes, DNAJB12, DNAJB14, and SGTA, are associated with poor prognosis and poor survival (Figure S6I, S6J, and S6M). The high copy number of DNAJB12, DNAJB14, and SGTA is also associated with poor prognosis in many other cancer types but with low significant scores. More data is needed to make significant differences (TCGA database). We suggest that the high expression of DNAJB12/14 and SGTA in those cancer types may account for the poor prognosis by inducing ERCYS and inhibiting pro-apoptotic signaling, increasing cancer cells' fitness.

      6- What do the authors mean by "just by mass action"?

      Answer: Mass action means increasing the amount of the protein (overexpression). We corrected this in the main text to overexpression.

      7- Figure 3C: Should be labelled to indicate membrane and cytosolic fraction. The AGR2 blot in the left part is not publication quality and should be replaced.

      Answer: We added the labelling to indicate cytosolic and membrane fractions to Figure 3C. We re-blotted the AGR2, new blot of AGR2 was added.

      8- What could be the reason for the fact that DNAJB12 is necessary and sufficient for ERCYS, while DNAJB14 is only necessary?

      Answer: Because of their very high homology, we speculate that the two proteins have partial redundancy. Partial because we believe that some of the roles of DNAJB12 cannot be carried by DNAJB14 in its absence. Although they are highly homologous, we expect that they probably have different affinities in recruiting other factors that are necessary for the reflux of proteins.

      We further developed around this point in the discussion and the main text.

      9- Figure 5A: Is the interaction between SGTA and JB12 UPR-independent?HCS70 seems to show only background binding. The interaction of JB12 with SGTA is not convincing. A better blot is needed.

      Answer: In the conditions of Figure 5A, we did not observe any induction of the UPR (Figure S3C-D). Thus, we concluded that in those condition of overexpression, DNAJB12 interacts with SGTA in UPR independent manner.

      We repeated this experiment another 3 times with very high number of cells (2X15cm2 culture dishes for each condition) and instead of coimmunoprecipitating with DNAJB12 antibodies we IP-ed with FLAG-beads, the results are very clear as shown in the new Figure 5A compared to Figure S5A.

      10- Figure 5B: the expression of DNAJB14 was induced by Tg50, but not by Tg25 or Tm. However, the authors have not commented on this. This should be mentioned in the text and discussed.

      Answer: In most of the experiments we did not see an increase in DNAJB14 upon ER stress except in this replicate. To be sure we looked at the DNAJB14 levels upon ER stress by protein and qPCR experiment as shown in new (in the Input of Figure 5 and Figure S5) and (Figure S5H-I). We also added new IP experiments in Figure 5 and Figure S5.

      11- Figure 6A: Why is a double knockdown important at all? DNAJB14 does not seem to do much at all (neither in overexpression nor with single knockdown).

      Answer: the data shows that DNAJB12 can compensate for the lack of DNAJB14 while DNAJB14 can only partially compensate for some of the DNAJB12 functions. DNAJB12 could have higher affinity to recruit other factor needed for the reflux process and thus the impact of DNAJB12 is higher. In summary, neither DNAJB12 or DNAJB14 is essential in the single knockdown which means that they compensate for each other. In the overexpression experiment, it is enough to have the endogenous DNAJB14 for the DNAJB12 activity. When DNAJB14 is overexpressed at very high levels, we believe that it binds to some factors that are needed for proper DNAJB12 activity (Figure 4 showing that the WT-DNAJB14 inhibits ER-stress induced ER protein reflux when overexpressed). We believe that DNAJB14 is important because only when we knock both DNAJB12 and DNAJB14 we see an effect on the ER-protein reflux. DNAJB14 is part of a complex of DNAJB12/HSC70 and DSGTA.

      (DNAJB12 is sufficient while DNAJB14 is not- please refer to point #8 above).

      **Referees cross-commenting**

      I agree with the comments raised by reviewer 1 about the manuscript. I also agree with the points written in this consultation session. In my opinion, the comments of reviewer 2 are phrased in a harsh tone and thus the reviewer reaches the conclusion that there are "serious" problems with this manuscript. However, I think that the authors could address many of the points of this reviewer in a matter of 3 months easily. For instance, it is easy to control for the expression levels of exogenous wild type and mutant D12 and compare it to the endogenous one (point 3). This is a very good point of this reviewer and I agree with this experiment. Likewise, it is easy to provide data about the levels of AGR2 to address the concern whether its synthesis is affected by D12 and D14 overexpression. Again, an excellent suggestion, but no reason for rejecting the story. As for not citing the literature, I think this can also easily be addressed and I am sure that this is just an oversight and no ill intention by the authors. __Overall, I am unable to see why the reviewer reaches such a negative verdict about this work. With proper revisions that might take 3 months, I think the points of all reviewers can be addressed. __

      Reviewer #1 (Significance (Required)):

      Significance: The strength of the work is that it provides further mechanistic insight into a novel cellular phenomenon (ERCYS). The functions for DNAJB12&14 are unprecedented and therefore of great interest for the proteostasis community. Potentially, the work is also of interest for cancer researchers, who might capitalize of the ERCYS to establish DNAJB12/14 as novel therapeutic targets. The major weaknesses are as follows: (i) the work is limited to a single cell line. To better probe the cancer relevance, the work should have used at least a panel of cell lines from one (or more) cancer entity. Ideally even data from patient derived samples would have been nice. Having said this, I also appreciate that the work is primarily in the field of cell biology and the cancer-centric work could be done by others. Certainly, the current work could inspire cancer specialists to explore the relevance of ERCYS. (ii) No physiological or pathological condition is shown where DNAJB12 is induced or depleted.

      Answer: We previously showed that ERCYS is conserved in many different cell lines including A549, MCF7, GL-261, U87, HEK293T, MRC5 and others and is also conserved in murine models of GBM (GL-261 and U87 derived tumors) and human patients with GBM (Sicari et al. 2021). Here, we tested the reflux process and the IP experiments in many different cell lines including A549, MCF-7, PC3 and Trex-293 cells. We also added new fractionation experiment in DNAJB12 and DNAJB14 -depleted MCF-7, PC3 and A549 cells. We added all those data to the revised version.

      We also added survival curves from the TCGA database showing that high copy number of DNAB12, DNAJB14 and SGTA are associated with poor prognosis compared to conditions where DNAJB12, DNAJB14, and SGTA are at low copy number (Figure S6E-M). Finally, we included immunofluorescent experiment to show that the interaction between the refluxed AGR2 and the cytosolic SGTA occurs in tumors collected from patients with colorectal cancer patients (Figure S5F-G) compared to non-cancerous tissue.

      This study is highly significant and is relevant not only to cancer but for other pathways that may behave in similar manner. For instance, DNAJB12 and DNAJB14 are part of the mechanism that is used by non-envelope viruses to escape the ER to the cytosol. Thus, the role of those DNAJB proteins seems to be mainly in the reflux of functional (not misfolded) proteins from the ER to the cytosol. We reported earlier that the UDP-Glucose-Glucosyl Transferase 1 (UGGT1) is also expelled during ER stress. UGGT1 is important because it is redeploy to the cytosol during enterovirus A71 (EA71) infection to help viral RNA synthesis (Huang et al, 2017). This redeployment of EAA71 is similar to what happens during the reflux process because on one hand, UGGT1 exit the ER by an ER stress mediated process (Sicari et al. 2021) and it is also a functional in the cytosol as a proteins which help viral RNA synthesis ((Huang et al, 2017). All those data showing that there is more of DNAJB12, DNAJB14, DNAJC14, DNAJC30 and DNAJC18 that still needs to be explored in addition to what is published. Thus, we suggest that viruses hijacked this evolutionary conserved machinery and succeeded to use it in order to escape the ER to the cytosol in a manner that depends on all the component needed for ER protein reflux.

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

      The authors present a study in which they ascribe a role for a complex containing DNAJB12/14-Hsc70-SGTA in facilitating reflux of a AGR2 from the ER to cytosol during ER-stress. This function is proposed to inhibit wt-P53 during ER-stress.

      Concerns: 1. The way the manuscript is written gives the impression that this is the first study about mammalian homologs of yeast HLJ1, while there are instead multiple published papers on mammalian orthologs of HLJ1. Section 1 and Figure 1 of the results section is redundant with a collection of previously published manuscripts and reviews. The lack of proper citation and discussion of previous literature prevents the reader from evaluating the results presented here, compared to those in the literature.

      Answer: We highly appreciate the reviewer’s comments. This paper is not to show that DNAJB12 and DNAJB14 are the orthologues of HLJ-1 but rather to show that DNAJB12 and DNAJB14 are part of a mechanism that we recently discovered and called ERCYS that cause proteins to be refluxed out of the ER. A mechanism that is regulated in by HLJ-1 in yeast. ERCYS is an adaptive and pro-survival mechanism that results in increased chemoresistance and survival in cancer cells. The papers that reviewer #2 refer to are the ones that report DNAJB12 can replace some of the ER-Associated Degradation (ERAD) functions of HLJ-1 in degradation of membranal proteins such as CFTR. These two mechanism are totally different and the role of the yeast HLJ-1 in degradation of CFTR is not needed for ERCYS. This is because we previously showed that the role of the yeast HLJ-1 and probably its orthologues in ERCYS is independent of their activity in ERAD(Igbaria et al. 2019). Surprisingly, the role of HLJ-1 in refluxing the ER proteins is not only independent of the reported ERAD-functions of HLJ1 and the mammalian DNAJBs but rather proceeds more rigorously when the ERAD is crippled (Igbaria et al. 2019). This role of DNAJBs is unique in cancer cells and is responsible in regulating the activity of p53 during the treatment of DNA damage agents.

      In our current manuscript we show by similarity, functionality, and topological orientation, that DNAJB12 and DNJB14 may be part of a well conserved mechanism to reflux proteins from the ER to the cytosol. A mechanism that is independent of DNAJB12/14’s reported activity in ERAD(Grove et al. 2011; Yamamoto et al. 2010; Youker et al. 2004). In addition, DNAJB12 and DNAJB14 facilitate the escape of non-envelope viruses from the ER to the cytosol in similar way to the reflux process(Goodwin et al. 2011; Igbaria et al. 2019; Sicari et al. 2021). All those data show that HLJ-1 reported function may be only the beginning of our understanding on the role that those orthologues carry and that are different from what is known about their ERAD function.

      Action: We added the references to the main text and discussed the differences between the reported DNAJB12 and HLJ-1 functions to the function of DNAJB12, DNAJB14 and the other DNAJ proteins in the reflux process. We also developed around this in the discussion.

      The conditions used to study DNAJB12 and DNAJ14 function in AGR2 reflux from the ER do not appear to be of physiological relevance. As seen below they involve two transfections and treatment with two cytotoxic drugs over a period of 42 hours. The assay for ERCY is accumulation of lumenal ER proteins in a cytosolic fraction. Yet, there is no data or controls that describe the path taken by AGR2 from the ER to cytosol. It seems like pleotropic damage to the ER due the experimental conditions and accompanying cell death could account for the reported results?

      Transfection of cells with siRNA for DNAJB12 or DNAJB14 with a subsequent 24-hour growth period.

      Transfection of cells with a p53-lucifease reporter.

      Treatment of cells with etoposide for 2-hours to inhibit DNA synthesis and induce p53. D. Treatment of cells for 16 hours with tunicamycin to inhibit addition of N-linked glycans to secretory proteins and cause ER-stress.

      Subcellular fractionation to determine the localization of AGR2, DNAJB11, and HYOU1

      KD of DNAJB12 or DNAJB14 have modest if any impact on AGR2 accumulation in the cytosol. There is an effect of the double KD of DNAJB12 or DNAJB14 on AGR2 accumulation in the cytosol. Yet there are no western blots showing AGR2 levels in the different cells, so it is possible that AGR2 is not synthesized in cells lacking DNAJB12 and DNAKB14. The lack of controls showing the impact of single and double KD or DNAJB12 and DNAJB14 on cell viability and ER-homeostasis make it difficult to interpret the result presented. How many control versus siRNA KD cells survive the protocol used in these assays?


      Answer: Despite the long protocol we see differences between the control cells and the DNAJB-silenced cells in terms of the quantity of the refluxed proteins to the cytosol. The luciferase construct was used to assess the activity of p53 so the step of the second transfection was used only in experiments were we assayed the p53-luciferase activity. The rest of the experiments especially those where we tested the levels of p53 and P21 levels, were performed with one transfection. Moreover, all the experiments with the subcellular protein fractionation were performed after one transfection without the second transfection of the p53-Luciferase reporter. Finally, the protocol of the subcellular protein fractionation requires first to trypsinize the cells to lift them up from the plates, at the time of the experiment the cells were almost at 70-80% confluency and in the right morphology under the microscope.

      Here, we performed XTT assay and Caspase-3 assay to asses cell death at the end of the experiment and before the fractionation assay. We did not observe any differences at this stage between the different cell lines (Figure-RV1 for reviewers Only). This can be explained by the fact that we use low concentrations of Tm and Tg for short time of 16 hour after the pulse of etoposide.

      Finally, the claim that and ER-membrane damage result in a mix between the ER and cytosolic components is not true for the following reasons: (1) In case of mixing we would expect that GAPDH levels in the membrane fraction will be increased and that we do not see, and (2) we used our previously described transmembrane-eroGFP (TM-eroGFP) that harbors a transmembrane domain and is attached to the ER membrane facing the ER lumen. The TM-eroGFP was found to be oxidized in all conditions tested. Those data argue against a rupture of the ER membrane which can results in a mix of the highly reducing cytosolic environment with the highly oxidizing ER environment by the passage of the tripeptide GSH from the cytosol to the ER. All those data argue against (1) cell death, and (2) rupture of the ER membrane. Figure RV1 Reviewers Only.

      Moreover, as it is shown in Figure S2, AGR2 is found in the membrane fraction in all the four different knock downs, thus it is synthesized in all of them. Moreover, we assayed the mRNA levels of AGR2 in all the knockdowns and we so that they are at the same levels in all the 4 different conditions and still AGR2 mRNA levels increase upon ER stress in all of the 4 knockdown cells in different backgrounds (Figure S2F-N).

      In Figure 3 the authors overexpress WT-D12 and H139Q-D12 and examine induction of the p53-reporter. There are no western blots showing the expression levels of WT-D12 and H139Q-D12 relative to endogenous DNAJB12. HLJ1 stands for high-copy lethal DnaJ1 as overexpression of HLJ1 kills yeast. The authors present no controls showing that WT-D12 and H139-D12 are not expressed at toxic levels, so the data presented is difficult to evaluate.

      Answer: The expression levels of the overexpression of DNAJB12 and DNAJB14 were present in the initial submission of the manuscript as Figure S3A and S3B. The data showing the relationship between the expression degree and the viability were also included in the initial submission as Figure S3C (Now S3H).

      There is no mechanistic data used to help explain the putative role DNAJB12 and DNAJB14 in ERCY? In Figure 4, why does H139Q JB12 prevent accumulation of AGR2 in the cytosol? There are no westerns showing the level to which DNAJB12 and DNAJB14 are overexpressed.


      Answer: The data showing the levels of DNAJB12 compared to the endogenous were present in the initial submission as Figure S3A and S3B.

      We suggest a mechanism by which DNAJB12 and DNAJB14 interact (Figure 5 and Figure S5) and oligomerize to expel those proteins in similar way to expelling non-envelope viruses to the cytosol. Thus, when expressing the mutant DNAJB12 H139Q may indicate that the J-domain dead-mutant can still be part of the complex but affects the J-domain activity in this oligomer and thus inhibit ER-protein reflux. In other words, we showed that the H139Q exhibits a dominant negative effect when overexpressed. Moreover, here we added another IP experiment in the D12/D14-DKD cells to show that in the absence of DNAJB12 and DNAJB14, SGTA cannot bind the ER-lumenal proteins because they are not refluxed (Figure 5 and Figure S5). Those data indicate that in order for SGTA bind the refluxed proteins they have to go through the DNAJB12 and DNAJB14 and their absence this interaction does not occur. This explanation was also present in the discussion of the initial submission.

      Mechanistically, we show that AGR2 interacts with DNAJB12/14 which are necessary for its reflux. This mechanism involves the functionality of cytosolic HSP70 chaperones and their cochaperones (SGTA) proteins that are recruited by DNAJB12 and 14. This mechanism is conserved from yeast to mammals. Moreover, by using the alpha-fold prediction tools, we found that AGR2 is predicted to interact with SGTA in the cytosol by the interaction between the cysteines of SGTA and AGR2 in a redox-dependent manner.

      **Referees cross-commenting**

      __ __ I appreciate the comments of the other reviewers. I agree that the authors could revise the manuscript. Yet, based on my concerns about the physiological significance of the process under study and lack of scholarship in the original draft, I would not agree to review a revised version of the paper.

      Answer: Regards the physiological relevance, we showed in our previous study (Sicari et al. 2021) how relevant is ERCYS in human patients of GBM and murine model of GBM. ERCYS is conserved from yeast to human and is constitutively active in GL-261 GBM model, U87 GBM model and human patients with GBM (Sicari et al. 2021). Here, extended that to other tumors and showed that DNAJB12, DNAJB14 and SGTA high levels are associated with poor prognosis in many cancer types (Figure S6). We also show some data from to show the relevance and added data showing the interaction of SGTA with AGR2 in CRC samples obtained from human patients compared to healthy tissue (Figure S5). This study is highly significant and is relevant not only to cancer but for other pathways that may behave in similar manner. For instance, DNAJB12 and DNAJB14 are part of the mechanism that is used by non-envelope viruses to escape the ER to the cytosol. Thus, the role of those DNAJB proteins seems to be mainly in the reflux of functional (not misfolded) proteins from the ER to the cytosol. We reported earlier that the UDP-Glucose-Glucosyl Transferase 1 (UGGT1) is also expelled during ER stress. UGGT1 is important because it is redeploy to the cytosol during enterovirus A71 (EA71) infection to help viral RNA synthesis (Huang et al, 2017). This redeployment of EAA71 is similar to what happens during the reflux process because on one hand, UGGT1 exit the ER by an ER stress mediated process (Sicari et al. 2021) and it is also a functional in the cytosol as a proteins which help viral RNA synthesis ((Huang et al, 2017). All those data showing that there is more of DNAJB12, DNAJB14, DNAJC14, DNAJC30 and DNAJC18 that still needs to be explored in addition to what is published. We suggest that viruses hijacked this evolutionary conserved machinery and succeeded to use it in order to escape.

      We appreciate the time spent to review our paper and we are sorry that the reviewer reached such verdict that is also not understood by the other reviewers. Most of the points raised by reviewer 2 were already addressed and explained in the initial submission, anyways we appreciate the time and the comments of reviewer #2 on our manuscript.

      Reviewer #2 (Significance (Required)):

      Overall, there are serious concerns about the writing of this paper as it gives the impression that it is the first study on higher eukaryotic and mammalian homologs of yeast HLJ1. The reader is not given the ability to compare the presented data to related published work. There are also serious concerns about the quality of the data presented and the physiological significance of the process under study. In its present form, this work does not appear suitable for publication.

      Answer: Again we thank reviewer #2 for giving us the opportunity to explain how significant is this manuscript especially for people who are less expert in this field. The significance of this paper (1) showing a the unique role of DNAJB12 and DNAJB14 in the molecular mechanism of the reflux process in mammalian cells (not their role in ERAD), (2) showing the implication of other cytosolic chaperones in the process including HSC70 and SGTA (3), our alpha-fold prediction show that this process may be redox dependent that implicate the cysteines of SGTA in extracting the ER proteins, (4) overexpression of the WT DNAJB12 is sufficient to drive this process, (5) mutation in the HPD motif prevent the reflux process probably by preventing the binding to the cytosolic chaperones, and (6) we need both DNAJB12 and DNAJB14 in order to make the interaction between the refluxed ER-proteins and the cytosolic chaperones occur.

      In Summary, this study is highly significant in terms of physiology, we previously reported that ERCYS is conserved in mammalian cells and is constitutively active in human and murine tumors (Sicari et al. 2021). Moreover, DNAJB12 and DNAJB14 are part of the mechanism that is used by non-envelope viruses to escape the ER to the cytosol in a mechanism that is similar to reflux process (Goodwin et al. 2011; Goodwin et al. 2014). Thus, the role of those DNAJB proteins seems to be mainly in the reflux of functional proteins from the ER to the cytosol, viruses used this evolutionary conserved machinery and succeeded to use in order to escape. This paper does not deal with the functional orthologues of the HLJ-1 in ERAD but rather suggesting a mechanism by which soluble proteins exit the ER to the cytosol.

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

      Summary: Reflux of ER based proteins to the cytosol during ER stress inhibits wt-p53. This is a pro-survival mechanism during ER stress, but as ER stress is high in many cancers, it also promotes survival of cancer cells. Using A549 cells, Dabsan et al. demonstrate that this mechanism is conserved from yeast to mammalian cells, and identify DNAJB12 and DNAJB14 as putative mammalian orthologues of yeast HLJ1.

      This paper shows that DNAJB12 and 14 are likely orthologues of HLJ1 based on their sequences, and their behaviour. The paper develops the pathway of ER-stress > protein reflux > cytosolic interactions > inhibition of p53. The authors demonstrate this nicely using knock downs of DNAJB12 and/or 14 that partially blocks protein reflux and p53 inhibition. Overexpression of WT DNAJB12, but not the J-domain inactive mutant, blocks etoposide-induced p53 activation (this is not replicated with DNAJB14) and ER-resident protein reflux. The authors then show that DNAJB12/14 interact with refluxed ER-resident proteins and cytosolic SGTA, which importantly, they show interacts with the ER-resident proteins AGR2, PRDX4 and DNAJB11. Finally, the authors show that inducing ER stress in cancer cell lines can increase proliferation (lost by etoposide treatment), and that this is partially dependent on DNAJB12/14.

      This is a very interesting paper that describes a nice mechanism linking ER-stress to inhibition of p53 and thus survival in the face of ER-stress, which is a double edged sword regarding normal v cancerous cells. The data is normally good, but the conclusions drawn oversimplify the data that can be quite complex. The paper opens a lot of questions that the authors may want to develop in more detail (non-experimentally) to work on these areas in the future, or alternatively to develop experimentally and develop the observations further. There are only a few experimental comments that I make that I think should be done to publish this paper, to increase robustness of the work already here, the rest are optional for developing the paper further.

      We thank the reviewer for his/her positive comments His/her comments contributed to make our manuscript stronger.

      __Major comments:____ __

      1. Number of experimental repeats must be mentioned in the figure legends. Figures and annotations need to be aligned properly

      __Answer____: __All experiments were repeated at least 3 times. We added the number of repeats on each figure in the figures legends

      Results section 2:

      No intro to the proteins you've looked at for relocalization. Would be useful to have some info on why you chose AGR2. Apart from them being ER-localized, do they all share another common characteristic? Does ability to inhibit p53 vary in potency?

      Answer: We previously showed that AGR2 is refluxed from the ER to the cytosol to bind and inhibit wt-p53 (Sicari et al. 2021). Here, we used AGR2 because, (1) we know that AGR2 is refluxed from the ER to the cytosol, and (2) we know which novel functions it gains in the cytosol so we are able to measure and provide a physiological significance of those novel functions when the levels of DNAJB12 and DNAJB14 are altered. Moreover, we used DNAJB11 (41 kDa) and HYOU1 (150 kDa) proteins to show that alteration in DNAJB12 or DNAJB14 prevent the reflux small, medium and large sized proteins. We added a sentence in the discussion stating that DNAJB12/14 are responsible for the reflux of ER-resident proteins independently of their size. We also added in the result section that we are looking at proteins of different sizes and activities.


      What are the roles of DNAJB12/14 if overexpression can induce reflux? Does it allow increased binding of an already cytosolic protein, causing an overall increase in an interaction that then causes inhibition of p53? What are your suggested mechanisms?

      Answer: Previously it was reported that over-expression of DNAJB12 and DNAJB14 tend to form membranous structures within cell nuclei, which was designate as DJANGOS for DNAJ-associated nuclear globular structures(Goodwin et al. 2014). Because those structures which contain both DNAJB12 and DNAJB14 also form on the ER membrane (Goodwin et al. 2014), we speculate that during stress DNAJB12/14 overexpression may facilitate ERCYS. Interestingly, those structures contain Hsc70 and markers of the ER lumen, the nuclear and ER and nuclear membranes (Goodwin et al. 2014).

      The discussion was edited accordingly to further strengthen and clarify this point

      Fig3: A+B show overexpression of individual DNAJs but not combined. As you go on to discuss the effect of the combination on AGR2 reflux, it would be useful to include this experimentally here.

      Answer: This is a great idea, we tried to do it for long time. Unfortunately when we used cells overexpress DNAJB12 under the doxycycline promoter and transfect with DNAJB14 plasmid expressing DNAJB14 under the CMV promoter, most of the cells float within 24 hours compared to cells transfected with the empty vector alone or with DNAJB14-H136Q. We also did overexpression of DNAJB14 in cells with DNAJB12 conditional expression and also were lethal in Trex293T cells and A549-cells.

      Fig 3C: Subfractionation of cells shows AGR2 in the cytosol of A549 cells. The quality of the data is good but the bands are very high on the blot. For publication is it possible to show this band more centralized so that we are sure that we are not missing bands cut off in the empty and H139Q lanes?

      Also, you have some nice immunofluorescence in the 2021 EMBO reports paper, is it possible to show this by IF too? It is not essential for the story, but it would enrich the figure and support the biochemistry nicely. Also it is notable that the membrane fraction of the refluxed proteins doesn't appear to have a decrease in parallel (especially for AGR2). Is this because the % of the refluxed protein is very small? Is there a transcriptional increase of any of them (the treatments are 12+24 h so it would be enough time)? This could be a nice opportunity to discuss the amount of protein that is refluxed, whether this response is a huge emptying of the ER or more like a gentle release, and also the potency of the gain of function and effect on p53 vs the amount of protein refluxed. This latter part isn't essential but it would be a nice element to expand upon.

      Answer: We re-blotted the AGR2 again, new blot of AGR2 was added. More blots also are added in Figure S2, the text is edited accordingly.

      In new Figure S5 we added immunofluorescence experiment from tumors and non-tumors tissues obtained from Colorectal cancer (CRC) patients showing that the interaction between SGTA and the refluxed AGR2 also occurs in more physiological settings. It is also to emphasize that the suggested mechanism that implicates SGTA is also valid in CRC tumors.

      We performed qPCR experiments in control, DNAJB12-KD, DNAJB14-KD and in the DNAJB12/DNAJB14 double knock down cells (in both A549 and PC3 cells) to follow the mRNA levels of DNAJB11. As shown in the Figure S2F-N, there is no increase in the mRNA levels of DNAJB11, AGR2 or HYOU1 in the different cells in normal (unstressed conditions). Upon ER stress with tunicamycin or thapsigargin there is a little increase in the mRNA levels of HYOU1 and AGR2 but in DNAJB11 mRNA levels. On the other hand, we also performed western blot analysis and we did not detect any difference between the different knockdown cells when we analyzed the levels of DNAJB11 compared to GAPDH. Those data are now added to Figure S2F-N. We must note that in AGR2 and HYOU1 are induced at the mRNA as a result of ER stress. The data with the overexpression of DNAJB12 and DNAJB14 are important control experiment where we show a reflux when DNAJB12 is overexpressed without inducing the ER stress (Figure 3, Figure 4, and Figure S3). In those conditions no induction of AGR2, HYOU1 or DNAJB11 were observed. Those results argue against the reflux as a result of protein induction and the increase in the proteins levels.

      The overall protein levels in steady state are function of how much proteins are made, degraded and probably secreted outside the cell. We do see in Figure S2 under ER stress there are some differences in the levels of the mRNA, moreover, from our work in yeast we showed that the expelled proteins have very long half-life in the cytosol (Igbaria et al. 2019). Because it is difficult to assay how many of the mRNA is translated and how much of it is stable/degraded and the stability of the cytosolic fraction vs the ER, it is hard to interpret on the stability and the levels of the proteins.

      Those data are now added to the manuscript, the text is edited accordingly.

      You still mention DNAJB12 and 14 as orthologues, even though DNAJB14 has no effect on p53 activity when overexpressed. Do you think that this piece of data diminishes this statement?

      Answer: The fact that DNAJB12 and DNAJB14 are highly homologous and that only the double knockdown has a great effect on the reflux process may indicate that they are redundant. Moreover, because only DNAJB12 is sufficient may indicate that some of DNAJB12 function cannot be carried by DNAJB14. In one hand they share common activities as shown in the double knock down and on the other hand DNAJB12 has a unique function that may not be compensated by DNAJB14 when overexpressed.

      __ __ Fig 3D/F: Overexpression of DNAJB14 induces reflux of DNAJB11 at 24h, what does this suggest? Does this indicate having the same role as DNAJB12 but less potently? What's your hypothesis?

      Answer: ERCYS is new and interesting phenomenon and the redistribution of proteins to the cytosol has been documented lately by many groups. Despite that we still do not know what is the specificity of DNAJB12 and DNAJB14 to the refluxed proteins. DNAJB11 is glycosylated protein and now we are testing whether other glycosylated proteins prefer the DNAJB14 pathway or not. This data is beyond the scope of this paper

      "This suggests that the two proteins may have different functions when overexpressed, despite their overlapping and redundant functions" What does it suggest about their dependence on each other? If overexpression of WT DNAJB12 inhibits Tg induced reflux, is it also blocking the ability of DNAJB14 to permit flux?

      Answer: We hypothesize that it is all about the stichometry and the ratios between proteins. When we overexpress DNAJB14 (the one that is not sufficient to cause reflux it may hijack common components and factor by non-specifically binding to them. Those factors may be needed for DNAJB12 to function properly (Like the dominant negative effect of the DNAJB12-HPD mutant for instance). On the other hand, DNAJB12 may have higher affinity for some cytosolic partner and thus can do the job when overexpressed. Here, we deal with the DNAJB12/DNAJB14 as essential components of the reflux process, yet we need to identify the interactome of each of the proteins during stress and the role of the other DNAJ proteins that also share some of the topological and structural similarity to DNAJB12, DNAJB14 and HLJ-1 (DNAJC30, DNAJC14, and DNAJC18). We edited the text accordingly and integrated this in the discussion.

      __ __ Fig 4: PDI shown in blots but not commented on in text. Then included in the schematics. Please comment in the text.

      Answer: We commented PDI in the text.

      Fig 4F: Although the quantifications of the blots look fine, the blot shown does not convincingly demonstrate this data for AGR2. The other proteins look fine, but again it could be useful to see the individual means for each experiment, or the full gels for all replicates in a supplementary figure.

      Answer: the other two repeats are in Figure S4

      __ __Results section 3

      Fig 5A, As there is obviously a difference between DNAJB12/14 it would be useful to do the pulldown with DNAJB14 too. Re. HSC70 binding to DNAJB12 and 14, the abstract states that DNAJB12/14 bind HSC70 and SGTA through their cytosolic J domains. Fig 5 shows pulldowns of DNAJB12 with an increased binding of SGTA in FLAG-DNAJB12 induced conditions, but the HSC70 band does not seem to be enriched in any of the conditions, including after DNAJB12 induction. This doesn't support the statement that DNAJB12 binds HSC70. In fact, in the absence of a good negative control, this would suggest that the HSC70 band seen is not specific. There is also no data to show that DNAJB14 binds HSC70. I recommend including a negative condition (ie beads only) and the data for DNAJB14 pulldown.

      Answer: In Figure 5A we used the Flp-In T-REx-293 cells as it is easier to control and to tune up and down the expression levels of DNAJB12 and DNAJB14. According to new Figure S5A, DNAJB12 binds at the basal levels to HSC70 all the time. It was also surprising for us not to see the differences in the overexpression and we relate that to the fact that all the HSC70 are saturated with DNAJB12. In order to better assay that we repeated the IP in Figure 5A but instead of the IP with DNAJB12, we IP-ed with FLAG antibodies to selectively IP the transfected DNAJB12. As shown in the new Fig 5A, the increase of DNAJB12-FLAG is accompanied with an increase in the binding of HSC70.

      We further tested the interaction between DNAJB12, DNAJB14 and HSC70 during ER stress in cancer cells. In those cells we found that DNAJB12 and DNAJB14 bind to HSC70 and they recruit SGTA upon stress. We also tested the binding between DNAJB12 and DNAJB14, in unstressed conditions, there was a basal binding between both, this interaction was stronger during ER stress. Those data are now added to Figure 5 and Figure S5 and the discussion was edited accordingly.

      The binding of DNAJB12 to SGTA under stress conditions in Fig5B looks much more convincing than SGTA to DNAJB12 in Fig 5A. Bands in all blots need to be quantified from 3 independent experiments, and repeated if not already n=3. If this is solely a technical difference, please explain in the text.

      The conclusions drawn from this interaction data are important and shold be elaborated upon to support th claims made in the paper. The authors may also chose to expand the pulldowns to demonstrate their claims made on olidomerisation of DNAJB12 and 14 here. It is also clear that the interaction data of the SGTA with ER-resident proteins AGR2, PRDX4 and DNAJB11 is strong. The authors may want to draw on this in their hypotheses of the mechanism. I would imagine a complex such as DNAJB14/DNAJB12 - SGTA - AGR2/PRDX4/DNAJB11 would be logical. Have any experiments been performed to prove if complexes like this would form?

      Answer: In Figure 5A we used the Flp-In T-REx-293 cells as it is easier to control and to tune up and down the expression levels of DNAJB12 and DNAJB14. T-REx-293 are highly sensitive to ER stress, they do not die (as we did not observe apoptosis markers to be elevated) but they float and can regrow after the stress is gone. In Figure 5B we are using ER stress without the need to express DNAJB12 in A549 cell line. In order to further verify those data, we repeated the IP in another cell line as well to confirm the data in 5B. We also repeated the IP in 5A with anti-FLAG antibody to improve the IP and to specifically map he interaction with the overexpressed FLAG-DNAJB12 (discussed above). All experiments were done in triplicates and added to Figure 5 and Figure S5.

      We agree with the reviewer on the complex between the refluxed proteins and SGTA. We believed that SGTA may form a complex with other refluxed ER-proteins but we were unable to see an interaction between AGR2-DNAJB11 in the cytosolic fraction or between AGR2-PRDX4 in the conditions tested in the cytosolic fraction. We could not do this in the whole cell lysate because those proteins bind each other in the ER. Finally, our structural prediction using Alpha-fold suggests that the interaction between SGTA and the refluxed AGR2 (and probably others) is redox depending and that it requires disulfide bridge between cysteine 81 on AGR2 and cysteine 153 on SGTA. Thus, we hypothesize that SGTA binds one refluxed protein at the time.

      We repeated the figure with improvement: (1) using more cells in order to increase the amount of IP-ed proteins and to overcome the problem of the faint bands, (2) performing the IP with the FLAG antibodies instead of the DNAJB12 endogenous antibodies.

      Fig 5B: It is clear that DNAJB12 interacts with SGTA. The authors state that DNAJB14 also interacts with SGTA under normal and stress conditions, but the band in 25/50 Tg is very feint. Why would there be stronger binding at the 2 extremes than during low stress induction? In the input, there is a much higher expression of DNAJB14 in 50 Tg. What does this say about the interaction? Is there an effect of ER stress on DNAJB14 expression? A negative control should be included to show any background binding, such as a "beads only" control

      __Answer: __DNAJB14 does not change with ER stress as shown in the Ips (Input) and in the qPCR experiment in Figure S5I. We added beads only control, we also added new Ips to assess the binding between DNAJB14 and DNAJB12, and between DNAJB14-SGTA. All the new Ips and controls now added as Figure 5 and Figure S5.

      Fig 5C data is sound, although a negative control should be included.

      Answer: Negative control was added in Figure S5.

      __Results section 4____ __

      Fig 6A-B: Given that there is the complexity of overexpression v KD of DNAJB12 v 14 causing similar effects on p53 actvity (Fig 2 v 3), it would be interesting to see whether the effect of overexpression mirrors the results in Fig 6A. Is it known what SGTA overexpression does (optional)?

      Answer: In the overexpression system, cells overexpressing DNAJB12 start to die between 24-48 hours as shown in Figure S3C. Thus, it is difficult to assay the proliferation of these cells in those conditions. On the other hand, overexpression of Myc-tagged SGTA in A549 cells, MCF7 or T-ReX293 did not show any reflux of ER-proteins to the cytosol and it didn’t show any significant changes in the proliferation index (Figure Reviewers only RV2).

      Fig 6D: resolution very low

      Answer: Figure 6D was changed

      __ __ Fig 6C-D: There is an interesting difference though between the proposed cytosolic actions of the refluxed proteins. You show that AGR2, PRDX4 and DNAJB11 all bind to SGTA in stress conditions, but in the schematics you show: DNAJB11 binding to HSC70 through SGTA (not shown in the paper), then also PDIA1, PDIA3 binding to SGTA and AGR2 binding to SGTA. What role does SGTA have in these varied reactions? Sometimes it is depicted as an intermediate, sometimes a lone binder, what is its role as a binder? It should be clarified which interactions are demonstrated in the paper (or before) and which are hypothesized in a graphical way (eg. for hypotheses dotted outlines or no solid fill etc). The schematics also suggest that DNAJB14 binding to HSC70 and SGTA is inducible in stress conditions, as is PDIA3, which is not shown in the paper. Discussion "In cancer cells, DNAJB12 and DNAJB14 oligomerize and recruit cytosolic chaperones and cochaperones (HSC70 and SGTA) to reflux AGR2 and other ER-resident proteins and to inhibit wt-p53 and probably different proapoptotic signaling pathways (Figure 5, and Figure 6C-6D)." You havent shown oligomerisation between DNAJB12/14. Modify the text to make it clear that it is a hypothesis.

      Answer: We removed “oligomerize” from the text and added that it as a hypothesis. Figure (C-D) also were changed to be compatible with the text.

      Minor comments:

      __ __ It would be useful to have page or line numbers to help with document navigation, please include them. Typos and inconsistency in how some proteins are named throughout the manuscript

      Answer: Page numbers and line numbers are added. Typos are corrected

      Title: Include reference to reflux. Suggest: "chaperone complexes (?proteins) reflux from the ER to cytosol..." I presume it would be more likely that the proteins go separately rather than in complex. Do you have any ideas on the size range of proteins that can undergo this process?

      Answer: this is true, proteins may cross the ER membrane separately and then be in a complex with cytosolic chaperones. The title is changed accordingly. As discussed earlier, the protein we chose were of different sizes to show that they are refluxed independently of their size. Moreover, our previous work showed that the proteins that were refluxed are of different sizes. Most importantly UGGT1 (around 180 Kda) which is reported to deploy to the cytosol upon viral infection (Huang et al. 2017; Sicari et al. 2020). In this study we used AGR2 (around 19 Kda) and HYOU1 (150Kda).

      ERCY in abstract, ERCYS in intro. There are typos throughout, could be a formatting problem, please check

      Answer: Checked and corrected

      What about the selection of refluxed proteins? Is this only a certain category of proteins? Could it be anything? Have you looked at other cargo / ER resident proteins?

      __ ____Answer: __in our previous study by (Sicari, Pineau et al. 2020) we looked at many other proteins especially glycoproteins from the ER. In (Sicari, Pineau et al. 2020) we used mass spectrometry in order to identify new refluxed proteins and we found 26 new glycoprotein that are refluxed from cells treated with ER stressor and from human tissues obtained from GBM patients (Sicari, Pineau et al. 2020).

      We previously showed that AGR2 is refluxed from the ER to the cytosol to bind and inhibit p53 (Sicari, Pineau et al. 2020). Here, we selected AGR2 because we know that (1) it is refluxed, and (2) we know which novel functions it acquires in the cytosol so we are able to measure and provide a physiological significance of those novel functions when the levels of DNAJB12 and DNAJB14 are altered. Moreover, we selected DNAJB11 (41 kDa) and HYOU1 (150 kDa) proteins to show that alteration in DNAJB12 or DNAJB14 prevent the reflux small, medium and large protein (independently of their size). We also showed earlier by mass spectrometry analysis that the refluxed proteins range from small to very large proteins such as UGGT1, thus we believe that soluble ER-proteins can be substrates of ERCYS independently of their size. In the discussion, we added a note that the reflux by the cytosolic and ER chaperones operates on different proteins independently of their size.

      "Their role in ERCYS and cells' fate determination depends..." Suggest change to "Their role in ERCYS and determination of cell fate..."

      Answer: changed and corrected

      I think that the final sentence of the intro could be made stronger and more concise. There's a repeat of ER and cytosol. Instead could you comment on the reflux permitting new interactions between proteins otherwise spatially separated, then the effect on wt-p53 etc.

      Answer: The sentence was rephrased as suggested to “ In this study, we found that HLJ1 is conserved through evolution and that mammalian cells have five putative functionality orthologs of the yeast HLJ1. Those five DNAJ- proteins (DNAJB12, DNAJB14, DNAJC14, DNAJC18, and DNAJC30) reside within the ER membrane with a J-domain facing the cytosol (Piette et al. 2021; Malinverni et al. 2023). Among those, we found that DNAJB12 and DNAJB14, which are strongly related to the yeast HLJ1 (Grove et al. 2011; Yamamoto et al. 2010), are essential and sufficient for determining cells' fate during ER stress by regulating ERCYS. Their role in ERCYS and determining cells' fate depends on their HPD motif in the J-domain. Downregulation of DNAJB12 and DNAJB14 increases cell toxicity and wt-p53 activity during etoposide treatment. Mechanistically, DNAJB12 and DNAJB14 interact and recruit cytosolic chaperones (HSC70/SGTA) to promote ERCYS. This later interaction is conserved in human tumors including colorectal cancer.

      In summary, we propose a novel mechanism by which ER-soluble proteins are refluxed from the ER to the cytosol, permitting new inhibitory interactions between spatially separated proteins. This mechanism depends on cytosolic and ER chaperones and cochaperones, namely DNAJB12, DNAJB14, SGTA, and HSC70. As a result, the refluxed proteins gain new functions to inhibit the activity of wt-p53 in cancer cells. “

      __Figure legends: __

      In some cases the authors state the number of replicates, but this should be stated for all experiments. If experiments don't already include 3 independent repeats, this should be done. Check text for typos, correct letter capitalisation, spaces and random bold text (some of this could be from incompatability when saving as PDF)

      Answer: all experiments were repeated at least three times. The number of repeats is now indicated in the figure legends of each experiment. Typos and capitalization is corrected as well.

      Fig2E: scrambled not scramble siRNA

      Answer: corrected

      Fig 3: "to expel" is a term not used in the rest of the paper for reflux. Useful to remain consistent with terminology where possible

      Answer: Rephrased and corrected

      Results section 1:

      "Protein alignment of the yeast HLJ1p showed high amino acids similarity to the mammalian..."

      Answer: Rephrased to “ Comparing the amino acid sequences revealed significant similarity between the yeast protein HLJ1p and the mammalian proteins DNAJB12 and DNAJB14”

      __ __ Fig 1C: state in legend which organism this is from (presumably human)

      Answer: in Figure 1C legends it is stated that: “ the HPD motif within the J-domain is conserved in HLJ-1 and its putative human orthologs DNAJB12, DNAJB14, DNAJC14, DNAJC18, and DNAJC30.”

      Results Section 2

      "Test the two strongest hits DNAJB12/14" Add reference to previous paper showing this

      Answer: the references were added.

      __ __ "In the WT and J-protein-silenced A549 cells, there were no differences in the cytosolic enrichment of the three ER resident proteins AGR2, DNAJB11, and HYOU1 in normal and unstressed conditions (Figure 2A-C and Figure S2C)." I think that this is an oversimplification, and in your following discussion, you show this it's more subtle than this.

      Answer: We expanded on this both in the discussion and the results section.

      __ __ The text here isn't so clear: normal and unstressed conditions? Do you mean stressed? Please be careful in your phrases: "DNAJB12-silenced cells are slightly affected in AGR2 and DNAJB11 cytosolic accumulation but not HYOU1." This is the wrong way around. DNAJB12 silencing effects AGR2, not that AGR2 effects the cells (which is how you have written it). This also occurs agan in the next para:

      Answer: Normal cells are non-cancer cells. Unstressed conditions= without ER stress. The sentence was rephrased to: In the absence of ER stress, the cytosolic levels of the three ER-resident proteins (AGR2, DNAJB11, and HYOU1) were similar in wild-type and J-protein-silenced A549 cells.

      "During stress, DNAJB12/DNAJB14 double knockdown was highly affected in the cytosolic..." I think you mean it highly affected the cytosolic accumulation, not that it was affected by the cytosolic accumulation. Please change in the text

      Answer: the sentence is now rephrased to” During stress, double knockdown of DNAJB12 and DNAJB14 highly affected the cytosolic accumulation of all three tested proteins”

      __ __ "DNAJB12 and DNAJB14 are strong hits of the yeast HLJ1" Not clear, I presume you mean they are likely orthologues? Top candidates for being closest orthologues?

      Answer: this is correct, the sentence is rephrased and corrected

      __ __ Fig 2D: typos in WB labelling? I think Tm should be - - +, not - + +as it is now (if it's not a typo, you need more controls, eto alone.

      Answer: the labeling is now corrected

      Fig 2D-E-F typos for DKD? D12/D12 or D12/14?

      Answer: This is correct, thank you for pointing this out. The labeling in corrected

      __ __ "We assayed the phosphorylation state of wt- p53 and p21 protein expression levels (a downstream target of p53 signaling) during etoposide treatment." What are the results of this? Explain what Fig 2D-E shows, then build on this with the +Tm results. Results should be explained didactically to be clear.

      Answer: The paragraph was edited and we explained the results: In these conditions, we saw an increase in the phosphorylation of wt-p53 in the control cells and in cells knocked-down with DNAJB12, DNAJB14 or both. This phosphorylation increased the protein levels of p21 as well (Figure 2D-G). Tm addition to cells treated with etoposide resulted in a reduction in wt-p53 phosphorylation, and as a consequence, the p21 protein levels were also decreased (Figure 2D-G and Figure S2O). Cells lacking DNAJB12 or DNAJB14 have partial protection in wt-p53 phosphorylation and p21 protein levels. Silencing both proteins in A549 and MCF7 cells rescued wt-p53 phosphorylation and p21 levels (Figure 2D-G and Figure S2D). Moreover, similar results were obtained when we assayed the transcriptional activity of wt-p53 in cells transfected with a luciferase reporter under the p53-DNA binding site (Figure 2H). These data confirm that DNAJB12 and DNAJB14 are involved in ER protein reflux and the inhibition of wt-p53 activity during ER stress.


      "(Figure 2D- E). Cells lacking DNAJB12 and or DNAJB14 have partial protection in wt-p53 phosphorylation and p21 protein levels."

      Answer: This sentence is now removed

      You comment on p53 phosphorylation, but you haven't quantified this. This should be done, normalized to p53 levels, if you want to draw these conclusions, especially as total p53 varies between condition. Does Eto increase p53 txn? Does Tm alone increase p53 activity/phospho-p53? These are shown in the Sicari EMBO reports paper in 2021, you should briefly reference those.

      Answer: The blots are now quantified and new blot is added to Figure S2D. The Paragraph was edited and referenced to our previous paper (Sicari et al. 2021). “We then wanted to examine whether the gain of function of AGR2 and the inhibition of wt-p53 depends on the activity of DNAJB12 and DNJAB14. We assayed the phosphorylation state of wt-p53 and p21 protein expression levels (a downstream target of wt-p53 signaling) during etoposide treatment. In these conditions, there was an increase in the phosphorylation of wt-p53 in the control cells and in cells knocked down with DNAJB12, DNAJB14, or both. This phosphorylation also increases protein levels of p21 (Figure 2D-G and Figure S2O). Tm addition to cells treated with etoposide resulted in a reduction in wt-p53 phosphorylation, and as a consequence, the p21 protein levels were also decreased (Figure 2D-G and Figure S2O). Silencing DNAJB12 and DNAJB14 in A549 and MCF-7 cells rescued wt-p53 phosphorylation and p21 levels (Figure 2D-G and Figure S2O). Moreover, similar results were obtained when we assayed the transcriptional activity of wt-p53 in cells transfected with a luciferase reporter under the p53-DNA binding site (Figure 2H). In the latter experiment, etoposide treatment increased the luciferase activity in all the cells tested. Adding ER stress to those cells decreased the luciferase activity except in cells silenced with DNAJB12 and DNAJB14.

      These data confirm that DNAJB12 and DNAJB14 are involved in the reflux of ER proteins in general and AGR2 in particular. Inhibition of DNAJB12 and DNAJB14 prevented the inhibitory interaction between AGR2 and wt-p53 and thus rescued wt-p53 phosphorylation and its transcriptional activity as a consequence. “

      Fig3A: overexpression of DNAJB12 decreases Eto induced p53 but not at steady state. Is this because at steady state the activity is already basal? Or is there another reason?

      Answer: yes, at steady state the activity is already basal

      Switch Figs S3D and S3C as they are not referred to in order. Also Fig S3C: vary colour (or add pattern) on bars more between conditions

      Answer: The Figures now are called by their order in the new version. Colors are now added to Figure S3C.

      Need to define HLJ1 at first mention

      Answer: defined as” HLJ1 - High copy Lethal J-protein -an ER-resident tail-anchored HSP40 cochaperone.

      Results section 3

      HSC70 cochaperone (SGTA) defined twice

      Answer: the second one was removed

      "These data are important because SGTA and the ER-resident proteins (PRDX4, AGR2, and DNAJB11) are known to be expressed in different compartments, and the interaction occurs only when those ER-resident proteins localize to the cytosol." Is there a reference for this?

      Answer: Peroxireoxin 4 is the only peroxerodin that is expressed in the ER. AGR2 and DNAJB11 are also ER luminal proteins that are known to be solely expressed in the ER. SGTA is part of the cytosolic quality control system and is expressed in the cytosol. The references are added in the main text.

      Results section 4

      "by almost two folds"

      Answer: corrected

      Fig 6A: It seems strange that the difference between purple and blue bars in scrambled, and D14-KD are very significant but D12-KD is only significant. Why is this? The error bars don't look that different. It would be interesting to see the individual means for each different replicate.

      Answer: Thank you for pointing this, the two asterixis were aligned in the middle as one during figure alignments. In D14 the purple one has a lower error bar thus this changes the significance when compared to the blue while in D12-KD, the error bars in the eto treatment and the eto-Tm both are slightly higher. Graphs of the three different replicates are now added in Figure S6. Each one of the three biological replicates was repeated in three different technical repeats (averaged in the graphs).

      Figures: Fig 6A: Scale bars not well placed. Annotation on final set should be D12/D14 DKD?

      Answer: both were Corrected

      __Discussion __47. The authors mention that they want to use DNAJB12/4-HSC70/SGTA axis to impair cancer cell fitness: What effect would this have though in a non cancer model? Would this be a viable approach Although it is obviously early days, which approach would the authors see as potentially favorable?


      Answer: In our previous study we used an approach to target AGR2 in the cytosol because the reflux of AGR2 occurs only in cancer cells and not in normal cells. In that study we targeted AGR2 with scFv that targets AGR2 and is expressed in the cytosol, in this case it will target AGR2 in the cytosol which only occurs in cancer. Here, we suggest to target the interaction between the refluxed proteins and their new partners in the cytosol or to target the mechanism that causes their reflx to the cytosol by inhibiting for instance the interaction between SGTA and DNAJB proteins.


      __ __ Second para: Should be "Here we present evidences"

      Answer: we replaced with “Here we present evidences”

      "DNAJB12 overexpression was also sufficient to promote ERCYS by refluxing AGR2 and inhibit wt-p53 signaling in cells treated with etoposide" Suggest:

      Answer: DNAJB12 overexpression is also sufficient to promote ERCYS by refluxing AGR2 and inhibit wt-p53 signaling in cancer cells treated with etoposide (Figure 3). This suggests that it is enough to increase the levels of DNAJB12 without inducing the unfolded protein response in order to activate ERCYS. Moreover, the downregulation of DNAJB12 and DNAJB14 rescued the inhibition of wt-p53 during ER stress (Figure 2). Thus, wt-p53 inhibition is independent of the UPR activation but depends on the inhibitory interaction of AGR2 with wt-p53 in the cytosol.

      .

      DNAJB12 overexpression was also sufficient to promote ERCYS by increasing reflux of AGR2 and inhibition of wt-p53 signaling in cells treated with etoposide

      Answer: This sentence is repeated twice and was removed

      "Moreover, DNAJB12 was sufficient to promote this phenomenon and cause ER protein reflux by mass action without causing ER stress (Figure 3, Figure 4, and Figure S3)." You dont look at induction of ER stress here, please change the text or explain in more depth with refs if suitable

      Answer: In the initial submission and in the revised version we assayed the activation of the UPR by looking at the levels of spliced Xbp1 and Bip in the different conditions when DNAJB12 and DNAJB14 are overexpressed (Figure S3C and S3D). Our data show that although DNAJB12 overexpression induces ERCYS, there was no UPR activation.

      The mention of viruses is sparse in this paper. If it is a main theory, put it more centrally to the concept, and explain in more detail. As it is, its appearance in the final sentence is out of context.

      Answer: DNAJB12 and DNAJB14 were reported to facilitate the escape of non-envelope viruses from the endoplasmic reticulum to the cytosol. The mechanism of non-envelope penetration is highly similar to the reflux of proteins from the ER to the cytosol. Interestingly, this mechanism takes place when the DNAJB12 and DNAJB14 form a complex with chaperones from both the ER and the cytosol including HSC70, SGTA and BiP (Walczak et al. 2014; Goodwin et al. 2011; Goodwin et al. 2014)..

      Moreover, the UGGT1 that was independently found in our previous mass spectrometry analysis of the digitonin fraction obtained from HEK293T cells treated with the ER stressor thapsigargin and from isolated human GBM tumors (Sicari et al. 2020), is known to deploy to the cytosol upon viral infection (Huang et al. 2017; Sicari et al. 2020). We therefore hypothesized that the same machinary that is known to allow viruses to escape the ER to penetrate the cytosol may play an important role in the reflux of ER proteins to the cytosol.

      Because ER protein reflux and the penetration of viruses from the ER to the cytosol behave similarly, we speculate that viruses hijacked an evolutionary conserved machinery -ER protein reflux- to penetrate to the cytosol. This is key because it was also reported that during the process of nonenveloped viruses penetration, large, intact and glycosylated viral particles are able to penetrate the ER membrane on their way to the cytosol (Inoue and Tsai 2011).

      Action: we developed the discussion around this point and clarified it better because we believe it central to show that viruses hijacked this conserved mechanism.

      **Referees cross-commenting**

      I agree with the comments from Reviewer 1.

      Reviewer 2 also is correct in many ways, but I think that they have somewhat overlooked the relevance of the ER-stress element and treatments. The authors do need to reference past papers more to give a full story, as this includes the groups own papers, I don't think that it is an ethical problem but rather an oversight in the writing. Regarding reviewer 2's concerns about overexpression levels and cell death, the authors do use an inducible cell line and show the levels of DNAJB12 induced (could CRISPR also be considered?). This could be used to further address reviewer 2's concerns. It would also be useful to see data on cell death in the conditions used in the paper. Re concerns about ER integrity, this could be addressed by using IF (or EM) to show a secondary ER marker that remains ER-localised, and this would also be of interest regarding my comment on which categories of proteins can undergo reflux. If everything is relocalised, then reviewer 2's point would be validated.

      Reviewer #3 (Significance (Required)):

      Significance

      General assessment: This paper robustly shows that the yeast system of ER to cytosol reflux of ER-resident proteins is conserved in mammalian cells, and it describes clearly the link between ER stress, protein reflux and inhibition of p53 in mammalian cells. The authors have the tools to delve deeper into this mechanism and robustly explore this pathway, however the mechanistic elements - where not instantly clear from the results - have been over interpreted somewhat The results have been oversimplified in their explanations and some points and complexities of the study need to be addressed further to make the most of them - these are often some of the more interesting concepts of the paper, for example the differences in DNAJB12/14 and how the proteins orchestrate in the cytosol to play their cytosol-specific effects. I think that many points can be addressed in the text, by the authors being clear and concise with their reporting, while other experiments would turn this paper from an observational one, into a very interesting mechanistic one.

      Advance: This paper is based on previous nice papers from the group. It is a nice progressions from yeast, to basic mechanism, to physiological model. But as mentioned, without a strong mechanistic improvement, the paper would remain observatory.

      Audience: This paper is interesting to cell biologists (homeostasis, quality control and trafficking) as well as cancer cell biologists (fitness of cancer cells and homeostasis) and it is a very interesting demonstration of a process that is a double edged sword, depending on the environment of the cells.

      My expertise: cell biology, trafficking, ER homeostasis

      Answer: We would like to thank the reviewer for his/her positive feedback on our manuscript. All the comments of the three reviewers are now addressed and the manuscript has been strengthen. We put more emphasis on the mechanistic aspect with more Ips and knockdowns. We also added data to show that it is physiologically relevant. We hope that after that the revised version addressed all the concerns raised by the reviewers.

      Goodwin, E. C., A. Lipovsky, T. Inoue, T. G. Magaldi, A. P. Edwards, K. E. Van Goor, A. W. Paton, J. C. Paton, W. J. Atwood, B. Tsai, and D. DiMaio. 2011. 'BiP and multiple DNAJ molecular chaperones in the endoplasmic reticulum are required for efficient simian virus 40 infection', MBio, 2: e00101-11.

      Goodwin, E. C., N. Motamedi, A. Lipovsky, R. Fernandez-Busnadiego, and D. DiMaio. 2014. 'Expression of DNAJB12 or DNAJB14 causes coordinate invasion of the nucleus by membranes associated with a novel nuclear pore structure', PLoS One, 9: e94322.

      Grove, D. E., C. Y. Fan, H. Y. Ren, and D. M. Cyr. 2011. 'The endoplasmic reticulum-associated Hsp40 DNAJB12 and Hsc70 cooperate to facilitate RMA1 E3-dependent degradation of nascent CFTRDeltaF508', Mol Biol Cell, 22: 301-14.

      Huang, P. N., J. R. Jheng, J. J. Arnold, J. R. Wang, C. E. Cameron, and S. R. Shih. 2017. 'UGGT1 enhances enterovirus 71 pathogenicity by promoting viral RNA synthesis and viral replication', PLoS Pathog, 13: e1006375.

      Igbaria, A., P. I. Merksamer, A. Trusina, F. Tilahun, J. R. Johnson, O. Brandman, N. J. Krogan, J. S. Weissman, and F. R. Papa. 2019. 'Chaperone-mediated reflux of secretory proteins to the cytosol during endoplasmic reticulum stress', Proc Natl Acad Sci U S A, 116: 11291-98.

      Inoue, T., and B. Tsai. 2011. 'A large and intact viral particle penetrates the endoplasmic reticulum membrane to reach the cytosol', PLoS Pathog, 7: e1002037.

      Malinverni, D., S. Zamuner, M. E. Rebeaud, A. Barducci, N. B. Nillegoda, and P. De Los Rios. 2023. 'Data-driven large-scale genomic analysis reveals an intricate phylogenetic and functional landscape in J-domain proteins', Proc Natl Acad Sci U S A, 120: e2218217120.

      Piette, B. L., N. Alerasool, Z. Y. Lin, J. Lacoste, M. H. Y. Lam, W. W. Qian, S. Tran, B. Larsen, E. Campos, J. Peng, A. C. Gingras, and M. Taipale. 2021. 'Comprehensive interactome profiling of the human Hsp70 network highlights functional differentiation of J domains', Mol Cell, 81: 2549-65 e8.

      Sicari, D., F. G. Centonze, R. Pineau, P. J. Le Reste, L. Negroni, S. Chat, M. A. Mohtar, D. Thomas, R. Gillet, T. Hupp, E. Chevet, and A. Igbaria. 2021. 'Reflux of Endoplasmic Reticulum proteins to the cytosol inactivates tumor suppressors', EMBO Rep: e51412.

      Sicari, Daria, Raphael Pineau, Pierre-Jean Le Reste, Luc Negroni, Sophie Chat, Aiman Mohtar, Daniel Thomas, Reynald Gillet, Ted Hupp, Eric Chevet, and Aeid Igbaria. 2020. 'Reflux of Endoplasmic Reticulum proteins to the cytosol yields inactivation of tumor suppressors', bioRxiv.

      Walczak, C. P., M. S. Ravindran, T. Inoue, and B. Tsai. 2014. 'A cytosolic chaperone complexes with dynamic membrane J-proteins and mobilizes a nonenveloped virus out of the endoplasmic reticulum', PLoS Pathog, 10: e1004007.

      Yamamoto, Y. H., T. Kimura, S. Momohara, M. Takeuchi, T. Tani, Y. Kimata, H. Kadokura, and K. Kohno. 2010. 'A novel ER J-protein DNAJB12 accelerates ER-associated degradation of membrane proteins including CFTR', Cell Struct Funct, 35: 107-16.

      Youker, R. T., P. Walsh, T. Beilharz, T. Lithgow, and J. L. Brodsky. 2004. 'Distinct roles for the Hsp40 and Hsp90 molecular chaperones during cystic fibrosis transmembrane conductance regulator degradation in yeast', Mol Biol Cell, 15: 4787-97.

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      Referee #3

      Evidence, reproducibility and clarity

      Summary:

      Reflux of ER based proteins to the cytosol during ER stress inhibits wt-p53. This is a pro-survival mechanism during ER stress, but as ER stress is high in many cancers, it also promotes survival of cancer cells. Using A549 cells, Dabsan et al. demonstrate that this mechanism is conserved from yeast to mammalian cells, and identify DNAJB12 and DNAJB14 as putative mammalian orthologues of yeast HLJ1.

      This paper shows that DNAJB12 and 14 are likely orthologues of HLJ1 based on their sequences, and their behaviour. The paper develops the pathway of ER-stress > protein reflux > cytosolic interactions > inhibition of p53. The authors demonstrate this nicely using knock downs of DNAJB12 and/or 14 that partially blocks protein reflux and p53 inhibition. Overexpression of WT DNAJB12, but not the J-domain inactive mutant, blocks etoposide-induced p53 activation (this is not replicated with DNAJB14) and ER-resident protein reflux. The authors then show that DNAJB12/14 interact with refluxed ER-resident proteins and cytosolic SGTA, which importantly, they show interacts with the ER-resident proteins AGR2, PRDX4 and DNAJB11. Finally, the authors show that inducing ER stress in cancer cell lines can increase proliferation (lost by etoposide treatment), and that this is partially dependent on DNAJB12/14.

      This is a very interesting paper that describes a nice mechanism linking ER-stress to inhibition of p53 and thus survival in the face of ER-stress, which is a double edged sword regarding normal v cancerous cells. The data is normally good, but the conclusions drawn oversimplify the data that can be quite complex. The paper opens a lot of questions that the authors may want to develop in more detail (non-experimentally) to work on these areas in the future, or alternatively to develop experimentally and develop the observations further. There are only a few experimental comments that I make that I think should be done to publish this paper, to increase robustness of the work already here, the rest are optional for developing the paper further.

      Major comments:

      1. Number of experimental repeats must be mentioned in the figure legends. Figures and annotations need to be aligned properly

      Results section 2: 2. No intro to the proteins you've looked at for relocalisation. Would be useful to have some info on why you chose AGR2. Apart from them being ER-localised, do they all share another common characteristic? Does ability to inhibit p53 vary in potency? 3. What are the roles of DNAJB12/14 if overexpression can induce reflux? Does it allow increased binding of an already cytosolic protein, causing an overall increase in an interaction that then causes inhibition of p53? What are your suggested mechanisms? 4. Fig3: A+B show overexpression of individual DNAJs but not combined. As you go on to discuss the effect of the combination on AGR2 reflux, it would be useful to include this experimentally here. 5. Fig 3C: Subfractionation of cells shows AGR2 in the cytosol of A549 cells. The quality of the data is good but the bands are very high on the blot. For publication is it possible to show this band more centralized so that we are sure that we are not missing bands cut off in the empty and H139Q lanes? Also, you have some nice immunofluorescence in the 2021 EMBO reports paper, is it possible to show this by IF too? It is not essential for the story, but it would enrich the figure and support the biochemistry nicely. Also it is notable that the membrane fraction of the refluxed proteins doesn't appear to have a decrease in parallel (especially for AGR2). Is this because the % of the refluxed protein is very small? Is there a transcriptional increase of any of them (the treatments are 12+24 h so it would be enough time)? This could be a nice opportunity to discuss the amount of protein that is refluxed, whether this response is a huge emptying of the ER or more like a gentle release, and also the potency of the gain of function and effect on p53 vs the amount of protein refluxed. This latter part isn't essential but it would be a nice element to expand upon. 6. You still mention DNAJB12 and 14 as orthologues, even though DNAJB14 has no effect on p53 activity when overexpressed. Do you think that this piece of data diminishes this statement? 7. Fig 3D/F: Overexpression of DNAJB14 induces reflux of DNAJB11 at 24h, what does this suggest? Does this indicate having the same role as DNAJB12 but less potently? What's your hypothesis? 8. "This suggests that the two proteins may have different functions when overexpressed, despite their overlapping and redundant functions" What does it suggest about their dependence on each other? If overexpression of WT DNAJB12 inhibits Tg induced reflux, is it also blocking the ability of DNAJB14 to permit flux? 9. Fig 4: PDI shown in blots but not commented on in text. Then included in the schematics. Please comment in the text. 10. Fig 4F: Although the quantifications of the blots look fine, the blot shown does not convincingly demonstrate this data for AGR2. The other proteins look fine, but again it could be useful to see the individual means for each experiment, or the full gels for all replicates in a supplementary figure. Results section 3 11. Fig 5A, As there is obviously a difference between DNAJB12/14 it would be useful to do the pulldown with DNAJB14 too. Re. HSC70 binding to DNAJB12 and 14, the abstract states that DNAJB12/14 bind HSC70 and SGTA through their cytosolic J domains. Fig 5 shows pulldowns of DNAJB12 with an increased binding of SGTA in FLAG-DNAJB12 induced conditions, but the HSC70 band does not seem to be enriched in any of the conditions, including after DNAJB12 induction. This doesn't support the statement that DNAJB12 binds HSC70. In fact, in the absence of a good negative control, this would suggest that the HSC70 band seen is not specific. There is also no data to show that DNAJB14 binds HSC70. I recommend including a negative condition (ie beads only) and the data for DNAJB14 pulldown. 12. The binding of DNAJB12 to SGTA under stress conditions in Fig5B looks much more convincing than SGTA to DNAJB12 in Fig 5A. Bands in all blots need to be quantified from 3 independent experiments, and repeated if not already n=3. If this is solely a technical difference, please explain in the text. The conclusions drawn from this interaction data are important and shold be elaborated upon to support th claims made in the paper. The authors may also chose to expand the pulldowns to demonstrate their claims made on olidomerisation of DNAJB12 and 14 here. It is also clear that the interaction data of the SGTA with ER-resident proteins AGR2, PRDX4 and DNAJB11 is strong. The authors may want to draw on this in their hypotheses of the mechanism. I would imagine a complex such as DNAJB14/DNAJB12 - SGTA - AGR2/PRDX4/DNAJB11 would be logical. Have any experiments been performed to prove if complexes like this would form? 13. Fig 5B: It is clear that DNAJB12 interacts with SGTA. The authors state that DNAJB14 also interacts with SGTA under normal and stress conditions, but the band in 25/50 Tg is very feint. Why would there be stronger binding at the 2 extremes than during low stress induction? In the input, there is a much higher expression of DNAJB14 in 50 Tg. What does this say about the interaction? Is there an effect of ER stress on DNAJB14 expression? A negative control should be included to show any background binding, such as a "beads only" control. 14. Fig 5C data is sound, although a negative control should be included. Results section 4 15. Fig 6A-B: Given that there is the complexity of overexpression v KD of DNAJB12 v 14 causing similar effects on p53 actvity (Fig 2 v 3), it would be interesting to see whether the effect of overexpression mirrors the results in Fig 6A. Is it known what SGTA overexpression does (optional)? 16. Fig 6D: resolution very low 17. Fig 6C-D: There is an interesting difference though between the proposed cytosolic actions of the refluxed proteins. You show that AGR2, PRDX4 and DNAJB11 all bind to SGTA in stress conditions, but in the schematics you show: DNAJB11 binding to HSC70 through SGTA (not shown in the paper), then also PDIA1, PDIA3 binding to SGTA and AGR2 binding to SGTA. What role does SGTA have in these varied reactions? Sometimes it is depicted as an intermediate, sometimes a lone binder, what is its role as a binder? It should be clarified which interactions are demonstrated in the paper (or before) and which are hypothesized in a graphical way (eg. for hypotheses dotted outlines or no solid fill etc). The schematics also suggest that DNAJB14 binding to HSC70 and SGTA is inducible in stress conditions, as is PDIA3, which is not shown in the paper. Discussion "In cancer cells, DNAJB12 and DNAJB14 oligomerize and recruit cytosolic chaperones and cochaperones (HSC70 and SGTA) to reflux AGR2 and other ER-resident proteins and to inhibit wt-p53 and probably different proapoptotic signaling pathways (Figure 5, and Figure 6C-6D)." You havent shown oligomerisation between DNAJB12/14. Modify the text to make it clear that it is a hypothesis. Minor comments: 18. It would be useful to have page or line numbers to help with document navigation, please include them. Typos and inconsistency in how some proteins are named throughout the manuscript 19. Title: Include reference to reflux. Suggest: "chaperone complexes (?proteins) reflux from the ER to cytosol..." I presume it would be more likely that the proteins go separately rather than in complex. Do you have any ideas on the size range of proteins that can undergo this process? 20. ERCY in abstract, ERCYS in intro. There are typos throughout, could be a formatting problem, please check 21. What about the selection of refluxed proteins? Is this only a certain category of proteins? Could it be anything? Have you looked at other cargo / ER resident proteins? 22. "Their role in ERCYS and cells' fate determination depends..." Suggest change to "Their role in ERCYS and determination of cell fate..." 23. I think that the final sentence of the intro could be made stronger and more concise. There's a repeat of ER and cytosol. Instead could you comment on the reflux permitting new interactions between proteins otherwise spatially separated, then the effect on wt-p53 etc.

      Figure legends:

      1. In some cases the authors state the number of replicates, but this should be stated for all experiments. If experiments don't already include 3 independent repeats, this should be done. Check text for typos, correct letter capitalisation, spaces and random bold text (some of this could be from incompatability when saving as PDF)
      2. Fig2E: scrambled not scramble siRNA
      3. Fig 3: "to expel" is a term not used in the rest of the paper for reflux. Useful to remain consistent with terminology where possible

      Results section 1:

      1. "Protein alignment of the yeast HLJ1p showed high amino acids similarity to the mammalian..."
      2. Fig 1C: state in legend which organism this is from (presumably human) Results Section 2
      3. "Test the two strongest hits DNAJB12/14" Add reference to previous paper showing this
      4. "In the WT and J-protein-silenced A549 cells, there were no differences in the cytosolic enrichment of the three ER resident proteins AGR2, DNAJB11, and HYOU1 in normal and unstressed conditions (Figure 2A-C and Figure S2C)." I think that this is an oversimplification, and in your following discussion, you show this it's more subtle than this.
      5. The text here isn't so clear: normal and unstressed conditions? Do you mean stressed? Please be careful in your phrases: "DNAJB12-silenced cells are slightly affected in AGR2 and DNAJB11 cytosolic accumulation but not HYOU1." This is the wrong way around. DNAJB12 silencing effects AGR2, not that AGR2 effects the cells (which is how you have written it). This also occurs agan in the next para:
      6. "During stress, DNAJB12/DNAJB14 double knockdown was highly affected in the cytosolic..." I think you mean it highly affected the cytosolic accumulation, not that it was affected by the cytosolic accumulation. Please change in the text
      7. "DNAJB12 and DNAJB14 are strong hits of the yeast HLJ1" Not clear, I presume you mean they are likely orthologues? Top candidates for being closest orthologues?
      8. Fig 2D: typos in WB labelling? I think Tm should be - - +, not - + +as it is now (if it's not a typo, you need more controls, eto alone.
      9. Fig 2D-E-F typos for DKD? D12/D12 or D12/14?
      10. "We assayed the phosphorylation state of wt- p53 and p21 protein expression levels (a downstream target of p53 signaling) during etoposide treatment." What are the results of this? Explain what Fig 2D-E shows, then build on this with the +Tm results. Results should be explained didactically to be clear.
      11. "(Figure 2D- E). Cells lacking DNAJB12 and or DNAJB14 have partial protection in wt-p53 phosphorylation and p21 protein levels."
      12. You comment on p53 phosphorylation, but you haven't quantified this. This should be done, normalized to p53 levels, if you want to draw these conclusions, especially as total p53 varies between condition. Does Eto increase p53 txn? Does Tm alone increase p53 activity/phospho-p53? These are shown in the Sicari EMBO reports paper in 2021, you should briefly reference those.
      13. Fig3A: overexpression of DNAJB12 decreases Eto induced p53 but not at steady state. Is this because at steady state the activity is already basal? Or is there another reason?
      14. Switch Figs S3D and S3C as they are not referred to in order. Also Fig S3C: vary colour (or add pattern) on bars more between conditions
      15. Need to define HLJ1 at first mention Results section 3
      16. HSC70 cochaperone (SGTA) defined twice
      17. "These data are important because SGTA and the ER-resident proteins (PRDX4, AGR2, and DNAJB11) are known to be expressed in different compartments, and the interaction occurs only when those ER-resident proteins localize to the cytosol." Is there a reference for this? Results section 4
      18. "by almost two folds"
      19. Fig 6A: It seems strange that the difference between purple and blue bars in scrambled, and D14-KD are very significant but D12-KD is only significant. Why is this? The error bars don't look that different. It would be interesting to see the individual means for each different replicate.
      20. Figures: Fig 6A: Scale bars not well placed. Annotation on final set should be D12/D14 DKD? Discussion
      21. The authors mention that they want to use DNAJB12/4-HSC70/SGTA axis to impair cancer cell fitness: What effect would this have though in a non cancer model? Would this be a viable approach? Although it is obviously early days, which approach would the authors see as potentially favourable?
      22. Second para: Should be "Here we present evidences"
      23. "DNAJB12 overexpression was also sufficient to promote ERCYS by refluxing AGR2 and inhibit wt-p53 signaling in cells treated with etoposide" Suggest:
      24. DNAJB12 overexpression was also sufficient to promote ERCYS by increasing reflux of AGR2 and inhibition of wt-p53 signaling in cells treated with etoposide
      25. "Moreover, DNAJB12 was sufficient to promote this phenomenon and cause ER protein reflux by mass action without causing ER stress (Figure 3, Figure 4, and Figure S3)." You dont look at induction of ER stress here, please change the text or explain in more depth with refs if suitable
      26. The mention of viruses is sparse in this paper. If it is a main theory, put it more centrally to the concept, and explain in more detail. As it is, its appearance in the final sentence is out of context.

      Referees cross-commenting

      I agree with the comments from Reviewer 1. Reviewer 2 also is correct in many ways, but I think that they have somewhat overlooked the relevance of the ER-stress element and treatments. The authors do need to reference past papers more to give a full story, as this includes the groups own papers, I don't think that it is an ethical problem but rather an oversight in the writing. Regarding reviewer 2's concerns about overexpression levels and cell death, the authors do use an inducible cell line and show the levels of DNAJB12 induced (could CRISPR also be considered?). This could be used to further address reviewer 2's concerns. It would also be useful to see data on cell death in the conditions used in the paper. Re concerns about ER integrity, this could be addressed by using IF (or EM) to show a secondary ER marker that remains ER-localised, and this would also be of interest regarding my comment on which categories of proteins can undergo reflux. If everything is relocalised, then reviewer 2's point would be validated.

      Significance

      General assessment: This paper robustly shows that the yeast system of ER to cytosol reflux of ER-resident proteins is conserved in mammalian cells, and it describes clearly the link between ER stress, protein reflux and inhibition of p53 in mammalian cells. The authors have the tools to delve deeper into this mechanism and robustly explore this pathway, however the mechanistic elements - where not instantly clear from the results - have been over interpreted somewhat. The results have been oversimplified in their explanations and some points and complexities of the study need to be addressed further to make the most of them - these are often some of the more interesting concepts of the paper, for example the differences in DNAJB12/14 and how the proteins orchestrate in the cytosol to play their cytosol-specific effects. I think that many points can be addressed in the text, by the authors being clear and concise with their reporting, while other experiments would turn this paper from an observational one, into a very interesting mechanistic one.

      Advance: This paper is based on previous nice papers from the group. It is a nice progressions from yeast, to basic mechanism, to physiological model. But as mentioned, without a strong mechanistic improvement, the paper would remain observatory.

      Audience: This paper is interesting to cell biologists (homeostasis, quality control and trafficking) as well as cancer cell biologists (fitness of cancer cells and homeostasis) and it is a very interesting demonstration of a process that is a double edged sword, depending on the environment of the cells.

      My expertise: cell biology, trafficking, ER homeostasis

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      Referee #2

      Evidence, reproducibility and clarity

      The authors present a study in which they ascribe a role for a complex containing DNAJB12/14-Hsc70-SGTA in facilitating reflux of a AGR2 from the ER to cytosol during ER-stress. This function is proposed to inhibit wt-P53 during ER-stress.

      Concerns:

      1. The way the manuscript is written gives the impression that this is the first study about mammalian homologs of yeast HLJ1, while there are instead multiple published papers on mammalian orthologs of HLJ1. Section 1 and Figure 1 of the results section is redundant with a collection of previously published manuscripts and reviews. The lack of proper citation and discussion of previous literature prevents the reader from evaluating the results presented here, compared to those in the literature.
      2. The conditions used to study DNAJB12 and DNAJ14 function in AGR2 reflux from the ER do not appear to be of physiological relevance. As seen below they involve two transfections and treatment with two cytotoxic drugs over a period of 42 hours. The assay for ERCY is accumulation of lumenal ER proteins in a cytosolic fraction. Yet, there is no data or controls that describe the path taken by AGR2 from the ER to cytosol. It seems like pleotropic damage to the ER due the experimental conditions and accompanying cell death could account for the reported results?

      A. Transfection of cells with siRNA for DNAJB12 or DNAJB14 with a subsequent 24-hour growth period.

      B. Transfection of cells with a p53-lucifease reporter.

      C. Treatment of cells with etoposide for 2-hours to inhibit DNA synthesis and induce p53.

      D. Treatment of cells for 16 hours with tunicamycin to inhibit addition of N-linked glycans to secretory proteins and cause ER-stress.

      E. Subcellular fractionation to determine the localization of AGR2, DNAJB11, and HYOU1

      KD of DNAJB12 or DNAJB14 have modest if any impact on AGR2 accumulation in the cytosol. There is an effect of the double KD of DNAJB12 or DNAJB14 on AGR2 accumulation in the cytosol. Yet there are no western blots showing AGR2 levels in the different cells, so it is possible that AGR2 is not synthesized in cells lacking DNAJB12 and DNAKB14. The lack of controls showing the impact of single and double KD or DNAJB12 and DNAJB14 on cell viability and ER-homeostasis make it difficult to interpret the result presented. How many control versus siRNA KD cells survive the protocol used in these assays? 3. In Figure 3 the authors overexpress WT-D12 and H139Q-D12 and examine induction of the p53-reporter. There are no western blots showing the expression levels of WT-D12 and H139Q-D12 relative to endogenous DNAJB12. HLJ1 stands for high-copy lethal DnaJ1 as overexpression of HLJ1 kills yeast. The authors present no controls showing that WT-D12 and H139-D12 are not expressed at toxic levels, so the data presented is difficult to evaluate. 4. There is no mechanistic data used to help explain the putative role DNAJB12 and DNAJB14 in ERCY? In Figure 4, why does H139Q JB12 prevent accumulation of AGR2 in the cytosol? There are no westerns showing the level to which DNAJB12 and DNAJB14 are overexpressed.

      Referees cross-commenting

      I appreciate the comments of the other reviewers. I agree that the authors could revise the manuscript. Yet, based on my concerns about the physiological significance of the process under study and lack of scholarship in the original draft, I would not agree to review a revised version of the paper.

      Significance

      Overall, there are serious concerns about the writing of this paper as it gives the impression that it is the first study on higher eukaryotic and mammalian homologs of yeast HLJ1. The reader is not given the ability to compare the presented data to related published work. There are also serious concerns about the quality of the data presented and the physiological significance of the process under study. In its present form, this work does not appear suitable for publication

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      The manuscript by Dabsan et al builds on earlier work of the Igbaria lab, who showed that ER-luminal chaperones can be refluxed into the cytosol (ERCYS) during ER stress, which constitutes a pro-survival pathway potentially used by cancer cells. In the current work, they extent these observations and a role for DNAJB12&14 in ERCYS. The work is interesting and the topic is novel and of great relevance for the proteostasis community. I have a number of technical comments:

      Major and minor comments:

      1. In the description of Figure 2, statistics is only show to compare untreated condition with those treated with Tg or Tm, but no comparison between condition and different proteins. As such, the statement made by the authors "...DNAJB14-silenced cells were only affected in AGR2 but not in DNAJB11 or HYOU1 cytosolic accumulation" cannot be made.
      2. Figure S2C: D11 seems to increase in the cytosolic fraction after Tm and Tg treatment. However, this is not reflected in the text. The membrane fraction also increases in the DKO. Is the increase of D11 in both cytosol and membrane and indication for a transcriptional induction of this protein by Tm/Tg? Again, the authors are not reflecting on this in their text.
      3. Figure 2D: Only p21 is quantified. phospho-p53 and p53 levels are not quantified.
      4. Figure 2D: There appears to be a labelling error
      5. Are there conditions where DNAJB12 would be higher?
      6. What do the authors mean by "just by mass action"?
      7. Figure 3C: Should be labelled to indicate membrane and cytosolic fraction. The AGR2 blot in the left part is not publication quality and should be replaced.
      8. What could be the reason for the fact that DNAJB12 is necessary and sufficient for ERCYS, while DNAJB14 is only necessary?
      9. Figure 5A: Is the interaction between SGTA and JB12 UPR-independent?HCS70 seems to show only background binding. The interaction of JB12 with SGTA is not convincing. A better blot is needed.
      10. Figure 5B: the expression of DNAJB14 was induced by Tg50, but not by Tg25 or Tm. However, the authors have not commented on this. This should be mentioned in the text and discussed.
      11. Figure 6A: Why is a double knockdown important at all? DNAJB14 does not seem to do much at all (neither in overexpression nor with single knockdown).

      Referees cross-commenting

      I agree with the comments raised by reviewer 1 about the manuscript. I also agree with the points written in this consultation session. In my opinion, the comments of reviewer 2 are phrased in a harsh tone and thus the reviewer reaches the conclusion that there are "serious" problems with this manuscript. However, I think that the authors could address many of the points of this reviewer in a matter of 3 months easily. For instance, it is easy to control for the expression levels of exogenous wild type and mutant D12 and compare it to the endogenous one (point 3). This is a very good point of this reviewer and I agree with this experiment. Likewise, it is easy to provide data about the levels of AGR2 to address the concern whether its synthesis is affected by D12 and D14 overexpression. Again, an excellent suggestion, but no reason for rejecting the story. As for not citing the literature, I think this can also easily be addressed and I am sure that this is just an oversight and no ill intention by the authors. Overall, I am unable to see why the reviewer reaches such a negative verdict about this work. With proper revisions that might take 3 months, I think the points of all reviewers can be addressed.

      Significance

      The strength of the work is that it provides further mechanistic insight into a novel cellular phenomenon (ERCYS). The functions for DNAJB12&14 are unprecedented and therefore of great interest for the proteostasis community. Potentially, the work is also of interest for cancer researchers, who might capitalize of the ERCYS to establish DNAJB12/14 as novel therapeutic targets.

      The major weaknesses are as follows:

      • (i) the work is limited to a single cell line. To better probe the cancer relevance, the work should have used at least a panel of cell lines from one (or more) cancer entity. Ideally even data from patient derived samples would have been nice. Having said this, I also appreciate that the work is primarily in the field of cell biology and the cancer-centric work could be done by others. Certainly, the current work could inspire cancer specialists to explore the relevance of ERCYS.
      • (ii) No physiological or pathological condition is shown where DNAJB12 is induced or depleted.
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      Reply to the reviewers

      Manuscript number: RC-2024-02491

      Corresponding author(s): Gilbert, Vassart

      1. General Statements [optional]

      We thank referees 1 and 2 for their in-depth analysis of our manuscript. They see interest in our study, with questions to be answered. Referee 3 is essentially negative, considering that there is nothing new ("novel finding is missing"). We respectfully disagree with him/her, comforted by the opinion of referee 2 that "the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field and ... the manuscript should attract a significant amount of attention in the intestinal field" and we provide evidence in our answers that he/she did not read the manuscript with the same attention as referees 1 and 2 (see in particular answer to his/her question 5).

      Here is a summary of the main reason why we consider that our study represents valuable new information in the field of intestinal regeneration.

      It is based on the serendipitous observation that dissociation of adult intestinal tissue by collagenase generates stably replatable spheroids upon culture in matrigel. Surprisingly and contrary to canonical EDTA-generated intestinal organoids and fetal spheroids, these spheroids are not traced in Rosa26Tomato mice harboring a VilCre transgene, despite expressing robustly endogenous Villin. Our interpretation is that adult intestinal spheroids originate from a cell lineage, distinct from the main developmental intestinal lineage, in which the VilCre transgene is unexpectedly not expressed, probaly due to the absence of cis regulatory sequences required for expression in this lineage.

      Adult spheroid transcriptome shares a gene signature with the YAP/TAZ signature commonly expressed in models of intestinal regeneration. This led us to look for VilCre negative crypts in the regenerating intestine of Lgr5/DTR mice in which Lgr5-positive stem cells have been ablated by diphtheria toxin. Numerous VilCre negative clones were observed, identifying a novel lineage of stem cells implicated in intestinal regeneration.

      FACS purification and scRNAseq analysis of the rare VilCre negative cells present at homeostasis identified a population of cells with characteristics of quiescent stem cells.

      In sum, we believe that our study demonstrates the existence of a hitherto undescribed stem cell lineage involved in intestinal regeneration. It points to the existence of a hierarchical model of intestinal regeneration in addition to the well-accepted plasticity model.

      2. Description of the planned revisions

      See section 3 below.

      3. Description of the revisions that have already been incorporated in the transferred manuscript

      Here is a point-by-point reply to the queries of the three referees, with indication of the revisions introduced in the manuscript.

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

      • *In this manuscript, Marefati et al report an Lgr5-independent lineage in the regenerating intestine using in vitro organoids and in vivo injury-coupled lineage tracing model. In organoids, collagenase/dispase dissociated resulted in "immortal spheroids" that maintain a cystic and undifferentiated phenotype in the absence of standard growth factors (Rspondin/Noggin/EGF). Bulk RNAseq of spheroids demonstrates downregulation of classical CBC signatures and upregulation of fetal spheroid, mesenchymal, inflammation and regenerative signatures. In mice, Villin-Cre lineage tracing revealed some Villin- negative progenies that lack reporter tracing throughout crypt-villus ribbons after injury.

      *The authors proposed that there is Lgr5-independent population support the regenerative response upon CBC depletion. A major caveat of this study is the identification of this population is based on absence of VilCre expression. *

      We respectfully disagree. It is precisely this characteristic that makes the interest of our study. Whereas mosaicism of transgene expression is widespread and usually of little significance, our study shows that the rare VilCre-negative cells in the intestinal epithelium are not randomly showing this phenotype: they give specifically birth to what we call adult spheroids and regenerating crypts, which cannot be due to chance. The absence of VilCre expression allows tracing these cells from the zygote stage of the various VilCre/Ros26 reporter mice. We have modified our text to emphasize this point.

      *It is surprising that there is no characterisation of Lgr5 expression throughout the manuscript whilst claiming of a Lgr5- independent lineage. *

      We understand the perplexity of the referee not to see direct Lgr5 expression data in our manuscript, given our title. However, our point is that it is the cells at the origin of adult spheroids and the regenerating crypts we have identified that are Lgr5-negative, not the spheroids or the regenerated crypts themselves. Those are downstream offspring that may, and indeed have, gained some Lgr5 expression (e.g. figure 3F). We believe that our data showing that VilCre-negative spheroids are not traced in Lgr5-CreERT2/Rosa reporter mice convincingly demonstrate absence of Lgr5 expression in the cells at the origin of adult spheroids (figure 4G). We think that this experiment is better evidence than attempts to show absence of two markers (Tom and Lgr5) in the rare "white" cells present in the epithelium. Regarding the Lgr5 status of cells at the origin of the regenerating "white" crypts that we have identified, the early appearance of these crypts following ablation of CBC (i.e. Lgr5+ve) cells is a strong argument that they originate from Lgr5-negative cells. Regarding the scRNAseq experiment, Lgr5 transcripts are notoriously low and difficult to measure reliably in CBCs (Haber et al 2017). However, blowing up the pertinent regions of the merged UMAP allows showing some Lgr5 transcripts in clusters 5,6 and none in cluster 1 of figure 8GH. Given the very low level of detection, we had chosen not to include these data in the manuscript, but we hope they may help answer the point of the referee (see portion of UMAP below, with Olfm4 as a control, together with the corresponding violin plot). Several markers that gave significant signals in the CBC cluster (Smoc2, Axin2, Slc12a2) were virtually undetectable in the Olfm4-low /Tom-negative cluster of our scRNAseq data (figure 8I) supporting our conclusion.

      Although the research question is potentially interesting, the concept of epithelial reprogramming upon injury is well documented in the field. The data generated in this manuscript also seem to be preliminary and lack of detailed characterisation. Below are specific comments.

      We do not question the existence of epithelial reprogramming upon injury. We believe our data show, in addition to this well demonstrated phenomenon, the existence of rare cells traced by absence of VilCre expression that are at the origin of a developmental cell lineage distinct from Lgr5+ stem cells and also implicated in regeneration.

      • Expression of Lgr5 should be properly characterised throughout the manuscript in both organoid models and injury-induced regeneration in vivo.
      • *

      See above for a detailed answer to this point.

      • An important question is the origin of these "Lgr5-independent" adult spheroids. They look and appear like fetal organoids, which could be induced by injury (e.g. upon collagenase/dispase dissociation). Have the authors tried to culture fetal spheroids in BCM over extensive period of time? Do they behave the same? This would be a great way to directly compare the collagenase/dispase-derived organoids with fetal origin. * *Fetal spheroids require ENR for survival and die in BCM. We have chosen to illustrate this point in Fig2A by showing that, contrary to adult spheroid, they die even when only Rspondin is missing.

      • Fig 1C, Why is the replating spheroid culture time different between mesenchymal cells and conditioned medium? We took the earliest time showing convincingly the return to the organoid phenotype. This timing difference does not modify the conclusion that EDTA organoids becoming spheroid-like when exposed to factors originating from mesenchymal cells revert to the organoid phenotype when returned to ENR medium without mesenchymal influence.

      • *It is unclear how the bulk RNA-seq data in Fig. 3 were compared. How long were the adult organoids and spheroids cultured for (how many passages)? Were they culture in the same condition of were they in ENR vs BCM? * Both EDTA organoids and spheroids displaying a stable phenotype were used in this experiment. Organoids were collected at passage 4, day 5; spheroids were collected at passage passage 9 day 3.

      As stated in the legend to the figure: "...to allow pertinent comparison spheroids and organoids were cultured in the same ENR-containing medium...".

      These are important information to consider when interpreting the results. For instance, are Ptgs1 & Ptgs2 expression in adult spheroids the same in ENR vs BCM? Are the gene signatures (regenerative, fetal and YAP) changed in adult spheroids culturing in ENR vs BCM?

      We did compare bulk RNAseq of EDTA organoids to ENR-cultured spheroids, short term (passage 6, day 6) BCM-cultured spheroids and long term BCM-cultured (passage 26, day 6) spheroids. To avoid overloading the manuscript these data were not shown in the original manuscript. In summary the BCM-cultured spheroids display a similar phenotype as those cultured in ENR, but with further de-differentiation. See in revision plan folder the results for PTGS, some differentiation markers and fetal regenerative markers including YAP induced genes.

      We have included a brief description of these data in the new version of the manuscript and added an additional supplementary file (Suppl table 2) presenting the whole data set.

      • It is stated: "In agreement with their aptitude to grow indefinitely, adult spheroids express a set of upregulated genes overlapping significantly with an "adult tissue stem cell module" [159/721 genes; q value 2.11 e-94) (Fig.S2F)].". What is the definition of "indefinitely"? Are they referring to the Fig 1B where spheroid were passaged to P10? The authors should avoid the term "indefinitely" but use a more specific time scale, e.g. passages, months etc.

      We agree that the term indefinitely should be avoided, as it is vague. We have introduced the maximum number of passages during which we have maintained the stable spheroid phenotype (26 passages). Also worth noting, the spheroids could be frozen and cultured repeatedly over many months.

      SuppFig 3D: Row Z-Score is missing the "e" in Score.

      Corrected

      • Fig 4E: Figure legend says QNRQ instead of CNRQ. Corrected

      • Fig 4G: The brightfield image of adult spheroids 5 days after 3x TAM injections doesn't look like a spheroid. It seems to be differentiating. True, the choice was not the best as the spheroids started to darken. When further replated, however, the offspring of these spheroids showing a clear phenotype remain negative 30 days after tamoxifen administration as shown on the figure. We are sorry, but for reasons explained in section 4 below, we cannot redo the experiment to get a better picture.

      • Fig 4: Most mouse model data are missing the number of mice & their respective age used for organoid isolation. We have introduced these data in the legend.

      • *Fig 4A-D, H-G: How was fluorescent signal of organoids quantified? *

      The settings of fluo imaging or time of LacZ staining were the same for organoids and spheroid pictures. This has been added to the material and methods of the figure and an example is shown below for Rosa26Tomato.

      *How many images? * 2 per animal per condition.

      *Were there equal numbers of organoids? *

      No, see number of total elements counted added to the figure

      This all needs to be included in methods/figure legends.

      We have introduced additional pertinent information in the material and methods section.

      • Figure 4B-D, G-H: Which culturing conditions were used for adult spheroids? Original method or sandwich method? These data were obtained with the original protocol

      • Fig 6D-E: Please add the timepoint after DT administration these samples are from. It is not listed in text or figure legend. These samples were those obtained from mice sacrificed at the end of the 5 day period as indicated in panel A. This has been emphasized in the legend of the figure.

      • SuppFig 6D: again timepoint is missing. In this experiment all samples were untreated as indicated. This has been emphasized in the legend of the figure.

      • SuppFig 6: How were the crypts of these mice (DT WT & DT HE) isolated? Was this via EDTA? This was RNA extracted from total uncultured EDTA-released material (crypts). This has been emphasized in the legend of the figure.

      Also, what is the timepoint for isolation for these samples? Even if untreated, the timepoint adds context to the data. Please add more context to describing these different experiments, either in the figure legends or methods section.

      All these experiments were from 2 month old animals. We have indicated this in the legend of the figure.

      • SuppFig 6E: The quality of the heatmap resolution is too poor to read gene names. We have improved the resolution of the figure and hope the name of the genes are readable now.

      • 5-7, are the regenerating crypt-villus units fully differentiated or are they maintained in the developmental state? Immunostaining of markers for stem cells (Lgr5), differentiated lineages (Alpi, Muc2, Lyz, ChgA etc.) and fetal state (Sca1, Trop2 etc) should be analysed in those "white" unrecombined crypt-villus units. The differentiation phenotype is shown by the clear presence of morphologically-identified Paneth and Goblet cells. We agree that specific immunostainings could have been performed to further explore this point. Regarding the fetal state, Clu expression was shown during the regeneration period (see figure 7D,E).

      Unfortunately, for reasons explained in section 4 below, we are not in a position to perform these additional experiments.

      • The following text needs clarification: "The kinetics of appearance of newly formed un-recombined ("white") crypts was studied after a single pulse of DT (Fig.7A). This demonstrated an increase at 48 hours, with further increase at day 10 and stable maintenance at day 30. The presence of newly formed white crypts one month after toxin administration indicates that the VilCre-negative lineage is developmentally stable and does not turn on the transgene during differentiation of the various epithelial lineages occurring after regeneration (Fig.7B).

      *Comment: The "newly formed" is an overstatement, the data doesn't conclude that those are "new" crypts. *

      Except if we do not understand the point, we think we can write that a fraction of "white" crypts must be "newly formed", since they are in excess of those present in untreated animals at the same time point.

      *The end of the sentence states that these "white" crypts form developmentally stable lineages, thus these white crypts at day 30 could originate from the initial injury. *

      As stated above, we consider that crypts found in excess of those present in untreated animals result from the initial injury.

      *There was no characterisation of the various epitheial lineages. Are they fully differentiated? *

      See above the point related to Paneth cells and Goblet cells.

      Is Lgr5 expressed one month after toxin administration? Can the VilCre neg lineage give rise to CBCs?

      We have tried hard to show presence or absence of Lgr5 in white crypts at the various times following DT administration. We tried double RFP / Lgr5-RNA scope labeling and double GFP/RFP immunolabeling. Unfortunately, we could not get these methods to produce convincing specific labeling of CBCs in homeostatic crypts, which explains why we could not reach a conclusion regarding the white crypts.

      However, there is an indirect indication that "chronic" white crypts (i.e. those caused by DTR expression in CBC, plus those observed 30 days after DT administration) do not express Lgr5. Indeed, acute regeneration indicated by Clu expression at day 5 in Fig.7C is lower in white crypts than in red ones strongly suggesting that white crypts preexisting DT administration (the "chronic ones) do not express Lgr5DTR.

      The relationship between white crypt generation and appearance of Clu-positive revival cells (Ayyaz et al., 2019) was then explored. In agreement with others and similar to what happens in the irradiation model, (Ayyaz et al., 2019; Yuan et al., 2023) Clu-positive cells were rare in crypts of untreated mice and their number transiently increased forty-eight hours after a single pulse of DT, and more so after three pulses of DT (Fig.7C,D).

      Comment: Comparing 1 pulse at day 2 vs 3 pulses at day 5 makes the data hard to interpret. How is the Clu ISH level for 1 pulse at day 5? Are they equivalent?

      After a single pulse of of DT, Clu is only transiently increased. As shown by Ayyaz et al it is back to the starting point at day 5 (supplementary figure 4 of Ayyaz et al).

      Clu-positive cells were less frequently observed in white crypts (see "Total" versus "White" in Fig.7C). This fits with the hypothesis that Clu expression marks acutely regenerating crypts and that a proportion of the white crypts are chronically regenerating due to DTR expression in CBCs."

      *Comment: I believe the authors suggested that the discrepancy of less Clu expression in white crypts is due to the ectopic expression of DTR in CBCs causing low grade injury without DT administration. This means that some white crypts could have been formed before the administration of DT, and thus are on a different regenerative timeline compared to the white crypts formed from DT administration. *

      Yes, this is our interpretation. We have clarified it in the text.

      Is there any proof of the chronic regeneration? Immunostaining of chronic regenerative markers such as Sca1, Anxa1 or Yap1 nuclear localization would support the claim. It'd be important to show only the white crypts, but not the RFP+ ones, show regenerative markers.

      We think that the steady state higher number of white crypts in untreated Lgr5-DTR animals, compared to wild type siblings indicates chronical low-grade regeneration, which is supported by the RNAseq data (Suppl fig6). It must be noted, however, that this phenotype is mild compared to the well described fetal-like regeneration phenotype described in most injury models. Since these white crypts were made at undetermined earlier stages, the great majority of them are not expected to show markers of acute regeneration like Clu, Sca1....

      Fig 7D-E: What are the timepoints of harvest for HE-WT-HE 1 pulse DT mice and HE- HE-HE PBS injected mice?

      We have added this information in the figure.

      • *Fig 8-9: Regarding the CBC-like Olfm4 low population, what is the status of Lgr5? This should be shown in the figure since the argument is that this is an Lgr5-independent lineage. * See response to the second point.

      And what about the regenerative, Yap, mesenchymal and inflammatory signatures? Are they enriched in the white crypts similar to the in vitro spheroids?

      In a portion of white crypts, those we believe are newly formed after CBC ablation (see above), there is a transient increase in Clu, which may be considered a marker of Yap activation. In the CBC-like Olfm4 low cells, as seen by scRNAseq, there is nothing like an actively regenerating phenotype. This is expected, since these cells are coming from homeostatic untreated VilCre/Rosa26Tom animals and are supposed to be quiescent "awaiting to be activated".

      Reviewer #1 (Significance (Required)):

      Strengths: The study employed a range of in vitro and in vivo models to test the hypothesis.

      • *

      *Limitations: Unfortunately, the models chosen did not provide sufficient evidence to draw the conclusions. Injury induced reprogramming, both in vivo and in vitro, has been well documented in the field. The new message here is to show that such reprogrammed state is continuous rather than transient; instead of regenerating Lgr5+ stem cells, it can continue to differentiate to all cell lineages in Lgr5-independent manner.

      *

      We respectfully disagree with this analysis of our results. What we show is not "that such reprogrammed state is continuous rather than transient; instead of regenerating Lgr5+ stem cells, it can continue to differentiate to all cell lineages in Lgr5-independent manner", but that a quiescent stem cell line, not previously identified, is activated to regenerate a portion of crypts following CBC ablation. These cells are not reprogrammed, they correspond to a developmental lineage waiting to be activated and keep their VilCre-negative state at least of 30 days. We believe that their "by default tracing" (VilCre negative from the zygote stage) is as strong an evidence for the existence of such a lineage as positive lineage tracing would be. The increase in crypts originating from this lineage after CBC ablation indicates that it is implicated in regeneration. We do not question the well-demonstrated plasticity-associated reprogramming taking place during regeneration; we simply suggest that this would coexist with the involvement of the quiescent VilCre-negative lineage we have identified.

      *However, through the manuscript, there was no immunostaining of Lgr5 and other differentiation markers. The conclusion is an overstatement without solid proof. * We have provided the best answer we could to this point in our answer to the second question of the referee hereabove.

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

      In this manuscript, the Marefati et al. developed a novel approach to generate spheroids from adult intestinal epithelium using a collagenase/dispase based protocol. Adult spheroids were found to be distinct from classic budding-type organoids normally generated from EDTA based release of the crypt epithelium. Transcriptional profiling indicated that adult spheroids were undifferentiated and similar to regenerating crypts or fetal spheroids. To identify the cell of origin that generates adult spheroids, the authors labelled epithelial cells with VilCreERT-LSL-Tom, VilCre-LSL-GFP and Lgr5CreERT- LSLTom mice. From these experiments the authors conclude that that spheroids are only generated from Vil-Cre negative and Lgr5 negative cells. Next the authors deleted the anti- apoptotic gene Mcl1 using Vil-CreERT mice. This led to a strong apoptotic response throughout the crypt epithelium and tissues processed from knockout mice readily generated spheroids, and in vivo, replenishment of the gut epithelium was mediated by unrecombined cells. In a second model, CBCs were ablated using Lgr5DTR mice and VilCre negative cells were found again to contribute to regeneration of the crypt epithelium. Finally based on the absence of Vil-Cre reporter activity, the authors were able to sort out and perform scRNAseq to profile VilCre negative cells. These cells were found to be quiescent, express the stem cell marker Olfm4 and were also abundant in ribosomal gene expression.

      • *

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

      • *

      As pointed out by the authors themselves the study has important limitations that diminish enthusiasm. The primary issue relates to the inability of the team to identify markers of VilCre neg cells other than the fact that these cells are Olfm4+ and quiescent. Nonetheless, for the reasons stated above the manuscript should reach the target audience within the research community, if the authors can address the specific points below related to issues with methodology as well as defining more precisely the characteristics and growth requirements of adult spheroid cultures.

      Thank you for this positive analysis of our study.

      Major comments

      The main conclusion of the study is that Vil-Cre neg cells are rare quiescent Olfm4+ crypt cells. If this is the case, then standard EDTA treatment should release these cells as well. Consequently, spheroids should also emerge from isolated crypts grown in the absence of ENR. If this is not the case how do the authors explain this?

      We have tried hard to generate spheroids by culturing EDTA organoids in medium lacking ENR and by treating EDTA organoids with collagenase/dispase, without success. Therefore, we are left with the conclusion that spheroid-generating cells must be more tightly attached to the matrix than those released by EDTA, and that it is their release from this attachment by collagenase that triggers a regeneration-like phenotype. This hypothesis is supported by several models of regeneration in other tissues as indicated in our references (Gilbert et al., 2010; Machado et al., 2021; Montarras et al., 2005).

      From the text the authors appear to suggest that growth of adult spheroids is dependent initially on "material" released by collagenase/dispase treatment. An obvious candidate would be mesenchymal cells, which are known to secrete factors such as Wnts and PGE2 that drive spheroid morphology. To test this, the authors should treat spheroid cultures with Porcupine and/or PGE2 inhibitors.

      We followed similar reasoning, considering that spheroids express strongly Ptgs1 ,2 (Figure 3A). We thought their phenotype might be maintained by autocrine prostaglandin action. We tested aspirin, a Ptgs inhibitor, which was without effect on the spheroid phenotype. Besides, we explored a wide variety of conditions to test whether they would affect the spheroid phenotype [Aspirin-see above, cAMP agonists/antagonists, YapTaz inhibitors (verteporfin and CA3), valproic acid, Notch inhibitors (DAPT, DBZ, LY511455), all-trans retinoic acid, NFkB inhibitors (TCPA, BMS), TGFbeta inhibitor (SB431542)]. As these results were negative, we did not include them in the manuscript.

      • If these inhibitors block growth then this would suggest that either stromal cells or autocrine signalling involving these pathways is important. Overall, more in-depth analysis of the growth requirements of adult spheroids is required.*

      Figure 1d indicates that adult spheroids can be propagated for at least 10 passages. The abstract mentions they are "immortal". The text itself does not address this issue. More precise information as to how long spheroids can be propagated is required. If these cultures can be propagated for 10 passages or more it becomes important to determine what nutrients/mitogens in the basal media are driving growth? Alternatively, what is the evidence that spheroid cultures are completely devoid of mesenchymal cells. The text only mentions that "Upon replating, these spheroids could be stably cultured free of mesenchymal cells (Fig.1B)". No validation is shown to support this.

      We agree that "immortal" is not a good way to characterize our spheroids, as also pointed out by referee nr 1. We have changed that in the text, indicating the maximal number of replating we tested was 26 and replacing immortal by stably replatable. Of note, the spheroids could frozen/thawed and recultured many times.

      Related to the question whether mesenchymal cells could still contaminate the spheroid cultures, we can provide the following answers:

      • No fibroblasts could be seen in replated cultures and multiple spheroids could be repeatedly propagated from a single starting spheroid.
      • The bulk RNAseq experiment comparing organoids to ENR or BCM cultured spheroids show, despite expression of several mesenchymal markers (see matrisome in Fig3), absence of significant expression of Pdgfra (see in revision plan folder for CP20Millions results from the raw data of new suppl table 2, with Clu, Tacstd2 and Alpi shown as controls).
      • Regarding the nutrients/mitogens in the medium driving spheroid growth, we did not explore the point further than showing that they grow in basal medium (i.e. advanced DMEM), given that the presence of Matrigel makes it difficult to pinpoint what is really needed. In Figure 2, the authors describe the growth requirements for adult spheroids and indicate that spheroids grown in ENR or EN became dark and shrink. The representative images showing this are clear, but this analysis should be quantified.

      Added to the manuscript.

      In SF3, the gene expression profile of organoids from the sandwich method only partially overlaps with that of organoids from the old protocol. What are the gene expression differences between the 2 culture systems? Secondly, the sandwich method appears to sustain growth of Tom+ spheroids based on RNAseq and the IF images. This suggest that Vil-Cre negative cells are not necessarily the only source of adult spheroids and thus this experiment seems to indicate that any cell may be converted to grow as a spheroid under the right conditions. These points should be addressed.

      Looking back to our data in order to answer the point raised by the referee, we realized that we had inadvertently-compared organoids to ENR-cultured spheroids generated by the first protocol to BCM-cultured spheroids generated by the sandwich method. We have corrected this error in a new version of suppl fig3. This shows increased correspondence between genes up- or downregulated in the spheroids obtained in the two protocols (from 49/48% to 57/57% (Venn diagram on the new figure). We agree that, even after this correction, the spheroids obtained with the two protocols present sizeable differences in their transcriptome. However, considering the very different way these spheroids were obtained and cultured initially, we do not believe this to be unexpected. The important point in our opinion is that the core of the up- and down-regulated genes typical of the de-differentiation phenotype of adult spheroids is very similar, as shown in the heatmap (which was made with the correct samples!). Also, a key observation is that that both kind of spheroids survive and can be replated in basal medium. As already stated, this characteristic is only seen rare cases [spheroids obtained from rare FACS-purified cells (Smith et al 2018) or helminth-infected intestinal tissue (Nusse et al.2018)]. Together with the observation that the majority of them is not traced by VilCre constitutes what we consider the halmark of the spheroids described in our study. As shown in figure 4E (old protocol) and Suppl Fig.3 (sandwich protocol) both red and white spheroids were extremely low in VilCre expression. As stated in the text, the fact that some spheroids are nevertheless red is most probably related to the extreme sensitivity of the Rosa26Tom marker to recombination (Liu et al., 2013), but this does not mean that there are two phenotypically different kind of spheroids. It means that the arbitrary threshold of Rosa26Tom recombination introduces an artificial subdivision of spheroids with no phenotypical significance.

      Regarding the point made by the referee that "that any cell may be converted to grow as a spheroid under the right conditions", we agree and have shown with others that organoids acquire indeed a spheroid phenotype when cultured for instance in fibroblasts-conditioned medium (see suppl fig1B and (Lahar et al., 2011; Roulis et al., 2020) quoted in the manuscript). However, these spheroids cannot be propagated in basal medium, and revert to an organoid phenotype when put back in ENR (Suppl fig1B).

      *In Figure 4, the authors conclude that spheroids do not originate from Lgr5 cell derived clones even after 30days post Tam induction. Does this suggest that in vivo and under homeostatic conditions VilCre neg cells are derived from a distinct stem cell pool or are themselves a quiescent stem cell. Given the rarity of VilCre neg cells, the latter seems unlikely.

      *

      Despite their rarity, we believe VilCre-negative cells observed under homeostatic conditions are themselves quiescent stem cells. Actually, if they were derived from a larger stem cell pool, this pool should also be VilCre-negative. And we do not see such larger number of VilCre-neg cells under homeostatic conditions.

      The problem with the original assertion is that Lgr5-CreERT mice are mosaic and therefore not all Lgr5+ cells are labelled in this model. "White" spheroids may thus derive from cells that in turn derive from these unlabelled Lgr5 cells.

      We had considered the possibility that mosaicism [very low for VilCre (Madison et al., 2002); in the 40-50% range for Lgr5CreERT2 (Barker & Clevers. Curr Protoc Stem Cell Biol. 2010 Chapter 5)] could explain our data. We think, however that we can exclude this possibility on the basis that spheroids do not conform to the expected ratio of unrecombined cells, given the observed level of mosaicism. Indeed, for VilCre, a few percent, at most, of unrecombined cells in the epithelium translates into almost 100% unrecombined spheroids. For Lgr5CreERT2 mice, the mosaicism level is in the range of 40%, which is what we observe for EDTA organoids (Figure 4G), while spheroids were in their vast majority unrecombined.

      We have included a discussion about the possible role of mosaicism in the new version.

      ATACseq experiments were briefly mentioned in the manuscript but unfortunately little information was extracted from this experiment. What does this experiment reveal about the chromatin landscape of adult spheroids relative to normal organoids?

      We only performed this experiment to search for an explanation to the paradoxical absence of expression of the VilCre transgene in spheroids, despite robust expression of endogenous villin (Suppl Fig.4). We chose to show the chromatin landscape of a gene equally expressed in both organoids and spheroids (Krt19), a gene specifically expressed in spheroids (Tacstd2) and the endogenous Villin gene also expressed in both. We believe that the observation of a clear difference in pattern of the chromatin accessibility around the endogenous villin gene in organoids and spheroids provides an explanation to the observed results. The cis regulatory sequences needed for expression of the endogenous villin gene seem to be different in organoids and spheroids, which may explain why the regulatory sequences present in the transgene (only 12.4kb) might not allow expression of the transgene in spheroids. We have added a sentence in the manuscript clarifying this point. Missing is obviously the chromatin landscape around the VilCre transgene, but this is beyond reach in such kind of experiments.

      Reviewer #2 (Significance (Required)):

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

      Reviewer #3 (Evidence, reproducibility and clarity (Required)): CR-2024-02491

      An Lgr5-independent developmental lineage is involved in mouse intestinal regeneration

      Marefati et al.

      Homeostatic maintenance of the intestinal epithelium has long been thought to rely upon Wnt signaling responsive Lgr5-expressing stem cells that reside at the crypt base.

      However, myriad reported mechanisms or populations have been reported to underlie epithelial regeneration after injury. Many groups have reported that reacquisition of a fetal- link intestinal phenotype is an import part of the regenerative response, however the originating cell type has not been definitively identified. Herein, the authors demonstrate that cells from adult homeostatic intestine can generate immortal spheroids that resemble fetal spheroids and are derived independent of Lgr5+ intestinal stem cells (ISCs). The authors then draw the conclusion that this indicates that a hierarchical stem cell model applies to regeneration of the intestinal epithelium, in addition to the plasticity model.

      • *

      Comments:

      1. Please indicate what species is used for studies in Fig 1.

      All experiments were performed in Mus musculus.

      Please clarify if Figure 2 studies utilize Matrigel or not.

      Yes

      RNA-seq analyses of adult intestinal generated spheroids lack the granularity of single cell analyses and thus it is unclear if this is a homogeneous population or if the population has diversity across it (i.e., enteroids/organoids have a high level of diversity). Many of the conclusions from the RNA-seq study are broad and generalized-for example Fig 3F indicates that markers of the +4 ISC populations (Bmi1, tert, lrig1, hopx) were all expressed similarly in adult spheroids as compared to adult organoids. However, while this may be true in the bulk-RNA-seq analyses, clearly scRNA-seq would provide a better foundation to make this statement, as enteroids/organoids are comprised of heterogeneous subpopulations. . .and it might indicate that these +4 markers have only very low expression in the spheroids. Based upon these concerns, misconclusions are likely to be drawn.

      We agree and it would be certainly worthwhile to perform scRNAseq of adult spheroid populations. This would certainly be worth doing in future studies to explore the possible heterogeneity of adult spheroids. We nevertheless believe that our scRNAseq performed on homeostatic intestinal tissue from VilCre/Rosa26Tom mice identify Olfm4-low VilCre-neg cells that are likely at the origin of adult spheroids and display a quite homogenous phenotype.

      *The language around Figure 4 results is confusing. Please define "white" and "red". It might be simpler to designate recombined versus not recombined lineage.

      *

      We have clarified this in the figure.

      The hypothesis that collagenase/dispase solution acts as a proxy for injury is not demonstrated and backed by data. Thus, it is difficult to make the conclusion that this approach could represent a "stable avatar" of intestinal regenerating cells. It is clear that subpopulations of crypt-based cells generate spheroids in culture without collagenase/dispase (see the cited reference Smith et al, 2018).

      * *Smith et al demonstrate clearly the possibility to obtain spheroids with properties probably similar to ours from EDTA derived intestinal crypt cells. However they need to prepurify them by FACS. Besides, Nusse et al describe spheroids similar to ours after infection of the intestine by helminths (Nusse et al. 2018). In our case, and for most labs preparing enteroids with the EDTA protocol, the result is close to 100% organoids. Even if we treat EDTA organoids with collagenase, we do not obtain spheroids. This brought us to the conclusion that spheroid-generating cells must be more tightly attached to the matrix than CBCs and that it is their release from the matrix that activates the spheroid regeneration-like phenotype. This hypothesis is supported by several models of regeneration in other tissues as indicated in our references (Gilbert et al., 2010; Machado et al., 2021; Montarras et al., 2005)

      A study based on the absence of recombination in a VilCre lineage tracing scenario is not well-established to be strong experimental approach, as there are many reasons why recombination may not cells may not be lineage marked. In order to use this system as the authors intend, they first need to demonstrate that villin is not expressed in the discrete cell population that they are targeting. For the presented observational studies, this would be difficult to do. While they do demonstrate differences in chromatin accessibility between cells from organoids versus spheroids (fig s4), some of these differences could merely be due to the bulk analytical nature of the study and the lack of comparing stem cell populations from spheroids to stem cell populations from organoids-since the spheroids are likely homogenous versus the organoids that only have a small fraction of stem cells-and thus represent a mix of stem cell and differentiated cell populations. The authors do not demonstrate that villin protein expression varies in these cells.

      If it were found that villin is not expressed in their "novel" population, then one would expect that the downstream use of villin-based recombination would demonstrate the same recombination potential (i.e., Mcl1 would not be recombined). Both recombination studies in Fig 6 are difficult to interpret, and thus it is not clear if these studies support the stated conclusions. Quantification of number of crypts that are negative should be reported as a percentage of recombined crypts.

      We are sorry but there seems to be a complete misunderstanding of our data regarding the point raised by the referee. The important point of our initial observation is that despite robust expression of villin in spheroids, the VilCre transgene is not expressed (see figure 4E). This in our opinion makes absence of VilCre expression (or of Rosa marker recombination) a trustful marker of a new developmental lineage. All the data in figure 4 constitute an answer.

      *The reasoning about heterogeneity of cell type in organoids versus probable homogeneity of spheroids is well taken. However, as the endogenous villin gene is expressed in all cells of both organoids and spheroids, it is highly significant that only spheroids do not express the transgene. *

      We performed the ATACseq experiment to search for an explanation to the paradoxical absence of expression of the VilCre transgene in spheroids, despite robust expression of endogenous villin (Suppl Fig.4). We chose to show the chromatin landscape of a gene equally expressed in both organoids and spheroids (Krt19), a gene specifically expressed in spheroids (Tacstd2) and the endogenous Villin gene also expressed in both. We believe that the observation of a clear difference in pattern of the chromatin accessibility around the endogenous villin gene in organoids and spheroids provides an explanation to the observed results. The cis regulatory sequences needed for expression of the endogenous villin gene seem to be different in organoids and spheroids, which may explain why the regulatory sequences present in the transgene (only 12.4kb) might not allow expression of the transgene in spheroids. We have added a sentence in the manuscript clarifying this point. Missing is obviously the chromatin landscape around the VilCre transgene, but this is beyond reach in such kind of experiments.

      *Figure 8 indicates that the cell population identified by scRNA-seq may be quiescent. Companion IF or IHC should be conducted to confirm this finding, as well as other conclusions from the informatics conducted.

      *

      We agree that additional experiments could be performed to support this point. We are unfortunately not in a position to perform these experiments (see section 4 below).

      Clearly the data is intriguing, however, the conclusion is strong and is an over interpretation of the presented data. There are a number of validation or extension data that would enhance the overall interpretation of the study: 1. validation of scRNA-seq or bulk RNA-seq concepts by protein staining of intestinal tissues in the damage model will serve as a secondary observation. 2. identification of the ISC that they are defining is critical and important. There is already the notion that this cell type exists and it has been shown with various different markers. 3. expand the analyses of the fetal-like expression profiling to injured intestines to demonstrate that the lineage negative cells indeed express fetal-like proteins. 4. expand the discussion of the Clu+ cell type. Is this cell the previously described revival cell? If so, how does this body of work provide unique aspects to the field?

      We agree that all these suggested experiments could be performed and would be of interest. However, we consider that they would not modify the main message of our study and would only constitute an expansion of the present work. As already stated, we are not in the position to perform them (see section 4).

      *There is some level of conflicting data, with the stem population being proliferative in culture stimulated by the stromal cells, but quiescent in vivo and also based upon scRNA- seq data in Fig 9.

      *

      We do not see any conflict in our observation regarding this point. The observation that cells that are quiescent in vivo become proliferative when subjected to culture (with or without addition of stromal cells) is routinely made in a multitude of cell culture systems. In particular, it has been shown that intestinal tissue dissociation activates the Yap/Taz pathway, resulting in proliferation (Yu et al. Hippo Pathway Regulation of Gastrointestinal Tissues. Annual Review of Physiology, 2015 Volume 77, 201-227).

      Many of the findings have been previously reported: Population that grows as spheroids (Figure 2), Population that is Wnt independent (Figure 2), Lgr5 independent regenerative growth of the intestine (figure 3F, Figure 4), Clu+ ISCs drive regeneration (Figure 7).

      Whereas these individual findings have indeed been reported, it was in a different context. We strongly disagree with the underlying suggestion that our study would not bring new information. We have identified here a developmental lineage involved in intestinal regeneration that has not been described up to now.

      Minor comments:

        • The statement that spheroids must originate from collagenase/dispase digested material might be an overstatement. As spheroids generation from EDTA treated intestines have been previously reported (Smith et al, 2018). * See answer to point 4 above. *Overall while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

      *

      Reviewer #3 (Significance (Required)):

      Overal while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

      We can only disagree.

      4. Description of analyses that authors prefer not to carry out

      • *

      We have answered most questions raised by the referees by explaining our view, by clarifying individual points and, in several cases, by providing additional information that was not included in the original manuscript.

      In a limited number of cases when additional experiments were suggested, we were unfortunately obliged to write that we are not in a position to perform them. This is because my lab is closing after more than fifty years of uninterrupted activity. There will unfortunately be nobody to perform additional experiments.

      Nevertheless, as written by referees 1 and 2, we believe that the revised manuscript, as it stands, contains data that will be of interest to the people in the field and may be the bases for future developments. We hope editors will find interest in publishing it.

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      Referee #3

      Evidence, reproducibility and clarity

      RC-2024-02491

      An Lgr5-independent developmental lineage is involved in mouse intestinal regeneration Marefati et al.

      Homeostatic maintenance of the intestinal epithelium has long been thought to rely upon Wnt signaling responsive Lgr5-expressing stem cells that reside at the crypt base. However, myriad reported mechanisms or populations have been reported to underlie epithelial regeneration after injury. Many groups have reported that reacquisition of a fetal-link intestinal phenotype is an import part of the regenerative response, however the originating cell type has not been definitively identified. Herein, the authors demonstrate that cells from adult homeostatic intestine can generate immortal spheroids that resemble fetal spheroids and are derived independent of Lgr5+ intestinal stem cells (ISCs). The authors then draw the conclusion that this indicates that a hierarchical stem cell model applies to regeneration of the intestinal epithelium, in addition to the plasticity model.

      Comments:

      1. Please indicate what species is used for studies in Fig 1.
      2. Please clarify if Figure 2 studies utilize Matrigel or not.
      3. RNA-seq analyses of adult intestinal generated spheroids lack the granularity of single cell analyses and thus it is unclear if this is a homogeneous population or if the population has diversity across it (i.e., enteroids/organoids have a high level of diversity). Many of the conclusions from the RNA-seq study are broad and generalized-for example Fig 3F indicates that markers of the +4 ISC populations (Bmi1, tert, lrig1, hopx) were all expressed similarly in adult spheroids as compared to adult organoids. However, while this may be true in the bulk-RNA-seq analyses, clearly scRNA-seq would provide a better foundation to make this statement, as enteroids/organoids are comprised of heterogeneous subpopulations. . .and it might indicate that these +4 markers have only very low expression in the spheroids. Based upon these concerns, misconclusions are likely to be drawn.
      4. The language around Figure 4 results is confusing. Please define "white" and "red". It might be simpler to designate recombined versus not recombined lineage.
      5. The hypothesis that collagenase/dispase solution acts as a proxy for injury is not demonstrated and backed by data. Thus, it is difficult to make the conclusion that this approach could represent a "stable avatar" of intestinal regenerating cells. It is clear that subpopulations of crypt-based cells generate spheroids in culture without collagenase/dispase (see the cited reference Smith et al, 2018).
      6. A study based on the absence of recombination in a VilCre lineage tracing scenario is not well-established to be strong experimental approach, as there are many reasons why recombination may not cells may not be lineage marked. In order to use this system as the authors intend, they first need to demonstrate that villin is not expressed in the discrete cell population that they are targeting. For the presented observational studies, this would be difficult to do. While they do demonstrate differences in chromatin accessibility between cells from organoids versus spheroids (fig s4), some of these differences could merely be due to the bulk analytical nature of the study and the lack of comparing stem cell populations from spheroids to stem cell populations from organoids-since the spheroids are likely homogenous versus the organoids that only have a small fraction of stem cells-and thus represent a mix of stem cell and differentiated cell populations. The authors do not demonstrate that villin protein expression varies in these cells. If it were found that villin is not expressed in their "novel" population, then one would expect that the downstream use of villin-based recombination would demonstrate the same recombination potential (i.e., Mcl1 would not be recombined). Both recombination studies in Fig 6 are difficult to interpret, and thus it is not clear if these studies support the stated conclusions. Quantification of number of crypts that are negative should be reported as a percentage of recombined crypts.
      7. Figure 8 indicates that the cell population identified by scRNA-seq may be quiescent. Companion IF or IHC should be conducted to confirm this finding, as well as other conclusions from the informatics conducted.
      8. Clearly the data is intriguing, however, the conclusion is strong and is an over interpretation of the presented data. There are a number of validation or extension data that would enhance the overall interpretation of the study:
        • a. validation of scRNA-seq or bulk RNA-seq concepts by protein staining of intestinal tissues in the damage model will serve as a secondary observation.
        • b. identification of the ISC that they are defining is critical and important. There is already the notion that this cell type exists and it has been shown with various different markers.
        • c. expand the analyses of the fetal-like expression profiling to injured intestines to demonstrate that the lineage negative cells indeed express fetal-like proteins.
        • d. expand the discussion of the Clu+ cell type. Is this cell the previously described revival cell? If so, how does this body of work provide unique aspects to the field?
      9. There is some level of conflicting data, with the stem population being proliferative in culture stimulated by the stromal cells, but quiescent in vivo and also based upon scRNA-seq data in Fig 9.
      10. Many of the findings have been previously reported: Population that grows as spheroids (Figure 2), Population that is Wnt independent (Figure 2), Lgr5 independent regenerative growth of the intestine (figure 3F, Figure 4), Clu+ ISCs drive regeneration (Figure 7).

      Minor comments:

      1. The statement that spheroids must originate from collagenase/dispase digested material might be an overstatement. As spheroids generation from EDTA treated intestines have been previously reported (Smith et al, 2018).

      Overall while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

      Significance

      Overall while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

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      Referee #2

      Evidence, reproducibility and clarity

      In this manuscript, the Marefati et al. developed a novel approach to generate spheroids from adult intestinal epithelium using a collagenase/dispase based protocol. Adult spheroids were found to be distinct from classic budding-type organoids normally generated from EDTA based release of the crypt epithelium. Transcriptional profiling indicated that adult spheroids were undifferentiated and similar to regenerating crypts or fetal spheroids. To identify the cell of origin that generates adult spheroids, the authors labelled epithelial cells with VilCreERT-LSL-Tom, VilCre-LSL-GFP and Lgr5CreERT-LSLTom mice. From these experiments the authors conclude that that spheroids are only generated from Vil-Cre negative and Lgr5 negative cells. Next the authors deleted the anti-apoptotic gene Mcl1 using Vil-CreERT mice. This led to a strong apoptotic response throughout the crypt epithelium and tissues processed from knockout mice readily generated spheroids, and in vivo, replenishment of the gut epithelium was mediated by unrecombined cells. In a second model, CBCs were ablated using Lgr5DTR mice and VilCre negative cells were found again to contribute to regeneration of the crypt epithelium. Finally based on the absence of Vil-Cre reporter activity, the authors were able to sort out and perform scRNAseq to profile VilCre negative cells. These cells were found to be quiescent, express the stem cell marker Olfm4 and were also abundant in ribosomal gene expression.

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

      As pointed out by the authors themselves the study has important limitations that diminish enthusiasm. The primary issue relates to the inability of the team to identify markers of VilCre neg cells other than the fact that these cells are Olfm4+ and quiescent. Nonetheless, for the reasons stated above the manuscript should reach the target audience within the research community, if the authors can address the specific points below related to issues with methodology as well as defining more precisely the characteristics and growth requirements of adult spheroid cultures.

      Major comments

      The main conclusion of the study is that Vil-Cre neg cells are rare quiescent Olfm4+ crypt cells. If this is the case, then standard EDTA treatment should release these cells as well. Consequently, spheroids should also emerge from isolated crypts grown in the absence of ENR. If this is not the case how do the authors explain this?

      From the text the authors appear to suggest that growth of adult spheroids is dependent initially on "material" released by collagenase/dispase treatment. An obvious candidate would be mesenchymal cells, which are known to secrete factors such as Wnts and PGE2 that drive spheroid morphology. To test this, the authors should treat spheroid cultures with Porcupine and/or PGE2 inhibitors. If these inhibitors block growth then this would suggest that either stromal cells or autocrine signalling involving these pathways is important. Overall, more in-depth analysis of the growth requirements of adult spheroids is required.

      Figure 1d indicates that adult spheroids can be propagated for at least 10 passages. The abstract mentions they are "immortal". The text itself does not address this issue. More precise information as to how long spheroids can be propagated is required. If these cultures can be propagated for 10 passages or more it becomes important to determine what nutrients/mitogens in the basal media are driving growth? Alternatively, what is the evidence that spheroid cultures are completely devoid of mesenchymal cells. The text only mentions that "Upon replating, these spheroids could be stably cultured free of mesenchymal cells (Fig.1B)". No validation is shown to support this.

      In Figure 2, the authors describe the growth requirements for adult spheroids and indicate that spheroids grown in ENR or EN became dark and shrink. The representative images showing this are clear, but this analysis should be quantified.

      In SF3, the gene expression profile of organoids from the sandwich method only partially overlaps with that of organoids from the old protocol. What are the gene expression differences between the 2 culture systems? Secondly, the sandwich method appears to sustain growth of Tom+ spheroids based on RNAseq and the IF images. This suggest that Vil-Cre negative cells are not necessarily the only source of adult spheroids and thus this experiment seems to indicate that any cell may be converted to grow as a spheroid under the right conditions. These points should be addressed.

      In Figure 4, the authors conclude that spheroids do not originate from Lgr5 cell derived clones even after 30days post Tam induction. Does this suggest that in vivo and under homeostatic conditions VilCre neg cells are derived from a distinct stem cell pool or are themselves a quiescent stem cell. Given the rarity of VilCre neg cells, the latter seems unlikely. The problem with the original assertion is that Lgr5-CreERT mice are mosaic and therefore not all Lgr5+ cells are labelled in this model. "White" spheroids may thus derive from cells that in turn derive from these unlabelled Lgr5 cells.

      ATACseq experiments were briefly mentioned in the manuscript but unfortunately little information was extracted from this experiment. What does this experiment reveal about the chromatin landscape of adult spheroids relative to normal organoids?

      Significance

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

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      Referee #1

      Evidence, reproducibility and clarity

      In this manuscript, Marefati et al report an Lgr5-independent lineage in the regenerating intestine using in vitro organoids and in vivo injury-coupled lineage tracing model. In organoids, collagenase/dispase dissociated resulted in "immortal spheroids" that maintain a cystic and undifferentiated phenotype in the absence of standard growth factors (Rspondin/Noggin/EGF). Bulk RNAseq of spheroids demonstrates downregulation of classical CBC signatures and upregulation of fetal spheroid, mesenchymal, inflammation and regenerative signatures. In mice, Villin-Cre lineage tracing revealed some Villin-negative progenies that lack reporter tracing throughout crypt-villus ribbons after injury. The authors proposed that there is Lgr5-independent population support the regenerative response upon CBC depletion. A major caveat of this study is the identification of this population is based on absence of VilCre expression. It is surprising that there is no characterisation of Lgr5 expression throughout the manuscript whilst claiming of a Lgr5-independent lineage. Although the research question is potentially interesting, the concept of epithelial reprogramming upon injury is well documented in the field. The data generated in this manuscript also seem to be preliminary and lack of detailed characterisation. Below are specific comments.

      • Expression of Lgr5 should be properly characterised throughout the manuscript in both organoid models and injury-induced regeneration in vivo.
      • An important question is the origin of these "Lgr5-independent" adult spheroids. They look and appear like fetal organoids, which could be induced by injury (e.g. upon collagenase/dispase dissociation). Have the authors tried to culture fetal spheroids in BCM over extensive period of time? Do they behave the same? This would be a great way to directly compare the collagenase/dispase-derived organoids with fetal origin.
      • Fig 1C, Why is the replating spheroid culture time different between mesenchymal cells and conditioned medium?
      • It is unclear how the bulk RNA-seq data in Fig. 3 were compared. How long were the adult organoids and spheroids cultured for (how many passages)? Were they culture in the same condition of were they in ENR vs BCM? These are important information to consider when interpreting the results. For instance, are Ptgs1 & Ptgs2 expression in adult spheroids the same in ENR vs BCM? Are the gene signatures (regenerative, fetal and YAP) changed in adult spheroids culturing in ENR vs BCM?
      • It is stated: "In agreement with their aptitude to grow indefinitely, adult spheroids express a set of upregulated genes overlapping significantly with an "adult tissue stem cell module" [159/721 genes; q value 2.11 e-94) (Fig.S2F)].". What is the definition of "indefinitely"? Are they referring to the Fig 1B where spheroid were passaged to P10? The authors should avoid the term "indefinitely" but use a more specific time scale, e.g. passages, months etc.
      • SuppFig 3D: Row Z-Score is missing the "e" in Score.
      • Fig 4E: Figure legend says QNRQ instead of CNRQ.
      • Fig 4G: The brightfield image of adult spheroids 5 days after 3x TAM injections doesn't look like a spheroid. It seems to be differentiating.
      • Fig 4: Most mouse model data are missing the number of mice & their respective age used for organoid isolation.
      • Fig 4A-D, H-G: How was fluorescent signal of organoids quantified? How many images? Were there equal numbers of organoids? This all needs to be included in methods/figure legends.
      • Figure 4B-D, G-H: Which culturing conditions were used for adult spheroids? Original method or sandwich method?
      • Fig 6D-E: Please add the timepoint after DT administration these samples are from. It is not listed in text or figure legend.
      • SuppFig 6D: again timepoint is missing.
      • SuppFig 6: How were the crypts of these mice (DT WT & DT HE) isolated? Was this via EDTA? Also, what is the timepoint for isolation for these samples? Even if untreated, the timepoint adds context to the data. Please add more context to describing these different experiments, either in the figure legends or methods section.
      • SuppFig 6E: The quality of the heatmap resolution is too poor to read gene names.
      • Fig.5-7, are the regenerating crypt-villus units fully differentiated or are they maintained in the developmental state? Immunostaining of markers for stem cells (Lgr5), differentiated lineages (Alpi, Muc2, Lyz, ChgA etc.) and fetal state (Sca1, Trop2 etc) should be analysed in those "white" unrecombined crypt-villus units.
      • The following text needs clarification:

      "The kinetics of appearance of newly formed un-recombined ("white") crypts was studied after a single pulse of DT (Fig.7A). This demonstrated an increase at 48 hours, with further increase at day 10 and stable maintenance at day 30. The presence of newly formed white crypts one month after toxin administration indicates that the VilCre-negative lineage is developmentally stable and does not turn on the transgene during differentiation of the various epithelial lineages occurring after regeneration (Fig.7B). Comment: The "newly formed" is an overstatement, the data doesn't conclude that those are "new" crypts. The end of the sentence states that these "white" crypts form developmentally stable lineages, thus these white crypts at day 30 could originate from the initial injury. There was no characterisation of the various epitheial lineages. Are they fully differentiated? Is Lgr5 expressed one month after toxin administration? Can the VilCre neg lineage give rise to CBCs?

      The relationship between white crypt generation and appearance of Clu-positive revival cells (Ayyaz et al., 2019) was then explored. In agreement with others and similar to what happens in the irradiation model, (Ayyaz et al., 2019; Yuan et al., 2023) Clu-positive cells were rare in crypts of untreated mice and their number transiently increased forty-eight hours after a single pulse of DT, and more so after three pulses of DT (Fig.7C,D). Comment: Comparing 1 pulse at day 2 vs 3 pulses at day 5 makes the data hard to interpret. How is the Clu ISH level for 1 pulse at day 5? Are they equivalent?

      Clu-positive cells were less frequently observed in white crypts (see "Total" versus "White" in Fig.7C). This fits with the hypothesis that Clu expression marks acutely regenerating crypts and that a proportion of the white crypts are chronically regenerating due to DTR expression in CBCs." Comment: I believe the authors suggested that the discrepancy of less Clu expression in white crypts is due to the ectopic expression of DTR in CBCs causing low grade injury without DT administration. This means that some white crypts could have been formed before the administration of DT, and thus are on a different regenerative timeline compared to the white crypts formed from DT administration. Is there any proof of the chronic regeneration? Immunostaining of chronic regenerative markers such as Sca1, Anxa1 or Yap1 nuclear localization would support the claim. It'd be important to show only the white crypts, but not the RFP+ ones, show regenerative markers. - Fig 7D-E: What are the timepoints of harvest for HE-WT-HE 1 pulse DT mice and HE-HE-HE PBS injected mice? - Fig 8-9: Regarding the CBC-like Olfm4 low population, what is the status of Lgr5? This should be shown in the figure since the argument is that this is an Lgr5-independent lineage. And what about the regenerative, Yap, mesenchymal and inflammatory signatures? Are they enriched in the white crypts similar to the in vitro spheroids?

      Significance

      Strengths: The study employed a range of in vitro and in vivo models to test the hypothesis.

      Limitations: Unfortunately, the models chosen did not provide sufficient evidence to draw the conclusions. Injury induced reprogramming, both in vivo and in vitro, has been well documented in the field. The new message here is to show that such reprogrammed state is continuous rather than transient; instead of regenerating Lgr5+ stem cells, it can continue to differentiate to all cell lineages in Lgr5-independent manner. However, through the manuscript, there was no immunostaining of Lgr5 and other differentiation markers. The conclusion is an overstatement without solid proof.

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      Reply to the reviewers

      Manuscript number: RC-2023-02306

      Corresponding author(s): John, Yates

      [Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

      • *

      If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

      1. General Statements [optional]

      We greatly appreciate the reviewers taking time from their busy scientific careers to evaluate our manuscript. We were elated to read all the positive comments, such as “the conclusions are well-supported and convincing”, “should contribute to a more nuanced understanding of SCZ pathogenesis”; “The potential implications for drug development underscore the broader significance of the study in advancing our knowledge of neurobiology and its relevance to neurological disorders like schizophrenia”, and “The study is informative, and has great potential to enrich the specific literature of this field”. We also found the constructive criticism very helpful for improving our manuscript. We performed additional experiments and bioinformatic analyses, as requested. We modified the manuscript to answer the reviewers’ questions. Due to its complexity, it is difficult to describe the different and sometimes conflicting hypotheses of SCZ pathogenesis in a single manuscript. This complexity is reflected in the conflicting requests from the reviewers. One reviewer requested we investigate and highlight the role of non-neuronal cells in SCZ while another reviewer suggested we did not focus enough on synaptic proteins. We believe we have achieved a balance to represent the intricacy of SCZ biology and the different opinions of the reviewers.

      Thanks again.

      2. Point-by-point description of the revisions

      This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

      • *

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

      Summary: Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). In this manuscript, McClatchy and colleagues used a conventional approach combining immunoprecipitation (IP) of endogenous target proteins (baits) followed by liquid chromatography mass spectrometry (MS) analysis of the co-immunoprecipitating proteins to map protein-protein interaction (PPI). This interaction network is centered around baits that had been annotated as susceptibility factors for schizophrenia (SCZ). A variety of previous studies have identified thousands of such SCZ susceptibility factors. Mostly based on the availability of antibodies, 8 bait proteins were selected in this study. The authors reasoned that immunoprecipitating endogenous proteins from tissues using specific antibodies was a more accurate view of physiological conditions than epitope tagging followed by affinity purification (AP) from cells in culture. The model system from which proteins were extracted was the hippocampus dissected from mice that had been treated or not by phencyclidine (PCP), a drug that has been shown to induce SCZ symptoms in humans and animals. By comparing the proteins identified and quantified from the PCP-treated samples against control IPs and/or saline-injected mouse controls, a large number of PPI were deemed statistically significant. Most of these potential interactors were not present in PPI databases (BioGRID), most likely because such databases are populated with large-scale APMS datasets from cell cultures, with very few studies using brain tissue. Strikingly, many of the co-immunoprecipitated proteins were also known as SCZ susceptibility factors, which lend weight to the hypothesis that these factors form a large protein interaction network, localized at the synapses.

      Major comments: - Are the key conclusions convincing? Overall, the conclusions drawn from the experimental design, data analysis, and corroboration with existing literature are well-supported and convincing. When selecting the SCZ susceptibility factors, the authors clearly state their goal, the databases used for gene selection, and the rationale for choosing proteins with synaptic localization. The inclusion of evidence from genetic studies and previous publications strengthens the credibility of the selected genes. The methodology used to establish the novel SCZ PPI network is mostly well-described (see minor comments below). The use of an 15N internal standard also adds rigor to the quantitation of PPI. The GO enrichment analysis provides valuable insights into the biological functions and cellular components associated with the SCZ PPI network. The annotation of identified proteins using the SynGo synaptic database and the distribution of annotated synaptic proteins among different baits further support the biological relevance of this PPI network. The cross-referencing of the PPI network with published genetic studies on SCZ susceptibility genes adds robustness to the findings. Specifically, the observation that 68% of protein interactors have evidence of being potential SCZ risk factors is a strong corroboration of the prevailing hypothesis in the field. Finally, the significant changes induced by PCP that were identified for all baits except Syt1, along with the comparison of altered proteins with SAINT-identified PPI, add depth to the understanding of PCP modulation.

      - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? No, but note that APMS/IPMS has been around for more than a decade (Introduction page 3).

      We agree and did not mean to imply that IP-MS is new technology. We tried to convey that IP-MS is not new technology, but the number of IP-MS studies employed to study the PPI of endogenous proteins in brain tissue is a small percentage of all the published PPI MS studies.

      We added the following to the Conclusions to clarify this point: “Although IP-LC-MS technology has been employed for more than a decade, quantitation of proteins using this strategy in mammalian tissue is scarce in the literature.”

      - 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. One piece of data that is missing are Western blots using the 8 selected antibodies against the proteins extracted from their experimental samples to validate the antibodies recognize 1 protein of the expected size from these tissue extracts.

      We took your suggestion and performed immunoblots with our 8 IP antibodies using the starting material (i.e. rat brain hippocampus). All antibodies recognized a single band of the approximate molecular weight of the target except for the Gsk3b, which produced a doublet instead of a single band. This image is similar to what has been observed with the phosphorylation of Gsk3b(Krishnankutty, Kimura et al. 2017, Vainio, Taponen et al. 2021). To provide evidence that the additional band observed for Gsk3b is the phosphorylated target protein, we searched our Gsk3b IP dataset for a differential phosphorylation (i.e. 79.9663) on S,T, or Y. Even though we did not perform phosphorylation enrichment, we identified S389 as abundantly phosphorylated in all Sal and PCP samples consistent with our immunoblot. Images of these immunoblots are now Supplementary Figure 1.

      • 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. Running SDS-PAGE and Western blotting should be straightforward and cheap.

      - 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 rationale for the short duration between PCP injection and animal sacrifice is only explained in the discussion section (page 17). The fact that this short treatment of less than 30 min should prevent any change in transcription or translation should be introduced earlier (in the experimental procedures).

      We agree this is an important aspect of the study and that it suggests that the effect of PCP is independent of changes in transcription and translation as stated in the Discussion.

      We added the following to the Introduction:

      “PCP was administered for less than 30min., which precluded any changes in transcription or translation and allowed us to focus on PPI.*” *

      Note that the duration is written as 26 min on page 4 and 25 min on page 9. Please reconcile these numbers*. *

      We have corrected this typo. It was 26min.<br /> Is there any biological significance for this SCZ study that the mice were maintained on a reverse day-night cycle?

      Rats are nocturnal animals, i.e. active at night and sleep during the day. In this study, rats were housed on a reverse day-night cycle so that assessment of the response to PCP could be evaluated during their active phase. This is not specific SCZ research and is the routine protocol for behavioral testing in the Powell laboratory. It is not clear from reading Experimental Procedures/Bioinformatic Analysis section (page 6) if normalized N14/N15 protein ratios measured in the bait-IPs and control-IPs were used for the SAINT analysis? Or did the authors used label-free quantitation with spectral counts?

      We apologize for not making the methods clearer. In the results, it is stated that the N14 identifications are used in the SAINT analysis, and we state in the Discussion that SAINT uses spectral counts. We modified the Experimental Procedures/Bioinformatic Analysis section (page 6) to state: The input for SAINT was only the 14N identifications.

      *- Are prior studies referenced appropriately? Yes

      • Are the text and figures clear and accurate? *Fig1C: The workflow is a little too simple, the authors might want to add more details.

      We revised Fig1C with more details as suggested.

      FigS1C: Please add x-axis title (spectral counts) directly to the figure.

      “Spectral counts” was added to the x-axis. FigS1C is now FigS2C ,with the addition of the immunoblots you suggested. Fig2B-D: The color scale bar should have number values to denote lower and upper limits in % (as opposed to "lowest" and "highest"). Numerical values were added to replace the upper and lower limits. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions? No * *

      Reviewer #1 (Significance (Required)):

      • Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. In this study, the authors have drastically expanded the protein interaction landscape around 8 known SCZ susceptibility factors by using a conventional IPMS approach. Performing the IPs on protein extracted from hippocampus dissected from mice treated with phencyclidine to model SCZ increases the biological significance of such lists of proteins. Furthermore, the co-immunoprecipitation of many other SCZ susceptibility factors along with the 8 selected baits supports the hypothesis that these proteins of varied functions are part of large interaction networks. Overall, the integration of experimental data with in silico networks, along with the quantification of PPI changes in response to PCP, should contribute to a more nuanced understanding of SCZ pathogenesis. The potential implications for drug development underscore the broader significance of the study in advancing our knowledge of neurobiology and its relevance to neurological disorders like schizophrenia.

      • Place the work in the context of the existing literature (provide references, where appropriate). Overall, this study contributes to the existing literature by providing experimental data on in vivo PPI networks related to SCZ risk factors. Not only do the authors validate 124 known interactions but also they identify many novel PPI, due to a gap in the existing literature regarding the comprehensive mapping of PPI directly from tissue extracts, especially brain tissue. The authors advocate for more IPMS studies in mammalian tissues to generate robust tissue-specific in silico networks, which agrees with the growing understanding of the importance of tissue-specific networks for identifying disease mechanisms and potential drug targets. Furthermore, the SCZ PPI network reported here is enriched in proteins previously associated with SCZ, which aligns with the existing literature emphasizing the involvement of certain proteins and pathways in the pathogenesis of SCZ [References: 78-85]. The authors also investigate the response of the SCZ network to PCP treatment, hence providing insights into the potential effects of post-translational modifications, protein trafficking, and PPI alterations in a model of schizophrenia, which adds to existing knowledge about the impact of PCP on the molecular processes associated with SCZ [References: 88, 89, 92].

      • State what audience might be interested in and influenced by the reported findings. Overall, the findings reported in this manuscript have implications for both basic research in molecular biology and potential translational applications in the development of targeted therapies for neurological disorders, particularly schizophrenia. The study delves into in vivo protein-protein interaction (PPI) networks related to genes implicated in schizophrenia (SCZ) risk factors. Researchers in neuroscience, molecular biology, and psychiatry would find the information valuable for understanding the molecular basis of SCZ. The study highlights the potential for identifying disease "hubs" that could be drug targets. Pharmacologists and drug developers interested in targeting protein complexes for drug development, especially in the context of neurological disorders, may find the study relevant.

      • 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. Technical Expertise | biochemistry, liquid chromatography mass spectrometry, proteomics, computational biology, protein engineering, protein interaction networks, post-translational modifications, protein crosslinking, proximity labeling, limited proteolysis, thermal shift assay, label-free and isotope-labeled quantitation. Biological Applications | human transcriptional complexes, apicomplexan parasites, viruses, nuclear envelope, ubiquitin ligases, non-model organisms.

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

      Summary: McClatchy, Powell and Yates aimed at identifying a protein interactome associated to schizophrenia. For that, they treated rats (N14 and N15) with PCP, which disturbs gutamatergic transmission, as a model for the disease and co-immunoprecipitated hippocampi proteins, which were further analyzed by standard LC-MS.

      The study is new, considering not much has been done in this direction in the field of schizophrenia. This justifies its publication. On the other hand, a major flaw of the is the lack of information on the level of interaction of the so called protein interactome. Meaning, we cannot distinguish, as the study was performed, which proteins are directly interacting with the targets of interest from proteins which are interacting with targets´ interactors. The different shells of interaction are crucial information in protein interactomics.

      Major: most of I am pointing below must be at least discussed or better presented in the paper, as It may not be solvable considering how the study has been conducted.

      1) The study fails in defining the level of interaction of the protein interactome with the considered targets. This has been shortly mentioned in the discussion, but must be more explicit to readers, for instance, in the abstract, introduction and in the methods sections. We agree this is crucial information that is absent from our dataset. As we explained in the Discussion, we cannot distinguish between PPI that are direct interactors with the target protein and PPI that reside in a multi-protein complex that includes the protein (i.e. indirect). This is an inherent problem with any IP-MS study. We amended the Introduction to highlight the ambiguity of the interaction data produced by the IP-MS approach, as you suggested.

      Text added to the Introduction:

      “Regardless of whether Ab or tagged proteins are employed to identify PPI from a biological sample, it cannot be determined if the identified interactor binds directly to the target protein or reside in a complex of proteins that includes the target protein (i.e. indirect).”

      Since this important information is routinely missing from IP-MS studies, we decided to try to determine the level of interaction by using the artificial intelligence algorithm AlphaFold3(AF3). We believe it is not yet optimized for PPI, but AF3 is a big leap forward in the field of structural biology. For example, we observed AF3 did not predict high confident structures for our large membrane target proteins and was unable to validate known direct PPI of these targets. In addition, analyzing data with AF3 is currently not automated or streamlined so with ~1600 PPI identified in our dataset, we chose to look at one target protein, Ppp1ca. AF3 identified many known direct binding proteins in our Ppp1ca PPI dataset, which gives high confidence to the novel PPI predicted to be direct interactors. The AF3 data is encompassed in an additional Figure 6.

      The following was added to the Results Section:

      “A disadvantage of IP-MS studies is that it cannot distinguish between a PPI that binds directly to the target protein, and a PPI in which the interactor and target protein reside the same multiprotein complex (i.e. indirect). We sought to predict which PPI may be directly interacting with its target protein by using the artificial intelligence algorithm AlphaFold3(AF3) (Abramson, Adler et al. 2024). First, we analyzed the predicted AF3 structure of the targets using the pTM score and the fraction of each structure calculated to be disordered (Figure 6A and Supplementary Table7). Our reasoning was that if targets have a poorly resolved structures, it will be difficult to screen them for direct PPI. A pTM score >0.5 suggests that the structure may be correct (the highest confidence score is 1). Undefined or disordered regions hinder the accuracy of the prediction. All targets possessed a pTM score > 0.5 except Syt1. The disordered fraction negatively correlated with the pTM score, as expected. Gsk3b, Ppp1ca, and Map2k1 had the highest pTM scores and were also the smallest of our target proteins (Figure 6B). Ppp1ca had the most confident structure (i.e. pTM 0.9) and the smallest disordered fraction (i.e. 0.07). Next, we determined the AF3 prediction of previously reported direct interactions of the targets. We used the iPTM score to determine interaction confidence. An iPTM score >0.8 is considered a highly confident direct interaction, whereas 0.8. These eight PPI have all previously been reported to form a direct interaction with Ppp1ca, except Phactr3 (Zhang, Zhang et al. 1998, Terrak, Kerff et al. 2004, Hurley, Yang et al. 2007, Marsh, Dancheck et al. 2010, Ragusa, Dancheck et al. 2010, Ferrar, Chamousset et al. 2012, Choy, Srivastava et al. 2024, Xu, Sadleir et al. 2024)*. Phactr3 is structurally similar to, but less studied than, the reported direct interactor Phactr1. These interactors are all inhibitors of PP1 except Ppp1r9b which targets Ppp1ca to specific subcellular compartments. Nine PPI were assigned a score The following has been added to the Discussion:

      Our SCZ PPI network consists of two types of PPI: direct physical interactions and “co-complex” or indirect interactions. Typically, the nature of the interaction can be distinguished in IP-MS studies. We decided to employ the new AF3 algorithm to screen the PPI of Ppp1ca to provide evidence for direct interactors. We chose to examine the PPI assigned to Ppp1ca, because its structure was the most confident among our target proteins and AF3 correctly predicted a known direct interactor with high confidence. Ppp1ca is a catalytic subunit of the phosphatase PP1, which is required to associate with regulatory subunits to create holoenzymes (Li, Wilmanns et al. 2013). Eighteen PPI were predicted to be directly interacting with Ppp1ca using a 0.6 or higher iPTM filter. This filter may be too conservative and generate false negatives, because another study employed a 0.3 filter followed by additional interrogation to screen for direct PPI (Weeratunga, Gormal et al. 2024). Forty-four percent of these predictions were confirmed by previous publications. Most of the validated direct interactions are inhibitors of the phosphatase, but one, Ppp1r9b (aka spinophilin), is known to target Ppp1ca to dendrite spines to enhance its activity to specific substrates (Allen, Ouimet et al. 1997, Salek, Claeboe et al. 2023). This high correlation with the literature provides substantial confidence in the novel PPI predicted to be direct Ppp1ca interactors. The AF3 screen predicted that NDRG2 directly interacts with Ppp1ca. This protein is known to regulate many phosphorylation dependent signaling pathways by directly interacting with other phosphatases including Pp1ma and PP2A (Feng, Zhou et al. 2022, Lee, Lim et al. 2022). Actin binding protein Capza1 was also predicted to directly interact with Ppp1ca and Ppp1ca interacts with actin and its binding proteins to maintain optimal localization for efficient activity to specific substrates (Foley, Ward et al. 2023). Hsp1e is a heat shock protein predicted to directly interact with Ppp1ca. Although there is no direct connection to Ppp1ca, other heat shock proteins have been reported to regulate Ppp1ca (Mivechi, Trainor et al. 1993, Flores-Delgado, Liu et al. 2007, Qian, Vafiadaki et al. 2011). We also observed that many of these direct PPI were altered with PCP treatment. One direct interactor, Ppp1r1b (aka DARPP-32), is phosphorylated at Thr34 by PKA in the brain upon PCP treatment. This phosphorylation event converts Ppp1rb to a potent inhibitor of Ppp1ca(Svenningsson, Tzavara et al. 2003). Importantly, manipulation of Thr34 attenuated the behavioral effects of PCP. Consistent with this report, Ppp1r1b-Ppp1ca interaction was only observed with PCP in our study. Further investigation is needed to determine if our novel direct interactors regulate the PCP phenotype. We conclude that AF3 can provide important structural insights into the nature of PPI obtained from large scale IP-MS studies.

      2) Considering the protein extraction protocol, it is fair to mention that only the most soluble proteins are being considered here. I am bringing this up since the importance of membrane receptors is clear in the studied context. This is an interesting point. It has been predicted that transmembrane proteins constitute 25-30% of the proteome(Dobson, Remenyi et al. 2015). Thus, we would predict our dataset will have more soluble proteins than membrane proteins. Half of our target proteins were transmembrane proteins, so in designing the protocol for this study we ensured that these membrane proteins could be significantly enriched compared to the control IPs (Supplementary Figure 2C). In addition, compared to soluble proteins, membrane proteins are notoriously difficult to identify by bottom-up proteomics (Savas, Stein et al. 2011). We decided to investigate how many of our protein interactors were transmembrane proteins. Using Uniprot, 199 (20%) of our protein interactors were determined to have a transmembrane domain. Therefore, this data does not support the statement that only the most soluble proteins are being considered in our study. We added this percentage of transmembrane proteins in our network to the text of the Results section.

      3) It is not clear from the methods description if antibodies from all 8 targets were all together in one Co-IP or have been incubated separately in 8 different hippocampi samples. It seems the first, given how results have been presented. If so, this maximizes the major issue raised above (in 1). We apologize for not clearly describing our experimental design. All the targets were immunoprecipitated separately and analyzed separately on the mass spectrometer. With all the biological replicates and two conditions (i.e. Saline and PCP), we performed 48 individual, separate IPs. There were an additional 48 individual, separate IPs run in parallel that were the control IPs.

      We modified the schematic of our experimental design in Figure 1C to clarify that the 8 targets IPs were analyzed separately. In addition, we modified the Results to read:

      “In total, 96 (48 bait and 48 control) IPs were performed, and each was analyzed separately by LC-MS analysis.”

      4) Definitely, results here are not representing a "SCZ PPI network". PCP-treated animals, as any other animal model, are rather limited models to schizophrenia. As a complex multifactorial disease, synaptic deficits, which is the focus of this study, can no longer be considered "the pivot" of the disease. Synaptic dysfunction is only one among many other factors associated to schizophrenia.

      We do agree that synaptic dysfunction is only one factor associated with SCZ and we will discuss this more in our response to your next comment.

      We understand the limitations of PCP as an animal model of SCZ. It is quite difficult to model a specific human complex multifactorial neurological disease in rodents and we would contend that there is no single universal SCZ model that everyone agrees with. We addressed this by adding the following to the Introduction:

      Since many SCZ symptoms are uniquely human, this is no single animal model that truly replicates all the complex human SCZ phenotypes(Winship, Dursun et al. 2019). In this respect, all SCZ animal models can be considered limited.* “ *

      We respectfully disagree, however, with the term SCZ PPI network. This study is focused on SCZ by choosing proteins implicated in SCZ, quantitating how the PPI changes in a SCZ model, and discussing how our findings are relevant to SCZ pathogenesis. So, it seems logical to call our dataset a SCZ PPI network. We do concede that without further experimentation we do not know if these PPI play a causal role in SCZ. Furthermore, our novel PPI may involve biological pathways unrelated to SCZ and that have relevance to other biological conditions.

      We added the following statement to the Discussion to address this comment:

      “Even though our network was constructed in the context of SCZ, our dataset has relevance to other neurological diseases where our targets have been implicated in the pathogenesis.

      5) Authors should look for protein interactions that might be happening also in glial cells. They are not the majority in hippocampus, but are present in the type of tissue analyzed here. Thus, some of the interactions observed might be more abundantly present in those cells. Maybe enriching using bioinformatics tools the PPI network to different cell types.

      As mentioned above, we agree that synaptic dysfunction is just one of the hypotheses of SCZ pathogenesis and emerging evidence suggests that dysfunction in astrocytes and microglia are factors. Since these non-neuronal cells can regulate synapses, these hypotheses are not mutually exclusively and suggests that at the cellular level SCZ etiology involves multiple cell types.

      We addressed your query by comparing our PPI network to an RNA-seq analysis of different cell types in the rodent brain(Zhang, Chen et al. 2014). First, we analyzed our target proteins, and found that they were expressed in all cell types to varying degrees except Syngap which was not in the RNA-seq database. This data is now represented in Figure 3E. We then determined the RNA abundance distribution of all the protein interactors, which is represented in Figure 3D as a heatmap. From a bird’s eye view, it suggests that some PPI exist in non-neuronal cells. Next, we determine how many of our protein interactors were enriched in one cell type, which is shown in Figure 3F. We defined an enriched protein as having >50% of the RNA signal in one cell type. We identified 175 proteins that were enriched in one cell type compared to the entire RNA-seq dataset which had 4008 enriched proteins. In the entire RNA-seq dataset, 24% of the enriched proteins were in neurons whereas 47% of our protein interactors were enriched in neurons. This is consistent with the enrichment of synaptic proteins in our network. There was also an increased percentage of astrocytes (19%) and oligodendrocytes (6%) in our network compared to the entire database (i.e. astrocytes-11% and oligodendrocytes-4%). In other cell types, such as microglia, there was less protein enrichment in our network compared to the database. We have amended this cell type analysis to our manuscript and concluded that a portion of our PPI network may occur in non-neuronal cells. We also created a supplementary table of our network with its associated RNA-seq data.

      Text added to the Results:

      “Non-synaptic proteins represented 59% of our network suggesting that some PPI may occur in non-neuronal cells. To investigate this possibility, we annotated our network with a transcriptome rodent brain database of eight cell types(Zhang, Chen et al. 2014). All the targets were detected in all cell types but there was obvious enrichment in specific cell types for some targets (Figure 3E). Syngap1 was not in the database. We also observed a large variation of cellular distributions for the interactors (Figure 3D). Next, we sought to determine how many interactors are enriched in a particular cell type by defining cell enrichment as a protein having >50% RNA signal in one cell type. We identified 175 protein interactors enriched in one cell type, whereas the entire database had 4008 proteins enriched (Figure 3F). Consistent with our synaptic enrichment, 47% of the enriched protein interactors were in neurons whereas only 24% of the enriched protein in the entire database were in neurons. We also observed an increase in protein interactors enriched in astrocytes compared to the database. Overall, this analysis provides evidence that our identified PPI may occur in non-neuronal cells.”

      Text added to the Discussion:

      “The exact etiology of SCZ, however, remains unclear and synaptic dysfunction is only one hypothesis (Misir and Akay 2023). There is evidence for the involvement of non-neuronal cell types, including endothelial cells, astrocytes, and microglia(Tarasov, Svistunov et al. 2019, Rodrigues-Neves, Ambrosio et al. 2022, Stanca, Rossetti et al. 2024). Although we observed an enrichment of synaptic proteins in our SCZ network, we provided evidence that a portion of our network may occur in non-neuronal cells. Since non-neuronal cells can regulate synapses(Vilalta and Brown 2018, Bauminger and Gaisler-Salomon 2022), synaptic dysfunction and perturbations in non-neuron cells in SCZ etiology are not mutually exclusive. Our data corresponds with emerging evidence that pathogenesis is multifaceted, involving dysfunction in multiple cell types.

      Minor: 1) in the abstract, it is not clear if 90% of the PPI are novel to brain tissue in general or specifically schizophrenia. We apologize for the confusing sentence. 90% are novel meaning the PPI have not been reported in any study. We changed the abstract to read:

      “Over 90% of the PPI have not been previously reported.”

      2) authors refer to LC-MS-based proteomics as "MS" all across the text. Who am I to say this to Yates et al, but I think it is rather simplified use "Mass Spectrometry Analysis", when this is a typical LC-MS type of analysis We agree with you. We have replaced MS analysis with LC-MS analysis in the manuscript.

      3) Several references used to construct the hypothesis of the paper are rather outdated: several from 10-15 years ago. It would be interesting to provide to the reader up to date references, given the rapid pace science has been progressing. We agree many of the references are 10-15 years old. Many of the hypotheses and biological mechanisms we discussed can be supported by too many studies to cite them all, due to space. If we could, we would. We also agree that there are many more recent studies that have confirmed and added more details to the original discovery or hypothesis cited. We cite the first study to support our conclusions because it deserves the most credit.

      4) "UniProt rat database". Please, state the version and if reviewed or unreviewed.

      This information was added to the Methods section. UniProt reviewed rat database with isoforms 03-25-2014.

      Reviewer #2 (Significance (Required)):

      The study is informative, and has great potential to enrich the specific literature of this field. But should tone down some arguments, given the experimental limitations of the PPI network (as described above) and should state PCP-treated rats as a limited model to schizophrenia.

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

      Summary

      It is now widely accepted that schizophrenia is polygenic disorder in which a large fraction of the genetic risk is in variants affecting the expression of synaptic proteins. Moreover, it is known that these synaptic proteins are found in multiprotein complexes and that many proteins encoded by schizophrenia risk genes interact directly or indirectly in these complexes. It is also known that some drugs including phencyclidine, which binds to NMDA receptors and to Dopamine D2 receptors (not mentioned by the authors) can induce schizophreniform psychosis. The authors have set out to advance on this position by performing proteomic mass spectrometry studies on proteins identified as encoded by schizophrenia risk genes. They target 8 proteins for immunoprecipitation from rat brain and identify coisolated proteins and perform various network analyses. In the most interesting part of the paper they ask if PCP-treatment altered protein interactions and report various changes.

      Major comments:

      1. Choice of target proteins. It was not until the first paragraph of the results section that the authors first name the 8 synaptic proteins that have chosen to study. This information should be in the abstract.

      This information was added to the abstract as requested.

      The authors then use figure 1A and 1B as evidence that these 8 "baits" are schizophrenia-relevant proteins. Figure 1A does not provide any evidence at all and Figure 1B is about as weak a line of evidence imaginable - a histogram of the number of papers that have the search term "schizophrenia" and the protein name. I tried this search for Grin2B and almost immediately found papers that reported no association between Grin2B and schizophrenia (e.g. PMID: 33237434). Figure 1B should be scrapped.

      The purpose of Figure 1A was not to demonstrate that there is evidence that our proteins are involved in SCZ. The purpose of this figure is to show that these proteins are diverse in function and structure (blue = membrane proteins; yellow = soluble proteins), and that there are published studies reporting physical and functional interactions between these 8 proteins. This suggests that a more extensive network may exist.

      We agree that Figure 1B does not specifically describe how each protein is related to SCZ but demonstrates how many papers investigating their connection to SCZ have been published. We understand how by itself, this can be considered weak. We still think it is important to show that multiple laboratories have published papers connecting these proteins to SCZ. Instead of scrapping this figure, we have moved it to the Supplementary Figure 2A.

      We read PMID: 33237434 and interpret their findings quite differently than you. This report examined whether one single nucleotide mutation (SNV) in Grin2b is associated with the cognitive dysfunction in SCZ but did not examine if this mutation is associated with the other major SCZ phenotypes (i.e. psychotic and emotional). Specifically, the study selected 117 “patients in whom cognitive dysfunctions are present despite effective antipsychotic treatment of other schizophrenia symptoms.” The study concluded that Grin2B SNV was not associated with this subset of patients but concluded that they need to search for other NMDAR variants and study their association with SCZ. We would argue that the only reason this group performed these experiments was the well-known association between Grin2b and SCZ. Many studies have found SNVs in Grin2B that are associated with SCZ, but there are conflicting reports. It is unclear if the discrepancies are connected to different cohorts, complexity of SCZ phenotype, or small sample sizes. Regardless of Grin2B mutations significantly associated with SCZ, there are several lines of evidence that Grin2B is involved in SCZ. Most importantly, Grin2b is a component of the NMDAR, which is a key player to the SCZ hypo-glutamate hypothesis and the receptor that binds PCP. By immunoprecipitating Grin2b, we are analyzing the PPI network of NMDAR, which is arguably the most studied complex in SCZ research.

      The remaining part of paragraph 1 of the results does not provide an adequate, let alone systematic, justification for the use of the 8 baits. It would be appropriate to construct a table with the 8 proteins and cite relevant papers and identify the basis for why they are implicated in schizophrenia (is it a direct mutation or some other evidence?). What makes these 8 proteins better than many others that are cited as synaptic schizophrenia relevant proteins?

      We apologize for not clearly and thoroughly describing the reasons for choosing our baits. As stated in the first paragraph of the Results, we chose the proteins that had evidence of being a SCZ risk factor in SCZ databases that included a plethora of human genomic studies. This criterion by itself results in ~5000 genes. To further narrow our candidates, we chose targets that were synaptic and were observed to have phosphorylation changes in response to PCP in an SCZ animal model. Since protein-protein interactions (PPI) are often dependent on phosphorylation, we believe this is an important criterion for quantitation of PPI in response to PCP. These requirements still resulted in a list of hundreds of proteins. So, what makes these better than any other SCZ relevant protein? As stated in the manuscript, the major limiting criterion was identifying commercial antibodies that can efficiently immunoprecipitate their target in brain tissue. Since there are many reports associating our targets with SCZ, we directed the reader to SCZ databases that compile large genomic association studies. We understand, however, the request for more specific information regarding the biological connection between these proteins and SCZ. We took your suggestion and constructed a table with our 8 targets, and it is now Figure 1A. In this table, we selected references to indicate if the target has reported changes in expression and/or activity in SCZ samples (i.e. human and animal model) or genetic association with SCZ in human studies.

      The methods of protein extraction are particularly concerning. The postsynaptic density of excitatory synapses (which contains several of the target proteins in this study) has been notoriously difficult to solubilise unless one uses high pH (9) and harsh detergent extraction (1% deoxycholate). The authors use pH 7 and weak detergent conditions, which are likely to be inefficient for solubilising at least several of the target proteins. Nowhere do the authors report how much of the total of their target protein is being solubilised. Indeed, there are no figures showing biochemical conditions at all. What if only a small percentage of the target protein is being immunoprecipitated - what does this mean for the interaction data? How do we know if the fraction being immunoprecipitated is from the synapse? (why did they not use synaptosomes).

      How do we know if the fraction being immunoprecipitated is from the synapse? (why did they not use synaptosomes). The absence of this kind of data undermines the reader's confidence in the findings.

      We apologize for not clearly explaining our experimental design We were not interested in identifying the PPI of the PSD. All these proteins have been localized to the synapse, but they are also localized to other neuronal compartments and non-neuronal cell types. Synaptic dysfunction is one hypothesis of SCZ pathogenesis, but there is evidence of other cell types, including astrocytes, microglia, and oligodendrocytes(Kerns, Vong et al. 2010, Ma, Abazyan et al. 2013, Goudriaan, de Leeuw et al. 2014, Park, Noh et al. 2020). For these reasons, we chose an unbiased approach to identifying PPI.

      The Results have been amended to read: “All the targets are localized to the synapse, but also localized to non-synaptic compartments and expressed in non-neuronal cells. Thus, since there is also evidence for non-synaptic perturbations contributing to SCZ pathogenesis, we chose to perform an unbiased analysis in unfractionated brain tissue (Tarasov, Svistunov et al. 2019, Rodrigues-Neves, Ambrosio et al. 2022, Stanca, Rossetti et al. 2024). “

      Why do we choose a specific solubilization strategy? Harsh detergents can disrupt PPI and prevent efficient enrichment of the target by disrupting the target-antibody interaction(Pankow, Bamberger et al. 2015). To identify protein interactions, mild detergent conditions are typically employed in PPI studies. We used a combination of “weak” detergents (i.e. 0.5% NP-40, 0.5% Triton, and 0.01% Deoxycholate) to help prevent non-specific PPI, but still allowing efficient enrichment of the target proteins. We do agree that with our conditions the targets were not completely solubilized. It is a balancing act to find the correct conditions for IP-MS analysis. Since we are unable to immunoprecipitate all the target protein, we did not identify all the PPI for each target, and we did not make this claim. Importantly, we did identify known interactions for all our targets. Our mild detergent protocol is similar to other PPI studies and our results validates results reported in previous studies. It is more important to significantly enrich the target protein over control than to achieve complete solubilization (Supplementary Figure 2D). This allows us to use control IPs to successfully employ the SAINT algorithm to determine which proteins are confident PPI using a 5% FDR.

      How do we know protein are being immunoprecipitated from the synapse? As we show in Figures 2B and 3A, multiple proteins are annotated to the synapse with different databases, Gene ontology and SynGO. Well-known synaptic PPI were also observed, such as Grin2B-Dlg4(i.e. PSD-95), providing further evidence for proteins being immunoprecipitated for the synapses. Besides validating over a hundred published PPI interactions, we also identified many reciprocal interactions between the target datasets demonstrating the reproducibility of our protocol. Thus, we respectfully disagree with you and assert that our PPI network is very confident.

      The immunoprecipitation protocol is unusual in that the homogenates were incubated overnight (twice), which is a very long period compared to most published protocols. This is a concern because spurious protein interactions could form during this long incubation.

      There are many different immunoprecipitation protocols in the literature. The IP conditions depend upon the target protein and the antibody employed. Specifically, the abundance of the target and the affinity of the antibody to the target will dictate the IP conditions. We routinely perform overnight incubation for our IP-MS studies(Pankow, Bamberger et al. 2016, McClatchy, Yu et al. 2018). In our experience with brain tissue, this results in the highest enrichment of the target protein and the best reproducibility between biological replicates compared to IP protocols with shorter incubation times. Many other laboratories use overnight incubations(Lin and Lai 2017, Iqbal, Akins et al. 2018, Lagundzin, Krieger et al. 2022), so we do not consider our protocol unusual. We do find that IPs with tagged proteins in cell culture are more amenable to short incubation times. We have no evidence that overnight incubation causes spurious protein interactions nor could find any in the literature. Non-specific interactions are a concern with IP-MS experiments regardless of the incubation time. We took multiple steps to reduce the non-specific PPI from affecting our dataset. The first overnight incubation was incubating the brain lysate with agarose beads linked to IgGs to preclear the lysate from “sticky” non-specific interactors binding to IgGs and the beads. In addition, control IPs with IgG crosslinked to beads were incubated with brain lysate in parallel to each target IP. We computationally compared the non-specific control IPs with the target IPs using the SAINT algorithm to generate a confident list of PPI with a stringent 5% FDR. Therefore, our pipeline is specifically designed to prevent spurious PPI.

      In the section "Biological interpretation of scz PPI network". Surprisingly the authors found that synaptic proteins that are exclusively postsynaptic (Grin2B, SynGAP) or exclusively presynaptic (Syt1) show very high percentages of their interacting proteins are from the synaptic compartments where the target protein is not expressed. The authors offer no explanation for this paradox. One explanation for this could be that spurious PPIs have formed in the protein extraction/immunoprecipitation protocol. These findings need validation by biochemical fractionation of synapses into pre and post synaptic fractions and immunohistochemistry to demonstrate the subsynaptic localisation of the proteins. Grin2b is traditionally described as exclusively post-synaptic, but there is evidence for other localizations, including presynaptic(Berretta and Jones 1996, Sjostrom, Turrigiano et al. 2003, Bouvier, Larsen et al. 2018) and expression in astrocytes(Serrano, Robitaille et al. 2008, Lee, Ting et al. 2010, Lalo, Koh et al. 2021, Kim, Choi et al. 2024). Syngap has been localized to non-synaptic sites and glia expression in addition to its heavily studied role at the post synapse(Moon, Sakagami et al. 2008, Araki, Zeng et al. 2015, Birtele, Del Dosso et al. 2023). Syt1 is commonly used as a presynaptic marker, but along with other proteins previously reported to be exclusively presynaptic (such as SNAP-25), it has been localized to the postsynapse (Selak, Paternain et al. 2009, Tomasoni, Repetto et al. 2013, Hussain, Egbenya et al. 2017, Madrigal, Portales et al. 2019, Sumi and Harada 2023). Similarly, SynGo database assigns both post-synaptic and pre-synaptic localizations to Grin2b as stated in the manuscript. Thus, our data is not paradoxical, but supports the emerging evidence against the canonical exclusivity of the pre- and post-synaptic compartments. Determining subsynaptic localization of a protein is a huge undertaking and requires expertise we do not possess. This is why we relied on synaptic databases and the literature for our interpretation of our data, as other publications have done.

      We added the following to the Discussion to address this issue:

      “Using the SynGo database, 418 proteins (i.e. 41% of our network) were identified as synaptic proteins consistent with the targets having a synaptic localization. Defining the synaptic proteome is inherently difficult because the synapse is an “open organelle”, and many synaptic proteins also have non-synaptic localizations and are expressed in non-neuronal cells. We further attempted to define our synaptic PPI by differentiating between pre- and post- synaptic compartments via SynGo. Half of our targets were annotated to both compartments and all targets had PPI that were annotated to both. This data supports the emerging evidence against the canonical localization exclusivity of the pre and post synapse(Bouvier, Larsen et al. 2018, Madrigal, Portales et al. 2019).”

      My concerns about spurious interactions are raised again because the authors say that 92% of their interactions are novel (I note that they authors have not compared their interaction data of the NMDA receptor with published datasets from Dr Seth Grant's laboratory). BioGrid itself is good but not enough for comparison, maybe at this point it worth taking String, which accumulates several sources of PPIs, just select the direct PPIs.

      Since the MS-IP experiments in our study have never been performed before, we are not surprised by the extent of novel data we produced. As described above, we took many steps to prevent spurious PPI from entering our final dataset, including the use of detergents, preclearing and stringent bioinformatic filtering. Our entire dataset is very large, so the 8% of PPI that we replicated from other studies represents 124 interactions. We believe this to be an impressive number which correlates to the confidence of our data. Providing more confidence, we identified many reciprocal PPI where shared protein interactors between target proteins were identified in both target protein datasets.

          The PPI described for our targets in BioGrid encompassed 713 publications.  Two of the BioGrid datasets that were compared to our Grin2b PPI data were from the laboratory of Seth Grant.  Arbuckle et al (2010) is a low-throughout paper that describes a Grin2b and DLG4 PPI (that we also identified) and Husi et al (__2000__) is a seminal paper using high-throughput LC-MS to identify PPI in the PSD of mouse brain.  There were many differences between Husi et al and our pipeline.  Husi et al employed the C-terminal Grin2b peptide to pull down interactors from the PSD fraction whereas we employed Grin2b antibody to enrich Grin2b and its interactors from unfractionated brain tissue.  Despite these differences, our studies found 8 proteins in common.
      

      We took your suggestion and compared our data to String which includes direct PPI and functional PPI. Our input was the high confidence PPI identified by SAINT with 5% FDR as with the BioGrid comparison. The PPI network for each target protein had a more significant enrichment (p We think the problem you suggest with SynGO is more of an inherent problem with characterizing the synaptic proteome. The synaptic proteome is difficult to define since it is an “open organelle” with proteins transporting in and out. In addition, most synaptic proteins, such as mitochondrial and translational proteins, also have non-synaptic localizations. It is not possible to isolate a contaminant-free “pure” synaptic preparation by biochemical fractionation. Recently, SynGO was used in a meta-analysis of previously published PSD datasets(Kaizuka, Hirouchi et al. 2024). Kaizuka et al. found 123 proteins identified in 20 PSD datasets. SynGo annotated proteins with post-synaptic localization from this list. To a lesser extent they also identified presynaptic localizations, but it is unclear if the presynaptic proteins are novel localizations. Kaizuka et al. continued the investigation and identified a novel PSD protein, thus demonstrating that our knowledge of pre- and post- synaptic proteomes is incomplete.

      Minor comments

      1. A number of papers have reported protein interactions of native NMDA receptor complexes and their associated proteins isolated from rodent brain and are neither referenced in this paper. It would be relevant to compare these published datasets with the Grin2B IP datasets.

      We employed BioGrid as a reference of reported PPI for each of our target proteins. For Grin2B, the PPI came from 142 different publications. For eight target proteins, we decided *BioGrid * was the best resource for determining the novelty of our PPI because it is routinely used for large-scale unbiased PPI analysis. To determine the novelty of our network, we compared our PPI network to 713 publications via BioGrid. We are unsure whether the papers you are referring to are included in the BioGrid database. To make it easier for readers with similar queries, we added an additional supplementary table (TableS4) including all the publications (i.e. PMID numbers) included in BioGrid comparison for each target protein.

      We amended the Results with the following sentence, so the readers realized the extensiveness of the Biogrid comparison analysis:

      “There were 713 publications in BioGrid that describe at least one interaction with one of our targets (Supplementary Table4).”

      The use of the term "bait" in purification experiments typically refers to a protein and not an antibody. I suggest removing the word bait to avoid ambiguity and simply use the word target. We took your suggestion and used “target” instead of “bait” to avoid ambiguity.

      26 mins of treatment gives completely different set of PPIs between PCP and saline which is very interesting, so both networks should be included in Supplementary. Also, it would be useful to have a list of modulated (phosphorylated in their case, but also ubiquitinated etc) proteins, which is not presented. Table S1 lists the PPI for each target, and we designated whether the interactors were for Sal, PCP, or both. Phosphorylated and ubiquitinated proteins are very hard to reproducibly identify without an additional enrichment step. Since we did not perform this enrichment step, we did not search for these modifications and do not have any modified proteins to report.

      As they say their final network is composed of "direct physical and "co-complex" interactors and they cannot distinguish between them. This is particularly bad for the postsynapse, where all the PSD components can be co-IP-ed in different combinations. It can explain the Figure 5C, where most of the proteins have FDR = 1, which means they do not reproduce. Figure 5C represents the intersection of 15N quantification and SAINT analysis. The x-axis is the FDR reported for SAINT analysis, and the y-axis is the significant proteins from the N15 analysis. This figure demonstrates that some proteins that were significantly different with PCP via N15 quantification also were annotated as PPI by SAINT (i.e. 5%. As stated in the Discussion, we concluded that the SAINT analysis and N15 quantitation are complementary in identifying PPI and that the quantification of a biological perturbation may aid the identification of PPI. Figure 5C is not related to whether our PPI are direct physical or "co-complex" interactors. Distinguishing between direct physical and co-complex interactors is an inherent problem for all IP studies. Since another reviewer also highlighted this deficit in our manuscript, we decided to analyze our PPI dataset with the artificial intelligence algorithm AlphaFold 3(AF3). The AF3 data is encompassed in Figure 6.

      The following AF3 data was added to the Results Section:

      “A disadvantage of IP-MS studies is that it cannot distinguish between a PPI that binds directly to the target protein, and a PPI in which the interactor and target protein reside in the same multiprotein complex (i.e. indirect). We sought to predict which PPI may be directly interacting with its target protein by using the artificial intelligence algorithm AlphaFold3(AF3) (Abramson, Adler et al. 2024). First, we analyzed the predicted AF3 structure of the targets using the pTM score, and determined the fraction of each structure that was calculated to be disordered (Figure 6A and Supplementary Table7). Our reasoning was that if our targets have a poorly resolved structures then it will be difficult to screen for direct PPI. A pTM score >0.5 suggests that the structure may be correct, with the highest confidence equaling 1. Undefined or disordered regions hinder the accuracy of the prediction, and all our targets possessed a pTM score > 0.5 except Syt1. The fraction of disordered negatively correlated with the pTM score, as expected. Gsk3b, Ppp1ca, and Map2k1 were the target proteins with the highest pTM scores and were also the smallest of our targets (Figure 6B). Ppp1ca had the most confident structure (i.e. pTM 0.9) and the least fraction disordered (i.e. 0.07). Next, we determined the AF3 prediction of previously reported direct interactions of the targets. We used the iPTM score to determine an interaction confidence. An iPTM score >0.8 is a highly confident direct interaction, whereas 0.8. These eight PPI have all previously been reported to form a direct interaction with Ppp1ca, except Phactr3 (Zhang, Zhang et al. 1998, Terrak, Kerff et al. 2004, Hurley, Yang et al. 2007, Marsh, Dancheck et al. 2010, Ragusa, Dancheck et al. 2010, Ferrar, Chamousset et al. 2012, Choy, Srivastava et al. 2024, Xu, Sadleir et al. 2024)*. Phactr3 is structurally similar to, but less studied than, the reported direct interactor, Phactr1. These interactors are all inhibitors of PP1 except for Ppp1r9b which targets Ppp1ca to specific subcellular compartments. Nine PPI were assigned a score The following AF3 interpretation was added to the Discussion:

      “Our SCZ PPI network consists of two types of PPI: direct physical interactions and “co-complex” or indirect interactions. Typically, the nature of the interaction cannot be distinguished in IP-MS studies. We decided to employ the new AF3 algorithm to screen the PPI of Ppp1ca to provide evidence for direct interactors. We chose to examine the PPI assigned to Ppp1ca, because its structure was the most confident among our target proteins and AF3 correctly predicted a known direct interactor with high confidence. Ppp1ca is a catalytic subunit of the phosphatase PP1, which is required to associate with regulatory subunits to create holoenzymes (Li, Wilmanns et al. 2013). Eighteen PPI were predicted to be directly interacting with Ppp1ca using a 0.6 or higher iPTM filter. This filter may be too conservative and may generate false negatives, because another study employed a 0.3 filter followed by additional interrogation to screen for direct PPI (Weeratunga, Gormal et al. 2024). Forty-four percent of these predictions were confirmed by previous publications. Most of these validated direct interactions are inhibitors of the phosphatase, but one, Ppp1r9b (aka spinophilin), is known to target Ppp1ca to dendritic spines (Allen, Ouimet et al. 1997, Salek, Claeboe et al. 2023). This high correlation with the literature provides substantial confidence to the novel PPI predicted to be direct Ppp1ca interactors. The AF3 screen predicted that NDRG2 directly interacts with Ppp1ca. This protein is known to regulate many phosphorylation dependent signaling pathways by directly interacting with other phosphatases including Pp1ma and PP2A (Feng, Zhou et al. 2022, Lee, Lim et al. 2022). Actin binding protein Capza1 was also predicted to directly interact with Ppp1ca and Ppp1ca interacts with actin and its binding proteins to maintain optimal localization for efficient activity to specific substrates (Foley, Ward et al. 2023). Hsp1e is a heat shock protein predicted to directly interact with Ppp1ca. Although there is no direct connection to Ppp1ca, other heat shock proteins have been reported to regulate Ppp1ca (Mivechi, Trainor et al. 1993, Flores-Delgado, Liu et al. 2007, Qian, Vafiadaki et al. 2011). We also observed that many of the direct PPI were altered with PCP treatment. One direct interactor, Ppp1r1b (aka DARPP-32), is phosphorylated at Thr34 by PKA in the brain upon PCP treatment. This phosphorylation event converts Ppp1rb to a potent inhibitor of Ppp1ca(Svenningsson, Tzavara et al. 2003). Importantly, the manipulation of Thr34 attenuated the behavioral effects of PCP. Consistent with this report, Ppp1r1b-Ppp1ca interaction was only observed with PCP in our study. Further investigation is needed to determine if our novel direct interactors regulate the PCP phenotype. We conclude that AF3 can provide important structural insights into the nature of PPI obtained from large scale IP-MS studies.”

      The way PPI data is reported can be improved so that I does not have to be extracted from Table 1 and 2. It would be good if they provide just two columns PPI list, with names or IDs, plus PSP/saline/both conditions in third column, for ease of comparison with other sources and building the graph. They can add it as another spreadsheet to Table 2. We generated this table (TableS2) as you requested.

      Is Figure 2 built for Sal or PCP conditions? as they have only 23% interactions in common (Figure 4A) the Figure 2 should be pretty different for two conditions. Are the 1007 interactors combined from SAL and PCP?

      Figure 2 contains ALL the unique PPI for each target regardless of Sal or PCP conditions. The 1007 protein interactors shown in Figure 2Awhere Sal and PCP were combined to generate a non-redundant list of proteins for each target.

      We amended the Results to make this clearer:

      “When the PCP and SAL datasets were combined, there were 1007 unique proteins.”

      This sentence was added to Figure 2A:

      “For this comparison, Sal and PCP PPI were combined into a unique PPI list for each target.”

      Figure 1F is mentioned but no figure is shown. We apologize for this oversight, and we have corrected the manuscript. 8. Overall the paper could be edited and made more concise, especially the introduction and discussion. We extensively edited the manuscript to be more concise.

      Reviewer #3 (Significance (Required)):

      General assessment

      Proteomic mass spectrometry of immunoprecipitated complexes from synapses has been extensively studied since Husi et al (2000) first study of NMDA receptor and AMPA receptor complexes. Since then, a wide variety of methods have been employed to purify synaptic protein complexes including peptide affinity, tandem-affinity purification of endogenous proteins tagged with FLAG and Histine-affinity tags amongst other methods. Purification of protein complexes and the postsynaptic density from the postsynaptic terminal of mammalian excitatory synapses have been crucial for establishing that schizophrenia is a polygenic disorder affecting synapses (e.g. Fernandez et al, 2009; Kirov et al, 2012; Purcell et al, 2014, Fromer et al, 2014 etc). Network analyses of the postsynaptic proteome have described networks of schizophrenia interacting proteins (e.g. Pocklington et al, 2006; Fernandez et al, 2009) and other neuropsychiatric disorders.

      Hundreds of synaptic protein complexes have been identified (Frank et al, 2016), but very few have been characterised using proteomic mass spectrometry. This paper has chosen 8 protein targets for such analysis and identified many proteins that a putative interactors of the target protein. At this level the current manuscript does not represent a conceptual advance and the value of the data lies in its utility as a resource that may be used in future studies.

      The findings from the 8 target proteins from normal adult rat brain were used for a secondary study that describes the effects that PCP has on the interaction networks. Interestingly, this work shows that 26 minutes of drug treatment leads to considerable changes in the interactomes of the target proteins. These descriptive data could be used in future studies to understand the cell biological mechanisms that mediate these rapid changes in the proteome. PCP and drugs that interact with NMDA receptors are known to induce changes in synaptic proteome phosphorylation including modifications in protein-protein interaction sites, which may explain the PCP effects.

      The study would benefit from validation of experimental protocols for solubilisation and immunoprecipitation and validation of described interactions using orthogonal biochemical or localisation experiments.

      Audience Specialists in synapse proteins and mechanisms of schizophrenia.

      Expertise

      The reviewers' expertise is in molecular biology of synapses including synapse proteomics, protein interaction and network analysis, and genetics of schizophrenia and other brain disorders.

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      Referee #3

      Evidence, reproducibility and clarity

      Summary

      It is now widely accepted that schizophrenia is polygenic disorder in which a large fraction of the genetic risk is in variants affecting the expression of synaptic proteins. Moreover, it is known that these synaptic proteins are found in multiprotein complexes and that many proteins encoded by schizophrenia risk genes interact directly or indirectly in these complexes. It is also known that some drugs including phencyclidine, which binds to NMDA receptors and to Dopamine D2 receptors (not mentioned by the authors) can induce schizophreniform psychosis. The authors have set out to advance on this position by performing proteomic mass spectrometry studies on proteins identified as encoded by schizophrenia risk genes. They target 8 proteins for immunoprecipitation from rat brain and identify coisolated proteins and perform various network analyses. In the most interesting part of the paper they ask if PCP-treatment altered protein interactions and report various changes.

      Major comments:

      1. Choice of target proteins. It was not until the first paragraph of the results section that the authors first name the 8 synaptic proteins that have chosen to study. This information should be in the abstract. The authors then use figure 1A and 1B as evidence that these 8 "baits" are schizophrenia-relevant proteins. Figure 1A does not provide any evidence at all and Figure 1B is about as weak a line of evidence imaginable - a histogram of the number of papers that have the search term "schizophrenia" and the protein name. I tried this search for Grin2B and almost immediately found papers that reported no association between Grin2B and schizophrenia (e.g. PMID: 33237434). Figure 1B should be scrapped. The remaining part of paragraph 1 of the results does not provide an adequate, let alone systematic, justification for the use of the 8 baits. It would be appropriate to construct a table with the 8 proteins and cite relevant papers and identify the basis for why they are implicated in schizophrenia (is it a direct mutation or some other evidence?). What makes these 8 proteins better than many others that are cited as synaptic schizophrenia relevant proteins?
      2. The methods of protein extraction are particularly concerning. The postsynaptic density of excitatory synapses (which contains several of the target proteins in this study) has been notoriously difficult to solubilise unless one uses high pH (9) and harsh detergent extraction (1% deoxycholate). The authors use pH 7 and weak detergent conditions, which are likely to be inefficient for solubilising at least several of the target proteins. Nowhere do the authors report how much of the total of their target protein is being solubilised. Indeed, there are no figures showing biochemical conditions at all. What if only a small percentage of the target protein is being immunoprecipitated - what does this mean for the interaction data? How do we know if the fraction being immunoprecipitated is from the synapse? (why did they not use synaptosomes). The absence of this kind of data undermines the reader's confidence in the findings.
      3. The immunoprecipitation protocol is unusual in that the homogenates were incubated overnight (twice), which is a very long period compared to most published protocols. This is a concern because spurious protein interactions could form during this long incubation.
      4. In the section "Biological interpretation of scz PPI network". Surprisingly the authors found that synaptic proteins that are exclusively postsynaptic (Grin2B, SynGAP) or exclusively presynaptic (Syt1) show very high percentages of their interacting proteins are from the synaptic compartments where the target protein is not expressed. The authors offer no explanation for this paradox. One explanation for this could be that spurious PPIs have formed in the protein extraction/immunoprecipitation protocol. These findings need validation by biochemical fractionation of synapses into pre and post synaptic fractions and immunohistochemistry to demonstrate the subsynaptic localisation of the proteins.
      5. My concerns about spurious interactions are raised again because the authors say that 92% of their interactions are novel (I note that they authors have not compared their interaction data of the NMDA receptor with published datasets from Dr Seth Grant's laboratory). BioGrid itself is good but not enough for comparison, maybe at this point it worth taking String, which accumulates several sources of PPIs, just select the direct PPIs.
      6. A major concern is that they use SynGO as a reference database, and even test the enrichment against it. SynGO is about ~ 2000 genes in size and was built around the presynaptic datasets, so it is biased and incomplete in terms of the whole synapse. This may be one of the reasons there is the strangely high percentage of presynaptic proteins interacting with postsynaptic proteins as noted above.

      Minor comments

      1. A number of papers have reported protein interactions of native NMDA receptor complexes and their associated proteins isolated from rodent brain and are neither referenced in this paper. It would be relevant to compare these published datasets with the Grin2B IP datasets.
      2. The use of the term "bait" in purification experiments typically refers to a protein and not an antibody. I suggest removing the word bait to avoid ambiguity and simply use the word target.
      3. 26 mins of treatment gives completely different set of PPIs between PCP and saline which is very interesting, so both networks should be included in Supplementary. Also, it would be useful to have a list of modulated (phosphorylated in their case, but also ubiquitinated etc) proteins, which is not presented.
      4. As they say their final network is composed of "direct physical and "co-complex" interactors and they cannot distinguish between them. This is particularly bad for the postsynapse, where all the PSD components can be co-IP-ed in different combinations. It can explain the Figure 5C, where most of the proteins have FDR = 1, which means they do not reproduce.
      5. The way PPI data is reported can be improved so that I does not have to be extracted from Table 1 and 2. It would be good if they provide just two columns PPI list, with names or IDs, plus PSP/saline/both conditions in third column, for ease of comparison with other sources and building the graph. They can add it as another spreadsheet to Table 2.
      6. Is Figure 2 built for Sal or PCP conditions? as they have only 23% interactions in common (Figure 4A) the Figure 2 should be pretty different for two conditions. Are the 1007 interactors combined from SAL and PCP?
      7. Figure 1F is mentioned but no figure is shown.
      8. Overall the paper could be edited and made more concise, especially the introduction and discussion.

      Significance

      General assessment

      Proteomic mass spectrometry of immunoprecipitated complexes from synapses has been extensively studied since Husi et al (2000) first study of NMDA receptor and AMPA receptor complexes. Since then, a wide variety of methods have been employed to purify synaptic protein complexes including peptide affinity, tandem-affinity purification of endogenous proteins tagged with FLAG and Histine-affinity tags amongst other methods. Purification of protein complexes and the postsynaptic density from the postsynaptic terminal of mammalian excitatory synapses have been crucial for establishing that schizophrenia is a polygenic disorder affecting synapses (e.g. Fernandez et al, 2009; Kirov et al, 2012; Purcell et al, 2014, Fromer et al, 2014 etc). Network analyses of the postsynaptic proteome have described networks of schizophrenia interacting proteins (e.g. Pocklington et al, 2006; Fernandez et al, 2009) and other neuropsychiatric disorders.

      Hundreds of synaptic protein complexes have been identified (Frank et al, 2016), but very few have been characterised using proteomic mass spectrometry. This paper has chosen 8 protein targets for such analysis and identified many proteins that a putative interactors of the target protein. At this level the current manuscript does not represent a conceptual advance and the value of the data lies in its utility as a resource that may be used in future studies.

      The findings from the 8 target proteins from normal adult rat brain were used for a secondary study that describes the effects that PCP has on the interaction networks. Interestingly, this work shows that 26 minutes of drug treatment leads to considerable changes in the interactomes of the target proteins. These descriptive data could be used in future studies to understand the cell biological mechanisms that mediate these rapid changes in the proteome. PCP and drugs that interact with NMDA receptors are known to induce changes in synaptic proteome phosphorylation including modifications in protein-protein interaction sites, which may explain the PCP effects.

      The study would benefit from validation of experimental protocols for solubilisation and immunoprecipitation and validation of described interactions using orthogonal biochemical or localisation experiments.

      Audience

      Specialists in synapse proteins and mechanisms of schizophrenia.

      Expertise

      The reviewers' expertise is in molecular biology of synapses including synapse proteomics, protein interaction and network analysis, and genetics of schizophrenia and other brain disorders.

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      Referee #2

      Evidence, reproducibility and clarity

      Summary: McClatchy, Powell and Yates aimed at identifying a protein interactome associated to schizophrenia. For that, they treated rats (N14 and N15) with PCP, which disturbs gutamatergic transmission, as a model for the disease and co-immunoprecipitated hippocampi proteins, which were further analyzed by standard LC-MS.

      The study is new, considering not much has been done in this direction in the field of schizophrenia. This justifies its publication. On the other hand, a major flaw of the is the lack of information on the level of interaction of the so called protein interactome. Meaning, we cannot distinguish, as the study was performed, which proteins are directly interacting with the targets of interest from proteins which are interacting with targets´ interactors. The different shells of interaction are crucial information in protein interactomics.

      Major: most of I am pointing below must be at least discussed or better presented in the paper, as It may not be solvable considering how the study has been conducted.

      1. The study fails in defining the level of interaction of the protein interactome with the considered targets. This has been shortly mentioned in the discussion, but must be more explicit to readers, for instance, in the abstract, introduction and in the methods sections.
      2. Considering the protein extraction protocol, it is fair to mention that only the most soluble proteins are being considered here. I am bringing this up since the importance of membrane receptors is clear in the studied context.
      3. It is not clear from the methods description if antibodies from all 8 targets were all together in one Co-IP or have been incubated separately in 8 different hippocampi samples. It seems the first, given how results have been presented. If so, this maximizes the major issue raised above (in 1).
      4. Definitely, results here are not representing a "SCZ PPI network". PCP-treated animals, as any other animal model, are rather limited models to schizophrenia. As a complex multifactorial disease, synaptic deficits, which is the focus of this study, can no longer be considered "the pivot" of the disease. Synaptic dysfunction is only one among many other factors associated to schizophrenia.
      5. Authors should look for protein interactions that might be happening also in glial cells. They are not the majority in hippocampus, but are present in the type of tissue analyzed here. Thus, some of the interactions observed might be more abundantly present in those cells. Maybe enriching using bioinformatics tools the PPI network to different cell types.

      Minor:

      1. in the abstract, it is not clear if 90% of the PPI are novel to brain tissue in general or specifically schizophrenia.
      2. authors refer to LC-MS-based proteomics as "MS" all across the text. Who am I to say this to Yates et al, but I think it is rather simplified use "Mass Spectrometry Analysis", when this is a typical LC-MS type of analysis
      3. Several references used to construct the hypothesis of the paper are rather outdated: several from 10-15 years ago. It would be interesting to provide to the reader up to date references, given the rapid pace science has been progressing.
      4. "UniProt rat database". Please, state the version and if reviewed or unreviewed.

      Significance

      The study is informative, and has great potential to enrich the specific literature of this field. But should tone down some arguments, given the experimental limitations of the PPI network (as described above) and should state PCP-treated rats as a limited model to schizophrenia.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

      In this manuscript, McClatchy and colleagues used a conventional approach combining immunoprecipitation (IP) of endogenous target proteins (baits) followed by liquid chromatography mass spectrometry (MS) analysis of the co-immunoprecipitating proteins to map protein-protein interaction (PPI). This interaction network is centered around baits that had been annotated as susceptibility factors for schizophrenia (SCZ). A variety of previous studies have identified thousands of such SCZ susceptibility factors. Mostly based on the availability of antibodies, 8 bait proteins were selected in this study. The authors reasoned that immunoprecipitating endogenous proteins from tissues using specific antibodies was a more accurate view of physiological conditions than epitope tagging followed by affinity purification (AP) from cells in culture. The model system from which proteins were extracted was the hippocampus dissected from mice that had been treated or not by phencyclidine (PCP), a drug that has been shown to induce SCZ symptoms in humans and animals. By comparing the proteins identified and quantified from the PCP-treated samples against control IPs and/or saline-injected mouse controls, a large number of PPI were deemed statistically significant. Most of these potential interactors were not present in PPI databases (BioGRID), most likely because such databases are populated with large-scale APMS datasets from cell cultures, with very few studies using brain tissue. Strikingly, many of the co-immunoprecipitated proteins were also known as SCZ susceptibility factors, which lend weight to the hypothesis that these factors form a large protein interaction network, localized at the synapses.

      Major comments:

      • Are the key conclusions convincing?

      Overall, the conclusions drawn from the experimental design, data analysis, and corroboration with existing literature are well-supported and convincing. When selecting the SCZ susceptibility factors, the authors clearly state their goal, the databases used for gene selection, and the rationale for choosing proteins with synaptic localization. The inclusion of evidence from genetic studies and previous publications strengthens the credibility of the selected genes. The methodology used to establish the novel SCZ PPI network is mostly well-described (see minor comments below). The use of an 15N internal standard also adds rigor to the quantitation of PPI. The GO enrichment analysis provides valuable insights into the biological functions and cellular components associated with the SCZ PPI network. The annotation of identified proteins using the SynGo synaptic database and the distribution of annotated synaptic proteins among different baits further support the biological relevance of this PPI network. The cross-referencing of the PPI network with published genetic studies on SCZ susceptibility genes adds robustness to the findings. Specifically, the observation that 68% of protein interactors have evidence of being potential SCZ risk factors is a strong corroboration of the prevailing hypothesis in the field. Finally, the significant changes induced by PCP that were identified for all baits except Syt1, along with the comparison of altered proteins with SAINT-identified PPI, add depth to the understanding of PCP modulation. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

      No, but note that APMS/IPMS has been around for more than a decade (Introduction page 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.

      One piece of data that is missing are Western blots using the 8 selected antibodies against the proteins extracted from their experimental samples to validate the antibodies recognize 1 protein of the expected size from these tissue extracts. - 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.

      Running SDS-PAGE and Western blotting should be straightforward and cheap. - 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 rationale for the short duration between PCP injection and animal sacrifice is only explained in the discussion section (page 17). The fact that this short treatment of less than 30 min should prevent any change in transcription or translation should be introduced earlier (in the experimental procedures). Note that the duration is written as 26 min on page 4 and 25 min on page 9. Please reconcile these numbers. Is there any biological significance for this SCZ study that the mice were maintained on a reverse day-night cycle? It is not clear from reading Experimental Procedures/Bioinformatic Analysis section (page 6) if normalized N14/N15 protein ratios measured in the bait-IPs and control-IPs were used for the SAINT analysis? Or did the authors used label-free quantitation with spectral counts? - Are prior studies referenced appropriately?

      Yes - Are the text and figures clear and accurate?

      Fig1C: The workflow is a little too simple, the authors might want to add more details. FigS1C: Please add x-axis title (spectral counts) directly to the figure. Fig2B-D: The color scale bar should have number values to denote lower and upper limits in % (as opposed to "lowest" and "highest"). - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

      No

      Significance

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

      In this study, the authors have drastically expanded the protein interaction landscape around 8 known SCZ susceptibility factors by using a conventional IPMS approach. Performing the IPs on protein extracted from hippocampus dissected from mice treated with phencyclidine to model SCZ increases the biological significance of such lists of proteins. Furthermore, the co-immunoprecipitation of many other SCZ susceptibility factors along with the 8 selected baits supports the hypothesis that these proteins of varied functions are part of large interaction networks. Overall, the integration of experimental data with in silico networks, along with the quantification of PPI changes in response to PCP, should contribute to a more nuanced understanding of SCZ pathogenesis. The potential implications for drug development underscore the broader significance of the study in advancing our knowledge of neurobiology and its relevance to neurological disorders like schizophrenia. - Place the work in the context of the existing literature (provide references, where appropriate).

      Overall, this study contributes to the existing literature by providing experimental data on in vivo PPI networks related to SCZ risk factors. Not only do the authors validate 124 known interactions but also they identify many novel PPI, due to a gap in the existing literature regarding the comprehensive mapping of PPI directly from tissue extracts, especially brain tissue. The authors advocate for more IPMS studies in mammalian tissues to generate robust tissue-specific in silico networks, which agrees with the growing understanding of the importance of tissue-specific networks for identifying disease mechanisms and potential drug targets.

      Furthermore, the SCZ PPI network reported here is enriched in proteins previously associated with SCZ, which aligns with the existing literature emphasizing the involvement of certain proteins and pathways in the pathogenesis of SCZ [References: 78-85]. The authors also investigate the response of the SCZ network to PCP treatment, hence providing insights into the potential effects of post-translational modifications, protein trafficking, and PPI alterations in a model of schizophrenia, which adds to existing knowledge about the impact of PCP on the molecular processes associated with SCZ [References: 88, 89, 92]. - State what audience might be interested in and influenced by the reported findings.

      Overall, the findings reported in this manuscript have implications for both basic research in molecular biology and potential translational applications in the development of targeted therapies for neurological disorders, particularly schizophrenia. The study delves into in vivo protein-protein interaction (PPI) networks related to genes implicated in schizophrenia (SCZ) risk factors. Researchers in neuroscience, molecular biology, and psychiatry would find the information valuable for understanding the molecular basis of SCZ. The study highlights the potential for identifying disease "hubs" that could be drug targets. Pharmacologists and drug developers interested in targeting protein complexes for drug development, especially in the context of neurological disorders, may find the study relevant. - 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.

      Technical Expertise | biochemistry, liquid chromatography mass spectrometry, proteomics, computational biology, protein engineering, protein interaction networks, post-translational modifications, protein crosslinking, proximity labeling, limited proteolysis, thermal shift assay, label-free and isotope-labeled quantitation. Biological Applications | human transcriptional complexes, apicomplexan parasites, viruses, nuclear envelope, ubiquitin ligases, non-model organisms.

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      Reply to the reviewers

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

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      Referee #3

      Evidence, reproducibility and clarity

      The manuscript by Balachandra and Amodeo presents Bellymount-Pulsed Tracking as a technique for continuous long-term imaging of Drosophila oogenesis. This approach modifies the existing Bellymount technique by exposing restrained female flies to pulses of CO2 anesthesia in combination with image acquisition. Flies that survived the restraint were kept alive for many hours by addition of a liquid diet in the restraint apparatus. This allowed for imaging and tracking of egg chamber development over longer time periods than capable with ex vivo culturing methods. However, the authors did report a 40% mortality rate and decreased fecundity compared to unrestrained flies. Using this method the authors were able to image and measure the growth rate of developing egg chambers in living flies, and capture events like vitellogenesis which relies on the interactions of multiple organ systems.

      This technique is a notable contribution to the fly community, as it could be useful for studying processes that require interactions between multiple tissues and organs, as well as for long-term imaging of other internal structures in the adult fly. The significance is somewhat reduced due to the relatively high mortality rate and the decreased fecundity and egg chamber growth rate reported. However, the authors should be commended for their diligence in documenting the limitations of the procedure, as this now provides a strong jumping off point to improve the technique if it becomes widely adopted by the fly community. Overall, the experiments appear to have been carefully performed and the manuscript is clearly written. However, there are several issues that should be addressed prior to publication.

      Major concerns

      1. The movies of egg chamber development are challenging to interpret. They could be improved by the addition of timestamps and other annotations. Having multiple example movies of the same process would also be valuable. It could be helpful to potential users of this technique to show the process the authors used for identifying the same egg chamber between such long time points.
      2. Figure 4 - Given that the Bellymount PT technique slows oogenesis and reduces egg chamber growth in vitellogenic stages (Figure 3E), it is possible that Bellymount PT slows yolk protein uptake. It would be important to establish a baseline for how much to expect yolk protein levels to change across stages to compare to measurements obtained with Bellymount PT. It would be a relatively simple experiment to show the change in yolk protein uptake across stages in fixed samples. This could also be performed for His2Av dynamics during nurse cell dumping.
      3. Movie 11 - The authors propose that Bellymount-PT can be used to visualize the process of border cell migration. However, there is no obvious movement of the cluster relative to the nurse cell nuclei over the course of the 3 hour long movie. The authors should either show a better movie of border cell migration, or remove this claim from the manuscript.
      4. Movie 13 - The authors claim that they see egg chamber rotation continue in stage 9 and 10 egg chambers. This movie is not convincing. There is also very strong evidence in the literature that egg chamber rotation ends at stage 8. Chen et al., Cell Reports, 2017 showed using a method that tracks follicle cell migration in vivo that rotational migration ends during stage 8. The only movement of follicle cells after stage 8 is due to the epithelial reorganization that occurs during the posterior movement of the follicle cells as the stretch cells flatten. Additionally, after stage 8 follicle cells lose their circumferentially oriented actin protrusions that drive rotation. This claim should be removed from the manuscript.

      Minor comments

      1. Line 104 - The authors mention that CO2 affects fertility in flies. They should also reference Sustar et al., Genetics, 2023 and Zimmerman and Berg, PLoS One, 2024 for wider ranging effects of CO2 on oogenesis.
      2. Line 244 - Although it is true that the original paper describing egg chamber rotation reported that it starts at 5, subsequent studies from multiple labs have confirmed that it begins much earlier. First shown by Cetera et al., Nature Communications, 2014 but later confirmed by Bilder, Dahmann, and Mirouse labs. Chen et al., Cell Reports, 2016 has even published a movie of an egg chamber initiating rotation as it buds from the germarium.
      3. Figures of egg chambers are generally oriented anterior on the left and posterior on the right. Reorienting all the figures would be challenging, so the recommendation is to be clear in the figure legends the orientation of the images. This is important given they are shown in different orientations in Figure 1 than throughout the rest of the paper, and also will be helpful for readers who may not be familiar with the structure of the ovary/egg chambers.
      4. Figure 1B and Methods line 334 - Should "Rely" be "Relay"?
      5. Figure 1E - Oocyte nuclei are missing from the diagrams of stage 7, 13 and 14 egg chambers. Also, "G" looks like a figure panel label, could just say Germarium
      6. Figure 3F-H - "Stagee" should be "Stage"
      7. Figure 4B - Why is the fluorescence for egg chamber #6 so much higher than the others? It makes the slopes of the other samples hard to see.
      8. Figure 4D,E,G - For clarity, the labeled boxes should be the same color as the lines on the associated graphs. In line 790 "Note the steady increase of H2Av in all three regions as it exits the nurse cell nuclei" - this is not actually shown without the nurse cell nuclei average intensity being on the graph as well.
      9. Line 787 - "Note the flow of H2Av" - "flow" is not actually shown in these static images. Consider a more precise description.

      Referee Cross-commenting

      The other reviewers make several excellent points. We personally feel that it is beyond the scope of this initial report to ask the authors to show that they can see all aspects of oogenesis with this technique. If the method becomes widely adopted by the oogenesis community, individual researchers can optimize it to suit the exact process they want to study. If the authors want to claim they can see a particular process, it needs to be well documented and convincing. For example, we agree that the movies that claim to show egg chamber rotation (both during established stages and later) and border cell migration need to be improved or the claims need to be removed. However, we feel that the authors have documented enough other interesting processes to make the study worthy of publication. Likewise, asking the authors to determine the minimal time window that can be used for imaging could take months of open-ended work and is something that could be better tackled by subsequent users depending on the requirements of the biological process they want to study. It seems better to get the work out into the public sooner rather than later so that improvements can be crowd sourced.

      Finally, although Flp-out clones were used for cell tracking in the original Belly mount paper, this technique will be less effective during the first half of oogenesis when the egg chamber is rotating, as the clone is likely to rotate into and out of sight between imaging time points.

      Significance

      This technique is a notable contribution to the fly community, as it could be useful for studying processes that require interactions between multiple tissues and organs, as well as for long-term imaging of other internal structures in the adult fly. The significance is somewhat reduced due to the relatively high mortality rate and the decreased fecundity and egg chamber growth rate reported. However, the authors should be commended for their diligence in documenting the limitations of the procedure, as this now provides a strong jumping off point to improve the technique if it becomes widely adopted by the fly community. Overall, the experiments appear to have been carefully performed and the manuscript is clearly written. However, there are several issues that should be addressed prior to publication.

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      Referee #2

      Evidence, reproducibility and clarity

      Summary:

      The authors describe an improvement of the Bellymount imaging method for internal tissues of the fly's abdomen. They are able to increase the total duration of the imaging by introducing pulsed anesthesia. This allows the immobilized flies to take up food in between the imaging; this increases survival rate and allows for longer total imaging times. The authors illustrate the technique by tracking the development of egg chambers.

      Major Points

      • The Bellymount PT method results in decreased fecundity, which might affect the processes (oogenesis) the authors looked at. Indeed, the authors conclude that "oogenesis is not completely stalled under the Bellymount-PT protocol" (line 140). The authors do provide some data indicating that egg chambers develop (Fig. 2G,H; Fig. 3F,H), in particular a stage 10 egg chamber proceeding to a stage where dorsal appendages seem to form. However, for early stage egg chambers this is less convincing. The egg chambers show an increase in (cross-sectional) area, however, what is the evidence that they also mature? For example, during egg chamber maturation, the ratio of oocyte/nurse cell volume changes, follicle cells re-arrange, etc. The authors should test whether any of these characteristics can be observed in egg chambers imaged using Bellymount PT. This may include the imaging of egg chambers in which both nuclei and plasma membranes are visualized.
      • A potential advantage of the Bellymount PT method is the ability to follow the dynamics of processes. A current drawback, however, is the rather low temporal resolution as the fly needs to wake up between single images. The authors should provide an estimate for the minimal possible cycle time and should test whether flies imaged at 10 minutes interval show lower survival/fecundity than flies imaged at 2 hours interval.
      • The authors claim that they can track on a cellular level (based on nuclei), but it is unclear how accurate the tracking is. Especially cell tracking over very long times might be challenging here, as the time delay between two time points is big. The authors should test the accuracy of their tracking, potentially by creating Flip-out clones and using them as a control.
      • The authors show that they can visualize cell membranes (Moesin-GFP, Fig. 2C). Tracking cells over time based on their membranes would greatly widen the applicability of the method as it would enable to analyze the complex cellular dynamics during egg chamber maturation. The authors should test whether cells can be tracked over time (e.g. using Moesin-GFP) using their technique.
      • Movie 11. The authors claim that they can capture border cell migration. However, it is unclear whether the border cells actually migrate towards posterior. The authors should track and quantitatively analyze the migration path of the border cells in their movies.
      • Movie 12. The authors claim that they can observe egg chamber rotation. However, it is unclear whether the egg chambers actually rotate. The authors should track cells and quantify the angular velocity of movement.

      Minor Points

      • Please move the labels of the scale bars to the legends.
      • The figures (especially 2 and 3) would benefit from a clearer structuring. Moving part of them to supplementary figures would also help.
      • "stage" typo in figure 3

      Significance

      The authors describe here an improvement of an existing technique. The advantage of the improved technique is the longer imaging time, which potentially allows users to track cells/organelles/proteins over time. However, tracking requires the user to connect single time points with each other, which is somewhat unclear at this time. Moreover, the potential applicability (and significance) of the technique would be widened if visualization and tracking of cell membranes/organelles/vesicles would be possible. With these further optimizations, the technique would add a useful tool to the Drosophila community.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary

      The Drosophila ovary is an established model system for many aspects of development and cell biology. In vitro culture of live ovaries has provided valuable insight, yet these methods do not accurately mimic oogenesis in vivo for some stages. Here the authors develop a new method that allows for sustained imaging of ovaries in intact flies, maintaining normal physiology.

      The method provides a valuable addition to the field. Processes such as growth, cell migration, egg chamber rotation, yolk uptake and nurse cell dumping can be observed in the intact fly. Time lapse and 3D reconstruction provide valuable tools. While the detail/resolution of the images is not as good as ex vivo or fixed samples, the ability to maintain normal development and homeostasis provides a novel advantage. The figures and movies are well-presented and sufficient detail is provided in the methods.

      Major comments

      1. Why do the authors think that growth is slowed? The imaging process or the trapping/anesthesia of the fly? For example, if the frequency of imaging was varied, it could reveal whether it was the actual imaging that affected development. Did the length of time the fly had been in the trap make a difference? The sentence on lines 190-191 is not clear.
      2. In Movie 6, the nurse cell nuclear shape does not look normal - more ovoid than round. Perhaps some settings are off in the 3D reconstruction.
      3. Movie 11 - why do the border cells seem stalled?
      4. There is no discussion of the earliest stages of oogenesis. Is it possible to see egg chambers forming from the germarium?

      Minor comments

      1. It would be helpful to mention if the egg chambers stay in similar locations or move around - is it challenging to locate the same egg chamber after 2 hours?
      2. Are any egg chambers degenerating? This could indicate stress in the fly.
      3. In Figure 4D, release of HisAV into the cytoplasm is described. Similar release of nuclear proteins was described by Cooley et al. 1992 so this paper could be cited.
      4. At 321 minutes in Figure 4D, a large nucleus is apparent in the oocyte. Is this an oocyte nucleus or evidence for nurse cell translocation to the oocyte as described in Ali-Murthy et al. 2021?

      Significance

      The technique provides a significant advance to the field, extending the time period currently possible to image ovaries through the Belly Mount method. It will immediately benefit researchers working on the ovary but could be extended to many other tissues in the fly abdomen such as the gut and tumor models.

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      Reply to the reviewers

      Reviewer #1

      __Evidence, reproducibility and clarity __

      The work by Przanowska et al., sought to understand the role of ORC2 in murine development and further wanted to discover its role in liver endo-reduplication. The overall methods used is sufficient enough to address its role but is not very conclusive based on their overall results and data provided as elaborated in below comments.

      Major Comments:

      1. The major issue of the paper is how well is ORC2 depleted in perinatal liver (Fig. 2C) and is not very clear from the data as all the western blots are at very low exposure levels and bands are very weak (still weak bands seen). There are good antibodies of ORC2 which can be used for IHC staining and can be used to address the extent of ORC2 depletion.

      We have now shown that ORC2 protein is significantly decreased in the hepatocytes of the Orc2 KO and DKO livers (New Fig. 2C and 6D). The decrease is consistent, with 4-5 mice examined, and all showing the depletion. We have been unable to do immunohistochemistry on tissue sections of the mouse livers with the anti-ORC antibodies we have tried, and this could be a reflection of the low level of the proteins. On hepatocytes in culture we have obtained faint signal with the anti-ORC2 antibody in WT cells, and this is clearly absent in 100% of the hepatocytes. See Fig. R1 below.

      __Reviewer Fig R1: __


      A) Immunofluorescence of hepatocytes in culture from livers of WT and two DKO mice.

      B) Quantitation of A) from counting 70-100 cells from each specimen.

      However, the calculations in the methods and the discussion are very compelling that at least the last 6-9 cell divisions in normal development start with 2n nuclei in the livers at baseline (Fig. 3B-G and 6I).

      Why in Fig 2C, the M2 mice is showing an equivalent level of ORC2 protein compared to mice M1 with NO CRE expression (compare lane1 and lane5). So, the results are based on one mouse which I do not think is significant enough to come to the conclusion. The authors need to add more data from different mice for statistical significance. Please use IHC to show the depletion of ORC2 protein in the liver sections.

      We had used total liver and had pointed out that residual ORC2 protein will be seen from stromal cells (endothelia, blood vessels and blood cells). We have therefore removed the figure which measured ORC2 levels in total liver and have now shown that when hepatocytes are isolated from five animals there was a massive depletion of ORC2 in all five animals (new Fig. 3C).

      As nicely demonstrated in the previous paper by Okano-Uchida et al., 2018 that ORC1 depletion in the liver shows an DNA ploidy effect from 6-week onwards. The authors need to demonstrate in this paper also when the 16N phenotype is observed starting from week1 to 12 months.

      Based on the results from our previous paper (Okano-Uchida et al., 2018) we decided to measure 16N phenotype at 6 weeks of age. The endoreduplication occurs at a stage when ORC2 protein is undetectable during normal development or during regeneration.

      In the double knockout experiments (ORC1 and ORC2) the authors are not even bothered to demonstrate that how much are both the proteins are actually depleted from the cells, so on the results obtained from these mice experiments are not conclusive or explanatory.

      We have performed immunoblotting of isolated hepatocytes and immunohistochemistry of livers for ORC1 and ORC2. Our data shows that both proteins are depleted in all four mice tested (New Fig. 6D).

      Minor points:

      1. Why are scale bars missing in right panel of Fig. 2G, Fig. 6D Supp Fig. 2B KO studies. The authors need to confirm that that all the large nuclei have NO or less significant ORC2 protein through IHC H&E staining.

      The scale bars are missing from the right panels to avoid redundancy. We have added “Both panels are at the same scale.” in the figure legend, according to https://doi.org/10.1371/journal.pbio.3001161.

      1. Please explain why is EYFP in Fig. 5G is cytoplasmic compared to Fig 4C (nuclear). We consistently see this variability and it was there in our previous results (Okano-Uchida et al., 2018), where EYFP was cytoplasmic in tissues, but was nuclear (and some cytoplasmic) in hepatocytes in culture.

      We do not know the reason for this difference but consistently see this difference. We now say in the text: “We did not explore why the EYFP protein is mostly nuclear in hepatocytes in culture (Fig. 4C) and mostly cytoplasmic in hepatocytes in the liver tissue (Fig. 5G, 7G), but speculate that differences in signaling pathways or fixation techniques between the two conditions contribute to this difference.”

      Are authors using the same genotype of Alb-Cre mice as shown by Okano-Uchida et al., 2018 as I do not find the reference of Schuler et. al., 2004 (PMID:15282742).

      We have been using two independent Alb-Cre animals. This is now described in the Methods.


      Significance

      The article is exactly based on their previous published paper but instead of ORC1, they were interested in dissecting the role of ORC2. Although they have discussed that CDC6 may be involved in replacing ORC1 KO mice to rescue the extensive DNA replication in endoreduplication, but instead of going to hunt the role of CDC6 in endoreduplication they checked the effect of ORC2 which actually lower the overall impact of the paper.

      We studied ORC2 conditional KO mice in a similar manner to the previously published ORC1 conditional KO in order to ensure (1) that the lack of effect in the Orc1 KO was not because ORC1 can theoretically be substituted for by CDC6 and (2) to establish the double KO of Orc1 and Orc2. To the best of our knowledge this is the first description of removal of two subunits of ORC complex at once in a mouse model. Moreover, in the light of rising recognition of sex as biological variable, we report sex-dependent effects which are very intriguing.

      We have not attempted knocking out CDC6 to uncover novel mechanisms of DNA replication, because we first needed to make sure that the mice can truly endo-reduplicate without two of the six subunits of ORC. Note that our published results in cancer cell lines (Shibata, 2016) show that CDC6 is still essential in the ORC KO cell lines, so a future experiment will likely reveal that CDC6 is still essential for endoreduplication in the ORC KO mice in vivo.

      Reviewer #2

      __Evidence, reproducibility and clarity __

      It has been reported that in the absence of ORC1, liver cells can still endoreduplicate and it has been speculated that this might occur if CDC6 can replace, at least partially, the function of ORC1. Here, authors evaluate if this is also true in the absence of ORC2 and found that ORC2 is required for cell proliferation in mouse hepatocytes but not for endoreduplication. This is also the case after combining the conditional mutations of ORC1 and ORC2. They propose that a mechanism must exist to load sufficient MCM2-7 to support DNA replication in the absence of these two ORC subunits. Some of the conclusions need further experimental support. The rationale for testing the requirement of ORC2, with or without ORC1, for endoreduplication is valid. However, a key point is that the endoreduplication level seems to be higher in the absence of ORC2 or both ORC1 and ORC2, and this is not properly addressed. Also, mechanistic details on how this could be triggered are absent from this study. As indicated below almost every figure in this manuscript contains weak points (see below).

      We now discuss the following: “One possible explanation of the greater endoreduplication in both our papers is that mitosis may be arrested earlier in development by G2 DNA damage checkpoints activated by incomplete licensing and replication of the genome in the absence of ORC. As a result, endoreduplication cycles could begin earlier in development resulting in greater endoreduplication.”

      Major 1. Fig 1G, needs a detailed comment and justification.

      We have added the following to the text: “The proliferation rate of the MEF were measured by MTT assays. Even in the Orc2+/+ MEF, the infection with adeno-Cre decreased proliferation a little (the orange line compared to the blue line in Fig. 1G). However, for Orc2f/f MEF infection with adeno-Cre impairs proliferation even further (yellow line compared to black line in Fig. 1G)..

      Note that Adeno-Cre has been reported to be toxic for cell proliferation (citations 1, 2, 3), and so we included Adeno-Cre expression in ORC2+/+ (WT) as a background control.

      Citation:

      1. Pfeifer A, Brandon EP, Kootstra N, Gage FH, Verma IM: Delivery of the Cre recombinase by a self deleting lentiviral vector: Efficient gene targeting in vivo. Proc Natl Acad Sci USA. 2001, 98: 11450-11455. 10.1073/pnas.201415498.
      2. Loonstra A, Vooijs M, Beverloo HB, Allak BA, Drunen EV, Kanaar R, Berns A, Jonkers J: Growth inhibition and DNA damage induced by Cre recombinase in mammalian cells. Proc Natl Acad Sci USA. 2001, 98: 9209-9214. 10.1073/pnas.161269798.
      3. Schmidt EE, Taylor DS, Prigge JR, Barnet S, Capecchi R: Illegitimate Cre-dependent chromosome rearrangements in transgenic mouse spermatids. Proc Natl Acad Sci USA. 2000, 97: 13702-13707. 10.1073/pnas.240471297.
      4. Fig 2D-F. Is this conclusion applicable to other endoreplicating tissues? Have authors consider to analyze body weight and liver weight measurements after normalization with similar data from a non-affected organ? The conditional KO was performed specifically in the liver. ORC is intact in other tissues in these animals. As a future direction our lab plans to study cardiac-specific conditional KO of ORC subunits to test whether other endo-reduplicating tissues can also synthesize DNA in the absence of ORC subunits.

      Fig 3 shows inconsistent results or results that lack proper justification in the text. The 2C peak is missing in Fig 3E (yellow line, positive control). However, 2n nuclei appear in Fig 3F-H. Also, the blue and yellow peaks do not coincide in the flow cytometry profiles, in particular for 8C and 16C.

      There was an error in the plotting of the former Fig. 3E. The information is better presented in the former Fig. 3F-H (now Fig. 3E-G) and so have removed the former Fig. 3E from the paper.

      Fig 4. Shorter EdU pulses could be more informative of the actual amount of S-phase cells. Thus, the use of a 2h EdU pulse needs a clear justification.

      The half-life of EDU incorporation differs slightly between in vivo and in vitro conditions. In vivo, slower cell proliferation requires a longer time, approximately 4 hours. However, in vitro, liver cells grow faster, and a 2-hour EDU pulse with 20 µM is sufficient for detection compared to a 3-hour pulse with 10 µM BrdU (Okano-Uchida et al., 2018). Several publications also use a 2-hour EDU incubation time (https://doi.org/10.1098/rsob.150172).

      Fig 5. EYFP is cytoplasmic, in contrast with results shown in Fig 4C

      We consistently see this variability and it was there in our previous results (Okano-Uchida et al., 2018), where EYFP was cytoplasmic in tissues, but was nuclear (and some cytoplasmic) in hepatocytes in culture.

      We do not know the reason for this difference but consistently see this difference. We now say in the text: “We did not explore why the EYFP protein is mostly nuclear in hepatocytes in culture (Fig. 4C) and mostly cytoplasmic in hepatocytes in the liver tissue (Fig. 5G, 7G), but speculate that differences in signaling pathways or fixation techniques between the two conditions contribute to this difference.”

      Fig 6. Results obtained with the double mutant are poorly described.

      We have split the figure into two figures (New Fig. 6 and 7) edited the results section to ensure that they are easily comprehended by the readers. We have also included Westerns from hepatocyte cell lysates of four DKO mice to show that ORC1 and ORC2 proteins are reproducible decreased (New Fig. 6D).

      What are the level of other pre-RC components in the mutants used in this study. This could be easily evaluated by Western blotting

      Despite the technical difficulty of not having antibodies that recognize all the mouse initiation proteins, we have now measured mouse ORC1, ORC2, ORC3, ORC5, ORC6, CDC6 and the MCM2 and MCM3 subunits of MCM2-7. The results do not show a consistent decrease or increase of any of these proteins in individual mice of the two genotypes, Orc2-/- or DKO (New Fig. 2D and 6E)

      How do authors justify their claim that a very limited amount of ORC are sufficient to load a vast excess of MCM2-7 hexamers?

      The rationale is stated in the introduction from data from cancer cell lines: “Given that WT cells have about 150,000 molecules of ORC2, even if this truncated protein is functional ORC2, ~150 molecules of the protein would be expected to load MCM2-7 double hexamers on at least 50,000 origins of replication. Experimentally, we show in Shibata, 2020 (Fig. 7C), that although ORC subunits are undetectable on Westerns, MCM2-7 association with the chromatin is unchanged. By the way, we do not say “vast excess” of MCM2-7, just sufficient MCM2-7 to fire 50,000 origins.

      Minor 1. The titles of the Results section could be more informative of the main conclusion rather than simply descriptive

      We updated our Results titles to be more informative.

      The Discussion is too long

      We have shortened the discussion by removing our calculations to the Results section and abbreviating some of the discussion on endoreduplication. However we had to insert new items brough forth by the reviewers. Due to the controversy of this topic in our field, we had to include extensive discussion of current literature and put our results in their proper context.

      Significance

      The topic is relevant and the hypothesis tested is reasonable, although the conceptual advance is limited (see also below). The major limitation is the absence of mechanistic details addressing the occurrence of extra endoreduplication cycles (compared to controls) in the ORC1 and ORC2 mutants.

      Reviewer #3

      __Evidence, reproducibility and clarity: __

      The origin recognition complex (ORC) is an essential loading factor for the replicative Mcm2-7 helicase complex. Despite ORC's critical role in DNA replication, there have been instances where the loss of specific ORC subunits has still seemingly supported DNA replication in cancer cells, endocycling hepatocytes, and Drosophila polyploid cells. Critically, all tested ORC subunits are essential for development and proliferation in normal cells. This presents a challenge, as conditional knockouts need to be generated, and a skeptic can always claim that there were limiting but sufficient ORC levels for helicase loading and replication in polyploid or transformed cells. That being said, the authors have consistently pushed the system to demonstrate replication in the absence or extreme depletion of ORC subunits.

      Here, the authors generate conditional ORC2 mutants to counter a potential argument with prior conditional ORC1 mutants that Cdc6 may substitute for ORC1 function based on homology. They also generate a double ORC1 and ORC2 mutant, which is still capable of DNA replication in polyploid hepatocytes. While this manuscript provides significantly more support for the ability of select cells to replicate in the absence or near absence of select ORC subunits, it does not shed light on a potential mechanism. While a mechanistic understanding of how these cells proliferate in the absence or extreme depletion of ORC subunits is outside the scope of the current manuscript, it would have been beneficial to see more functional analyses to help guide the field. For example, is there a delay or impairment in Mcm2-7 loading in G1 (FACs-based loading assay from the Cook Lab (Matson et al., eLife. 2017)) in primary hepatocytes with the ORC2 conditional deletion? Is copy number maintained as cells increase polyploidy in the absence of ORC subunits, or are some regions of the genome more sensitive to ORC depletion (CGH arrays or sequencing of the flow-sorted polyploid cells)?

      We thank the reviewer for recognizing the main point of these experiments: to dispel the argument that CDC6 can substitute for ORC1 in the six-subunit ORC (although no one has demonstrated this, the argument is made on the basis of close sequence homology between CDC6 and ORC1). The second point, also appreciated by the reviewer is to show that it is possible to find cells that replicate in the absence or near absence of two ORC subunits.

      The mechanistic questions raised are important, and we will address them here:

      Is there a delay or impairment of MCM2-7 loading in G1? The hepatocytes in culture are fragile and not immortalized and thus, this issue can be much more easily addressed in the cancer cell lines we have made that are missing several ORC subunits and will do that in a later paper. Note however, the surprising lack of change in MCM2-7 association in cell lines where both ORC2 and ORC5 are deleted (Shibata, 2020, Fig. 7C).

      Are some regions of the genome more sensitive to ORC deletion during the polyploidization? We could not find any paper where people have investigated whether the whole genome is uniformly polyploidized in livers. In other words, the baseline conditions in WT livers have not been established. We therefore have postponed experiments to answer this question for a later paper. Note that in unpublished data from mapping SNS-seq origins in WT and ORC deletion cell lines there does not appear to be selective firing of certain origins over others in the deletion cell lines.

      Additional points: I didn't understand how the numbers were derived in Table 2. Was there really a 20-fold decrease in nuclear density for female ORC1 and ORC2 double-deletion hepatocytes? The differences in Figure S2 are dramatic, but not 20-fold dramatic.

      We measure the relative nuclear density by counting the number of plump nuclei (hepatocytes) per field as described for Fig. 5F and 7F now in the Methods section. The reviewer is correct in that we overestimated the decrease of nuclear density in the female DKO mice by two-fold. The revised calculations suggest that 6 cell divisions occur in the female DKO mice after the ORC proteins have decreased to at least __Significance: __

      The strengths of this manuscript are the mouse genetics and the generation of conditional alleles of Orc2 and the rigorous assessment of phenotypes resulting from limiting amounts of specific ORC subunits. It also builds on prior work with ORC1 to rule out Cdc6 complementing the loss of ORC1. The weakness is that it is a very hard task to resolve the fundamental question of how much ORC is enough for replication in cancer cells or hepatocytes. Clearly, there is a marked reduction in specific ORC subunits that is sufficient to impact replication during development and in fibroblasts, but the devil's advocate can always claim limiting levels of ORC remaining in these specialized cells. The significance of the work is that the authors keep improving their conditional alleles (and combining them), thus making it harder and harder (but not impossible) to invoke limiting but sufficient levels of ORC. At this point, the investigators and the field are well-positioned to attempt future functional CRISPR screens to identify other factors that may modulate the response to the loss of ORC subunits. This work will be of interest to the DNA replication, polyploidy, and genome stability communities.

      We thank the reviewer for getting the important point of this paper: “making it harder and harder (but not impossible) to invoke limiting but sufficient levels of ORC….” In other words, either ORC is completely dispensable for loading MCM2-7 in certain cancer cell lines and hepatocytes or it is highly catalytic and one molecule of ORC can load a few hundred MCM2-7 doublets so that most origins in the genome are licensed and capable of firing. We are trying the CRISPR screens in cancer cell lines that the reviewer envisages

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      Referee #3

      Evidence, reproducibility and clarity

      The origin recognition complex (ORC) is an essential loading factor for the replicative Mcm2-7 helicase complex. Despite ORC's critical role in DNA replication, there have been instances where the loss of specific ORC subunits has still seemingly supported DNA replication in cancer cells, endocycling hepatocytes, and Drosophila polyploid cells. Critically, all tested ORC subunits are essential for development and proliferation in normal cells. This presents a challenge, as conditional knockouts need to be generated, and a skeptic can always claim that there were limiting but sufficient ORC levels for helicase loading and replication in polyploid or transformed cells. That being said, the authors have consistently pushed the system to demonstrate replication in the absence or extreme depletion of ORC subunits.

      Here, the authors generate conditional ORC2 mutants to counter a potential argument with prior conditional ORC1 mutants that Cdc6 may substitute for ORC1 function based on homology. They also generate a double ORC1 and ORC2 mutant, which is still capable of DNA replication in polyploid hepatocytes. While this manuscript provides significantly more support for the ability of select cells to replicate in the absence or near absence of select ORC subunits, it does not shed light on a potential mechanism. While a mechanistic understanding of how these cells proliferate in the absence or extreme depletion of ORC subunits is outside the scope of the current manuscript, it would have been beneficial to see more functional analyses to help guide the field. For example, is there a delay or impairment in Mcm2-7 loading in G1 (FACs-based loading assay from the Cook Lab (Matson et al., eLife. 2017)) in primary hepatocytes with the ORC2 conditional deletion? Is copy number maintained as cells increase polyploidy in the absence of ORC subunits, or are some regions of the genome more sensitive to ORC depletion (CGH arrays or sequencing of the flow-sorted polyploid cells)?

      Additional points: I didn't understand how the numbers were derived in Table 2. Was there really a 20-fold decrease in nuclear density for female ORC1 and ORC2 double-deletion hepatocytes? The differences in Figure S2 are dramatic, but not 20-fold dramatic.

      Significance

      The strengths of this manuscript are the mouse genetics and the generation of conditional alleles of Orc2 and the rigorous assessment of phenotypes resulting from limiting amounts of specific ORC subunits. It also builds on prior work with ORC1 to rule out Cdc6 complementing the loss of ORC1. The weakness is that it is a very hard task to resolve the fundamental question of how much ORC is enough for replication in cancer cells or hepatocytes. Clearly, there is a marked reduction in specific ORC subunits that is sufficient to impact replication during development and in fibroblasts, but the devil's advocate can always claim limiting levels of ORC remaining in these specialized cells. The significance of the work is that the authors keep improving their conditional alleles (and combining them), thus making it harder and harder (but not impossible) to invoke limiting but sufficient levels of ORC. At this point, the investigators and the field are well-positioned to attempt future functional CRISPR screens to identify other factors that may modulate the response to the loss of ORC subunits. This work will be of interest to the DNA replication, polyploidy, and genome stability communities.

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      Referee #2

      Evidence, reproducibility and clarity

      It has been reported that in the absence of ORC1, liver cells can still endoreduplicate and it has been speculated that this might occur if CDC6 can replace, at least partially, the function of ORC1. Here, authors evaluate if this is also true in the absence of ORC2 and found that ORC2 is required for cell proliferation in mouse hepatocytes but not for endoreduplication. This is also the case after combining the conditional mutations of ORC1 and ORC2. They propose that a mechanism must exist to load sufficient MCM2-7 to support DNA replication in the absence of these two ORC subunits.

      Some of the conclusions need further experimental support. The rationale for testing the requirement of ORC2, with or without ORC1, for endoreduplication is valid. However, a key point is that the endoreduplication level seems to be higher in the absence of ORC2 or both ORC1 and ORC2, and this is not properly addressed. Also, mechanistic details on how this could be triggered are absent from this study. As indicated below almost every figure in this manuscript contains weak points (see below).

      Major

      1. Fig 1G, needs a detailed comment and justification.
      2. Fig 2D-F. Is this conclusion applicable to other endoreplicating tissues? Have authors consider to analyze body weight and liver weight measurements after normalization with similar data from a non-affected organ?
      3. Fig 3 shows inconsistent results or results that lack proper justification in the text. The 2C peak is missing in Fig 3E (yellow line, positive control). However, 2n nuclei appear in Fig 3F-H. Also, the blue and yellow peaks do not coincide in the flow cytometry profiles, in particular for 8C and 16C.
      4. Fig 4. Shorter EdU pulses could be more informative of the actual amount of S-phase cells. Thus, the use of a 2h EdU pulse needs a clear justification.
      5. Fig 5. EYFP is cytoplasmic, in contrast with results shown in Fig 4C
      6. Fig 6. Results obtained with the double mutant are poorly described.
      7. What are the level of other pre-RC components in the mutants used in this study. This could be easily evaluated by Western blotting
      8. How do authors justify their claim that a very limited amount of ORC are sufficient to load a vast excess of MCM2-7 hexamers?

      Minor

      1. The titles of the Results section could be more informative of the main conclusion rather than simply descriptive
      2. The Discussion is too long

      Significance

      The topic is relevant and the hypothesis tested is reasonable, although the conceptual advance is limited (see also below). The major limitation is the absence of mechanistic details addressing the occurrence of extra endoreduplication cycles (compared to controls) in the ORC1 and ORC2 mutants

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      Referee #1

      Evidence, reproducibility and clarity

      The work by Przanowska et al., sought to understand the role of ORC2 in murine development and further wanted to discover its role in liver endo-reduplication. The overall methods used is sufficient enough to address its role but is not very conclusive based on their overall results and data provided as elaborated in below comments.

      Major Comments:

      1. The major issue of the paper is how well is ORC2 depleted in perinatal liver (Fig. 2C) and is not very clear from the data as all the western blots are at very low exposure levels and bands are very weak (still weak bands seen). There are good antibodies of ORC2 which can be used for IHC staining and can be used to address the extent of ORC2 depletion.
      2. Why in Fig 2C, the M2 mice is showing an equivalent level of ORC2 protein compared to mice M1 with NO CRE expression (compare lane1 and lane5). So, the results are based on one mouse which I do not think is significant enough to come to the conclusion. The authors need to add more data from different mice for statistical significance. Please use IHC to show the depletion of ORC2 protein in the liver sections.
      3. As nicely demonstrated in the previous paper by Okano-Uchida et al., 2018 that ORC1 depletion in the liver shows an DNA ploidy effect from 6-week onwards. The authors need to demonstrate in this paper also when the 16N phenotype is observed starting from week1 to 12 months.
      4. In the double knockout experiments (ORC1 and ORC2) the authors are not even bothered to demonstrate that how much are both the proteins are actually depleted from the cells, so on the results obtained from these mice experiments are not conclusive or explanatory.

      Minor points:

      1. Why are scale bars missing in right panel of Fig. 2G, Fig. 6D Supp Fig. 2B KO studies. The authors need to confirm that that all the large nuclei have NO or less significant ORC2 protein through IHC H&E staining.
      2. Please explain why is EYFP in Fig. 5G is cytoplasmic compared to Fig 4C (nuclear).
      3. Are authors using the same genotype of Alb-Cre mice as shown by Okano-Uchida et al., 2018 as I do not find the reference of Schuler et. al., 2004 (PMID:15282742).

      Significance

      The article is exactly based on their previous published paper but instead of ORC1, they were interested in dissecting the role of ORC2. Although they have discussed that CDC6 may be involved in replacing ORC1 KO mice to rescue the extensive DNA replication in endoreduplication, but instead of going to hunt the role of CDC6 in endoreduplication they checked the effect of ORC2 which actually lower the overall impact of the paper.

    1. 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

      R1 Cell profiling is an emerging field with many applications in academia and industry. Finding better representations for heterogeneous cell populations is important and timely. However, unless convinced otherwise after a rebuttal/revision, the contribution of this paper, in our opinion, is mostly conceptual, but in its current form - not yet practical. This manuscript combined two concepts that were previously reported in the context of cell profiling, weakly supervised representations. Our expertise is in computational biology, and specifically applications of machine learning in microscopy.

      In our revised manuscript, we have aimed to better clarify the practical contributions of our work by demonstrating the effectiveness of the proposed concepts on real-world datasets. We hope that these revisions and our detailed responses address your concerns and highlight the potential impact of our approach.

      R1.1a. CytoSummaryNet is evaluated in comparison to aggregate-average profiling, although previous work has already reported representations that capture heterogeneity and self-supervision independently. To argue that both components of contrastive learning and sets representations are contributing to MoA prediction we believe that a separate evaluation for each component is required. Specifically, the authors can benchmark their previous work to directly evaluate a simpler population representation (PMID: 31064985, ref #13) - we are aware that the authors report a 20% improvement, but this was reported on a separate dataset. The authors can also compare to contrastive learning-based representations that rely on the aggregate (average) profile to assess and quantify the contribution of the sets representation.

      We agree that evaluating the individual contributions of the contrastive learning framework and single-cell data usage is important for understanding CytoSummaryNet's performance gains.

      To assess the impact of the contrastive formulation independently, we applied CytoSummaryNet to averaged profiles from the cpg0004 dataset. This isolated the effect of contrastive learning by eliminating single-cell heterogeneity. The experiment yielded a 32% relative improvement in mechanism of action retrieval, compared to the 68% gain achieved with single-cell data. These findings suggest that while the contrastive formulation contributes significantly to CytoSummaryNet's performance, leveraging single-cell information is crucial for maximizing its effectiveness. We have added a discussion of this experiment to the Results section:

      “We conducted an experiment to determine whether the improvements in mechanism of action retrieval were due solely to CytoSummaryNet's contrastive formulation or also influenced by the incorporation of single-cell data. We applied the CytoSummaryNet framework to pre-processed average profiles from the 10 μM dose point data of Batch 1 (cpg0004 dataset). This approach isolated the effect of the contrastive architecture by eliminating single-cell data variability. We adjusted the experimental setup by reducing the learning rate by a factor of 100, acknowledging the reduced task complexity. All other parameters remained as described in earlier experiments.

      This method yielded a less pronounced but still substantial improvement in mechanism of action retrieval, with an increase of 0.010 (32% enhancement - Table 1). However, this improvement was not as high as when the model processed single-cell level data (68% as noted above). These findings suggest that while CytoSummaryNet's contrastive formulation contributes to performance improvements, the integration of single-cell data plays a critical role in maximizing the efficacy of mechanism of action retrieval.”

      We don't believe comparing with PMID: 31064985 is useful: while the study showcased the usefulness of modeling heterogeneity using second-order statistics, its methodology is limited in scalability due to the computational burden of computing pairwise similarities for all perturbations, particularly in large datasets. Additionally, the study's reliance on similarity network fusion, while expedient, introduces complexity and inefficiency. We contend that this comparison does not align with our objective of testing the effectiveness of heterogeneity in isolation, as it primarily focuses on capturing second and first-order information. Thus, we do not consider this study a suitable baseline for comparison.

      R1.1b. The evaluation metric of mAP improvement in percentage is misleading, because a tiny improvement for a MoA prediction can lead to huge improvement in percentage, while a much larger improvement in MoA prediction can lead to a small improvement in percentage. For example, in Fig. 4, MEK inhibitor mAP improvement of ~0.35 is measured as ~50% improvement, while a much smaller mAP improvement can have the same effect near the origins (i.e., very poor MoA prediction).

      We agree that relying solely on percentage improvements can be misleading, especially when small absolute changes result in large percentage differences.

      However, we would like to clarify two key points regarding our reporting of percentage improvements:

      • We calculate the percentage improvement by first computing the average mAP across all compounds for both CytoSummaryNet and average profiling, and then comparing these averages. This approach is less susceptible to the influence of outlier improvements compared to calculating the average of individual compound percentage improvements.
      • We report percentage improvements alongside their corresponding absolute improvements. For example, the mAP improvement for Stain4 (test set) is reported as 0.052 (60%). To further clarify this point, we have updated the caption of Table 1 to explicitly state how the percentage improvements are calculated:

      The improvements are calculated as mAP(CytoSummaryNet)-mAP(average profiling). The percentage improvements are calculated as (mAP(CytoSummaryNet)-mAP(average profiling))/mAP(average profiling).

      R1.1b. (Subjective) visual assessment of this figure does not show a convincing contribution of CytoSummaryNet representations of the average profiling on the test set (3.33 uM). This issue might also be relevant for the task of replicate retrieval. All in all, the mAP improvement reported in Table 1 and throughout the manuscript (including the Abstract), is not a proper evaluation metric for CytoSummaryNet contribution. We suggest reporting the following evaluations:

      1. Visualizing the results of cpg0001 (Figs. 1-3) similarly to cpg0004 (Fig. 4), i.e., plotting the matched mAP for CytoSummaryNet vs. average profile.

      2. In Table 1, we suggest referring to the change in the number of predictable MoAs (MoAs that pass a mAP threshold) rather than the improvement in percentages. Another option is showing a graph of the predictability, with the X axis representing a threshold and Y-axis showing the number of MoAs passing it. For example see (PMID: 36344834, Fig. 2B) and (PMID: 37031208, Fig. 2A), both papers included contributions from the corresponding author of this manuscript.

      Regarding the suggestion to visualize the results for compound group cpg0001 similarly to cpg0004, unfortunately, this is not feasible due to the differences in data splitting between the two datasets. In cpg0001, an MoA might have one compound in the training set and another in the test or validation set. Reporting a single value per MoA would require combining these splits, which could be misleading as it would conflate performance across different data subsets.

      However, we appreciate the suggestion to represent the number of predictable MoAs that surpass a certain mAP threshold, as it provides another intuitive measure of performance. To address this, we have created a graph that visualizes the predictability of MoAs across various thresholds, similar to the examples provided in the referenced papers (PMID: 36344834, Figure 2B and PMID: 37031208, Figure 2A). This graph, with the x-axis depicting the threshold and the y-axis showing the number of MoAs meeting the criterion, has been added to Supplementary Material K.

      R1.1c.i. "a subset of 18 compounds were designated as validation compounds" - 5 cross-validations of 18 compounds can make the evaluation complete. This can also enhance statistical power in figures 1-3.

      We appreciate your suggestion and acknowledge the potential benefits of employing cross-validation, particularly in enhancing statistical power. While we understand the merit of cross-validation for evaluating model performance and generalization to unseen data, we believe the results as presented already highlight the generalization characterics of our methods.

      Specifically, (the new) Figure 3 demonstrates the model's improvement over average profiling in both training and validation plates, supporting its ability to generalize to unseen compounds (but not to unseen plates).

      While cross-validation could potentially enhance our analysis, retraining five new models solely for different validation set results may not substantially alter our conclusions, given the observed trends in Suppl Figure A1 and (the new) Figure 4, both of which show results across multiple stain sets (but a single train-test-validation split).


      R1.1c.ii. Clarify if the MoA results for cpg0001 are drawn from compounds from both the training and the validation datasets. If so, describe how the results differ between the sets in text and graphs.

      We confirm that the Mechanism of Action (MoA) retrieval results for cpg0001 are derived from all available compounds. It's important to note that the training and validation dataset split for the replicate retrieval task is different from the MoA prediction task. For replicate retrieval, we train using all available compounds and validate on a held-out set (see Figure 2). For MoA prediction, we train using the replicate retrieval task as the objective on all available compounds but validate using MoA retrieval, which is a distinct task. We have added a brief clarification in the main text to highlight the distinction between these tasks and how validation is performed for each:

      “We next addressed a more challenging task: predicting the mechanism of action class for each compound at the individual well level, rather than simply matching replicates of the exact same compound (Figure 5). It's also important to note that mechanism of action matching is a downstream task on which CytoSummaryNet is not explicitly trained. Consequently, improvements observed on the training and validation plates are more meaningful in this context, unlike in the previous task where only improvements on the test plate were meaningful. For similar reasons, we calculate the mechanism of action retrieval performance on all available compounds, combining both the training and validation sets. This approach is acceptable because we calculate the score on so-called "sister compounds" only—that is, different compounds that have the same mechanism of action annotation. This ensures there is no overlap between the mechanism of action retrieval task and the training task, maintaining the integrity of our evaluation. ”

      R1.1c.iii. "Mechanism of action retrieval is evaluated by quantifying a profile's ability to retrieve the profile of other compounds with the same annotated mechanism of action.". It was unclear to us if the evaluation of mAP for MoA identification can include finding replicates of the same compound. That is, whether finding a close replicate of the same compound would be included in the AP calculation. This would provide CytoSummaryNet with an inherent advantage as this is the task it is trained to do. We assume that this was not the case (and thus should be more clearly articulated), but if it was - results need to be re-evaluated excluding same-compound replicates.

      The evaluation excludes replicate wells of the same compound and only considers wells of other compounds with the same MoA. This methodology ensures that the model's performance on the MoA prediction task is not inflated by its ability to find replicates of the same compound, which is the objective of the replicate retrieval task. Please see the explanation we have added to the main text in our response to R1.1c.ii. Additionally, we have updated the Methods section to clearly describe this evaluation procedure:

      “Mechanism of action retrieval is evaluated by quantifying a profile’s ability to retrieve the profile of different compounds with the same annotated mechanism of action.”



      __R1.2a. __The description of Stain2-5 was not clear for us at first (and second) read. The information is there, but more details will greatly enhance the reader's ability to follow. One suggestion is explicitly stating that these "stains" partitioning was already defined in ref 26. Another suggestion is laying out explicitly a concrete example on the differences between two of these stains. We believe highlighting the differences between stains will strengthen the claim of the paper, emphasizing the difficulty of generalizing to the out-of-distribution stain.

      We appreciate your feedback on the clarity of the Stain2-5 dataset descriptions; we certainly struggled to balance detail and concepts in describing these. We have made the following changes:

      • Explicitly mentioned that the partitioning of the Stain experiments was defined in https://pubmed.ncbi.nlm.nih.gov/37344608/: “The partitioning of the Stain experiments have been defined and explained previously [21].”
      • Moved an improved version of (now) Figure 2 from the Methods section to the main text to help visually explain how the stratification is done early on.
      • Added a new section in the Experimental Setup: Diversity of stain sets, which includes a concrete example highlighting the differences between Stain2, and Stain5 to emphasize the diversity in experimental setups within the same dataset: “Stain2-5 comprise a series of experiments which were conducted sequentially to optimize the experimental conditions for image-based cell profiling. These experiments gradually converged on the most optimal set of conditions; however, within each experiment, there were significant variations in the assay across plates. To illustrate the diversity in experimental setups within the dataset, we will highlight the differences between Stain2 and Stain5.

      Stain2 encompasses a wide range of nine different experimental protocols, employing various imaging techniques such as Widefield and Confocal microscopy, as well as specialized conditions like multiplane imaging and specific stains like MitoTracker Orange. This subset also includes plates acquired with strong pixel binning instead of default imaging and plates with varying concentrations of dyes like Hoechst. As a result, Stain2 exhibits greater variance in the experimental conditions across different plates compared to Stain5.

      In contrast, Stain5, the last experiment in the series, follows a more systematic approach, consistently using either confocal or default imaging across three well-defined conditions. Each condition in Stain5 utilizes a lower cell density of 1,000 cells per well compared to Stain2's 2,500 cells per well. Being the final experiment in the series, Stain5 had the least variance in experimental conditions.

      For training the models, we typically select the data containing the most variance to capture the broadest range of experimental variation. Therefore, we chose Stain2-4 for training, as they represented the majority of the data and captured the most experimental variation. We reserved Stain5 for testing to evaluate the model's ability to generalize to new experimental conditions with less variance.

      All StainX experiments were acquired in different passes, which may introduce additional batch effects.”

      These changes aim to provide a clearer understanding of the dataset's complexity and the challenges associated with generalizing to out-of-distribution data.

      R1.2b. What does each data point in Figures 1-3 represent? Is it the average mAP for the 18 validation compounds, using different seeds for model training? Why not visualize the data similarly to Fig. 4 so the improvement per compound can be clearly seen?

      The data points in (the new) Figures 3,4,5 represent the average mAP for each plate, calculated by first computing the mAP for each compound and then averaging across compounds to obtain the average mAP per plate. We have updated the figure captions to clarify this:

      "... (each data point is the average mAP of a plate) ..."

      While visualizing the mAP per compound, similar to (the new) Figure 6 for cpg0004, could provide insights into compound-level improvements, it would require creating numerous additional figures or one complex figure to adequately represent all the stratifications we are analyzing (plate, compound, Stain subset). By averaging the data per plate across different stratifications, we aim to provide a clearer and more comprehensible overview of the trends and improvements while allowing us to draw conclusions about generalization.

      Please note: this comment is related to the comment R1.1b (Subjective)

      R1.2.c [On the topic of enhancing clarity and readability:] Justification and interpretation of the evaluation metrics.

      Please refer to our response to comment R1.1b, where we have addressed your concerns regarding the justification and interpretation of the evaluation metrics.

      R1.2d. Explicitly mentioning the number of MoAs for each datasets and statistics of number of compounds per MoA (e.g., average\median, min, max).

      We have added the following to the Experimental Setup: Data section:

      “A subset of the data was used for evaluating the mechanism of action retrieval task, focusing exclusively on compounds that belong to the same mechanism class. The Stain plates contained 47 unique mechanisms of action, with each compound replicated four times. Four mechanisms had only a single compound; the four mechanisms (and corresponding compounds) were excluded, resulting in 43 unique mechanisms used for evaluation. In the LINCS dataset, there were 1436 different mechanisms, but only 661 were used for evaluation because the remaining had only one compound.”

      R1.2e. The data split in general is not easily understood. Figure 8 is somewhat helpful, however in our view, it can be improved to enhance understanding of the different splits. Specifically, the training and validation compounds need to be embedded and highlighted within the figure.

      Thank you for highlighting this. We have completely revised the figure, now Figure 2 which we hope more clearly conveys the data split strategy.

      Please note: this comment is related to the comment R1.2a.





      R1.3a. Why was stain 5 used for the test, rather than the other stains?

      Stain2-5 were part of a series of experiments aimed at optimizing the experimental conditions for image-based cell profiling using Cell Painting. These experiments were conducted sequentially, gradually converging on the most optimal set of conditions. However, within each experiment, there were significant variations in the assay across plates, with earlier iterations (Stain2-4) having more variance in the experimental conditions compared to Stain5. As Stain5 was the last experiment in the series and consisted of only three different conditions, it had the least variance. For training the models, we typically select the data containing the most variance to capture the broadest range of experimental variation. Therefore, Stain2-4 were chosen for training, while Stain5 was reserved for testing to evaluate the model's ability to generalize to new experimental conditions with less variance.

      We have now clarified this in the Experimental Setup: Diversity of stain sets section. Please see our response to comment R1.2a. for the full citation.

      R1.3b How were the 18 validation compounds selected?

      20% of the compounds (n=18) were randomly selected and designated as validation compounds, with the remaining compounds assigned to the training set. We have now clarified this in the Results section:

      “Additionally, 20% of the compounds (n=18) were randomly selected and designated as validation compounds, with the remaining compounds assigned to the training set (Supplementary Material H).”

      R1.3c. For cpg0004, no justification for the specific doses selected (10uM - train, 3.33 uM - test) for the analysis in Figure 4. Why was the data split for the two dosages? For example, why not perform 5-fold cross validation on the compounds (e.g., of the highest dose)?

      We chose to use the 10 μM dose point as the training set because we expected this higher dosage to consist of stronger profiles with more variance than lower dose points, making it more suitable for training a model. We decided to use a separate test set at a different dose (3.33 μM) to assess the model's ability to generalize to new dosages. While cross-validation on the highest dose could also be informative, our approach aimed to balance the evaluation of the model's generalization capability with its ability to capture biologically relevant patterns across different dosages.

      This explanation has been added to the text:

      “We chose the 10 μM dose point for training because we expected this high dosage to produce stronger profiles with more variance than lower dose points, making it more suitable for model training.”

      “The multiple dose points in this dataset allowed us to create a separate hold-out test set using the 3.33 μM dose point data. This approach aimed to evaluate the model's performance on data with potentially weaker profiles and less variance, providing insights into its robustness and ability to capture biologically relevant patterns across dosages. While cross-validation on the 10 μM dose could also be informative, focusing on lower dose points offers a more challenging test of the model's capacity to generalize beyond its training conditions, although we do note that all compounds’ phenotypes would likely have been present in the 10 μM training dataset, given the compounds tested are the same in both.”

      R1.3d. A more detailed explanation on the logic behind using a training stain to test MoA retrieval will help readers appreciate these results. In our first read of this manuscript we did not grasp that, we did in a second read, but spoon-feeding your readers will help.

      This comment is related to the rationale behind training on one task and testing on another, which is addressed in our responses to comments R1.1.cii and R1.1.ciii.

      R1.4 Assessment of interpretability is always tricky. But in this case, the authors can directly confirm their interpretation that the CytoSummaryNet representation prioritizes large uncrowded cells, by explicitly selecting these cells, and using their average profile re

      We progressively filtered out cells based on a quantile threshold for Cells_AreaShape features (MeanRadius, MaximumRadius, MedianRadius, and Area), which were identified as important in our interpretability analysis, and then computed average profiles using the remaining cells before determining the replicate retrieval mAP. In the exclusion experiment, we gradually left out cells as the threshold increased, while in the inclusion experiment, we progressively included larger cells from left to right.

      The results show that using only the largest cells does not significantly increase the performance. Instead, it is more important to include the large cells rather than only including small cells. The mAP saturates after a threshold of around 0.4, indicating that larger cells define the profile the most, and once enough cells are included to outweigh the smaller cell features, the profile does not change significantly by including even larger cells.

      These findings support our interpretation that CytoSummaryNet prioritizes large, uncrowded cells. While this approach could potentially be used as a general outlier removal strategy for cell profiling, further investigation is needed to assess its robustness and generalizability across different datasets and experimental conditions.

      We have created Supplementary Material L to report these findings and we additionally highlight them in the Results:

      “To further validate CytoSummaryNet's prioritization of large, uncrowded cells, we progressively filtered cells based on Cells_AreaShape features and observed the impact on replicate retrieval mAP (Supplementary Material L). The results support our interpretation and highlight the key role of larger cells in profile strength.”

      __R1.5. __Placing this work in context of other weakly supervised representations. Previous papers used weakly supervised labels of proteins / experimental perturbations (e.g., compounds) to improve image-derived representations, but were not discussed in this context. These include PMID: 35879608, https://www.biorxiv.org/content/10.1101/2022.08.12.503783v2 (from the same research groups and can also be benchmarked in this context), https://pubs.rsc.org/en/content/articlelanding/2023/dd/d3dd00060e , and https://www.biorxiv.org/content/10.1101/2023.02.24.529975v1. We believe that a discussion explicitly referencing these papers in this specific context is important.

      While these studies provide valuable insights into improving cell population profiles using representation learning, our work focuses specifically on the question of single-cell aggregation methods. We chose to use classical features for our comparisons because they are the current standard in the field. This approach allows us to directly assess the performance of our method in the context of the most widely used feature extraction pipeline in practice. However, we see the value in incorporating them in future work and have mentioned them in the Discussion:

      “Recent studies exploring image-derived representations using self-supervised and self-supervised learning [35][36] could inspire future research on using learned embeddings instead of classical features to enhance model-aggregated profiles.”

      R1.minor1. "Because the improved results could stem from prioritizing certain features over others during aggregation, we investigated each cell's importance during CytoSummaryNet aggregation by calculating a relevance score for each" - what is the relevance score? Would be helpful to provide some intuition in the Results.

      We have included more explanation of the relevance score in the Results section, following the explanation of sensitivity analysis (SA) and critical point analysis (CPA):

      “SA evaluates the model's predictions by analyzing the partial derivatives in a localized context, while CPA identifies the input cells with the most significant contribution to the model's output. The relevance scores of SA and CPA are min-max normalized per well and then combined by addition. The combination of the two is again min-max normalized, resulting in the SA and CPA combined relevance score (see Methods for details).”

      R1.minor2. Figure 1:

      1. Colors of the two methods too similar
      2. The dots are too close. It will be more easily interpreted if they were further apart.
      3. What do the dots stand for?
      4. We recommend considering moving this figure to the supp. material (the most important part of it is the results on the test set and it appears in Fig.2).
      1. We chose a lighter and darker version of the same color as a theme to simplify visualization, as this theme is used throughout (the new) Figures 3,4,5.
      2. We agree; we have now redrawn the figure to fix this.
      3. Each data point is the average mAP of a plate. Please see our answer for R1.2b as well.
      4. We believe that (the new) Figures 3,4,5 serve distinct purposes in testing various generalization hypotheses. We have added the following text to emphasize that the first figures are specifically about generalization hypothesis testing: “We first investigated CytoSummaryNet’s capacity to generalize to out-of-distribution data: unseen compounds, unseen experimental protocols, and unseen batches. The results of these investigations are visualized in Figures 3, 4, and 5, respectively.”

      R1.minor3 Figure 4: It is somewhat misleading to look at the training MoAs and validation MoAs embedded together in the same graph. We recommend showing only the test MoAs (train MoAs can move to SI).

      We addressed this comment in R1.1c.ii. To reiterate briefly, there are no training, validation, or test MoAs because these are not used as labels during the training process. There is an option to split them based on training and validation compounds, which is addressed in R1.1c.ii.


      R1.minor4 Figure 5

      1. Why only Stain3? What happens if we look at Stains 2,3 and 4 together? Stain 5?

      2. Should validation compounds and training compounds be analyzed separately?

      3. Subfigure (d): it is expected that the data will be classified by compound labels as it is the training task, but for this to be persuasive I would like to see this separately on the training compounds first and then and more importantly on the validation compounds.

      4. For subfigures (b) and (d): it appears there are not enough colors for d, which makes it partially not understandable. For example, the pink label in (d) shows a single compound which appears to represent two different MoAs. This is probably not the case, and it has two different compounds, but it cannot be inferred when they are represented by the same color.

      5. For the Subfigure (e) - only 1 circle looks justified (in the top left). And for that one, is it not a case of an outlier plate that would perhaps need to be removed from analysis? Is it not good that such a plate will be identified?

      We have addressed this point in the text, stating that the results are similar for Stain2 and Stain4. Stain5 represents an out-of-distribution subset because of a very different set of experimental conditions (see Experimental Setup: Diversity of stain sets). To improve clarity, we have revised the figure caption to reiterate this information:

      “... Stain2 and Stain4 yielded similar results (data not shown). …”

      1. For replicate retrieval, analyzing validation and training compounds separately is appropriate. However, this is not the case for MoA retrieval, as discussed in our responses to R1.1c.ii and R1.1c.i.
      2. We have created the requested plot (below) but ultimately decided not to include it in the manuscript because we believe that (the new) Figures 3 and 4 are more effective for making quantitative comparative claims.

      [Please see the full revision document for the figures]

      Top: training compounds (validation compounds grayed out); not all compounds are listed in the legend.

      *Bottom: validation compounds (training compounds grayed out). *

      Left: average profiling; Right: CytoSummaryNet

      1. We agree with your observation and have addressed this issue by labeling the center mass as a single class (gray) and highlighting only the outstanding pairs in color. Please refer to the updated figure and our response to R3.6 for more details.

      2. In the updated figure, we have revised the figure caption to focus solely on the annotation of same mechanism of action profile clusters, as indicated by the green ellipses. The annotation of isolated plate clusters has been removed (Figures 7e and 7f) to maintain consistency and avoid potential confusion. Despite being an outlier for Stain3, the plate (BR00115134bin1) clusters with Stain4 plates (Supplementary Figure F1, green annotated square inside the yellow annotated square), indicating it is not merely a noisy outlier and can provide insights into the out-of-sample performance of our model.

      R1.minor5a. Discussion: "perhaps in part due to its correction of batch effects" - is this statement based on Fig. 5F - we are not convinced.

      We appreciate the reviewer's scrutiny regarding our statement about batch effect correction. Upon reevaluation, we agree that this claim was not adequately substantiated by empirical data. We quantified the batch effects using comparison mean average precision for both average profiles and CytoSummaryNet profiles, and the statistical analysis revealed no significant difference between these profiles in terms of batch effect correction. Therefore, we have removed this theoretical argument from the manuscript entirely to ensure that all claims are strongly supported by the data presented.

      R1.minor5b. "Overall, these results improve upon the ~20% gains we previously observed using covariance features" - this is not the same dataset so it is hard to reach conclusions - perhaps compare performance directly on the same data?

      We have now explicitly clarified this is a different dataset. Please see our response to R1.1a for why a direct comparison was not performed. The following clarification can be found in the Discussion:

      “These results improve upon the ~20% gains previously observed using covariance features [13] albeit on a different dataset, and importantly, CytoSummaryNet effectively overcomes the challenge of recomputation after training, making it easier to use.”

      Reviewer 2

      R2.1 The authors present a well-developed and useful algorithm. The technical motivation and validation are very carefully and clearly explained, and their work is potentially useful to a varied audience.

      That said, I think the authors could do a better job, especially in the figures, of putting the algorithm in context for an audience that is unfamiliar with the cell painting assay. (a) For example, a figure towards the beginning of the paper with example images might help to set the stage. (b) Similarly a schematic of the algorithm earlier in the paper would provide a graphical overview. (c) For the sake of a biologically inclined audience, I would consider labeling the images in the caption by cell type and label.

      Thank you for your valuable suggestions on improving the accessibility of our figures for readers unfamiliar with the Cell Painting assay. We have made the following changes to address your comments:

      1. and b. To provide visual context and a graphical overview of the algorithm, we have moved the original Figure 7 to Figure 1. This figure now includes example images that help readers new to the Cell Painting assay.
      2. We have added relevant details to the example images in (the new) Figure 1

        R2.2 The interpretability results were intriguing. The authors might consider further validating these interpretations by removing weakly informative cells from the dataset and retraining. Are the cells so uninformative that the algorithm does better without them, or are they just less informative than other cells?

      Please see our responses to R1.4 and R3.0

      R2.3 As far as I can tell, the authors only oblique state whether the code associated with the manuscript is openly available. Posting the code is needed for reproducibility. I would provide not only a github, but a doi linked to the code, or some other permanent link.

      We have now added a Code Availability and Data Availability section, clearing stating that the code and data associated with the manuscript are openly available.

      R2.4 Incorporating biological heterogeneity into machine-learning driven problems is a critical research question. Replacing means/modes and such with a machine learning framework, the authors have identified a problem with potentially wide significance. The application to cell painting and related assays is of broad enough significance for many journals, However, the authors could further broaden the significance by commenting on other possible cell biology applications. What other applications might the algorithm be particularly suited for? Are there any possible roadblocks to wider use. What sorts of data has the code been tested on so far?

      We have added the following paragraph to discuss the broader applicability of CytoSummaryNet:

      “The architecture of CytoSummaryNet holds significant potential for broader applications beyond image-based cell profiling, accommodating tabular, permutation-invariant data and enhancing downstream task performance when applied to processed population-level profiles. Its versatility makes it valuable for any omics measurements where downstream tasks depend on measuring similarity between profiles. Future research could also explore CytoSummaryNet's applicability to genetic perturbations, expanding its utility in functional genomics.”

      Reviewer 3

      R3.0 The authors have done a commendable job discussing the method, demonstrating its potential to outperform current models in profiling cell-based features. The work is of considerable significance and interest to a wide field of researchers working on the understanding of cell heterogeneity's impact on various biological phenomena and practical studies in pharmacology.

      One aspect that would further enhance the value of this work is an exploration of the method's separation power across different modes of action. For instance, it would be interesting to ascertain if the method's performance varies when dealing with actions that primarily affect size, those that affect marker expression, or compounds that significantly diminish cell numbers.

      Thank you for encouraging comments!

      We have added the following to Results: Relevance scores reveal CytoSummaryNet's preference for large, isolated cells:

      “Statistical t-tests were conducted to identify the features that most effectively differentiate mechanisms of action from negative controls in average profiles, focusing on the three mechanisms of action where CytoSummaryNet demonstrates the most significant improvement and the three mechanisms where it shows the least. Consistent with our hypothesis that CytoSummaryNet emphasizes larger, more sparse cells, the important features for the CytoSummaryNet-improved mechanisms of action (Supplementary Material I1) often involve the radial distribution for the mitochondria and RNA channels. These metrics capture the fraction of those stains near the edge of the cell versus concentric rings towards the nucleus, which are more readily detectable in larger cells compared to small, rounded cells.

      In contrast, the important features for mechanisms of action not improved by CytoSummaryNet (Supplementary Material I) predominantly include correlation metrics between brightfield and various fluorescent channels, capturing spatial relationships between cellular components. Some of these mechanisms of action included compounds that were not individually distinguishable from negative controls, and CytoSummaryNet did not overcome the lack of phenotype in these cases. This suggests that while CytoSummaryNet excels in identifying certain cellular features, its effectiveness is limited when dealing with mechanisms of action that do not exhibit pronounced phenotypic changes.”

      We have also added supplementary material to support (I. Relevant features for CytoSummaryNet improvement).

      R3.0 Another test on datasets that are not concerned with chemical compounds, but rather genetic perturbations would greatly increase the reach of the method into the functional genomics community and beyond. This additional analysis could provide valuable insights into the versatility and applicability of the proposed method.

      We agree that testing the method's behavior on genetic perturbations would be interesting and could provide insights into its versatility. However, the efficacy of the methodology may vary depending on the specific properties of different genetic perturbation types.

      For example, the penetrance of phenotypes may differ between genetic and chemical perturbations. In some experimental setups, a selection agent ensures that nearly all cells receive a genetic perturbation (though not all may express a phenotype due to heterogeneity or varying levels of the target protein). Other experiments may omit such an agent. Additionally, different patterns might be observed in various classes of reagents, such as overexpression, CRISPR-Cas9 knockdown (CRISPRn), CRISPR-interference (CRISPRi), and CRISPR-activation (CRISPRa).

      We believe that selecting a single experiment with one of these technologies would not adequately address the question of versatility. Instead, we propose future studies that may conclusively assess the method's performance across a variety of genetic perturbation types. This would provide a more comprehensive understanding of CytoSummaryNet's applicability in functional genomics and beyond. We have update the Discussion section to reflect this:

      “Future research could also explore CytoSummaryNet's applicability to genetic perturbations, expanding its utility in functional genomics.”

      R3.1. The datasets were stratified based on plates and compounds. It would be beneficial to clarify the basis for data stratification applied for compounds. Was the data sampled based on structural or functional similarity of compounds? If not, what can be expected from the model if trained and validated using structurally or functionally diverse and non-diverse compounds?

      Thank you for raising the important question of data stratification based on compound similarity. In our study, the data stratification was performed by randomly sampling the compounds, without considering their structural or functional similarity.

      This approach may limit the generalizability of the learned representations to new structural or functional classes not captured in the training set. Consequently, the current methodology may not fully characterize the model’s performance across diverse compound structures.

      In future work, it would be valuable to explore the impact of compound diversity on model performance by stratifying data based on structural or functional similarity and comparing the results to our current random stratification approach to more thoroughly characterize the learned representations.

      R3.2. Is the method prioritizing a particular biological reaction of cells toward common chemical compounds, such as mitotic failure? Could this be oncology-specific, or is there more utility to it in other datasets?

      Our analysis of CytoSummaryNet's performance in (the new) Figure 6 reveals a strong improvement in MoAs targeting cancer-related pathways, such as MEK, HSP, MDM, dehydrogenase, and purine antagonist inhibitors. These MoAs share a common focus on cellular proliferation, survival, and metabolic processes, which are key characteristics of cancer cells.

      Given the composition of the cpg0004 dataset, which contains 1,258 unique MoAs with only 28 annotated as oncology-related, the likelihood of randomly selecting five oncology-related MoAs that show strong improvement is extremely low. This suggests that the observed prioritization is not due to chance.

      Furthermore, the prioritization cannot be solely attributed to the frequency of oncology-related MoAs in the dataset. Other prevalent disease areas, such as neurology/psychiatry, infectious disease, and cardiology, do not exhibit similar improvements despite having higher MoA counts.

      While these findings indicate a potential prioritization of oncology-related MoAs by CytoSummaryNet, further research is necessary to fully understand the extent and implications of this bias. Future work should involve conducting similar analyses across other disease areas and cell types to assess the method's broader utility and identify areas for refinement and application. However, given the speculative nature of these observations, we have chosen not to update the manuscript to discuss this potential bias at this time.

      R3.3 Figures 1 and 2 demonstrate that the CytoSummaryNet profiles outperform average-aggregated profiles. However, the average profiling results seem more consistent when compared to CytoSummaryNet profiling. What further conditions or approaches can help improve CytoSummaryNet profiling results to be more consistent?

      The observed variability in CytoSummaryNet's performance is primarily due to the intentional technical variance in our datasets, where each plate tested different staining protocol variations. It's important to note that this level of technical variance is not typical in standard cell profiling experiments. In practice, the variance across plates would be much lower. We want to emphasize that while a model capable of generalizing across diverse experimental conditions might seem ideal, it may not be as practically useful in real-world scenarios. This is because such non-uniform conditions are uncommon in typical cell profiling experiments. In normal experimental settings, where technical variance is more controlled, we expect CytoSummaryNet's performance to be more consistent.

      R3.4 Can the poor performance on unseen data (in the case of stain 5) be overcome? If yes, how? If no, why not?

      We believe that the poor performance on unseen data, such as Stain 5, can be overcome depending on the nature of the unseen data. As shown in Figure 4 (panel 3), the model improves upon average profiling for unseen data when the experimental conditions are similar to the training set.

      The issue lies in the different experimental conditions. As explained in our response to R3.3, this could be addressed by including these experimental conditions in the training dataset. As long as CytoSummaryNet is trained (seen) and tested (unseen) on data generated under similar experimental conditions, we are confident that it will improve or perform as well as average profiling.

      It's important to note that the issue of generalization to vastly different experimental conditions was considered out of scope for this paper. The main focus is to introduce a new method that improves upon average profiling and can be readily used within a consistent experimental setup.

      R3.5 It needs to be mentioned how the feature data used for CytoSummaryNet profiling was normalized before training the model. What would be the impact of feature data normalization before model training? Would the model still outperform if the skewed feature data is normalized using square or log transformation before model training?

      We have clarified in the manuscript that we standardized the feature data on a plate-by-plate basis to achieve zero mean and unit variance across all cells per feature within each plate. We have added the following statement to improve clarity:

      “The data used to compute the average profiles and train the model were standardized at the plate-level, ensuring that all cell features across the plate had a zero mean and unit variance. The negative control wells were then removed from all plates."

      We chose standardization over transformations like squaring or logging to maintain a balanced scale across features while preserving the biological and morphological information inherent in the data. While transformations can reduce skewness and are useful for data spanning several orders of magnitude, they might distort biological relevance by compressing or expanding data ranges in ways that could obscure important cellular variations.

      Regarding the potential impact of square or log transformations on skewed feature data, these methods could improve the model's learning efficiency by making the feature distribution more symmetrical. However, the suitability and effectiveness of these techniques would depend on the specific data characteristics and the model architecture.

      Although not explored in this study, investigating various normalization techniques could be a valuable direction for future research to assess their impact on the performance and adaptability of CytoSummaryNet across diverse datasets and experimental setups.

      R3.6. In Figure 5 b and c, MoAs often seem to be represented by singular compounds and thus, the test (MoA prediction) is very similar to the training (compound ID). Given this context, a discussion about the extent this presents a circular argument supported by stats on the compound library used for training and testing would be beneficial.

      Clusters in (the new) Figure 7 that contain only replicates of a single compound would not yield an improved performance on the MoA task unless they also include replicates of other compounds sharing the same MoA in close proximity. Please see our response to R1.1c.iii. for details. To improve visual clarity and avoid misinterpretation, we have recomputed the colors for (the new) Figure 7 and grayed out overlapping points.

      R3.7 Can you estimate the minimum amount of supervision (fuzzy/sparse labels, often present in mislabeled compound libraries with dirty compounds and polypharmacology being present) that is needed for it to be efficiently trained?

      It's important to note that the metadata used by the model is only based on identifying replicates of the same compound. Mechanism of action (MoA) annotations, which can be erroneous due to dirty compounds, polypharmacology, and incomplete information, are not used in training at all. MoA annotations are only used in our evaluation, specifically for calculating the mAP for MoA retrieval.

      We have successfully trained CytoSummaryNet on 72 unique compounds with 4 replicates each. This is the current empirical minimum, but it is possible that the model could be trained effectively with even fewer compounds or replicates.

      Determining the absolute minimum amount of supervision required for efficient training would require further experimentation and analysis. Factors such as data quality, feature dimensionality, and model complexity could influence the required level of supervision.

      R3.minor1 Figure 5: The x-axis and y-axis tick values are too small, and image resolution/size needs to be increased.

      We have made the following changes to address the concerns:

      • Increased the image resolution and size to improve clarity and readability.
      • Removed the x-axis and y-axis tick values, as they do not provide meaningful information in the context of UMAP visualizations. We believe these modifications enhance the visual presentation of the data and make it easier for readers to interpret the results.

      R3.minor2 The methods applied to optimize hyperparameters in supplementary data need to be included.

      We added the following to Supplementary Material D:

      “We used the Weights & Biases (WandB) sweep suite in combination with the BOHB (Bayesian Optimization and HyperBand) algorithm for hyperparameter sweeps. The BOHB algorithm [47] combines Bayesian optimization with bandit-based strategies to efficiently find optimal hyperparameters.

      Additionally Table D1 provides an overview of all tunable hyperparameters and their chosen values based on a BOHB hyperparameter optimization.”

      R3.minor3 Figure 5(c, d): The names of compound 2 and Compound 5 need to be included in the labels.

      These compounds were obtained from external companies and are proprietary, necessitating their anonymization in our study. This has now been added in the caption of (the new) Figure 7:

      “Note that Compound2 and Compound5 are intentionally anonymized.”

      R3.minor4 Table C1: Plate descriptions need to be included.

      *Table C1: The training, validation, and test set stratification for Stain2, Stain3, Stain4, and Stain5. Five training, four validation, and three test plates are used for Stain2, Stain3, and Stain4. Stain5 contains six test set plates only. *

      __Stain2 __

      Stain3

      Stain4

      Stain5

      Training plates

      Test plates

      BR00113818

      BR00115128

      BR00116627

      BR00120532

      BR00113820

      BR00115125highexp

      BR00116631

      BR00120270

      BR00112202

      BR00115133highexp

      BR00116625

      BR00120536

      BR00112197binned

      BR00115131

      BR00116630highexp

      BR00120530

      BR00112198

      BR00115134

      200922_015124-Vhighexp

      BR00120526

      Validation plates

      BR00120274

      BR00112197standard

      BR00115129

      BR00116628highexp

      BR00112197repeat

      BR00115133

      BR00116629highexp

      BR00112204

      BR00115128highexp

      BR00116627highexp

      BR00112201

      BR00115127

      BR00116629

      Test plates

      BR00112199

      BR00115134bin1

      200922_044247-Vbin1

      BR00113819

      BR00115134multiplane

      200922_015124-V

      BR00113821

      BR00115126highexp

      BR00116633bin1

      We have added a reference to the metadata file in the description of Table C1: https://github.com/carpenter-singh-lab/2023_Cimini_NatureProtocols/blob/main/JUMPExperimentMasterTable.csv

      R3.minor5 Figure F1: Does the green box (stain 3) also involve training on plates from stain 4 (BR00116630highexp) and 5 (BR00120530) mentioned in Table C1? Please check the figure once again for possible errors.

      We have carefully re-examined Figure F1 and Table C1 to ensure their accuracy and consistency. Upon double-checking, we can confirm that the figure is indeed correct. We intentionally omitted the training and validation plates from Figure F1 to maintain clarity and readability, as including them resulted in a cluttered and difficult-to-interpret figure.

      Regarding the specific plates mentioned:

      • BR00116630highexp (Stain4) is used for training, as correctly stated in Table C1. This plate is considered an outlier within the Stain4 dataset and happens to cluster with the Stain3 plates in Figure F1.
      • BR00120530 (Stain5) is part of the test set only and correctly falls within the Stain5 cluster in Figure F1. To improve the clarity of the training, validation, and test split in Table C1, we have added a color scheme that visually distinguishes the different data subsets. This should make it easier for readers to understand the distribution of plates across the various splits.
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      Referee #3

      Evidence, reproducibility and clarity

      Summary:

      In the manuscript by Van Dijk et al., a novel deep learning technique is introduced that aims to summarize informative cells from heterogeneous populations in image-based profiling. This technique is based on a network that utilizes contrastive learning with a multiple-instance learning framework, a significant departure from existing average-based cell profiling models.

      The authors have done a commendable job discussing the method, demonstrating its potential to outperform current models in profiling cell-based features. The work is of considerable significance and interest to a wide field of researchers working on the understanding of cell heterogeneity's impact on various biological phenomena and practical studies in pharmacology.

      One aspect that would further enhance the value of this work is an exploration of the method's separation power across different modes of action. For instance, it would be interesting to ascertain if the method's performance varies when dealing with actions that primarily affect size, those that affect marker expression, or compounds that significantly diminish cell numbers. Another test on datasets that are not concerned with chemical compounds, but rather genetic perturbations would greatly increase the reach of the method into the functional genomics community and beyond. This additional analysis could provide valuable insights into the versatility and applicability of the proposed method. Please find my detailed comments below:

      Major Comments:

      1. The datasets were stratified based on plates and compounds. It would be beneficial to clarify the basis for data stratification applied for compounds. Was the data sampled based on structural or functional similarity of compounds? If not, what can be expected from the model if trained and validated using structurally or functionally diverse and non-diverse compounds?
      2. Is the method prioritizing a particular biological reaction of cells toward common chemical compounds, such as mitotic failure? Could this be oncology-specific, or is there more utility to it in other datasets?
      3. Figures 1 and 2 demonstrate that the CytoSummaryNet profiles outperform average-aggregated profiles. However, the average profiling results seem more consistent when compared to CytoSummaryNet profiling. What further conditions or approaches can help improve CytoSummaryNet profiling results to be more consistent?
      4. Can the poor performance on unseen data (in the case of stain 5) be overcome? If yes, how? If no, why not?
      5. It needs to be mentioned how the feature data used for CytoSummaryNet profiling was normalized before training the model. What would be the impact of feature data normalization before model training? Would the model still outperform if the skewed feature data is normalized using square or log transformation before model training?
      6. In Figure 5 b and c, MoAs often seem to be represented by singular compounds and thus, the test (MoA prediction) is very similar to the training (compound ID). Given this context, a discussion about the extent this presents a circular argument supported by stats on the compound library used for training and testing would be beneficial.
      7. Can you estimate the minimum amount of supervision (fuzzy/sparse labels, often present in mislabeled compound libraries with dirty compounds and polypharmacology being present) that is needed for it to be efficiently trained?

      Minor Comments:

      1. Figure 5: The x-axis and y-axis tick values are too small, and image resolution/size needs to be increased.
      2. The methods applied to optimize hyperparameters in supplementary data need to be included.
      3. Figure 5(c, d): The names of compound 2 and Compound 5 need to be included in the labels.
      4. Table C1: Plate descriptions need to be included.
      5. Figure F1: Does the green box (stain 3) also involve training on plates from stain 4 (BR00116630highexp) and 5 (BR00120530) mentioned in Table C1? Please check the figure once again for possible errors.

      Significance

      This work presents a significant move forward in the ways we deal with cellular heterogeneity in all single-cell assays. Though the model in its current state has trouble extrapolating to out of distribution data, I am confident that it provides a considerable step forward in the process of extracting "informative" knowledge from data in the form of optimized profiles.

      The optimization is yet based on optimizing a similarity metric for group assignments, I will be interesting to see if other objectives could be more effective in developing aggregation techniques.

      The work is of considerable significance and interest to a wide field of researchers working on the understanding of cell heterogeneity's impact on various biological phenomena and practical studies in pharmacology.

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      Referee #2

      Evidence, reproducibility and clarity

      The authors present a well-developed and useful algorithm. The technical motivation and validation are very carefully and clearly explained, and their work is potentially useful to a varied audience.

      That said, I think the authors could do a better job, especially in the figures, of putting the algorithm in context for an audience that is unfamiliar with the cell painting assay. For example, a figure towards the beginning of the paper with example images might help to set the stage. Similarly a schematic of the algorithm earlier in the paper would provide a graphical overview. For the sake of a biologically inclined audience, I would consider labeling the images in the caption by cell type and label.

      The interpretability results were intriguing. The authors might consider further validating these interpretations by removing weakly informative cells from the dataset and retraining. Are the cells so uninformative that the algorithm does better without them, or are they just less informative than other cells?

      As far as I can tell, the authors only oblique state whether the code associated with the manuscript is openly available. Posting the code is needed for reproducibility. I would provide not only a github, but a doi linked to the code, or some other permanent link.

      Significance

      Incorporating biological heterogeneity into machine-learning driven problems is a critical research question. Replacing means/modes and such with a machine learning framework, the authors have identified a problem with potentially wide significance. The application to cell painting and related assays is of broad enough significance for many journals, However, the authors could further broaden the significance by commenting on other possible cell biology applications. What other applications might the algorithm be particularly suited for? Are there any possible roadblocks to wider use. What sorts of data has the code been tested on so far?

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

      Cell (non-genetic) heterogeneity is an important concept in cell biology, but there are currently only a few studies that try to incorporate this information to represent cell populations in the field of high-content image-based phenotypic profiling. The authors present CytoSummaryNet, a machine learning approach for representing heterogeneous cell populations, and apply it to a high-content image-based Cell Painting dataset to demonstrate superior performance in predicting a compound's mechanism of action (MoA), in relation to the average profile representation. CytoSummaryNet relies on Cell Profiler morphological features and simultaneous optimization of two components, both novel in the cell profiling field: (i) learning representations using weakly supervised contrastive learning according to the perturbation identifications (i.e., the compound), (ii) using a representation method called Deep Sets to create permutation-invariant population representations. The authors evaluate their representation on the task of replicate retrieval and of MoA retrieval using the public dataset cpg0001 (and cpg0004), and report superior performance in respect to the average-aggregated profiles for the experimental protocols and compounds seen on training (that do not generalize to out-of-distribution compounds + experimental protocols). By interpreting which cells were most important for the MoA model predictions, the authors propose that their representation prioritizes large uncrowded cells.

      Major comments:

      The strength of the manuscript is the new idea of combining contrastive learning and sets representations for better representation of heterogeneous cell populations. However, we are not convinced that the conclusion that this representation improves MoA prediction is fully supported by the data, for several reasons.

      1. Evaluations. This is the most critical point in our review.

      a. CytoSummaryNet is evaluated in comparison to aggregate-average profiling, although previous work has already reported representations that capture heterogeneity and self-supervision independently. To argue that both components of contrastive learning and sets representations are contributing to MoA prediction we believe that a separate evaluation for each component is required. Specifically, the authors can benchmark their previous work to directly evaluate a simpler population representation (PMID: 31064985, ref #13) - we are aware that the authors report a 20% improvement, but this was reported on a separate dataset. The authors can also compare to contrastive learning-based representations that rely on the aggregate (average) profile to assess and quantify the contribution of the sets representation.

      b. The evaluation metric of mAP improvement in percentage is misleading, because a tiny improvement for a MoA prediction can lead to huge improvement in percentage, while a much larger improvement in MoA prediction can lead to a small improvement in percentage. For example, in Fig. 4, MEK inhibitor mAP improvement of ~0.35 is measured as ~50% improvement, while a much smaller mAP improvement can have the same effect near the origins (i.e., very poor MoA prediction). (Subjective) visual assessment of this figure does not show a convincing contribution of CytoSummaryNet representations of the average profiling on the test set (3.33 uM). This issue might also be relevant for the task of replicate retrieval. All in all, the mAP improvement reported in Table 1 and throughout the manuscript (including the Abstract), is not a proper evaluation metric for CytoSummaryNet contribution. We suggest reporting the following evaluations:

      i. Visualizing the results of cpg0001 (Figs. 1-3) similarly to cpg0004 (Fig. 4), i.e., plotting the matched mAP for CytoSummaryNet vs. average profile. ii. In Table 1, we suggest referring to the change in the number of predictable MoAs (MoAs that pass a mAP threshold) rather than the improvement in percentages. Another option is showing a graph of the predictability, with the X axis representing a threshold and Y-axis showing the number of MoAs passing it. For example see (PMID: 36344834, Fig. 2B) and (PMID: 37031208, Fig. 2A), both papers included contributions from the corresponding author of this manuscript.

      c. Additional evaluation-related concerns were: i. "a subset of 18 compounds were designated as validation compounds" - 5 cross-validations of 18 compounds can make the evaluation complete. This can also enhance statistical power in figures 1-3.

      ii. Clarify if the MoA results for cpg0001 are drawn from compounds from both the training and the validation datasets. If so, describe how the results differ between the sets in text and graphs.

      iii. "Mechanism of action retrieval is evaluated by quantifying a profile's ability to retrieve the profile of other compounds with the same annotated mechanism of action.". It was unclear to us if the evaluation of mAP for MoA identification can include finding replicates of the same compound. That is, whether finding a close replicate of the same compound would be included in the AP calculation. This would provide CytoSummaryNet with an inherent advantage as this is the task it is trained to do. We assume that this was not the case (and thus should be more clearly articulated), but if it was - results need to be re-evaluated excluding same-compound replicates. 2. Lack of clarity in the description of the data and evaluation. While the concept of constructive learning + sets representation is elegant and intuitive, we found it very hard to follow the technical aspects of data and performance evaluation, even after digging in deep into the Methods. Figuring out these important aspects required us for vast investment in time, more than the vast majority of manuscripts we reviewed in the last couple of years. It is highly recommended that the authors provide more details to make this manuscript easier to follow. Some examples include:

      a. The description of Stain2-5 was not clear for us at first (and second) read. The information is there, but more details will greatly enhance the reader's ability to follow. One suggestion is explicitly stating that these "stains" partitioning was already defined in ref 26. Another suggestion is laying out explicitly a concrete example on the differences between two of these stains. We believe highlighting the differences between stains will strengthen the claim of the paper, emphasizing the difficulty of generalizing to the out-of-distribution stain.

      b. What does each data point in Figures 1-3 represent? Is it the average mAP for the 18 validation compounds, using different seeds for model training? Why not visualize the data similarly to Fig. 4 so the improvement per compound can be clearly seen?

      c. Justification and interpretation of the evaluation metrics.

      d. Explicitly mentioning the number of MoAs for each datasets and statistics of number of compounds per MoA (e.g., average\median, min, max).

      e. The data split in general is not easily understood. Figure 8 is somewhat helpful, however in our view, it can be improved to enhance understanding of the different splits. Specifically, the training and validation compounds need to be embedded and highlighted within the figure. 3. Lack of justification of design choices. There were multiple design choices that were not justified. This adds to the lack of clarity and makes it harder to evaluate the merits of the new method. For example:

      a. Why was stain 5 used for the test, rather than the other stains?

      b. How were the 18 validation compounds selected?

      c. For cpg0004, no justification for the specific doses selected (10uM - train, 3.33 uM - test) for the analysis in Figure 4. Why was the data split for the two dosages? For example, why not perform 5-fold cross validation on the compounds (e.g., of the highest dose)?

      d. A more detailed explanation on the logic behind using a training stain to test MoA retrieval will help readers appreciate these results. In our first read of this manuscript we did not grasp that, we did in a second read, but spoon-feeding your readers will help. 4. The interpretability analysis is speculative. Assessment of interpretability is always tricky. But in this case, the authors can directly confirm their interpretation that the CytoSummaryNet representation prioritizes large uncrowded cells, by explicitly selecting these cells, and using their average profile representation to demonstrate that they achieve improved results. If this works, it could be applied as a general outlier removal strategy for cell profiling.

      a. "We identified the likely mechanism by which the learned CytoSummaryNet aggregates cells: the most salient cells are generally larger and more isolated from other cells, while the least salient cells appear to be smaller and more crowded, and tend to contain spots of high-intensity pixels (whether dying, debris or in some stage of cell division)." - doesn't such a mechanism should generalize to out-of-distribution data? 5. Placing this work in context of other weakly supervised representations. Previous papers used weakly supervised labels of proteins / experimental perturbations (e.g., compounds) to improve image-derived representations, but were not discussed in this context. These include PMID: 35879608, https://www.biorxiv.org/content/10.1101/2022.08.12.503783v2 (from the same research groups and can also be benchmarked in this context),https://pubs.rsc.org/en/content/articlelanding/2023/dd/d3dd00060e , and https://www.biorxiv.org/content/10.1101/2023.02.24.529975v1. We believe that a discussion explicitly referencing these papers in this specific context is important.

      Minor comments:

      In our opinion, evaluation of the training task using the training data (Figure 1) is not contributing to the manuscript and could be excluded. Also we feel that the subjectiveness of the UMAP analysis (Figure 5) is not contributing much and could be excluded, especially if the authors follow our suggestions regarding quantification. Of course, this is up to the authors to decide (along with most of the other suggestions below).

      Suggested clarifications:

      1. "Because the improved results could stem from prioritizing certain features over others during aggregation, we investigated each cell's importance during CytoSummaryNet aggregation by calculating a relevance score for each" - what is the relevance score? Would be helpful to provide some intuition in the Results.
      2. Figure 1:

      a. Colors of the two methods too similar

      b. The dots are too close. It will be more easily interpreted if they were further apart.

      c. What do the dots stand for?

      d. We recommend considering moving this figure to the supp. material (the most important part of it is the results on the test set and it appears in Fig.2). 3. Figure 4: It is somewhat misleading to look at the training MoAs and validation MoAs embedded together in the same graph. We recommend showing only the test MoAs (train MoAs can move to SI). 4. Figure 5

      a. Why only Stain3? What happens if we look at Stains 2,3 and 4 together? Stain 5?

      b. Should validation compounds and training compounds be analyzed separately?

      c. Subfigure (d): it is expected that the data will be classified by compound labels as it is the training task, but for this to be persuasive I would like to see this separately on the training compounds first and then and more importantly on the validation compounds.

      d. For subfigures (b) and (d): it appears there are not enough colors for d, which makes it partially not understandable. For example, the pink label in (d) shows a single compound which appears to represent two different MoAs. This is probably not the case, and it has two different compounds, but it cannot be inferred when they are represented by the same color.

      e. For the Subfigure (e) - only 1 circle looks justified (in the top left). And for that one, is it not a case of an outlier plate that would perhaps need to be removed from analysis? Is it not good that such a plate will be identified? 5. Discussion:

      a. "perhaps in part due to its correction of batch effects" - is this statement based on Fig. 5F - we are not convinced.

      b. "Overall, these results improve upon the ~20% gains we previously observed using covariance features" - this is not the same dataset so it is hard to reach conclusions - perhaps compare performance directly on the same data?

      Significance

      Cell profiling is an emerging field with many applications in academia and industry. Finding better representations for heterogeneous cell populations is important and timely. However, unless convinced otherwise after a rebuttal/revision, the contribution of this paper, in our opinion, is mostly conceptual, but in its current form - not yet practical. This manuscript combined two concepts that were previously reported in the context of cell profiling, weakly supervised representations. Our expertise is in computational biology, and specifically applications of machine learning in microscopy.

  4. Jul 2024
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      Reply to the reviewers

      The authors do not wish to post a response at this time. This is because this is not the submission of the revised version, which we have not completed yet. This is a preliminary revision together with a revision plan instead.

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      Referee #3

      Evidence, reproducibility and clarity

      In this manuscript, Singh et al. demonstrate that infection of D. melanogaster flies with B. bassiana fungus induces neurodegeneration via Toll/wek/sarm signalling. It is already known that fungal infection can be associated with neurodegeneration, but the exact mechanism is unclear. The authors demonstrate that the fungus enters the brain, causes hallmark symptoms of neurodegeneration, and requires Toll-1, Wek, and Sarm in order to do so. This is an important step forward as it demonstrates specific genes in the fly immune pathways that are involved in fungus-induced neurodegeneration, which could be informative for infections in humans. Overall, the manuscript is thorough and well-written and the conclusions are broadly supported. A few mostly minor comments and questions are below, which could mostly be addressed by including additional details in the methods or discussion. The only major comments would be 1) that the control fly genotypes used in experiments were not always the most ideal controls (eg, compared WT genotypes to RNAi against a gene of interest; ideally would be RNAi against a control gene compared to RNAi against a gene of interest), and 2) negative controls of fluorescence microscopy imaging were not always included. It would be important to address these through clarification in the figures/methods, and/or discussion of the potential caveats, even though it is likely the conclusions would still hold. Notably, these comments are relatively easily addressed through edits in the text.

      Major comments:

      • For fluorescence imaging, were negative controls included (no infection or no gene expression etc.) for all stains (as with Figure 1H)? If so, it would help to include representative images as supplemental figures. Also, for all positive samples, was presence of the fungus noted in all samples?
      • Figure 4: Here, it appears that the control fly genotypes are wildtype vs an RNAi line (similar for some other figures/assays as well, but using this one as an example). The best control would be RNAi against a control gene compared to RNAi against a gene of interest, rather than just a control WT genotype with no RNAi compared to RNAi against a gene of interest. This should be included as a caveat in the discussion since the experiments do not all account for the effect of RNAi (or other gene expression) on the phenotypes regardless of the gene.

      Minor comments:

      • It would help to have line numbers throughout
      • Figure 1- what are the arrows in panels D-G?
      • Methods: A few details are unclear:
        • Was only one fly sex used or were both used for the various assays? If both were used, were they statistically assessed for differences? Sex is only mentioned in a couple of the methods sections.
        • How old were the flies at the start of the experiments? A few experiments noted age, but it was not clear for all
        • For longevity, was the fungal culture ever replaced during the experiment?
        • For the climbing assay when the flies were initially flipped, how much time was there between flips?
      • Figures 2A, 2D, 2E, 3E, & 3H: If multiple replicates or samples are represented in the data, it would help to be able to see the data points underlying these bars. If so, please add them to the graphs to see the spread of data points.
      • Figure 3F- what do arrows indicate?
      • It is interesting that Wek-RNAi with infection not only rescues loss caused by the infection alone, but also increases YFP cells beyond the uninfected controls (Figure 5C). The same is true with toll-1 RNAi (Figure 4C). Why might this be?
      • It would be ideal if data underlying data points and full statistical models and outputs could be included through a public repository such as Dryad. This would be ideal for full assessment of statistical approaches

      Very Minor comments:

      • Check italicizing throughout- missed a few "Drosophila" or "B. bassiana" in main text or figures
      • Looks like no space between C. and elegans in C. elegans in a few cases
      • Word missing: "No effect was seen after three days exposure to B. bassiana, but seven days exposure impaired climbing"... seven days of exposure?
      • Toll-1 misspelled pg 6 last paragraph

      Referee Cross-Commenting

      Regarding the major comments, I agree with Reviewer 1 that more thorough proof of spores entering the brain (and what proportion of exposed flies this happens to) would be beneficial. I also agree with Reviewer 2 that a rescue experiment for the climbing assay and my earlier suggestion for more controls in the microscopy could help address this concern, at least in part. Other responses or experiments may also be appropriate to address some of the major concerns- maybe additional assay(s) of brain function other than climbing?

      Reviewer 1 also brought up the point that flies with advanced infection were used for the experiments- it would be helpful to know if earlier time points were ever checked for BBB damage, loss of brain cells, or presence of fungus etc. This would clarify if the same phenotypes are present in flies that die early, along with other concerns from Reviewer 1.

      However, whether directly or indirectly, several later figures show loss of brain cells with infection followed by rescue with RNAi against genes of interest. This does lend support to the conclusions that fungal infection negatively impacts brain cells and the fungus requires these host genes to do so.

      Other concerns Reviewer 2 and I raised about the fly genetic controls being unclear should also be addressed. What is the full genotype of the flies in each case? What is considered "+" in each case? Were these driver background strains, WT (like Oregon R), or RNAi against control genes (best controls)?

      Significance

      General assessment: The manuscript by Singh et al. is a thorough investigation into the fungus-host interactions in the brain, demonstrating that the common insect fungal pathogen B. bassiana requires the host genes Toll, wek, and sarm to induce negative phenotypes in the brain. The strengths are in the multi-pronged approaches that use several independent techniques (fly behavior assays, gene expression, microscopy, etc.) and multiple genes, conducted with many replicates, that all show clear and consistent trends supporting the conclusions of the authors. The weaknesses include some cases where controls are either not completely clear or not the most ideal controls. This weakness could be addressed with either edits to the text, where appropriate, or addition of supplemental figures. However, the conclusions are still broadly supported.

      Advance: Although it is known that fungal infections can impair brain function, it is not fully understood how this happens. This manuscript identifies Toll-associated molecules that are required for fungus-mediated neurodegeneration, which is a critical first step to understanding the process and for future development of therapies.

      Audience: This finding would be of broad interest to scientists in immunology, microbiology, neuroscience, and other areas.

      Expertise of reviewer: Drosophila, fly genetics, invertebrate immunology, insect-fungal interactions

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      Referee #2

      Evidence, reproducibility and clarity

      Summary

      The authors describe a role for Toll signaling in detrimental neuronal loss associated with B. bassiana fungal infection in Drosophila melanogaster model. They show that this effect is mediated by wek/sarm as silencing either of them prevents neuronal loss after the infection. Similar results are obtained with Toll-1 RNAi, suggesting that the response is dependent on the activation of Toll signaling by B. bassiana. The study is well executed,main conclusions are backed up by the data presented and experiments are conducted with adequate numbers of replications and individuals. Below I give some comments that I think would help in further improving the manuscript.

      Major comments

      As the initial experiments (including the effect on survival and climbing assay) have been performed using OR/CantonS, it would be interesting to investigate if the same is seen with a more similar background to that what is used in the genetic experiments. In addition, I'd suggest an experiment to see if the Toll (or wek/sarm) RNAi in the brain rescues the climbing defect caused by the fungal infection.

      It is somewhat unclear what are the controls in the genetic experiments. For example, in Figure 2, the control is UAS-TrpA1/+. Does this mean that the UAS-TrpA1 flies have been crossed to something (like the driver background strain) or used as it is? In Figure 4, controls are ">+". Again, are MyD88>histoneYFP;tubulinGal80ts flies crossed to something (in this case, maybe the w1118 background of the KK library RNAi strains) or used as homozygous? And same for the subsequent figures. I'd ask the authors to clarify these points in the manuscript.

      Could the authors please explain why they opted for MyD88-GAL4 in the experiments in Figures 5-7? What is the overall expression pattern of MyD88-GAL4? Is there a possibility that some of the effects seen could arise from the Toll/sarm/wek knockdown elsewhere in the fly? How do the flies survive the infection with Toll knockdown in MyD88-epressing cells (expressed at least in all immunogenic tissues)? A bit more explanation would clarify the situation.

      Minor comments

      Page 3: Full species name should be given here (Drosophila melanogaster)

      A short description of the FM4-64 dye (what it stains etc) would be useful for the readers unfamiliar with it.

      Page 6: Please explain shortly why TrpA1 overexpression was used to activate the neurons.

      Figure 2E: What is the genotype of the flies? mtk is lacking statistics

      Page 8: third row refers to Figure 2 but should be Figure 3.

      Although antibody stainings are performed using "standard methods", a short overview on the process should be presented also in the current manuscript. Also, I imagine fungal spores are all over the flies retrieved from the infection chamber. I'd like to know (and this could also be described in the materials) how the flies (and the brains) were treated/washed prior to preparing brains for immunostaining and imaging?

      Some typos and inconsistencies at various places. For example, at some occasions B. bassiana written without a space in between "B" and "bassiana" and not in italics (both in figures and in text); on page 5, first line: "mimicked" misspelled

      Referee Cross-Commenting

      As the fungal infiltration into the brain is central to the conclusions made in the manuscript, I agree that care should be taken in making this argument solid. I believe this can be achieved adding controls as reviewer #3 suggests together with additional experiment(s) verifying that Toll/wek/sarm in the brain is mediating the neuronal loss caused by the fungal infection (rescue experiments). Of note, I wonder if, similarly to mammalian macrophages, hemocytes could be responsible for delivering the fungal cells into the brain?

      I agree with the reviewer #1 that the climbing defect could be because of multiple reasons other than the fungal spores in the brain causing neuronal loss (for instance flies being generally weak at this point, ). However, the authors do show convincingly that there is neuronal loss in fungal-infected flies.

      Significance

      Fungal infections are understudied in any research model considering the threat they pose to humans and other animals alike. Due to the high conservation of the signaling components studied here, the results provide a good basis for future research, extending to mammalian models. I think these results will be of interest to a wider audience because of the reasons stated above.

      My fields of expertise are Drosophila melanogaster, innate immunity, cell-mediated immunity, blood cell homeostasis

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      Referee #1

      Evidence, reproducibility and clarity

      Singh et al. report that, after exposure to the entomopathogenic fungus Beauveria bassiana, the Drosophila adults impaired fly locomotion and died within two weeks. During which time, the authors designed experiments and showed the decline of brain cells via a Toll-1/Wek/Sarm pathway, mimicking the neurodegenerative diseases in humans in association with fungal infections. Providing that the rather solid genetic evidence was shown for the pathway in mediating fly brain cell losses, critical issues of experiment design/setup and conclusion validity were concerned.

      Specific comments:

      The fungus-exposed flies died within two weeks were largely typical. However, it was unclear how those flies could be uniformly contaminated with fungal spores in the infection chamber shown in Fig. 1A, by landing on fungal "carpet"? It is publicly known that entomopathogenic fungi (EPF) like B. bassiana infect insects via spore germination on cuticle and then penetration of cuticles by fungal hyphae/mycelia (e.g., Trends Microbiol. 2024. 32, 302-316).

      It is typical that EPF killed and mycosed insects within 5-14 days after topical infection by immersion in or spraying spore suspensions, or dusting on the sporulated plates. Fungal spores can be ingested by insects, largely those with chewing mouthparts. However, fungal spores can barely survive the highly-alkaline foreguts. It is questionable that flies could ingest spores and spores "infiltrated" the brains.

      Regarding the detection of fungal cells in fly brains, on the one hand, the authors argued that detection of fungal SPORES in fly brain THREE days post exposure (page 5) by infiltration. It would be impossible that, even fungus could breach the blood brain barrier (BBB), it might be the fungal hyphae/mycelia but not the spores. One the other hand, the authors provided the evidence of the damaged BBB SEVEN days post exposure, a few days LATER than the detection of fungal spores in brains (THREE days) post treatment mentioned above. Did "spore infiltration" (even impossible) occur before BBB damage?

      The authors stated that "by day seven more than half of the flies had died" (Fig. 1B). It is questionable therefore that the "other half" of the diseased and dying insects were used for the following experiments. There would be no wonder that the climbing of these diseased and dying flies was impaired, however, which could be due to muscle damage, hemocyte number decline and reduction of energy production etc. apart from brain cell loss. The brain function of dying animals could be compromised by multiple direct or indirect factors.

      Issue of Fig. 2D labelling.

      Referee Cross-Commenting

      I agree with that Reviewers 2 and 3 that rather solid evidence of fly brain loss was shown in this work, however, at most in association with exposure to fungal cultures (volatiles could not be excluded etc.). "Spores" entry into fly brains were suspicious or impossible. If the dying flies had been used for these neurological experiments, the reliability of conclusions would be highly concerned.

      Significance

      Since there are critical concerns of experiment designs/setup in this work, it is questionable that fly brain cell loss was caused by fungal entry into brains.

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      Reply to the reviewers

      Manuscript number: RC-2024-02491

      Corresponding author(s): Gilbert, Vassart

      1. General Statements [optional]

      We thank referees 1 and 2 for their in-depth analysis of our manuscript. They see interest in our study, with questions to be answered. Referee 3 is essentially negative, considering that there is nothing new ("novel finding is missing"). We respectfully disagree with him/her, comforted by the opinion of referee 2 that "the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field and ... the manuscript should attract a significant amount of attention in the intestinal field" and we provide evidence in our answers that he/she did not read the manuscript with the same attention as referees 1 and 2 (see in particular answer to his/her question 5).

      Here is a summary of the main reason why we consider that our study represents valuable new information in the field of intestinal regeneration.

      It is based on the serendipitous observation that dissociation of adult intestinal tissue by collagenase generates stably replatable spheroids upon culture in matrigel. Surprisingly and contrary to canonical EDTA-generated intestinal organoids and fetal spheroids, these spheroids are not traced in Rosa26Tomato mice harboring a VilCre transgene, despite expressing robustly endogenous Villin. Our interpretation is that adult intestinal spheroids originate from a cell lineage, distinct from the main developmental intestinal lineage, in which the VilCre transgene is unexpectedly not expressed, probaly due to the absence of cis regulatory sequences required for expression in this lineage.

      Adult spheroid transcriptome shares a gene signature with the YAP/TAZ signature commonly expressed in models of intestinal regeneration. This led us to look for VilCre negative crypts in the regenerating intestine of Lgr5/DTR mice in which Lgr5-positive stem cells have been ablated by diphtheria toxin. Numerous VilCre negative clones were observed, identifying a novel lineage of stem cells implicated in intestinal regeneration.

      FACS purification and scRNAseq analysis of the rare VilCre negative cells present at homeostasis identified a population of cells with characteristics of quiescent stem cells.

      In sum, we believe that our study demonstrates the existence of a hitherto undescribed stem cell lineage involved in intestinal regeneration. It points to the existence of a hierarchical model of intestinal regeneration in addition to the well-accepted plasticity model.

      2. Description of the planned revisions

      See section 3 below.

      3. Description of the revisions that have already been incorporated in the transferred manuscript

      Here is a point-by-point reply to the queries of the three referees, with indication of the revisions introduced in the manuscript.

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

      • *In this manuscript, Marefati et al report an Lgr5-independent lineage in the regenerating intestine using in vitro organoids and in vivo injury-coupled lineage tracing model. In organoids, collagenase/dispase dissociated resulted in "immortal spheroids" that maintain a cystic and undifferentiated phenotype in the absence of standard growth factors (Rspondin/Noggin/EGF). Bulk RNAseq of spheroids demonstrates downregulation of classical CBC signatures and upregulation of fetal spheroid, mesenchymal, inflammation and regenerative signatures. In mice, Villin-Cre lineage tracing revealed some Villin- negative progenies that lack reporter tracing throughout crypt-villus ribbons after injury.

      *The authors proposed that there is Lgr5-independent population support the regenerative response upon CBC depletion. A major caveat of this study is the identification of this population is based on absence of VilCre expression. *

      We respectfully disagree. It is precisely this characteristic that makes the interest of our study. Whereas mosaicism of transgene expression is widespread and usually of little significance, our study shows that the rare VilCre-negative cells in the intestinal epithelium are not randomly showing this phenotype: they give specifically birth to what we call adult spheroids and regenerating crypts, which cannot be due to chance. The absence of VilCre expression allows tracing these cells from the zygote stage of the various VilCre/Ros26 reporter mice. We have modified our text to emphasize this point.

      *It is surprising that there is no characterisation of Lgr5 expression throughout the manuscript whilst claiming of a Lgr5- independent lineage. *

      We understand the perplexity of the referee not to see direct Lgr5 expression data in our manuscript, given our title. However, our point is that it is the cells at the origin of adult spheroids and the regenerating crypts we have identified that are Lgr5-negative, not the spheroids or the regenerated crypts themselves. Those are downstream offspring that may, and indeed have, gained some Lgr5 expression (e.g. figure 3F). We believe that our data showing that VilCre-negative spheroids are not traced in Lgr5-CreERT2/Rosa reporter mice convincingly demonstrate absence of Lgr5 expression in the cells at the origin of adult spheroids (figure 4G). We think that this experiment is better evidence than attempts to show absence of two markers (Tom and Lgr5) in the rare "white" cells present in the epithelium. Regarding the Lgr5 status of cells at the origin of the regenerating "white" crypts that we have identified, the early appearance of these crypts following ablation of CBC (i.e. Lgr5+ve) cells is a strong argument that they originate from Lgr5-negative cells. Regarding the scRNAseq experiment, Lgr5 transcripts are notoriously low and difficult to measure reliably in CBCs (Haber et al 2017). However, blowing up the pertinent regions of the merged UMAP allows showing some Lgr5 transcripts in clusters 5,6 and none in cluster 1 of figure 8GH. Given the very low level of detection, we had chosen not to include these data in the manuscript, but we hope they may help answer the point of the referee (see portion of UMAP below, with Olfm4 as a control, together with the corresponding violin plot). Several markers that gave significant signals in the CBC cluster (Smoc2, Axin2, Slc12a2) were virtually undetectable in the Olfm4-low /Tom-negative cluster of our scRNAseq data (figure 8I) supporting our conclusion.

      Although the research question is potentially interesting, the concept of epithelial reprogramming upon injury is well documented in the field. The data generated in this manuscript also seem to be preliminary and lack of detailed characterisation. Below are specific comments.

      We do not question the existence of epithelial reprogramming upon injury. We believe our data show, in addition to this well demonstrated phenomenon, the existence of rare cells traced by absence of VilCre expression that are at the origin of a developmental cell lineage distinct from Lgr5+ stem cells and also implicated in regeneration.

      • Expression of Lgr5 should be properly characterised throughout the manuscript in both organoid models and injury-induced regeneration in vivo.
      • *

      See above for a detailed answer to this point.

      • An important question is the origin of these "Lgr5-independent" adult spheroids. They look and appear like fetal organoids, which could be induced by injury (e.g. upon collagenase/dispase dissociation). Have the authors tried to culture fetal spheroids in BCM over extensive period of time? Do they behave the same? This would be a great way to directly compare the collagenase/dispase-derived organoids with fetal origin. * *Fetal spheroids require ENR for survival and die in BCM. We have chosen to illustrate this point in Fig2A by showing that, contrary to adult spheroid, they die even when only Rspondin is missing.

      • Fig 1C, Why is the replating spheroid culture time different between mesenchymal cells and conditioned medium? We took the earliest time showing convincingly the return to the organoid phenotype. This timing difference does not modify the conclusion that EDTA organoids becoming spheroid-like when exposed to factors originating from mesenchymal cells revert to the organoid phenotype when returned to ENR medium without mesenchymal influence.

      • *It is unclear how the bulk RNA-seq data in Fig. 3 were compared. How long were the adult organoids and spheroids cultured for (how many passages)? Were they culture in the same condition of were they in ENR vs BCM? * Both EDTA organoids and spheroids displaying a stable phenotype were used in this experiment. Organoids were collected at passage 4, day 5; spheroids were collected at passage passage 9 day 3.

      As stated in the legend to the figure: "...to allow pertinent comparison spheroids and organoids were cultured in the same ENR-containing medium...".

      These are important information to consider when interpreting the results. For instance, are Ptgs1 & Ptgs2 expression in adult spheroids the same in ENR vs BCM? Are the gene signatures (regenerative, fetal and YAP) changed in adult spheroids culturing in ENR vs BCM?

      We did compare bulk RNAseq of EDTA organoids to ENR-cultured spheroids, short term (passage 6, day 6) BCM-cultured spheroids and long term BCM-cultured (passage 26, day 6) spheroids. To avoid overloading the manuscript these data were not shown in the original manuscript. In summary the BCM-cultured spheroids display a similar phenotype as those cultured in ENR, but with further de-differentiation. See in revision plan folder the results for PTGS, some differentiation markers and fetal regenerative markers including YAP induced genes.

      We have included a brief description of these data in the new version of the manuscript and added an additional supplementary file (Suppl table 2) presenting the whole data set.

      • It is stated: "In agreement with their aptitude to grow indefinitely, adult spheroids express a set of upregulated genes overlapping significantly with an "adult tissue stem cell module" [159/721 genes; q value 2.11 e-94) (Fig.S2F)].". What is the definition of "indefinitely"? Are they referring to the Fig 1B where spheroid were passaged to P10? The authors should avoid the term "indefinitely" but use a more specific time scale, e.g. passages, months etc.

      We agree that the term indefinitely should be avoided, as it is vague. We have introduced the maximum number of passages during which we have maintained the stable spheroid phenotype (26 passages). Also worth noting, the spheroids could be frozen and cultured repeatedly over many months.

      SuppFig 3D: Row Z-Score is missing the "e" in Score.

      Corrected

      • Fig 4E: Figure legend says QNRQ instead of CNRQ. Corrected

      • Fig 4G: The brightfield image of adult spheroids 5 days after 3x TAM injections doesn't look like a spheroid. It seems to be differentiating. True, the choice was not the best as the spheroids started to darken. When further replated, however, the offspring of these spheroids showing a clear phenotype remain negative 30 days after tamoxifen administration as shown on the figure. We are sorry, but for reasons explained in section 4 below, we cannot redo the experiment to get a better picture.

      • Fig 4: Most mouse model data are missing the number of mice & their respective age used for organoid isolation. We have introduced these data in the legend.

      • *Fig 4A-D, H-G: How was fluorescent signal of organoids quantified? *

      The settings of fluo imaging or time of LacZ staining were the same for organoids and spheroid pictures. This has been added to the material and methods of the figure and an example is shown below for Rosa26Tomato.

      *How many images? * 2 per animal per condition.

      *Were there equal numbers of organoids? *

      No, see number of total elements counted added to the figure

      This all needs to be included in methods/figure legends.

      We have introduced additional pertinent information in the material and methods section.

      • Figure 4B-D, G-H: Which culturing conditions were used for adult spheroids? Original method or sandwich method? These data were obtained with the original protocol

      • Fig 6D-E: Please add the timepoint after DT administration these samples are from. It is not listed in text or figure legend. These samples were those obtained from mice sacrificed at the end of the 5 day period as indicated in panel A. This has been emphasized in the legend of the figure.

      • SuppFig 6D: again timepoint is missing. In this experiment all samples were untreated as indicated. This has been emphasized in the legend of the figure.

      • SuppFig 6: How were the crypts of these mice (DT WT & DT HE) isolated? Was this via EDTA? This was RNA extracted from total uncultured EDTA-released material (crypts). This has been emphasized in the legend of the figure.

      Also, what is the timepoint for isolation for these samples? Even if untreated, the timepoint adds context to the data. Please add more context to describing these different experiments, either in the figure legends or methods section.

      All these experiments were from 2 month old animals. We have indicated this in the legend of the figure.

      • SuppFig 6E: The quality of the heatmap resolution is too poor to read gene names. We have improved the resolution of the figure and hope the name of the genes are readable now.

      • 5-7, are the regenerating crypt-villus units fully differentiated or are they maintained in the developmental state? Immunostaining of markers for stem cells (Lgr5), differentiated lineages (Alpi, Muc2, Lyz, ChgA etc.) and fetal state (Sca1, Trop2 etc) should be analysed in those "white" unrecombined crypt-villus units. The differentiation phenotype is shown by the clear presence of morphologically-identified Paneth and Goblet cells. We agree that specific immunostainings could have been performed to further explore this point. Regarding the fetal state, Clu expression was shown during the regeneration period (see figure 7D,E).

      Unfortunately, for reasons explained in section 4 below, we are not in a position to perform these additional experiments.

      • The following text needs clarification: "The kinetics of appearance of newly formed un-recombined ("white") crypts was studied after a single pulse of DT (Fig.7A). This demonstrated an increase at 48 hours, with further increase at day 10 and stable maintenance at day 30. The presence of newly formed white crypts one month after toxin administration indicates that the VilCre-negative lineage is developmentally stable and does not turn on the transgene during differentiation of the various epithelial lineages occurring after regeneration (Fig.7B).

      *Comment: The "newly formed" is an overstatement, the data doesn't conclude that those are "new" crypts. *

      Except if we do not understand the point, we think we can write that a fraction of "white" crypts must be "newly formed", since they are in excess of those present in untreated animals at the same time point.

      *The end of the sentence states that these "white" crypts form developmentally stable lineages, thus these white crypts at day 30 could originate from the initial injury. *

      As stated above, we consider that crypts found in excess of those present in untreated animals result from the initial injury.

      *There was no characterisation of the various epitheial lineages. Are they fully differentiated? *

      See above the point related to Paneth cells and Goblet cells.

      Is Lgr5 expressed one month after toxin administration? Can the VilCre neg lineage give rise to CBCs?

      We have tried hard to show presence or absence of Lgr5 in white crypts at the various times following DT administration. We tried double RFP / Lgr5-RNA scope labeling and double GFP/RFP immunolabeling. Unfortunately, we could not get these methods to produce convincing specific labeling of CBCs in homeostatic crypts, which explains why we could not reach a conclusion regarding the white crypts.

      However, there is an indirect indication that "chronic" white crypts (i.e. those caused by DTR expression in CBC, plus those observed 30 days after DT administration) do not express Lgr5. Indeed, acute regeneration indicated by Clu expression at day 5 in Fig.7C is lower in white crypts than in red ones strongly suggesting that white crypts preexisting DT administration (the "chronic ones) do not express Lgr5DTR.

      The relationship between white crypt generation and appearance of Clu-positive revival cells (Ayyaz et al., 2019) was then explored. In agreement with others and similar to what happens in the irradiation model, (Ayyaz et al., 2019; Yuan et al., 2023) Clu-positive cells were rare in crypts of untreated mice and their number transiently increased forty-eight hours after a single pulse of DT, and more so after three pulses of DT (Fig.7C,D).

      Comment: Comparing 1 pulse at day 2 vs 3 pulses at day 5 makes the data hard to interpret. How is the Clu ISH level for 1 pulse at day 5? Are they equivalent?

      After a single pulse of of DT, Clu is only transiently increased. As shown by Ayyaz et al it is back to the starting point at day 5 (supplementary figure 4 of Ayyaz et al).

      Clu-positive cells were less frequently observed in white crypts (see "Total" versus "White" in Fig.7C). This fits with the hypothesis that Clu expression marks acutely regenerating crypts and that a proportion of the white crypts are chronically regenerating due to DTR expression in CBCs."

      *Comment: I believe the authors suggested that the discrepancy of less Clu expression in white crypts is due to the ectopic expression of DTR in CBCs causing low grade injury without DT administration. This means that some white crypts could have been formed before the administration of DT, and thus are on a different regenerative timeline compared to the white crypts formed from DT administration. *

      Yes, this is our interpretation. We have clarified it in the text.

      Is there any proof of the chronic regeneration? Immunostaining of chronic regenerative markers such as Sca1, Anxa1 or Yap1 nuclear localization would support the claim. It'd be important to show only the white crypts, but not the RFP+ ones, show regenerative markers.

      We think that the steady state higher number of white crypts in untreated Lgr5-DTR animals, compared to wild type siblings indicates chronical low-grade regeneration, which is supported by the RNAseq data (Suppl fig6). It must be noted, however, that this phenotype is mild compared to the well described fetal-like regeneration phenotype described in most injury models. Since these white crypts were made at undetermined earlier stages, the great majority of them are not expected to show markers of acute regeneration like Clu, Sca1....

      Fig 7D-E: What are the timepoints of harvest for HE-WT-HE 1 pulse DT mice and HE- HE-HE PBS injected mice?

      We have added this information in the figure.

      • *Fig 8-9: Regarding the CBC-like Olfm4 low population, what is the status of Lgr5? This should be shown in the figure since the argument is that this is an Lgr5-independent lineage. * See response to the second point.

      And what about the regenerative, Yap, mesenchymal and inflammatory signatures? Are they enriched in the white crypts similar to the in vitro spheroids?

      In a portion of white crypts, those we believe are newly formed after CBC ablation (see above), there is a transient increase in Clu, which may be considered a marker of Yap activation. In the CBC-like Olfm4 low cells, as seen by scRNAseq, there is nothing like an actively regenerating phenotype. This is expected, since these cells are coming from homeostatic untreated VilCre/Rosa26Tom animals and are supposed to be quiescent "awaiting to be activated".

      Reviewer #1 (Significance (Required)):

      Strengths: The study employed a range of in vitro and in vivo models to test the hypothesis.

      • *

      *Limitations: Unfortunately, the models chosen did not provide sufficient evidence to draw the conclusions. Injury induced reprogramming, both in vivo and in vitro, has been well documented in the field. The new message here is to show that such reprogrammed state is continuous rather than transient; instead of regenerating Lgr5+ stem cells, it can continue to differentiate to all cell lineages in Lgr5-independent manner.

      *

      We respectfully disagree with this analysis of our results. What we show is not "that such reprogrammed state is continuous rather than transient; instead of regenerating Lgr5+ stem cells, it can continue to differentiate to all cell lineages in Lgr5-independent manner", but that a quiescent stem cell line, not previously identified, is activated to regenerate a portion of crypts following CBC ablation. These cells are not reprogrammed, they correspond to a developmental lineage waiting to be activated and keep their VilCre-negative state at least of 30 days. We believe that their "by default tracing" (VilCre negative from the zygote stage) is as strong an evidence for the existence of such a lineage as positive lineage tracing would be. The increase in crypts originating from this lineage after CBC ablation indicates that it is implicated in regeneration. We do not question the well-demonstrated plasticity-associated reprogramming taking place during regeneration; we simply suggest that this would coexist with the involvement of the quiescent VilCre-negative lineage we have identified.

      *However, through the manuscript, there was no immunostaining of Lgr5 and other differentiation markers. The conclusion is an overstatement without solid proof. * We have provided the best answer we could to this point in our answer to the second question of the referee hereabove.

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

      In this manuscript, the Marefati et al. developed a novel approach to generate spheroids from adult intestinal epithelium using a collagenase/dispase based protocol. Adult spheroids were found to be distinct from classic budding-type organoids normally generated from EDTA based release of the crypt epithelium. Transcriptional profiling indicated that adult spheroids were undifferentiated and similar to regenerating crypts or fetal spheroids. To identify the cell of origin that generates adult spheroids, the authors labelled epithelial cells with VilCreERT-LSL-Tom, VilCre-LSL-GFP and Lgr5CreERT- LSLTom mice. From these experiments the authors conclude that that spheroids are only generated from Vil-Cre negative and Lgr5 negative cells. Next the authors deleted the anti- apoptotic gene Mcl1 using Vil-CreERT mice. This led to a strong apoptotic response throughout the crypt epithelium and tissues processed from knockout mice readily generated spheroids, and in vivo, replenishment of the gut epithelium was mediated by unrecombined cells. In a second model, CBCs were ablated using Lgr5DTR mice and VilCre negative cells were found again to contribute to regeneration of the crypt epithelium. Finally based on the absence of Vil-Cre reporter activity, the authors were able to sort out and perform scRNAseq to profile VilCre negative cells. These cells were found to be quiescent, express the stem cell marker Olfm4 and were also abundant in ribosomal gene expression.

      • *

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

      • *

      As pointed out by the authors themselves the study has important limitations that diminish enthusiasm. The primary issue relates to the inability of the team to identify markers of VilCre neg cells other than the fact that these cells are Olfm4+ and quiescent. Nonetheless, for the reasons stated above the manuscript should reach the target audience within the research community, if the authors can address the specific points below related to issues with methodology as well as defining more precisely the characteristics and growth requirements of adult spheroid cultures.

      Thank you for this positive analysis of our study.

      Major comments

      The main conclusion of the study is that Vil-Cre neg cells are rare quiescent Olfm4+ crypt cells. If this is the case, then standard EDTA treatment should release these cells as well. Consequently, spheroids should also emerge from isolated crypts grown in the absence of ENR. If this is not the case how do the authors explain this?

      We have tried hard to generate spheroids by culturing EDTA organoids in medium lacking ENR and by treating EDTA organoids with collagenase/dispase, without success. Therefore, we are left with the conclusion that spheroid-generating cells must be more tightly attached to the matrix than those released by EDTA, and that it is their release from this attachment by collagenase that triggers a regeneration-like phenotype. This hypothesis is supported by several models of regeneration in other tissues as indicated in our references (Gilbert et al., 2010; Machado et al., 2021; Montarras et al., 2005).

      From the text the authors appear to suggest that growth of adult spheroids is dependent initially on "material" released by collagenase/dispase treatment. An obvious candidate would be mesenchymal cells, which are known to secrete factors such as Wnts and PGE2 that drive spheroid morphology. To test this, the authors should treat spheroid cultures with Porcupine and/or PGE2 inhibitors.

      We followed similar reasoning, considering that spheroids express strongly Ptgs1 ,2 (Figure 3A). We thought their phenotype might be maintained by autocrine prostaglandin action. We tested aspirin, a Ptgs inhibitor, which was without effect on the spheroid phenotype. Besides, we explored a wide variety of conditions to test whether they would affect the spheroid phenotype [Aspirin-see above, cAMP agonists/antagonists, YapTaz inhibitors (verteporfin and CA3), valproic acid, Notch inhibitors (DAPT, DBZ, LY511455), all-trans retinoic acid, NFkB inhibitors (TCPA, BMS), TGFbeta inhibitor (SB431542)]. As these results were negative, we did not include them in the manuscript.

      • If these inhibitors block growth then this would suggest that either stromal cells or autocrine signalling involving these pathways is important. Overall, more in-depth analysis of the growth requirements of adult spheroids is required.*

      Figure 1d indicates that adult spheroids can be propagated for at least 10 passages. The abstract mentions they are "immortal". The text itself does not address this issue. More precise information as to how long spheroids can be propagated is required. If these cultures can be propagated for 10 passages or more it becomes important to determine what nutrients/mitogens in the basal media are driving growth? Alternatively, what is the evidence that spheroid cultures are completely devoid of mesenchymal cells. The text only mentions that "Upon replating, these spheroids could be stably cultured free of mesenchymal cells (Fig.1B)". No validation is shown to support this.

      We agree that "immortal" is not a good way to characterize our spheroids, as also pointed out by referee nr 1. We have changed that in the text, indicating the maximal number of replating we tested was 26 and replacing immortal by stably replatable. Of note, the spheroids could frozen/thawed and recultured many times.

      Related to the question whether mesenchymal cells could still contaminate the spheroid cultures, we can provide the following answers:

      • No fibroblasts could be seen in replated cultures and multiple spheroids could be repeatedly propagated from a single starting spheroid.
      • The bulk RNAseq experiment comparing organoids to ENR or BCM cultured spheroids show, despite expression of several mesenchymal markers (see matrisome in Fig3), absence of significant expression of Pdgfra (see in revision plan folder for CP20Millions results from the raw data of new suppl table 2, with Clu, Tacstd2 and Alpi shown as controls).
      • Regarding the nutrients/mitogens in the medium driving spheroid growth, we did not explore the point further than showing that they grow in basal medium (i.e. advanced DMEM), given that the presence of Matrigel makes it difficult to pinpoint what is really needed. In Figure 2, the authors describe the growth requirements for adult spheroids and indicate that spheroids grown in ENR or EN became dark and shrink. The representative images showing this are clear, but this analysis should be quantified.

      Added to the manuscript.

      In SF3, the gene expression profile of organoids from the sandwich method only partially overlaps with that of organoids from the old protocol. What are the gene expression differences between the 2 culture systems? Secondly, the sandwich method appears to sustain growth of Tom+ spheroids based on RNAseq and the IF images. This suggest that Vil-Cre negative cells are not necessarily the only source of adult spheroids and thus this experiment seems to indicate that any cell may be converted to grow as a spheroid under the right conditions. These points should be addressed.

      Looking back to our data in order to answer the point raised by the referee, we realized that we had inadvertently-compared organoids to ENR-cultured spheroids generated by the first protocol to BCM-cultured spheroids generated by the sandwich method. We have corrected this error in a new version of suppl fig3. This shows increased correspondence between genes up- or downregulated in the spheroids obtained in the two protocols (from 49/48% to 57/57% (Venn diagram on the new figure). We agree that, even after this correction, the spheroids obtained with the two protocols present sizeable differences in their transcriptome. However, considering the very different way these spheroids were obtained and cultured initially, we do not believe this to be unexpected. The important point in our opinion is that the core of the up- and down-regulated genes typical of the de-differentiation phenotype of adult spheroids is very similar, as shown in the heatmap (which was made with the correct samples!). Also, a key observation is that that both kind of spheroids survive and can be replated in basal medium. As already stated, this characteristic is only seen rare cases [spheroids obtained from rare FACS-purified cells (Smith et al 2018) or helminth-infected intestinal tissue (Nusse et al.2018)]. Together with the observation that the majority of them is not traced by VilCre constitutes what we consider the halmark of the spheroids described in our study. As shown in figure 4E (old protocol) and Suppl Fig.3 (sandwich protocol) both red and white spheroids were extremely low in VilCre expression. As stated in the text, the fact that some spheroids are nevertheless red is most probably related to the extreme sensitivity of the Rosa26Tom marker to recombination (Liu et al., 2013), but this does not mean that there are two phenotypically different kind of spheroids. It means that the arbitrary threshold of Rosa26Tom recombination introduces an artificial subdivision of spheroids with no phenotypical significance.

      Regarding the point made by the referee that "that any cell may be converted to grow as a spheroid under the right conditions", we agree and have shown with others that organoids acquire indeed a spheroid phenotype when cultured for instance in fibroblasts-conditioned medium (see suppl fig1B and (Lahar et al., 2011; Roulis et al., 2020) quoted in the manuscript). However, these spheroids cannot be propagated in basal medium, and revert to an organoid phenotype when put back in ENR (Suppl fig1B).

      *In Figure 4, the authors conclude that spheroids do not originate from Lgr5 cell derived clones even after 30days post Tam induction. Does this suggest that in vivo and under homeostatic conditions VilCre neg cells are derived from a distinct stem cell pool or are themselves a quiescent stem cell. Given the rarity of VilCre neg cells, the latter seems unlikely.

      *

      Despite their rarity, we believe VilCre-negative cells observed under homeostatic conditions are themselves quiescent stem cells. Actually, if they were derived from a larger stem cell pool, this pool should also be VilCre-negative. And we do not see such larger number of VilCre-neg cells under homeostatic conditions.

      The problem with the original assertion is that Lgr5-CreERT mice are mosaic and therefore not all Lgr5+ cells are labelled in this model. "White" spheroids may thus derive from cells that in turn derive from these unlabelled Lgr5 cells.

      We had considered the possibility that mosaicism [very low for VilCre (Madison et al., 2002); in the 40-50% range for Lgr5CreERT2 (Barker & Clevers. Curr Protoc Stem Cell Biol. 2010 Chapter 5)] could explain our data. We think, however that we can exclude this possibility on the basis that spheroids do not conform to the expected ratio of unrecombined cells, given the observed level of mosaicism. Indeed, for VilCre, a few percent, at most, of unrecombined cells in the epithelium translates into almost 100% unrecombined spheroids. For Lgr5CreERT2 mice, the mosaicism level is in the range of 40%, which is what we observe for EDTA organoids (Figure 4G), while spheroids were in their vast majority unrecombined.

      We have included a discussion about the possible role of mosaicism in the new version.

      ATACseq experiments were briefly mentioned in the manuscript but unfortunately little information was extracted from this experiment. What does this experiment reveal about the chromatin landscape of adult spheroids relative to normal organoids?

      We only performed this experiment to search for an explanation to the paradoxical absence of expression of the VilCre transgene in spheroids, despite robust expression of endogenous villin (Suppl Fig.4). We chose to show the chromatin landscape of a gene equally expressed in both organoids and spheroids (Krt19), a gene specifically expressed in spheroids (Tacstd2) and the endogenous Villin gene also expressed in both. We believe that the observation of a clear difference in pattern of the chromatin accessibility around the endogenous villin gene in organoids and spheroids provides an explanation to the observed results. The cis regulatory sequences needed for expression of the endogenous villin gene seem to be different in organoids and spheroids, which may explain why the regulatory sequences present in the transgene (only 12.4kb) might not allow expression of the transgene in spheroids. We have added a sentence in the manuscript clarifying this point. Missing is obviously the chromatin landscape around the VilCre transgene, but this is beyond reach in such kind of experiments.

      Reviewer #2 (Significance (Required)):

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

      Reviewer #3 (Evidence, reproducibility and clarity (Required)): CR-2024-02491

      An Lgr5-independent developmental lineage is involved in mouse intestinal regeneration

      Marefati et al.

      Homeostatic maintenance of the intestinal epithelium has long been thought to rely upon Wnt signaling responsive Lgr5-expressing stem cells that reside at the crypt base.

      However, myriad reported mechanisms or populations have been reported to underlie epithelial regeneration after injury. Many groups have reported that reacquisition of a fetal- link intestinal phenotype is an import part of the regenerative response, however the originating cell type has not been definitively identified. Herein, the authors demonstrate that cells from adult homeostatic intestine can generate immortal spheroids that resemble fetal spheroids and are derived independent of Lgr5+ intestinal stem cells (ISCs). The authors then draw the conclusion that this indicates that a hierarchical stem cell model applies to regeneration of the intestinal epithelium, in addition to the plasticity model.

      • *

      Comments:

      1. Please indicate what species is used for studies in Fig 1.

      All experiments were performed in Mus musculus.

      Please clarify if Figure 2 studies utilize Matrigel or not.

      Yes

      RNA-seq analyses of adult intestinal generated spheroids lack the granularity of single cell analyses and thus it is unclear if this is a homogeneous population or if the population has diversity across it (i.e., enteroids/organoids have a high level of diversity). Many of the conclusions from the RNA-seq study are broad and generalized-for example Fig 3F indicates that markers of the +4 ISC populations (Bmi1, tert, lrig1, hopx) were all expressed similarly in adult spheroids as compared to adult organoids. However, while this may be true in the bulk-RNA-seq analyses, clearly scRNA-seq would provide a better foundation to make this statement, as enteroids/organoids are comprised of heterogeneous subpopulations. . .and it might indicate that these +4 markers have only very low expression in the spheroids. Based upon these concerns, misconclusions are likely to be drawn.

      We agree and it would be certainly worthwhile to perform scRNAseq of adult spheroid populations. This would certainly be worth doing in future studies to explore the possible heterogeneity of adult spheroids. We nevertheless believe that our scRNAseq performed on homeostatic intestinal tissue from VilCre/Rosa26Tom mice identify Olfm4-low VilCre-neg cells that are likely at the origin of adult spheroids and display a quite homogenous phenotype.

      *The language around Figure 4 results is confusing. Please define "white" and "red". It might be simpler to designate recombined versus not recombined lineage.

      *

      We have clarified this in the figure.

      The hypothesis that collagenase/dispase solution acts as a proxy for injury is not demonstrated and backed by data. Thus, it is difficult to make the conclusion that this approach could represent a "stable avatar" of intestinal regenerating cells. It is clear that subpopulations of crypt-based cells generate spheroids in culture without collagenase/dispase (see the cited reference Smith et al, 2018).

      * *Smith et al demonstrate clearly the possibility to obtain spheroids with properties probably similar to ours from EDTA derived intestinal crypt cells. However they need to prepurify them by FACS. Besides, Nusse et al describe spheroids similar to ours after infection of the intestine by helminths (Nusse et al. 2018). In our case, and for most labs preparing enteroids with the EDTA protocol, the result is close to 100% organoids. Even if we treat EDTA organoids with collagenase, we do not obtain spheroids. This brought us to the conclusion that spheroid-generating cells must be more tightly attached to the matrix than CBCs and that it is their release from the matrix that activates the spheroid regeneration-like phenotype. This hypothesis is supported by several models of regeneration in other tissues as indicated in our references (Gilbert et al., 2010; Machado et al., 2021; Montarras et al., 2005)

      A study based on the absence of recombination in a VilCre lineage tracing scenario is not well-established to be strong experimental approach, as there are many reasons why recombination may not cells may not be lineage marked. In order to use this system as the authors intend, they first need to demonstrate that villin is not expressed in the discrete cell population that they are targeting. For the presented observational studies, this would be difficult to do. While they do demonstrate differences in chromatin accessibility between cells from organoids versus spheroids (fig s4), some of these differences could merely be due to the bulk analytical nature of the study and the lack of comparing stem cell populations from spheroids to stem cell populations from organoids-since the spheroids are likely homogenous versus the organoids that only have a small fraction of stem cells-and thus represent a mix of stem cell and differentiated cell populations. The authors do not demonstrate that villin protein expression varies in these cells.

      If it were found that villin is not expressed in their "novel" population, then one would expect that the downstream use of villin-based recombination would demonstrate the same recombination potential (i.e., Mcl1 would not be recombined). Both recombination studies in Fig 6 are difficult to interpret, and thus it is not clear if these studies support the stated conclusions. Quantification of number of crypts that are negative should be reported as a percentage of recombined crypts.

      We are sorry but there seems to be a complete misunderstanding of our data regarding the point raised by the referee. The important point of our initial observation is that despite robust expression of villin in spheroids, the VilCre transgene is not expressed (see figure 4E). This in our opinion makes absence of VilCre expression (or of Rosa marker recombination) a trustful marker of a new developmental lineage. All the data in figure 4 constitute an answer.

      *The reasoning about heterogeneity of cell type in organoids versus probable homogeneity of spheroids is well taken. However, as the endogenous villin gene is expressed in all cells of both organoids and spheroids, it is highly significant that only spheroids do not express the transgene. *

      We performed the ATACseq experiment to search for an explanation to the paradoxical absence of expression of the VilCre transgene in spheroids, despite robust expression of endogenous villin (Suppl Fig.4). We chose to show the chromatin landscape of a gene equally expressed in both organoids and spheroids (Krt19), a gene specifically expressed in spheroids (Tacstd2) and the endogenous Villin gene also expressed in both. We believe that the observation of a clear difference in pattern of the chromatin accessibility around the endogenous villin gene in organoids and spheroids provides an explanation to the observed results. The cis regulatory sequences needed for expression of the endogenous villin gene seem to be different in organoids and spheroids, which may explain why the regulatory sequences present in the transgene (only 12.4kb) might not allow expression of the transgene in spheroids. We have added a sentence in the manuscript clarifying this point. Missing is obviously the chromatin landscape around the VilCre transgene, but this is beyond reach in such kind of experiments.

      *Figure 8 indicates that the cell population identified by scRNA-seq may be quiescent. Companion IF or IHC should be conducted to confirm this finding, as well as other conclusions from the informatics conducted.

      *

      We agree that additional experiments could be performed to support this point. We are unfortunately not in a position to perform these experiments (see section 4 below).

      Clearly the data is intriguing, however, the conclusion is strong and is an over interpretation of the presented data. There are a number of validation or extension data that would enhance the overall interpretation of the study: 1. validation of scRNA-seq or bulk RNA-seq concepts by protein staining of intestinal tissues in the damage model will serve as a secondary observation. 2. identification of the ISC that they are defining is critical and important. There is already the notion that this cell type exists and it has been shown with various different markers. 3. expand the analyses of the fetal-like expression profiling to injured intestines to demonstrate that the lineage negative cells indeed express fetal-like proteins. 4. expand the discussion of the Clu+ cell type. Is this cell the previously described revival cell? If so, how does this body of work provide unique aspects to the field?

      We agree that all these suggested experiments could be performed and would be of interest. However, we consider that they would not modify the main message of our study and would only constitute an expansion of the present work. As already stated, we are not in the position to perform them (see section 4).

      *There is some level of conflicting data, with the stem population being proliferative in culture stimulated by the stromal cells, but quiescent in vivo and also based upon scRNA- seq data in Fig 9.

      *

      We do not see any conflict in our observation regarding this point. The observation that cells that are quiescent in vivo become proliferative when subjected to culture (with or without addition of stromal cells) is routinely made in a multitude of cell culture systems. In particular, it has been shown that intestinal tissue dissociation activates the Yap/Taz pathway, resulting in proliferation (Yu et al. Hippo Pathway Regulation of Gastrointestinal Tissues. Annual Review of Physiology, 2015 Volume 77, 201-227).

      Many of the findings have been previously reported: Population that grows as spheroids (Figure 2), Population that is Wnt independent (Figure 2), Lgr5 independent regenerative growth of the intestine (figure 3F, Figure 4), Clu+ ISCs drive regeneration (Figure 7).

      Whereas these individual findings have indeed been reported, it was in a different context. We strongly disagree with the underlying suggestion that our study would not bring new information. We have identified here a developmental lineage involved in intestinal regeneration that has not been described up to now.

      Minor comments:

        • The statement that spheroids must originate from collagenase/dispase digested material might be an overstatement. As spheroids generation from EDTA treated intestines have been previously reported (Smith et al, 2018). * See answer to point 4 above. *Overall while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

      *

      Reviewer #3 (Significance (Required)):

      Overal while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

      We can only disagree.

      4. Description of analyses that authors prefer not to carry out

      • *

      We have answered most questions raised by the referees by explaining our view, by clarifying individual points and, in several cases, by providing additional information that was not included in the original manuscript.

      In a limited number of cases when additional experiments were suggested, we were unfortunately obliged to write that we are not in a position to perform them. This is because my lab is closing after more than fifty years of uninterrupted activity. There will unfortunately be nobody to perform additional experiments.

      Nevertheless, as written by referees 1 and 2, we believe that the revised manuscript, as it stands, contains data that will be of interest to the people in the field and may be the bases for future developments. We hope editors will find interest in publishing it.

    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

      RC-2024-02491

      An Lgr5-independent developmental lineage is involved in mouse intestinal regeneration Marefati et al.

      Homeostatic maintenance of the intestinal epithelium has long been thought to rely upon Wnt signaling responsive Lgr5-expressing stem cells that reside at the crypt base. However, myriad reported mechanisms or populations have been reported to underlie epithelial regeneration after injury. Many groups have reported that reacquisition of a fetal-link intestinal phenotype is an import part of the regenerative response, however the originating cell type has not been definitively identified. Herein, the authors demonstrate that cells from adult homeostatic intestine can generate immortal spheroids that resemble fetal spheroids and are derived independent of Lgr5+ intestinal stem cells (ISCs). The authors then draw the conclusion that this indicates that a hierarchical stem cell model applies to regeneration of the intestinal epithelium, in addition to the plasticity model.

      Comments:

      1. Please indicate what species is used for studies in Fig 1.
      2. Please clarify if Figure 2 studies utilize Matrigel or not.
      3. RNA-seq analyses of adult intestinal generated spheroids lack the granularity of single cell analyses and thus it is unclear if this is a homogeneous population or if the population has diversity across it (i.e., enteroids/organoids have a high level of diversity). Many of the conclusions from the RNA-seq study are broad and generalized-for example Fig 3F indicates that markers of the +4 ISC populations (Bmi1, tert, lrig1, hopx) were all expressed similarly in adult spheroids as compared to adult organoids. However, while this may be true in the bulk-RNA-seq analyses, clearly scRNA-seq would provide a better foundation to make this statement, as enteroids/organoids are comprised of heterogeneous subpopulations. . .and it might indicate that these +4 markers have only very low expression in the spheroids. Based upon these concerns, misconclusions are likely to be drawn.
      4. The language around Figure 4 results is confusing. Please define "white" and "red". It might be simpler to designate recombined versus not recombined lineage.
      5. The hypothesis that collagenase/dispase solution acts as a proxy for injury is not demonstrated and backed by data. Thus, it is difficult to make the conclusion that this approach could represent a "stable avatar" of intestinal regenerating cells. It is clear that subpopulations of crypt-based cells generate spheroids in culture without collagenase/dispase (see the cited reference Smith et al, 2018).
      6. A study based on the absence of recombination in a VilCre lineage tracing scenario is not well-established to be strong experimental approach, as there are many reasons why recombination may not cells may not be lineage marked. In order to use this system as the authors intend, they first need to demonstrate that villin is not expressed in the discrete cell population that they are targeting. For the presented observational studies, this would be difficult to do. While they do demonstrate differences in chromatin accessibility between cells from organoids versus spheroids (fig s4), some of these differences could merely be due to the bulk analytical nature of the study and the lack of comparing stem cell populations from spheroids to stem cell populations from organoids-since the spheroids are likely homogenous versus the organoids that only have a small fraction of stem cells-and thus represent a mix of stem cell and differentiated cell populations. The authors do not demonstrate that villin protein expression varies in these cells. If it were found that villin is not expressed in their "novel" population, then one would expect that the downstream use of villin-based recombination would demonstrate the same recombination potential (i.e., Mcl1 would not be recombined). Both recombination studies in Fig 6 are difficult to interpret, and thus it is not clear if these studies support the stated conclusions. Quantification of number of crypts that are negative should be reported as a percentage of recombined crypts.
      7. Figure 8 indicates that the cell population identified by scRNA-seq may be quiescent. Companion IF or IHC should be conducted to confirm this finding, as well as other conclusions from the informatics conducted.
      8. Clearly the data is intriguing, however, the conclusion is strong and is an over interpretation of the presented data. There are a number of validation or extension data that would enhance the overall interpretation of the study:
        • a. validation of scRNA-seq or bulk RNA-seq concepts by protein staining of intestinal tissues in the damage model will serve as a secondary observation.
        • b. identification of the ISC that they are defining is critical and important. There is already the notion that this cell type exists and it has been shown with various different markers.
        • c. expand the analyses of the fetal-like expression profiling to injured intestines to demonstrate that the lineage negative cells indeed express fetal-like proteins.
        • d. expand the discussion of the Clu+ cell type. Is this cell the previously described revival cell? If so, how does this body of work provide unique aspects to the field?
      9. There is some level of conflicting data, with the stem population being proliferative in culture stimulated by the stromal cells, but quiescent in vivo and also based upon scRNA-seq data in Fig 9.
      10. Many of the findings have been previously reported: Population that grows as spheroids (Figure 2), Population that is Wnt independent (Figure 2), Lgr5 independent regenerative growth of the intestine (figure 3F, Figure 4), Clu+ ISCs drive regeneration (Figure 7).

      Minor comments:

      1. The statement that spheroids must originate from collagenase/dispase digested material might be an overstatement. As spheroids generation from EDTA treated intestines have been previously reported (Smith et al, 2018).

      Overall while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

      Significance

      Overall while the study includes an extensive amount of work and different approaches, a foundationally supported novel finding is missing. Many of the statements have already been demonstrated by others in the fields. In addition, one of the most intriguing aspects of the study is that the stromal population impacts this stem cell population, however, interactions and factors stimulating the crosstalk are not addressed.

    3. 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 Marefati et al. developed a novel approach to generate spheroids from adult intestinal epithelium using a collagenase/dispase based protocol. Adult spheroids were found to be distinct from classic budding-type organoids normally generated from EDTA based release of the crypt epithelium. Transcriptional profiling indicated that adult spheroids were undifferentiated and similar to regenerating crypts or fetal spheroids. To identify the cell of origin that generates adult spheroids, the authors labelled epithelial cells with VilCreERT-LSL-Tom, VilCre-LSL-GFP and Lgr5CreERT-LSLTom mice. From these experiments the authors conclude that that spheroids are only generated from Vil-Cre negative and Lgr5 negative cells. Next the authors deleted the anti-apoptotic gene Mcl1 using Vil-CreERT mice. This led to a strong apoptotic response throughout the crypt epithelium and tissues processed from knockout mice readily generated spheroids, and in vivo, replenishment of the gut epithelium was mediated by unrecombined cells. In a second model, CBCs were ablated using Lgr5DTR mice and VilCre negative cells were found again to contribute to regeneration of the crypt epithelium. Finally based on the absence of Vil-Cre reporter activity, the authors were able to sort out and perform scRNAseq to profile VilCre negative cells. These cells were found to be quiescent, express the stem cell marker Olfm4 and were also abundant in ribosomal gene expression.

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

      As pointed out by the authors themselves the study has important limitations that diminish enthusiasm. The primary issue relates to the inability of the team to identify markers of VilCre neg cells other than the fact that these cells are Olfm4+ and quiescent. Nonetheless, for the reasons stated above the manuscript should reach the target audience within the research community, if the authors can address the specific points below related to issues with methodology as well as defining more precisely the characteristics and growth requirements of adult spheroid cultures.

      Major comments

      The main conclusion of the study is that Vil-Cre neg cells are rare quiescent Olfm4+ crypt cells. If this is the case, then standard EDTA treatment should release these cells as well. Consequently, spheroids should also emerge from isolated crypts grown in the absence of ENR. If this is not the case how do the authors explain this?

      From the text the authors appear to suggest that growth of adult spheroids is dependent initially on "material" released by collagenase/dispase treatment. An obvious candidate would be mesenchymal cells, which are known to secrete factors such as Wnts and PGE2 that drive spheroid morphology. To test this, the authors should treat spheroid cultures with Porcupine and/or PGE2 inhibitors. If these inhibitors block growth then this would suggest that either stromal cells or autocrine signalling involving these pathways is important. Overall, more in-depth analysis of the growth requirements of adult spheroids is required.

      Figure 1d indicates that adult spheroids can be propagated for at least 10 passages. The abstract mentions they are "immortal". The text itself does not address this issue. More precise information as to how long spheroids can be propagated is required. If these cultures can be propagated for 10 passages or more it becomes important to determine what nutrients/mitogens in the basal media are driving growth? Alternatively, what is the evidence that spheroid cultures are completely devoid of mesenchymal cells. The text only mentions that "Upon replating, these spheroids could be stably cultured free of mesenchymal cells (Fig.1B)". No validation is shown to support this.

      In Figure 2, the authors describe the growth requirements for adult spheroids and indicate that spheroids grown in ENR or EN became dark and shrink. The representative images showing this are clear, but this analysis should be quantified.

      In SF3, the gene expression profile of organoids from the sandwich method only partially overlaps with that of organoids from the old protocol. What are the gene expression differences between the 2 culture systems? Secondly, the sandwich method appears to sustain growth of Tom+ spheroids based on RNAseq and the IF images. This suggest that Vil-Cre negative cells are not necessarily the only source of adult spheroids and thus this experiment seems to indicate that any cell may be converted to grow as a spheroid under the right conditions. These points should be addressed.

      In Figure 4, the authors conclude that spheroids do not originate from Lgr5 cell derived clones even after 30days post Tam induction. Does this suggest that in vivo and under homeostatic conditions VilCre neg cells are derived from a distinct stem cell pool or are themselves a quiescent stem cell. Given the rarity of VilCre neg cells, the latter seems unlikely. The problem with the original assertion is that Lgr5-CreERT mice are mosaic and therefore not all Lgr5+ cells are labelled in this model. "White" spheroids may thus derive from cells that in turn derive from these unlabelled Lgr5 cells.

      ATACseq experiments were briefly mentioned in the manuscript but unfortunately little information was extracted from this experiment. What does this experiment reveal about the chromatin landscape of adult spheroids relative to normal organoids?

      Significance

      The fact that the authors developed a protocol to reproducibly generate fetal-like spheroids from adult tissue is an important advancement in the field. Previous reports have shown that treatment with various small molecule inhibitors can revert budding organoids into a spheroid morphology, but this manuscript demonstrates that spheroids can also be generated from otherwise untreated cells. This new methodology will provide new tools to dissect the molecular determinants of fetal/regenerative cells in the gut. Based on this, the manuscript should attract a significant amount of attention in the intestinal field.

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      Referee #1

      Evidence, reproducibility and clarity

      In this manuscript, Marefati et al report an Lgr5-independent lineage in the regenerating intestine using in vitro organoids and in vivo injury-coupled lineage tracing model. In organoids, collagenase/dispase dissociated resulted in "immortal spheroids" that maintain a cystic and undifferentiated phenotype in the absence of standard growth factors (Rspondin/Noggin/EGF). Bulk RNAseq of spheroids demonstrates downregulation of classical CBC signatures and upregulation of fetal spheroid, mesenchymal, inflammation and regenerative signatures. In mice, Villin-Cre lineage tracing revealed some Villin-negative progenies that lack reporter tracing throughout crypt-villus ribbons after injury. The authors proposed that there is Lgr5-independent population support the regenerative response upon CBC depletion. A major caveat of this study is the identification of this population is based on absence of VilCre expression. It is surprising that there is no characterisation of Lgr5 expression throughout the manuscript whilst claiming of a Lgr5-independent lineage. Although the research question is potentially interesting, the concept of epithelial reprogramming upon injury is well documented in the field. The data generated in this manuscript also seem to be preliminary and lack of detailed characterisation. Below are specific comments.

      • Expression of Lgr5 should be properly characterised throughout the manuscript in both organoid models and injury-induced regeneration in vivo.
      • An important question is the origin of these "Lgr5-independent" adult spheroids. They look and appear like fetal organoids, which could be induced by injury (e.g. upon collagenase/dispase dissociation). Have the authors tried to culture fetal spheroids in BCM over extensive period of time? Do they behave the same? This would be a great way to directly compare the collagenase/dispase-derived organoids with fetal origin.
      • Fig 1C, Why is the replating spheroid culture time different between mesenchymal cells and conditioned medium?
      • It is unclear how the bulk RNA-seq data in Fig. 3 were compared. How long were the adult organoids and spheroids cultured for (how many passages)? Were they culture in the same condition of were they in ENR vs BCM? These are important information to consider when interpreting the results. For instance, are Ptgs1 & Ptgs2 expression in adult spheroids the same in ENR vs BCM? Are the gene signatures (regenerative, fetal and YAP) changed in adult spheroids culturing in ENR vs BCM?
      • It is stated: "In agreement with their aptitude to grow indefinitely, adult spheroids express a set of upregulated genes overlapping significantly with an "adult tissue stem cell module" [159/721 genes; q value 2.11 e-94) (Fig.S2F)].". What is the definition of "indefinitely"? Are they referring to the Fig 1B where spheroid were passaged to P10? The authors should avoid the term "indefinitely" but use a more specific time scale, e.g. passages, months etc.
      • SuppFig 3D: Row Z-Score is missing the "e" in Score.
      • Fig 4E: Figure legend says QNRQ instead of CNRQ.
      • Fig 4G: The brightfield image of adult spheroids 5 days after 3x TAM injections doesn't look like a spheroid. It seems to be differentiating.
      • Fig 4: Most mouse model data are missing the number of mice & their respective age used for organoid isolation.
      • Fig 4A-D, H-G: How was fluorescent signal of organoids quantified? How many images? Were there equal numbers of organoids? This all needs to be included in methods/figure legends.
      • Figure 4B-D, G-H: Which culturing conditions were used for adult spheroids? Original method or sandwich method?
      • Fig 6D-E: Please add the timepoint after DT administration these samples are from. It is not listed in text or figure legend.
      • SuppFig 6D: again timepoint is missing.
      • SuppFig 6: How were the crypts of these mice (DT WT & DT HE) isolated? Was this via EDTA? Also, what is the timepoint for isolation for these samples? Even if untreated, the timepoint adds context to the data. Please add more context to describing these different experiments, either in the figure legends or methods section.
      • SuppFig 6E: The quality of the heatmap resolution is too poor to read gene names.
      • Fig.5-7, are the regenerating crypt-villus units fully differentiated or are they maintained in the developmental state? Immunostaining of markers for stem cells (Lgr5), differentiated lineages (Alpi, Muc2, Lyz, ChgA etc.) and fetal state (Sca1, Trop2 etc) should be analysed in those "white" unrecombined crypt-villus units.
      • The following text needs clarification:

      "The kinetics of appearance of newly formed un-recombined ("white") crypts was studied after a single pulse of DT (Fig.7A). This demonstrated an increase at 48 hours, with further increase at day 10 and stable maintenance at day 30. The presence of newly formed white crypts one month after toxin administration indicates that the VilCre-negative lineage is developmentally stable and does not turn on the transgene during differentiation of the various epithelial lineages occurring after regeneration (Fig.7B). Comment: The "newly formed" is an overstatement, the data doesn't conclude that those are "new" crypts. The end of the sentence states that these "white" crypts form developmentally stable lineages, thus these white crypts at day 30 could originate from the initial injury. There was no characterisation of the various epitheial lineages. Are they fully differentiated? Is Lgr5 expressed one month after toxin administration? Can the VilCre neg lineage give rise to CBCs?

      The relationship between white crypt generation and appearance of Clu-positive revival cells (Ayyaz et al., 2019) was then explored. In agreement with others and similar to what happens in the irradiation model, (Ayyaz et al., 2019; Yuan et al., 2023) Clu-positive cells were rare in crypts of untreated mice and their number transiently increased forty-eight hours after a single pulse of DT, and more so after three pulses of DT (Fig.7C,D). Comment: Comparing 1 pulse at day 2 vs 3 pulses at day 5 makes the data hard to interpret. How is the Clu ISH level for 1 pulse at day 5? Are they equivalent?

      Clu-positive cells were less frequently observed in white crypts (see "Total" versus "White" in Fig.7C). This fits with the hypothesis that Clu expression marks acutely regenerating crypts and that a proportion of the white crypts are chronically regenerating due to DTR expression in CBCs." Comment: I believe the authors suggested that the discrepancy of less Clu expression in white crypts is due to the ectopic expression of DTR in CBCs causing low grade injury without DT administration. This means that some white crypts could have been formed before the administration of DT, and thus are on a different regenerative timeline compared to the white crypts formed from DT administration. Is there any proof of the chronic regeneration? Immunostaining of chronic regenerative markers such as Sca1, Anxa1 or Yap1 nuclear localization would support the claim. It'd be important to show only the white crypts, but not the RFP+ ones, show regenerative markers. - Fig 7D-E: What are the timepoints of harvest for HE-WT-HE 1 pulse DT mice and HE-HE-HE PBS injected mice? - Fig 8-9: Regarding the CBC-like Olfm4 low population, what is the status of Lgr5? This should be shown in the figure since the argument is that this is an Lgr5-independent lineage. And what about the regenerative, Yap, mesenchymal and inflammatory signatures? Are they enriched in the white crypts similar to the in vitro spheroids?

      Significance

      Strengths: The study employed a range of in vitro and in vivo models to test the hypothesis.

      Limitations: Unfortunately, the models chosen did not provide sufficient evidence to draw the conclusions. Injury induced reprogramming, both in vivo and in vitro, has been well documented in the field. The new message here is to show that such reprogrammed state is continuous rather than transient; instead of regenerating Lgr5+ stem cells, it can continue to differentiate to all cell lineages in Lgr5-independent manner. However, through the manuscript, there was no immunostaining of Lgr5 and other differentiation markers. The conclusion is an overstatement without solid proof.

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      Reply to the reviewers

      The work would have significant impact in the cilia community, if the conclusion is correct. This reviewer, however, has a concern about the authors concluding the presence/absence of TZ, based on only B9D1 and the H-shaped body among nine doublet microtubules. First, is it really established how the structure of Xenopus embryo TZ is? While Chlamydomonas is well known to have a H-shaped TZ, other species have different form inside the 9+0 doublet, or no feature (Comparison of TZ from various species in Dennis Diener https://doi.org/10.1016/B978-0-12-822508-0.00007-1). Fig.2B of this manuscript shows visible densities in the panel "Pre", but it does not look like an H-shape. The tomogram of TZ before deciliation seems clearer (but judging from wavy MTs and membrane in this tomogram, there could be unevenness of embedding and staining), while the tomogram after deciliation is thin and does not cover the entire width. Therefore it is not sure that absence of TZ can be concluded. If the author claims Xenopus embryo cilia have a H-shaped TZ, they have to provide multiple micrographs (ideally tomogram or serial section TEM to cover the entire TZ structure) and/or past literature on Xenopus embryo TZ. B9D1 is likely a membrane associated protein (according to their deciliation by detergent and mechanical force). This may mean B9D1 is located on or near the membrane, in vicinity to TZ, and thus binds to TZ after the main part of TZ is built. In this case, it is risky to judge presence of TZ based on B9D1. Also in this point, TEM imaging will be helpful to confirm the authors' conclusion.

      RESPONSE: We appreciate the reviewer’s thoughtful comments on the loss of TZ upon deciliation and its absence during the initial regeneration period. The reviewer is right in their assessment that the TZ of Xenopus cilia has not been well defined before in any manuscript. We want the reviewer to consider that our goal was not to define the TZ in Xenopus but to study deciliation and how cilia regenerate in a vertebrate model system for the first time. We unexpectedly discovered that cilia are deciliated distal to the basal body at the plasma membrane, and the “H-shaped structure,” similar to TZ, was also removed and did not come back for first hour during regeneration. Given this surprising observation, we felt obliged to study and explain our results. To that end, we explored different resources (antibodies and markers of TZ) and different methods over 6 years trying to define TZ in Xenopus.

      Our conclusion about the TZ structure came from multiple lines of evidence from our experiments and published literature, including the similarity in structure compared to other organisms and its physical location in the cilium. Specifically, 1) In a review of the basal bodies, Mitchell indirectly suggested that the electron-dense “H-shaped” structure could be a TZ in Xenopus. 2) The electron-dense “H” shaped structure in Chlamydomonas is similar, if not identical, to that shown in Xenopus cilia. 3) The physical location of TZ is always shown to be distal to the basal body and transition fibers (except in clubmoss Phylloglosum) while proximal to the central pair. The electron-dense “H-shaped” structure in Xenopus fulfills these criteria, suggesting that this structure is the TZ in Xenopus. 4) The TZ bonafide protein B9D1 is localized distal to Chibby, which labels the distal end of the basal body, suggesting that the TZ is localized distal to the basal body. Moreover, the loss of an “H-shaped” structure determined using TEM and tomograms corresponds to the loss of the B9D1 signal, further strengthening the conclusion that the H-shaped structure is the TZ.

      We will include serial sectioning and imaging of multiple Xenopus cilia in control and 0hr (after deciliation) to address this reviewer's concerns further. Our preliminary data has suggested that the ciliary membrane is tightened around this electron-dense structure, similar to what has been shown before for other organisms like Chlamydomonas. and thus boosts our confidence that this structure likely corresponds to the TZ in Xenopus.

      The reviewer has raised a concern that “the tomogram after deciliation is thin and does not cover the entire width. Therefore, it is not sure that absence of TZ can be concluded”. We note that even if the tomograms do not go through the entire cilium (supplementary videos 2 and 3), it does go through more than the center of cilium as seen by the presence of central pair microtubules and we can observe that the electron-dense “H-shaped” structure is not present in these cilia. Further, in the supplementary videos 5 and 6, even if the tomogram again only covers half of the cilia, we can see the presence of the structure, confirming that our tomograms can demonstrate the presence or absence of the H-shaped structure confidently. We have also provided TEM sections in addition to the tomograms to show the same result.

      The Reviewer has commented that “B9D1 is located on or near the membrane, in vicinity to TZ, and thus binds to TZ after the main part of TZ is built”. This reviewer is correct in their assessment. This is why we argue that the presence or absence of B9D1 may be a good marker for understanding the presence or absence of TZ assembly.

      TIMELINE: We are performing additional serial TEM in the control and deciliated (0hr.) embryos to address the reviewer’s concern. We will need 1 month to finish these experiments.

      Their discussion about length/number of cilia and force generated by cilia is interesting, but in the context of this research, this reviewer is skeptical about its value. The calcium induced deciliation is not a physiological phenomenon, but an artificial event (please correct if I am wrong). The argument how length and number of cilia are regulated upon deciliation makes sense only in case deciliation happens regularly and the species must optimize themselves to survive. The argument about possible passway of protein transport to control ciliary number and length (Line408-) seems, although it is an interesting topic in general, not suitable in this manuscript. For this reviewer's view, it is relatively straightforward to interpret the result of cilia number/length under normal growth, without new protein expression (CHX), with protein degradation blocked. Cilia will extend when components are provided. Growth will slow down when it is exhausted. Existing cilia start degrading, when they lack proteins, which are necessary for turn-over. With the current experimental output, there is no point to describe redistribution of proteins.

      RESPONSE: We appreciate the reviewer’s comment; however, we would like to argue that different methods of deciliation have been used in different model systems, such as Chlamydomonas, to study cilia regeneration. Although this reviewer may not find some of the experiments and conclusions appropriate for this manuscript, other research groups have found these results interesting. For example, reviewer 2 states, “To support their observations that cilia length is favored over cilia number under conditions of limiting ciliary precursor availability, the authors use a mathematical model that leads to the conclusion that force generation is optimized by increasing cilia length. This is a convincing conclusion and in agreement with other comparable modeling studies performed in the field.” We have already had great discussions about these results with many cilia researchers at multiple conferences. Therefore, we prefer to keep these experiments and results in the manuscript and let readers come to their own conclusions about their importance.

      Minor points:

      Line65: do they mean "selected few basal bodies"? – we have removed the word “select”

      Line73: extracellular flow is not limited to developmental system. – we have altered the statement to add “growth, development and homeostasis”

      Line124: alpha-tubulin signal and SEM image – we have added “and scanning electron microscopy (SEM)”

      Line139: Could you define explicitly the two hypotheses? – Now, we have reworded the sentences to clarify the two hypotheses. “Therefore, we considered two hypotheses: First, Xenopus MCCs regenerate cilia or second, Xenopus depend on stem cell-based replacement of damaged MCCs.”

      Line164: 10,31-33 are not suitable citation for the location of calcium induced deciliation in Chlamydomonas. cite Sanders and Salisbury JCB 108, 1751 – We have changed the citation.

      Line181: Later -> latter – We have changed the text.

      Line195: by mechanical shearing, B9D1 remained with cilia. They concluded that TZ stays with the axoneme by deciliation. How can they exclude the possibility that mechanical separation works differently from calcium shock? – We do not intend to claim that both calcium-based and mechanical ripping of cilia from cells adopt the same deciliation mechanism, and we have mentioned in line 193 that ‘we adopted an alternative approach of mechanical deciliation’. Using these two methods as complimentary to each other, our aim was to show that TZ is lost by both ciliation methods. For the calcium method, because the membrane is ripped with detergent, we show the loss of TZ by examining the MCCs devoid of cilia. In the mechanical deciliation protocol, since no detergent is involved, we can examine cilia that are likely to have intact membranes and thus maintain a B9D1 signal.

      Line214: 1.33uM -> 1.33um - We have made these changes to the text.

      __RESPONSE: __All the minor points in the manuscript are addressed.

      Overall, the results are well presented and allow strong conclusions to be drawn. The results are based on both immunofluorescence studies and EM analysis. To support their observations that cilia length is favored over cilia number under conditions of limiting ciliary precursor availability, the authors use a mathematical model that leads to the conclusion that force generation is optimized by increasing cilia length. This is a convincing conclusion, and in agreement with other comparable modeling studies performed in the field. It would be fascinating to be able to measure the flow parameters at the cell surface during cilia regeneration to see whether this regeneration actually leads to an increase in the overall flow or force generated by the cilia. But as the authors explain, this is probably a difficult experiment to carry out and appears to be optional in the context of this study.

      __RESPONSE: __We thank the reviewer for recognizing and stating that “the results are well presented and allow strong conclusions to be drawn”. We also want to sincerely thank the reviewer for understanding the technical difficulties in performing these experiments.

      The authors are apparently only able to detect a single TZ protein, B9D1, to follow the fate of the TZ during the deciliation and reciliation process. In some ways, this provides an incomplete demonstration that all the TZ is indeed removed during deciliation, although this is supported by EM observations. It also provides a limited understanding of the time course of TZ re-formation during reciliation. Given the limitations of antibody availability, could it be possible to express tagged proteins in the animal cap system to track more TZ proteins? In particular, would it be possible to track for example Cby and NPHP proteins. What is the behavior of Cep290? This would greatly reinforce the conclusions on the molecular reorganisation of the TZ after deciliation and during cilia regeneration.

      __RESPONSE: __We appreciate this reviewer’s brilliant questions on understanding the time course of TZ re-formation during reciliation. When we started this project and observed that TZ was lost upon deciliation in our preliminary TEM experiment, our first goal was to confirm this outstanding result. Thus, we did more TEMs and EM tomography, used bonafide TZ protein B9D1 to label the structure, and observed its loss upon deciliation. Taken together, we feel highly confident that TZ is lost upon deciliation. To address this reviewer’s concerns, we will performing additional serial TEMs to confirm the loss of TZ after deciliation.

      Our next goal was to understand what the reviewer has mentioned, the TZ assembly time course. We started with TEMs at different time points and again saw a surprising result: TZ assembly was delayed compared to cilia axoneme. We were driven by this question of understanding how cilia “put together” the complex structure of TZ structurally and molecularly using EM and fluorescence data. We first attempted a few antibodies, including B9D1, CEP290, MKS5, and NPHP4, to localize to the TZ in the Xenopus cilia. Despite our efforts with different fixation strategies, only B9D1 appeared to localize to the TZ, whereas others did not give any signal or localized at the basal body. Next, we tried localizing TMEM216, TMEM67, and NPHP4 using fluorescent tags, but we again found the same result: they localized to the basal body but not at the TZ. We are perplexed by this result and are pursuing the reasons behind them. However, these experiments are out of the scope of this paper. We want to note that we have used Chibby in our experiments and that it is not lost upon deciliation (Fig S1). This is because Chibby is a distal transition fiber protein (distal end of basal body) and does not extend up to the transition zone.

      TIMELINE: To address the reviewer's concern, we are performing additional serial TEM in the control and deciliated (0hr.) embryos. We will attempt to localize CEP290-GFP, requiring approximately 1 month to finish the experiment. However, we would like to note that we cannot guarantee that this experiment will work, as similar experiments with other TZ markers have failed before.

      Minor comments

      1. Figure 4: The images are poorly defined, and it is difficult to distinguish individual basal bodies and cilia. Therefore, it is not clear how the authors can confidently quantify the number of basal bodies in each condition to construct the graph at the bottom of the figure. In addition, it would be interesting to label the basal body with a centriolar marker to better define it. - Figure 4 labels the Transition Zone protein B9D1 and cilia marker acetylated tubulin and not basal bodies. The graph represents the number of cells with the presence or absence of elongated B9d1 signal.

      2. Figure 5: not clear why the graph on the lower right does not include the control at 3 and 6 hrs? Is it because the number is too high and difficult to quantify? – Yes, the reviewer is right. Cilia become too long and too many to quantify their number reliably.

      3. References: I would like to draw the authors' attention to studies of deciliation in Paramecia that could be cited in the introduction or discussion of the conservation of this pathway through evolution. – We have added multiple references to paramecia throughout the manuscript. Specifically, we mention that deciliation and regeneration in unicellular models like paramecia have added to our understanding of ciliogenesis. Line 102 “While it is important to remember that regeneration of cilia may not be identical to de novo assembly, cilia regeneration studies in Chlamydomonas reinhardtii, Paramecium and Tetrahymena etc., have provided significant insights into ciliogenesis, g., cargo transport, the presence of precursor pool, regulation of ciliary gene expression.18,23–26”. Further, we also added the reference to paramecia in results, line164 “Next, we determined the location where the deciliation treatment severed cilia. Unicellular models such as Chlamydomonas, Paramecium and Tetrahymena lose cilia distal to the TZ and below the central pair (CP) microtubules33.”. We also add discussion on the importance of TZ in paramecia, line 203 “Interestingly in Paramecium also a unicellular multiciliated cell, displays constant shedding of cilia when TZ proteins are depleted.25”. These statements have been supported by the following studies that are now cited in the manuscript: Machemer and Ogura 1979 Journal of Cell Physiology (10.1113/jphysiol.1979.sp012990) and Gogenddeau et al., Plos Biology (10.1371/journal.pbio.3000640).

      RESPONSE: All the minor points in the manuscript are addressed.

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      Referee #3

      Evidence, reproducibility and clarity

      The manuscript by Rao et al. focuses on determining the mechanism of cilia regeneration using Xenopus mucociliary epithelium. The authors employ a simple yet powerful approach to trigger deciliation of multiciliated cells, enabling them to study the mechanism of cilia regeneration. This research has a significant impact on the field of cilia biology and enhances our understanding of ciliopathies. Through detailed cell biological methodologies, the authors obtained intriguing results, including the finding that deciliation removes the transition zone and that cilia repair precedes the transition zone assembly. Additionally, the authors demonstrate that IFT proteins involved in cilia construction concentrate at selected basal bodies. Although there are open questions that the authors also highlight, this manuscript provides solid, pioneering insights into the process of cilia regeneration in vivo.

      Significance

      The manuscript characterizes the mechanism of cilia regeneration, providing new insights into processes that could be harnessed to restore ciliary function in patients suffering from chronic respiratory diseases.

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      Referee #2

      Evidence, reproducibility and clarity

      Summary

      This manuscript investigates how cilia regenerate in multi-ciliated cells. The authors have exploited an original multi-ciliated cell system derived from the Xenopus embryonic cap and use chemical and mechanical deciliation to understand the different steps of cilia regeneration. In this model, they show that cilia are excised just above the BB and below the ciliary transition zone. Their results indicate that during ciliary regeneration, axoneme reassembly precedes TZ formation and that ciliary reassembly relies on de novo protein synthesis. In the context of limited protein synthesis, cells regenerate fewer cilia, but of almost the same size as control cells, suggesting the existence of a cell control system to maximise force generation. Mathematical modelling of the forces exerted by defined numbers of cilia of different lengths supports this hypothesis.

      Major comments

      Overall, the results are well presented and allow strong conclusions to be drawn. The results are based on both immunofluorescence studies and EM analysis. To support their observations that cilia length is favored over cilia number under conditions of limiting ciliary precursor availability, the authors use a mathematical model that leads to the conclusion that force generation is optimized by increasing cilia length. This is a convincing conclusion, and in agreement with other comparable modeling studies performed in the field. It would be fascinating to be able to measure the flow parameters at the cell surface during cilia regeneration to see whether this regeneration actually leads to an increase in the overall flow or force generated by the cilia. But as the authors explain, this is probably a difficult experiment to carry out and appears to be optional in the context of this study.

      The authors are apparently only able to detect a single TZ protein, B9D1, to follow the fate of the TZ during the deciliation and reciliation process. In some ways, this provides an incomplete demonstration that all the TZ is indeed removed during deciliation, although this is supported by EM observations. It also provides a limited understanding of the time course of TZ re-formation during reciliation. Given the limitations of antibody availability, could it be possible to express tagged proteins in the animal cap system to track more TZ proteins? In particular, would it be possible to track for example Cby and NPHP proteins. What is the behavior of Cep290? This would greatly reinforce the conclusions on the molecular reorganisation of the TZ after deciliation and during cilia regeneration.

      Minor comments

      Figure 4: The images are poorly defined and it is difficult to distinguish individual basal bodies and cilia. It is therefore not clear how the authors can confidently quantify the number of basal bodies in each condition to construct the graph at the bottom of the figure. In addition, it would be interesting to label the basal body with a centriolar marker to better define the basal body.

      Figure 5: not clear why the graph on the lower right does not include the control at 3 and 6 hrs? Is it because the number is too high and difficult to quantify?

      References: I would like to draw the authors' attention to studies of deciliation in Paramecia that could be cited in the introduction or discussion of the conservation of this pathway through evolution.

      Significance

      The mechanisms of deciliation and re-ciliation have mostly been studied in protozoa (Chlamydomonas, Paramecia) or in primary ciliated cell cultures. Only a few studies have described deciliation in multiciliated cells, such as sea urchins, or physiological deciliation in the oviduct. The Xenopus deciliation system described here has already been used to determine the dynamics of IFT proteins during ciliogenesis or to define the ciliary proteome. In this study, the authors go one step further by describing more precisely which part of the cilium is shed upon induction of deciliation and the dynamics of the recruitment of the Tip and of the TZ proteins.

      This study provides a completely new perspective on the deciliation process:

      1. the authors show that, contrary to what is generally accepted from protozoan studies, the deciliation process, in Xenopus multiciliated cells, expels the TZ, leaving only the basal body in the cell;
      2. While ciliogenesis is described in various models to begin with the formation of the TZ, in this Xenopus system the TZ maturates after the onset of axonemal elongation, calling into question the precise function of the TZ in axonemal elongation. The observations could be further strengthened by analyzing more TZ proteins to better understand the time course of events involved in the deciliation-reciliation program.

      The protocol used to deciliate Xenopus multiciliated cells has been described in previous manuscripts. Its use here reveals striking differences in the deciliation-reconciliation pathways from what is known in the field. It provides new conceptual perspectives for researchers working on the basic mechanisms of ciliogenesis. Note that, as a geneticist and specialist in ciliogenesis using various model organisms, I am not fully competent to critically evaluate the mathematical models developed in this study.

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      Referee #1

      Evidence, reproducibility and clarity

      In this manuscript entitled "Machanisms of cilia regeneration in Xenopus multiciliated epithelium in vivo", the authors mostly focus on the question, whether TZ (transition zone of cilia) plays an essential role for ciliogenesis during cilia regeneration in multiciliated cells. They used Xenopus embryo as a system to examine this question. While cilia regeneration has been actively studies in unicellular green algae, Chlamydomonas reinhardtii, the mechanism of cilia regeneration is not known yet. Their approach is to investigate cells after deciliation by calcium shock, based on a TZ protein B9D1, as well as ultrastructure observation using conventional electron microscopy.

      The authors observed loss of signal from B9D1 and H-shaped objects, which is typical for TZ, upon deciliation induced by calcium and also during the following re-growth of cilia. Based on these experiments they concluded that TZ formation is not necessary for cilia regeneration in multiciliated cells, differently from Chlamydomonas. They further conducted experiments to pursue source of component proteins for re-generation. They compared CHX-treated cells (lacking new protein production) and CHX/MG132 (reduced protein degradation) treated cells to find how the massive amount of protein components upon re-ciliation for multiple cilia will be supplied and regulated. This reviewer found the results of the experiments clearly presented and conducted properly.

      The work would have significant impact in the cilia community, if the conclusion is correct. This reviewer, however, has a concern about the authors concluding the presence/absence of TZ, based on only B9D1 and the H-shaped body among nine doublet microtubules. First, is it really established how the structure of Xenopus embryo TZ is? While Chlamydomonas is well known to have a H-shaped TZ, other species have different form inside the 9+0 doublet, or no feature (Comparison of TZ from various species in Dennis Diener https://doi.org/10.1016/B978-0-12-822508-0.00007-1). Fig.2B of this manuscript shows visible densities in the panel "Pre", but it does not look like an H-shape. The tomogram of TZ before deciliation seems clearer (but judging from wavy MTs and membrane in this tomogram, there could be unevenness of embedding and staining), while the tomogram after deciliation is thin and does not cover the entire width. Therefore it is not sure that absence of TZ can be concluded. If the author claims Xenopus embryo cilia have a H-shaped TZ, they have to provide multiple micrographs (ideally tomogram or serial section TEM to cover the entire TZ structure) and/or past literature on Xenopus embryo TZ. B9D1 is likely a membrane associated protein (according to their deciliation by detergent and mechanical force). This may mean B9D1 is located on or near the membrane, in vicinity to TZ, and thus binds to TZ after the main part of TZ is built. In this case, it is risky to judge presence of TZ based on B9D1. Also in this point, TEM imaging will be helpful to confirm the authors' conclusion.

      Their discussion about length/number of cilia and force generated by cilia is interesting, but in the context of this research, this reviewer is skeptical about its value. The calcium induced deciliation is not a physiological phenomena, but an artificial event (please correct if I am wrong). The argument how length and number of cilia are regulated upon deciliation makes sense only in case deciliation happens regularly and the species must optimize themselves to survive. The argument about possible passway of protein transport to control ciliary number and length (Line408-) seems, although it is an interesting topic in general, not suitable in this manuscript. For this reviewer's view, it is relatively straightforward to interpret the result of cilia number/length under normal growth, without new protein expression (CHX), with protein degradation blocked. Cilia will extend when components are provided. Growth will slow down when it is exhausted. Existing cilia start degrading, when they lack proteins, which are necessary for turn-over. With the current experimental output, there is no point to describe redistribution of proteins.

      Minor points:

      Line65: do they mean "selected few basal bodies"?

      Line73: extracellular flow is not limited to developmental system.

      Line124: alpha-tubulin signal and SEM image

      Line139: Could you define explicitly the two hypotheses?

      Line164: 10,31-33 are not suitable citation for the location of calcium induced deciliation in Chlamydomonas. cite Sanders and Salisbury JCB 108, 1751

      Line181: Later -> latter

      Line195: by mechanical shearing, B9D1 remained with cilia. They concluded that TZ stays with the axoneme by deciliation. How can they exclude the possibility that mechanical separation works differently from calcium shock?

      Line214: 1.33uM -> 1.33um

      Significance

      The work would have significant impact in the cilia community, if the conclusion is correct. Their discussion about length/number of cilia and force generated by cilia is interesting, but in the context of this research, this reviewer is skeptical about its value.

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      Reply to the reviewers

      Manuscript number: RC-2024-02470

      Corresponding author(s): Milán, Somogyvári; Csaba, Sőti

      1. General Statements

      We thank both Reviewers for their constructive comments, and we hope that our reply clarifies the concerns and the revised manuscript will be recommended for publication in Review Commons affiliated journals.

      2. Description of the planned revisions

      As the first major concern, Reviewer #1 raised the question of resolving the link between SIR-2.1 and HSF-1.

      In order to address this issue, we plan to utilize a two-way approach:

      • We plan to check the acetylation status of C. elegans HSF-1 using Mass Spectrometry.
      • We aim to evaluate changes in its promoter binding by utilizing a form of Chromatin Immuno-Precipitation combined with RT-qPCR.
      • As an alternative approach, we plan to utilize the cbp-1GoF mutant strain MH2430, that was described to acetylate HSF-1 and therefore change its transactivational function (Barrett & Westerheide, 2022). We'd like to see whether this can achieve a phenocopy of the sir-2.1(null) genetic background - on the level of the lipolysis phenotype and HSF-1-acetylation. These experiments are to be performed in both wildtype and sir-2.1-silenced animals under fed and starved conditions.

      The second issue raised by Reviewer #1 was to confirm that the miR-53 activity on atgl-1 3' UTR is crucial for the described phenotype.

      Our planned solution for this issue is to create novel C. elegans strains that expresses green fluorescent protein under the regulation of the atgl-1-promoter and with either the wildtype 3'UTR of atgl-1 attached or a mutated one, to which mir-53-binding is not possible. Through fluorescence microscopy experiments involving fed and starved animals, we hope to be able to sufficiently assess the necessity of mir-53 activity to changes in atgl-1 expression and function.* *

      The following minor concern of Reviewer #1 regarding the Results section are addressed here:

      (b) Supporting our ORO results with using the transgene idrIs1[dhs-3p::dhs-3::GFP] to label lipid droplets.

      After acquiring the LIU1 strain harboring the aforementioned transgene, we plan to validate some of the results gained from ORO experiments.

      • *

      Reviewer #2 brought into our attention several concerns that need to be addressed:

      1- Firstly, it was mentioned that the overabundance of histograms and the lack of indications on the representative images makes it difficult for the reader to assess the information on the panels.

      We plan to include more images of stained worms while also indicating the changes that the histograms are meant to show. We hope these efforts will make our results more convincing.

      2- Reviewer #2 mentioned that some of the results shown in our manuscript was already published in Zaarur N et al, 2019.

      We thank the Reviewer for bringing this issue to our attention. We'd like to however point out that the mentioned paper by Zaarur et al. is indeed referenced in two places in the Introduction of our manuscript: first, when highlighting that longevity pathways, fat metabolism and lifespan determination are interconnected (line 56), and second, indicating that ATGL-1 mediates longevity in response to dietary restriction and reduced insulin-like signaling (line 65). The regulation of ATGL-1 by starvation and of lipid mobilization by ATGL-1 are not among the novel results of this study. The novelty of our data lies mainly in HSF-1 being involved through specific microRNAs - which to the best of our knowledge has not yet been published. We agree with Reviewer #2 that the visual representation of the data in Zaarur et al. is more pleasing, therefore we plan to incorporate representative images here as well.

      5- Selection of mircoRNA genes

      It was rightly pointed out by Reviewer #2 that mir-53 was reported to be upregulated by HSF-1 upon heat-shock, while there's no mention of it behaving so upon starvation. However, we considered examining it a potentially worthwhile direction given that in C. elegans it is a common observation that various stresses lead to the activation of similar/overlapping stress-response pathways. As seen at Figure 5E, our data supports the idea that mir-53 expression responds to starvation, as its pre-miRNA levels are elevated by starvation in sir-2.1-silenced animals. As for mir-60 and mir-75, we indeed do not have evidence for them being regulated by HSF-1, however their mutants have been associated with reduced body fat content (Brosnan, Palmer & Zuryn, 2021), thus we considered them also to be potential candidates for the role of mediator in the observed lipolysis phenomenon. We aim to make our reasons for choosing these specific miRs clearer in the manuscript.

      3. Description of the revisions that have already been incorporated in the transferred manuscript

      In accordance with the minor concerns of Reviewer #1, the following changes have already been made to the manuscript:

      In the Abstract, two sentences were changed: (a) "In starving worms, a SIR-2.1-dependent suppression of specific HSF-1 transcriptional activity leads to the inhibition of lipolysis through mitigating miR-53-expression" & (b) "potential crosstalk" was introduced to the last sentence in order to better reflect the nature of our results.

      In Introduction, the start of the first sentence was changed to "Lipids are a diverse group of cellular constituents".

      In Results, the suggested changes in the C. elegans nomenclature were performed (a), where we substituted "sir-2.1 knockout" with "sir-2.1(null)" and "hsf-1 knockout" with "hsf-1(null)".

      The following concerns of Reviewer #2 are addressed in the text of the transferred manuscript:

      4- Stage of synchronized populations in the starvation protocol.

      We thank the Reviewer for highlighting this issue. The life-stage of the animals should indeed be specified at this particular method. It may have been omitted due to RNAi treatments being described just above, where it is mentioned that L4 animals are washed onto RNAi plates where they spend 2 days. Any starvation protocol starts only after these RNAi treatments, since almost all our experiments include some form of RNAi. Therefore, in any trials that do not have RNAi in them, we still only applied starvation from 2 days after L4 stage - for comparability's sake. This issue is clarified in the revised manuscript.

      4. Description of analyses that authors prefer not to carry out

      The third major concern mentioned by Reviewer #1 is the epistatic relationships between our novel regulatory pathway and the KIN-1/PKA.

      We'd like to thank Reviewer #1 for turning our attention towards the issue. We feel that the phosphorylation of ATGL-1 by KIN-1 - most probably on Serine 303 - was well established in Lee JH et al, 2014, as seen at Figure 5B - which, naturally, must occur downstream from any transcriptional regulation done by the SIR-2.1-HSF-1-MIR-53 axis. Nevertheless, it would be interesting to see if a non-phosphorylatable ATGL-1 will not support lipolysis upon starvation even if its mRNA expression is activated - which is something that was not tested for in Lee JH et al, 2014. However, since this was not the main subject of our manuscript - more of an addition to ATGL-1-regulation - while our work focused on the regulatory axis going through HSF-1, we do not consider it crucial to perform further experiments aimed at the KIN-1/PKA-mediated regulation of ATGL-1.

      The following minor concerns of Reviewer #1 regarding the Results section are addressed here:

      (c) Fatty acid profiling in the different experimental conditions.

      Even though we feel the potential significance of such data, it does not fit under the scope of our current study. We feel this to be better fitting for a later, follow-up research project.

      (d) Concern about double RNAi treatment in Figure 2D.

      In such particular experiments, where the nematode strain is already a mutant one (where RNAi can only affect intestinal cells), it would require time-consuming crossings with the sir-2.1 and hsf-1 mutant animals. For this reason, we opted to use double RNAi, since according to literature - as well as to our previous experience - double RNAi can be a reliable method to silence the expression of two genes simultaneously. Since the effectivity of RNAi can be influenced by dosage, we compensated for this by mixing the single RNAi treatments with Empty Vector containing bacteria. The results themselves show the silencing-treatments to be effective - to a similar extent as the single RNAi treatments seen in Figure 2A.

      (e) Improving statistical power.

      We agree with Reviewer #1 that in some cases the addition of biological replicates may have the potential to strengthen our conclusions. We argue however, that even though in each case we applied statistical post-hoc tests in order to avoid a type I error, going above the customary 3 biological replicates at each and every experiment would increase the probability of such an error occurring.

      The following concerns of Reviewer #2 are addressed here:

      3- Reviewer #2 inquired about RNAi efficiency and the usage of knock-out mutants.

      Here, we'd like to highlight that throughout the manuscript we utilized sir-2.1(null) mutants in Fig. 1A-B, Fig. 2A-B, Fig. 3D & Fig. S3A; while using hsf-1(null) mutants in Fig. 2A, Fig. 3B & Fig. 8D-F - among other mutants and transgenics. The list of strains can be found in Supplementary Table 1. Regarding the hsf-1(RNAi), it is a strain used for silencing hsf-1-expression reliably in the past by the lab of origin at ELTE University (Barna et al. 2012 BMC Developmental Biology). The silencing of hsf-1 does not lead to any noticeable phenotypes, but it does fully eliminate hsp-70-induction by heat-shock or starvation as shown on Fig. 5A-B.

      6- KIN-1 & KIN-2's role and place in lipolysis regulation

      As Reviewer #2 pointed out, both a mutation in kin-1 and kin-2 seemingly lead to the inhibition of lipolysis. However, since kin-2 codes for the regulatory subunit of KIN-1/PKA, a Loss of Function mutation in it leads to a constitutively active PKA - which in turn is expected (among other outcomes) to continuously phosphorylate and thus stabilize ATGL-1. In accordance with this, loss of KIN-1 resulted in an inability to utilize lipid-reserves - therefore the ORO staining levels of these mutants remained similar to wildtype and fed state even upon starvation - while loss of KIN-2 lead to a significantly decreased basal lipid staining, that could not be further decreased by starvation. We argue that the lack of any effect of sir-2.1(RNAi) (or hsf-1(RNAi)) on these phenotypes, while atgl-1(RNAi) was able to revert the kin-2(null)-related basal lipid loss, strongly supports the epistatic relationships proposed.

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      Referee #2

      Evidence, reproducibility and clarity

      Review

      An intestinal Sir2-HSF1-ATGL1 pathway regulates lipolysis in C. elegans

      In the manuscript by Somogyvári et al., the authors focus on the differences between the fed and the fasted state using C. elegans. In particular the authors find that in the fasted state, the C. elegans SIRT1 ortholog, SIR-2.1, activates lipolysis by upregulation of ATGL-1. Further studies show that in fed worms regulation occurs in the intestine by HSF-1, ATGL-1, and the microRNA system. In contrast, in fasted worms, SIR-2.1 functions with the miR-53 microRNA to affect lipolysis and hsf-1. Further experiments attempt to implicate protein kinase A and proteostasis. Ultimately, the authors attempt to invoke a model for stress resilience and aging. Overall, the data as presented is not very convincing. All of the data is presented as histograms which show only mild effects. Images that are shown are not convincing. Some of the data has been previously published (mentioned below). Therefore, the manuscript needs extensive revisions prior to resubmission and should address the comments below.

      1. why is most of the data presented as a histogram?

      Why are there not representative images that help readers examine the results? /

      For example figure 1A does not really show anything but could guide the reader. The worm images throughout the manuscript do not give any indication of what the authors want the data to show the reader. 2. some of the data has already been published.

      Mol Metab. 2019 Sep:27:75-82. doi: 10.1016/j.molmet.2019.07.001. Epub 2019 Jul 5. Nava Zaarur et al. fig 1

      ' ATGL-1 is up-regulated by fasting of C. elegans. (A) Wild type (N2) and atgl-1::gfp worms w

      control (Fed) and Fasted groups and stained with Oil Red O.<br /> (B) Triglyceride content was measured in Fed and Fasted groups of N2 and atgl-1::gfp worms. (C) RNA was extracted from Fed and Fasted groups, and atgl-1 mRNA levels were measured by qRT-PCR; actin-1/3 was used for normalization. (D) Fed and Fasted L4 stage atgl-1::gfp worms were visualized by fluorescence microscopy (200X, equal exposure times). Bar e 50 mM. (E) Quantification of the results shown in panel D by ImageJ (10 randomly selected worms per group). '

      this is not referenced or discussed and more convincing than simply a histogram 3. - why is there no analysis with mutants and simply Rnai? for example why is sir2 mutant not used.? - does the rnai show any phenotypes? ex hsf-1 rnai = hsf mutant? - Do you know the knockdown efficiency for the rnai clones? 4. Starvation protocol

      560 Synchronized populations were washed 3 times with M9 buffer and placed either on 561 plates containing bacterial food source, or empty plates for 18 hours.

      - what stage were the Synchronized populations?
      
        1. Brunquell, J., Snyder, A., Cheng, F. & Westerheide, S. D. HSF-1 is a regulator of 699 miRNA expression in Caenorhabditis elegans. PLoS One 12, 1-24 (2017) This is the reference used to define the connection to micrornas. However, this manuscript describes miRNAs induced by heat shock. How does heat shock connect to starvation? The fed or the fasted state? Overall, the rationale for the specific microRNAs shown in the manuscript example mir-53 is unclear.
      1. Figure 6. The protein kinase A KIN-1 affects lipolysis and ATGL-1 function 330 downstream from SIR-2.1 and HSF-1.

        • there is no difference between kin-1 knockout and Kin-2 knock out-so how does one say that it is only Kin-1?
        • where are the differences between fig 6b and 6c?
        • 'The complete 306 inhibition of lipolysis in the absence of sir-2.1 or kin-1 suggests that Sir2 and PKA pathways 307 are equally indispensable and cooperate in lipolysis regulation in the wildtype'
        • does data really show this? ?- not much difference between kin-1 and kin-2- can you really separate the requirements?

      Significance

      Overall, the data as presented is not very convincing. All of the data is presented as histograms which show only mild effects. Images that are shown are not convincing. Some of the data has been previously published (mentioned below). Therefore, the manuscript needs extensive revisions prior to resubmission and should address the comments below.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary.

      This study elucidates the contribution of sirtuin 1 ortholog SIR-2.1 in lipid mobilization upon starvation in the nematode Caenorhabditis elegans. The authors claim that HSF-1 controls the expression of adipose triglyceride lipase ATGL-1 in C. elegans gut. Furthermore, they show that SIR-2.1 modulates ATGL-1 activity by regulating the expression of microRNA miR-53 in an HSF-1-dependent manner. The manuscript also describes the interplay between SIR-2.1/HSF-1 and protein kinase A (KIN-1/PKA) in modulating ATGL-1 activity and proteostasis. Finally, the authors claim that lipid mobilization correlates with HSF-1-dependent proteostasis according to the feeding state of the organism.

      Major concerns.

      This manuscript consists of at least three parts that are relatively connected: - The impact of SIR-2.1 deficiency on ATGL-1 expression. Here, the main novelty is that HSF-1-dependent regulation of miR-53 defines atgl-1 expression during starvation. - The contribution of KIN-1/PKA in lipid mobilization and ATGL-1 activity downstream SIR-2.1 and HSF-1. This link was partially described in a few previous studies (e.g., Lee JH et al, 2014).<br /> - The contribution of HSF-1 in intestinal proteotoxic stress and fat metabolism. The role of HSF-1 in proteostasis has been well documented, whereas its participation to lipid metabolism has been described in a few studies (e.g., Oleson BJ, 2024).

      The authors provide novel findings that give a better picture of the signaling cascade regulating these biological processes.

      1. However, this study does not conclusively resolve the link between SIR-2.1 and HSF-1. Does Sirtuin 1 influence HSF-1 through histone deacetylation and, therefore, HSF-1 deposition to target genes? Or does Sirtuin regulate HSF-1 acetylation state and therefore its activity? The authors attempted to address these questions with some experiments (Figure 5), however the data are indirect evidence.
      2. Furthermore, microRNAs have multiple targets with various biological functions. Although the authors provide first line of evidence demonstrating the impact of miR-53 on starvation-induced lipolysis, it may be important to confirm that the miR-53 activity on atgl-1 3' UTR is crucial for the described phenotype. Thus, the authors may consider to generate C. elegans strains carrying an atgl-1 3' UTR that is not recognized by the endogenous miR-53 (OPTIONAL).
      3. The role of KIN-1/PKA and ATGL-1 was previously reported (Lee JH et al, 2014) as mentioned in the manuscript. In the submitted manuscript, the authors tried to link KIN-1/PKA, ATGL-1, SIR-2.1 and HSF-1. The authors suggest that "KIN-1 acts downstream from the SIR-2.1 pathway" and "KIN-1 acts downstream of ATGL-1 post-transcriptional regulation". Most of the authors' conclusions are based on RNAi experiments. Could the authors support their claims by providing evidence that the downstream substrates are differentially posttranslationally modified according to the experimental conditions (starvation vs feeding)? Apart from RNAi methods, could the authors support their claims by using non-phosphorylatable ATGL-1 mutants?

      Minor concerns.

      Abstract.

      (a) "SIR-2.1 suspends a miR-53-mediated suppression...". Please adjust the text to make it more understandable.

      (b) "Our findings reveal a crosstalk between proteostasis and lipid/energy metabolism, which may modulate stress resilience and aging.". Which evidence do the authors have that this newly identified crosstalk influences aging? Figure 8 is not sufficient to make such a strong claim.

      Introduction.

      I would encourage the authors to re-word some of their sentences. For example, "lipids are diverse constitutes" sounds strange.

      Results.

      (a) Please, keep in mind the internationally accepted C. elegans nomenclature. For example, substitute "sir-2.1 knockout" with "sir-2.1(null)".

      (b) The authors used Oil Red O (ORO staining) to assess lipid content in nematodes. However, the method has a few limitations and the accurate assessments of fat stores may be variable across experiments. One option is that the authors corroborate their findings with another approach. For example, they may consider to use the transgene idrIs1[dhs-3p::dhs-3::GFP] to label lipid droplets in intestinal cells.

      (c) The authors assessed free-fatty acid content in fed and starved animals. It may be informative to report the individual fatty acid molecules that are mobilized in the different experimental conditions.

      (d) It is always difficult to obtain reproducible results by using two RNAi clones (Figure 2D). The authors should corroborate their results with sir-2.1 and hsf-1 mutant worms.

      (e) For some of the experiments, the statistics may be improved. Since some panels show tendency towards statistical significance (e.g., 8F), it may be important that the authors strengthen their analyses with additional biological replicates. This would help to consolidate their findings and conclusions.

      Significance

      This study reports how Sirtuin 1 can modulate ATGL-1 expression by regulating a microRNA (miR-53). It remains unclear if it is through a direct interaction or via epigenetic remodelling of histone acetylation of target genes. By building up on previous studies, the authors provide additional molecular players that take part in lipid mobilisation during starvation.. The audience can be defined as "specialised" and "basic research".

      My fields of expertise are: metabolism, aging and epigenetics. I work with mice and C. elegans.

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      Reply to the reviewers

      1. General Statements [optional]

      This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

      We thank the reviewers for their insights and helpful suggestions on the manuscript. Based on these, we have prepared a revision plan for this manuscript, which is outlined below. We believe these revisions will improve the overall quality of the manuscript.

      2. Description of the planned revisions

      Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

      • *

      Reviewer #1

      (Evidence, reproducibility and clarity (Required)):

      Summary:

      This study builds on previous work from the same group, where they use Drosophila photoreceptors as a model system to investigate the role or ER-plasma membrane contact sites in an in vivo setting. The authors recently described a role of the ER-PM contact site protein dEsyt in regulating photoreceptor function in Drosophila. In this follow-up study, they explore whether this function of dEsyt is connected Ca2+ signaling downstream of photoreceptor activation. Using a dEsyt mutant that should be unable to bind Ca2+, they find that Ca2+ to some extent is required for dEsyt localization, membrane contact site formation and photoreceptor function.

      Major comments:

      The use of photoreceptor cells in Drosophila is an elegant model system that enable studies of membrane contact sites and associated proteins in a native condition. The data presented by the authors clearly shows that these structures are important for photoreceptor function, and that dEsyt plays a role at these sites. However, this was already known from previous studies by the same group. When it comes to whether these contacts are sensing Ca2+ changes and if these changes are acting through dEsyt, which is the focus of the current manuscript, the results are unclear to me and would need to be clarified by the authors both in text and with new experiments.

      1) What is the role of cellular Ca2+ signaling in the regulation of dEsyt function? There are several aspects here that needs to be clarified. 1) How is WT dEsyt localization regulated by Ca2+? This could for example be evaluated in the mutant flies used in Fig. 1 (trpl302; trp343), where lack of light-induced Ca2+ influx would be predicted to result in a localization of dEsyt that resembles that observed for dEsytCaBM. 2) Is Ca2+ important for dEsyt localization, lipid exchange or both? The authors express a version of dEsyt with mutation made in all three C2 domains. In mammalian E-Syts, Ca2+ binding to the C2A domain is important for lipid exchange while binding to C2C (in E-Syt1) is important for interactions with lipids in the plasma membrane. Using more carefully designed mutants will allow the authors to determine how Ca2+ regulates dEsyt function in vivo. In addition, the authors must show experimentally that the mutant dEsytCaBM is unable to bind Ca2+ (could e.g. be done by acute Ca2+ changes in the cell-based model used in Fig. 3). Writing that "This transgene carrying a total of nine mutations should render the protein unable to bind calcium" (p. 6, line 173) is not sufficient.

      1) How is WT dEsyt localization regulated by Ca2+?

      We agree that further experimental evidence would be helpful in establishing the significance of cellular Ca2+ signaling in the control of dEsyt function. As suggested by the reviewer, the localization of wild type dEsyt will be examined in the mutants: norpAP24 (PLC null mutant) and trpl302; trp343 (protein null mutants of TRPL and TRP channels respectively) in which light induced calcium influx is eliminated. These data will be included in the revision.

      2) Is Ca2+ important for dEsyt localization, lipid exchange or both?

      We have already performed experiments to address the question of how important calcium binding to dEsyt is for lipid transport at the ER-PM interface in Drosophila photoreceptors. This results indicate a previously unexpected role for lipid exchange and will be included in the revision.

      3). Writing that "This transgene carrying a total of nine mutations should render the protein unable to bind calcium" (p. 6, line 173) is not sufficient.

      We concur with the reviewers that at present we do not have experimental data to demonstrate that dEsytCaBM can't bind Ca2+. However, as Reviewer 4 pointed out, it will be challenging to demonstrate this experimentally. A direct proof would only come from measurements of the calcium binding affinity of dEsyt (which involves protein purification that is beyond the scope of the current work). An indirect demonstration would be any cellular or in vivo experiment. In addition to the in silico analysis already included in Fig 2 C-F, we propose the following to provide additional evidence to strengthen our in silico analysis: Use AlphaFold model to demonstrate that the arrangement of the calcium binding residues in the C2 domain of dEsyt is compatible with Ca2+ binding.

      2) The localization of dEsyt shown in Fig. 3B is a bit confusing. First of all, I would recommend including markers of the ER and the plasma membrane, because without these it is difficult to make statements about the localization of dEsyt to these structures.

      As suggested, to better appreciate the localization of dEsyt in photoreceptors, we will perform colocalization of dEsyt with markers of the PM (Rhabdomere) and ER (Sub Microvillar Cisternae).

      Second, it appears that WT dEsyt localize to the reticular ER, and that the CaBM version localize to the plasma membrane. This is somewhat opposite to mammalian ESyts, where mutations that prevent Ca2+ binding either had no effect (for ESyt2) or prevented (for ESyt1) the interaction with the plasma membrane. It also appears different from the localization in vivo (Fig. 3C). Clarifying this will be important. It will also be important to connect this localization to changes in Ca2+ and not just to the localization of a mutant that may or may not be deficient in Ca2+ binding (see comment above).

      In considering this comment, we need to bear in mind the following:

      • Mammalian cells have three genes that encode for Esyt: Esyt 1, 2 and 3 whereas the Drosophila genome encodes only a single gene for Esyt.
      • In terms of sequence similarity and structure, dEsyt and hEsyt2 are very similar. However, in contrast to hEsyt2 and hEsyt3, which localize to the plasma membrane (PMID: 17360437), dEsyt acts like hEsyt1 and localizes to the ER-PM junctions.
      • A single study (PMID: 27065097) has shown that the SMP domain of Esyt1 can transfer lipids in an in vitro assay. In our studies, we have noted an unexpected function for the SMP domain of dEsyt for in vivo function as measured through phenotypes in the eye (data will be presented in the revised ms).
      • While knocking out the single dEsyt in Drosophila photoreceptor neurons results in phenotypes (Nath et.al PMID: 32716137) to date, knocking out all three Esyts in mammalian cell culture models or mice has not revealed an in vivo Bearing these points in mind it may not be reasonable to expect every observation on mammalian Esyt to be recapitulated in the fly system or vice versa. 3) I don't fully understand the time course of events. The authors show that dEsytCaBM is mislocalized already at day 1 in dark-reared flies (Fig. 3C) but this mislocalization is not accompanied by a change in MCS density or gap distance, and consistently does not influence the localization of RDGB. The authors next expose the flies to constant light illumination to trigger Ca2+ dependent signaling, and this leads to mislocalization of RDGB, perhaps indicating changes in MCS (this is not shown). From these results it is difficult to know what the role of dEsyt is. It would be necessary to also show a control where Ca2+ signaling is not induced, e.g. a parallel dark-control (same number of days but no illumination).

      It is important to remember that even complete loss of Esyt does not result in altered MCS or mislocalization of RDGB on day 1 post eclosion. This has been published by us previously (Nath et.al PMID: 32716137). Since we show in this manuscript that dEsytCaBM exerts a dominant negative effect when expressed in wild type and phenocopies dEsytKO, one might expect expression of dEsytCaBM to also lead to altered MCS density and mislocalization of RDGB by 6D constant light.

      Bearing this in mind, we will incorporate the following data in the manuscript: Addition of MCS density in dEsytKO photoreceptors at Day1 in Figure 3C.

      • Electron Microscopy to check MCS density in Rh1>dEsytCaBM at Day 6CL with appropriate control genotypes.
      • Confocal Imaging: RDGB staining in Rh1>dEsytCaBM- Day 6CD reared flies with appropriate control genotypes- dark control where only reduced Ca2+ signaling is induced due to dark noise or spontaneous PLC activation. This is particularly important given that the authors show in Fig. 1 that preventing Ca2+ influx had a dramatic impact on MCS density even at day 1 (which is in sharp contrast to dEsytCaBM-expressing flies, that show normal morphology at day 1, which rather implies that dEsyt is not a major Ca2+ effector).

      In thinking about this comment, it is important to bear in mind the details of the experimental paradigm in use in each of the experiments while drawing comparisons between the observed results. It is to be noted that throughout the manuscript dEsytCaBM is expressed selectively in photoreceptors using the Rhodopsin enhancer which drives expression of the transgene during late eye development. By contrast, in germ line mutant strains such as trpl302;trp343 the channels are blocked throughout development. Thus the phenotypes of trpl302;trp343 might be broader than that of expressing dEsytCaBM. Therefore, mutating the calcium binding residues of dEsyt and expressing it using Rh1 enhancer at a specific developmental time window might not have the same impact on the contact site density as completely blocking the major calcium permeable channels, TRP and TRPL that is important to sustain the ongoing phototransduction cascade all through the development.

      4) The experiments done in dEsyt KO flies are important, and here the authors show that dEsyt1 could to some extent rescue all phenotypes. Some results are a bit puzzling. For example, dEsyt1CaBM localization in dEsyt1 KO flies is identical to that of WT dEsyt (Fig. 5C), which is in sharp contrast to the data shown in Fig. 3C. What is the reason for this? I would have anticipated the opposite (i.e. that in WT flies, dEsytCaBM can form dimers with endogenous dEsyt through SMP-domain interactions which may have an impact on its localization and the function of endogenous dEsyt, but that in the dEsyt KO cells, dEsytCaBM would show a different localization due to the lack of endogenous dEyt to interact with). It is important to clarify as one of the major observations here is that dEsytCaBM no longer localize to MCS. Since the CaBM version of dEsyt could rescue, to some extent, MCS density and delay photoreceptor degeneration, this implies that Ca2+ may not be required for regulation of dEsyt function or that the mutant is still able to partially bind to Ca2+.

      The localization shown in Fig 5C is not of dEsytCaBM in dEsytKO photoreceptors but the localization of RDGB in Rh1>dEsytCaBM; dEsytKO at Day 1 (Figure 5C i) and as a function of age and illumination- Day 6CL (Figure 5C ii).

      One experiment that would help the authors determining the function of dEsyt in vivo would be to use a mutant that lacks functional SMP domain (ideally also with and without mutations in the C2-domains).

      There is information available to address the question of how the lipid binding module, SMP is important to render dEsyt functional at the ER-PM interface in Drosophila photoreceptors. The same will be included in the revision.

      5) PLC activation typically couples to rapid signaling and involved hydrolysis of PIP2 and release of Ca2+ from the ER. Mammalian Esyts also require PIP2 for plasma membrane binding (through interactions with C2-domains), so constitutive PLC activity would be expected to impair ESyt localization to MCS. Here, the authors expose flies for days of constant illumination. How does this influence plasma membrane PIP2 levels and could this be of relevance for how data is interpreted?

      This is an interesting question from the reviewer. However, we would like to clarify the fact that constitutive activation of PLC is different from constant activation of PLC during illumination. Flies have robust mechanisms for controlling PLC turnover and PIP2 levels during continuous illumination and Ca2+ is a key regulator of this process; the underlying mechanisms have been described by Raghu and Hardie in multiple past papers (PMID: 11343651, PMID: 15355960). This is why, apart from adaptation, flies grown in constant light for many days do not show electrophysiological defects and neither do they undergo retinal degeneration. We will however measure the kinetics of PIP2 resynthesis in (i) wild type (Day 1 vs Day 6CD vs Day 6CL) and (ii) Control, Rh1>dEsyt and Rh1>dEsytCaBM (Day 1 vs Day6CL). This might reveal some interesting insight into the mutants.

      Do the authors know whether the CaBM mutant has reduced affinity for PIP2?

      The ability of wild type dEsyt to bind PIP2 has not been determined. We will test this and if it does so, the impact of CaBM on PIP2 binding can be tested.

      Minor comments:

      • The overexpression of WT dEsyt had a dramatic impact on MCS density and gap distance, while expression of dEsytCaBM did not. If these contacts are important for photoreceptor function, is it not surprising that such a dramatic change in photoreceptor structure was without effect on function? This should be further discussed. The establishment of more contact sites and reduction in contact site distance in Rh1>dEsyt::GFP photoreceptors is likely indicative of the proposed tethering role of the protein at the ER-PM MCS. Increase in contact site density or reduction in distance need not directly parallel to the increase in the levels of MCS proteins that are expressed at these contact sites to enhance the ongoing signal transduction. We will test this idea proposed by the reviewer and include the following data in a revision to strengthen our statement:

      • RDGB levels in control vs Rh1>dEsyt::GFP - Western blot

      • Electroretinograms from the genotypes indicated above as a functional readout of the ongoing signaling cascade.
      • PIP2 kinetics in control vs Rh1>dEsyt::GFP to understand if establishing more contact sites can enhance the replenishment of the lipid at the PM. 2) How is quantification of MCS density and gap distance influenced by retinal degeneration (e.g. induced by dEsyt KO)?

      Wherever we have analyzed MCS density or gap distance, these experiments have been done in flies at ages prior to the onset of retinal degeneration defined as collapse of the microvilli of the rhabdomere. Therefore, our measurements of MCS density and gap in this paper are not affected by retinal degeneration.

      3) The graphical abstract is a bit confusing. It seems to suggest that changes in dEsyt is a consequence of ageing and does not show any role of this protein in photoreceptor function. I think that the abstract could be improved to more clearly highlight the findings in the manuscript. For example, it doesn't at all show the difference in localization between WT and CaBM.

      We will modify the graphical abstract.

      4) P. 5, line 135 the authors state that "The tethering and lipid transfer activity of mammalian Esyts are reported to be influenced by Ca2+". This is a massive understatement. Ca2+ is a critical regulator of Esyt function in mammalian cells.

      The statement will be modified.

      5) In figure legend 1B and C: correct µM to µm.

      Changes will be incorporated as per the suggestion.

      6) In figure legend 2A: should be red rectangles and not black rectangles.

      Changes will be incorporated as per the suggestion.

      7) In Fig. 2B: specify which isoform of human ESyt that is shown.

      Changes will be incorporated as per the suggestion.

      8) In Fig. 2C: do the authors mean D374 or D384 (as indicated in Fig. 2A)?

      Changes will be incorporated as per the suggestion; the residue is D374.

      Significance

      Light-induced signal transduction in photoreceptor cells involves Ca2+ influx and signaling and also depends on correct formation of ER-plasma membrane contact sites. In mammalian cells, the Esyts (esp. Esyt1 and Esyt2) localize to ER-PM contacts in a Ca2+-dependent manner, and the ion has dual effects in both enriching the protein at the membrane contact sites and in promoting lipid transport. Mammalian Esyts form homo- and heterodimers, and the properties of the dimers depends on their composition (PMID: 26202220). Drosophila only have one Esyt (dEsyt) which is structurally most similar to mammalian Esyt2, and the authors have previously shown how this protein is required for photoreceptor function (PMID: 32716137), although the role of Ca2+ was not investigated in that study. However, an earlier study has shown that mutations of all Ca2+-coordinating residues in dEsyt impairs protein function in Drosophila neurons (PMID: 28882990), so a similar Ca2+-dependence in the retina would be expected. The results from the present study confirm the requirement of Ca2+ signaling for dEsyt function, and extends this Ca2+-dependent regulation to also involve photoreceptor-induced Ca2+ signaling, which corroborates many other studies showing the requirement of Ca2+ signaling for the regulation of Esyt function in mammalian cells (e.g. PMID: 23791178; PMID: 27065097; PMID: 29222176; PMID: 26202220; PMID: 24183667; PMID: 30589572). As such, the results from this study represent an incremental step towards understanding Esyt function in vivo. These results would be of greatest interest to researchers working of photoreceptor function, and of some interest to a broader audience working on membrane contact sites and signal transduction. My own background is in mammalian cell biology, with a focus on lipid and Ca2+ signaling and inter-organelle communication. I have limited understanding of the model system used here (Drosophila photoreceptor cells).


      We would like to provide an alternative perspective on the reviewer’s view that “As such, the results from this study represent an incremental step towards understanding Esyt function in vivo.”

      We are well aware of the content in several studies of Esyt in mammalian cells including the ones cited by the reviewer (e.g. PMID: 23791178; PMID: 27065097; PMID: 29222176; PMID: 26202220; PMID: 24183667; PMID: 30589572). These have been cited in our manuscript. However, it is important to recognize that each of these studies is an analysis of the properties of mammalian Esyt as a molecule in the context of Ca2+. However, none of these studies addresses the key question of whether the regulation of Esyt by Ca2+ is important for cellular function or to support cell physiology. The reason for this is quite straightforward and well known in the field. To date, there is no cellular or physiological phenotype that is reported to depend on endogenous Esyt function in mammalian cellular or animal models. As an illustrative example, deletion of all three mammalian Esyt does not affect cell signalling (PMID 23791178) including Ca2+ signalling and a triple knockout of all three Esyt in mice (PMID: 27348751) has no discernable phenotype.

      By contrast, deletion of the single Esyt gene in Drosophila results in robust phenotypes in adult photoreceptors (PMID: 32716137). Using these phenotypes, in this manuscript we study the importance of Ca2+ dependent regulation of cellular functions mediated by dEsyt. Therefore, this study fills an important unfilled gap in establishing the mechanism by which dEsyt proteins regulate cellular functions in vivo, in a Ca2+ dependent manner. We respectfully ask that this not be caricatured as an incremental step.


      Reviewer #2

      Evidence, reproducibility and clarity

      Esyt is a C domain (a Ca2+ binding domain) containing protein that localizes to the ER-MCS, playing a role in ER-mitochondria tethering and lipid transfer. At the same time, proteins at the ER-MCS are well-positioned to sense changing levels of Ca2+. Previous studies reported that loss of Esyt in Drosophila causes a loss of ER-PM integrity and retinal degeneration. Here, the authors report the consequence of disrupting the Esyt C domain in Drosophila photoreceptor cells. They used in-silico strategies to identify the Ca2+ contacting residues within the C domain and generated transgenic flies containing either the wild type or the Esyt-CaBM mutants. They show that the wild type transgene rescues several Esyt KO phenotypes in the Drosophila photoreceptors. In some cases, they report dominant negative effects of Esyt-CaBM overexpression.

      This is a straightforward structure-function analysis of the Esyt C domain. Overall, the experiments are well executed. At the same time, a few aspects of the manuscript could be further improved. For example, the authors analyze multiple aspects of photoreceptor integrity. In some cases, they show that the mutant Esyt transgene shows dominant negative effects. In others, there is no evidence or even a partial function. Clarifying these points could be helpful. Below are a few specific points for the authors' consideration:

      Major Comments

      1. RDGB is a protein that localizes to the ER-MCS. Esyt-CABM-GFP expression causes RDGB mis-localization even in the presence of wild type Esyt expression, suggestive of a dominant negative effect (Fig. 4C). But Esyt CaBM-GFP expression doesn't seem to have a dominant negative effect on contact site distance (Fig. 4D). Are the authors not seeing a dominant negative effect because they didn't examine older flies? Or, is there a distinct effect of Esyt CaBM on RDGB localization and contact site distance? If there is a distinct effect, what is the reason? As the reviewer correctly mentions, we are not seeing a dominant negative effect of dEsytCaBM::GFP expression on contact site distance because we didn't examine older flies.

      Dominant negative effect of dEsytCaBM on the wild type protein is observed in all phenotypes analyzed. The contact site distance analysis shown in the paper is done on day 1 old constant dark reared flies. Contact site distance exhibited by dEsytCaBM is like that of dEsytKO photoreceptors at day 1 post eclosion. dEsyt deprived photoreceptors are comparable to its wild type counterpart at Day 1 in all aspects of phototransduction (PMID: 32716137). But as a function of age and illumination, the dEsytKO photoreceptors exhibit progressive loss in contact site integrity, followed by induction of retinal degeneration and RDGB mis-localisation (PMID: 32716137). These observations are consistent in dEsytCaBM.

      During the revision, the following experiments will be included to strengthen this statement:

      • Add the MCS density and gap distance in dEsytKO photoreceptors at Day1 in Figure 3C.
      • Electron Microscopy to check MCS density and distance in Rh1>dEsytCaBM at Day 6CL with appropriate control genotypes.

      Esyt-CABM-GFP partially rescues the Esyt KO phenotype in retinal degeneration (Fig 6). This is surprising since cellular assays in Fig 4 show a failure of Esyt-CaBM to localize to ER-MCS. The results here contrast with earlier data showing that Esyt-CABM has dominant negative effects. How will the authors interpret the results? Is it possible that Esyt-CAMB still has some residual Ca2+ binding activity? Alternatively, does this result imply that Esyt can still function (albeit at lower capacity) without binding Ca2+? Is there Esyt function unrelated to ER-MCS site maintenance when it comes to its role in retinal degeneration? A reasonable explanation is warranted.

      Partial rescue of dEsytKO phenotypes by Rh1>dEsytCaBM; dEsytKO photoreceptors indicate that apart from calcium sensing, there might be another function for dEsyt at the ER-PM interface which is yet to be discovered.


      Minor Comments:

      Figure legends refer to "SMC" (I am guessing they are referring to Sub microvillar cisternae) without defining it in the text.

      Changes will be incorporated as per the suggestion.


      Significance

      This study will be of interest to those generally interested in the ER mitochondria contact sites. The main significance here is in dissecting the role of the C-domain within the Esyt protein. The authors demonstrate a physiological role using Drosophila photoreceptors as a model.

      We thank the reviewer for appreciating the significance of our study which seeks to show the in vivo significance of the Ca2+ regulation of dEsyt for in vivo function.

      __Reviewer #3 __

      (Evidence, reproducibility and clarity (Required)):

      Summary

      In the present work, the authors explore the role of Ca2+ binding to Esyt in the regulation of ER-PM contact sites using drosophila photoreceptors as a model system. By expressing in wild type or in EsytKO flies a mutated version of dEsyt which is predicted to lose Ca2+ binding, they highlight a potential role of Ca2+ binding to Esyt in the regulation of ER-PM contact sites density and the development of rhabdomeres. The data clearly show the effect of Esyt mutant during development of photoreceptors in Drosophila. However, as discussed below, one essential missing point is the experimental proof that the mutant has indeed lost its ability to bind Ca2+, and that PIP2 binding is not perturbed.

      Major comments

      1. One major comment is the lack of experimental proof that the EsytCABM mutant is indeed unable to bind Ca2+. The MIB tool only gives a prediction and it is not sufficient to prove their statements throughout the manuscript on the requirement of Ca2+ binding for the regulation of MCS. We understand the reviewer’s comment that this manuscript does not contain experimental data demonstrating that dEsytCaBM does not bind Ca2+. However, as Reviewer 4 pointed out, it will be challenging to demonstrate this experimentally. A direct proof would likely come from measurements of the calcium binding affinity of dEsyt (which involves protein purification that is beyond the scope of this work). An indirect demonstration would be any cellular or in vivo experiment oar any additional in silico analysis. To provide additional indirect evidence to address this question, we will:

      2. Use the AlphaFold model to demonstrate that the arrangement of the calcium binding residues in dEsyt is compatible with Ca2+

      3. Evaluate if the wild type dEsyt is mislocalized in the photoreceptors upon eliminating the calcium entry to these specialized sensory neurons. The localization of wild type dEsyt will be examined in the mutants: norpAP24 (PLC null mutant) and trpl302; trp343 (protein null mutant of TRPL and TRP channels respectively) in which light induced calcium influx is eliminated. Moreover, they should check experimentally the potential differences in the capacity of EsytCABM mutant to bind PI(4,5)P2, which can potentially perturb its subcellular localization.

      As recommended by the reviewer, it is important to determine the PIP2 binding capacity of dEsytCaBM. The ability of wild type dEsyt to bind PIP2 has not been determined. We will test this and if it does so, the impact of CaBM on PIP2 binding can be tested.

      Figure 1A: the legend on the right side of the scheme is missing. On the left, RDGB and dEsyt don't associate with the PM.

      Changes will be incorporated as per the suggestion.

      line 125: the authors should describe more precisely the Trp mutant that they used.

      The text will be modified.

      Concerning the quantification of MCS density done throughout the paper, can the authors mention what they considered as an MCS, in other words, what distance they defined as the maximal distance between the ER and the PM.

      We used fixation methods that allow enhanced membrane preservation and better visualization of membranes and MCS (PMID: 2496206). Such images allowed us to quantify the fraction of SMC that are present at the base of the microvilli in each ultrathin section of a photoreceptor. The MCS is the dark stretch that can be seen at the base of the rhabdomere in each TEM image (PMID: 32716137). Contact site distance measured is the absolute distance between the visible demarcation of the PM and SMC as indicated by the yellow arrows in Figure 4D iii, vi, and ix.

      Figure 3: the localization of Esyt and EsytCABM in S2R cells and in vivo is not precisely analyzed: a co-staining with PM and ER markers should be added in order to state the localization at ER-PM MCS or at apical PM.

      As suggested, to better understand the compartmental localization of dEsyt in photoreceptors, we will use markers of PM (Rhabdomere) and ER (Sub Microvillar Cisternae) and conduct co-localization assays.

      line 181: the authors should precise in which membrane compartments Esyt is localized.

      The text will be modified.

      line 185-187: the conclusion here doesn't seem to fit the data, as the EsytCABM mutant looks enriched at ER-PM contact sites.

      As previously answered, we will remark on whether there is an enrichment of dEsytCaBM at the ER-PM contact sites following the co-localization experiment that is recommended in Q5.

      a paragraph on the production of Drosophila transgene mutants should be added to the Mat et Med section.

      The text will be added as suggested.

      considering the phenotypes observed for the EsytCABM mutant in vivo, the authors should provide an analysis of the level of expression of the exogenous proteins Esyt and EsytCABM by western blot in the different backgrounds. EsytCABM seems to be expressed at lower levels in Figure 3C.

      As per the suggestion, western blot analysis will be conducted and better representative confocal images depicting the protein levels will be added in the manuscript.

      Fig 4D: considering the perturbation of RDGB localization observed at Day 6, the authors should analyze the organization of MCS by TEM at Day 6, in addition to Day 1.

      We agree that to support the observation of RDGB mis-localization, the decrease in contact site integrity as a function of age and illumination (Day6CL) should be evaluated in Rh1>dEsytCaBM photoreceptors. The manuscript revision will include data from this experiment.

      the EsytCABM mutant exhibits strong dominant negative effects, but rescues completely or partially some of the phenotypes of Esyt KO: could the authors discuss and provide some hypothesis on this apparent discrepancy?

      We are unsure what the reviewer means by “apparent discrepancy”. When dEsytCaBM is expressed in wild type photoreceptors, it exhibits a strong dominant negative effect presumably by inhibiting the function of wild type dEsyt protein.

      dEsytKO is a protein null allele. Therefore, when dEsytCaBM is expressed in the dEsytKO background it does not exert a dominant negative effect as there is no wild type protein to interact with. The partial rescue of dEsytKO phenotypes by Rh1>dEsytCaBM; dEsytKO photoreceptors likely indicates that calcium binding is not the sole factor affecting dEsyt function at the ER-PM interface.

      lines 230-233: the sentence is not clear. I don't see any consistency between data in Figure 5B, showing only very partial rescue by EsytCABM, and the data in Figure 5C (ii) showing complete rescue of RDGB localization by EsytCABM.

      The time point (six days of continuous light exposure following eclosion) at which RDGB localization was analyzed becomes extremely important in thinking about this reviewer comment. If we look at the degeneration kinetics depicted in figure 5B, we can see that neurodegeneration begins in both dEsytKO and Rh1>dEsytCaBM on Day 8 post-eclosion; prior to which, on Day 6, RDGB is mislocalized from the base. However, in Rh1>dEsytCaBM; dEsytKO, the onset of degeneration is delayed, and the photoreceptors show intact structure until Day 8 or Day 10, and measurable retinal degeneration begins on Day 12. This may be the reason why, RDGB continues to be correctly localized in Rh1>dEsytCaBM; dEsytKO at Day 6CL.

      Figure 6D: could the authors comment the increase of MCS density observed in Esyt-GFP expressing flies.

      Esyt is proposed to function as a tether that connects the ER and PM (PMID: 23791178; PMID: 27065097; PMID: 29222176), bringing them closer together. Based on this idea, perhaps by expressing dEsyt::GFP we are drawing the membranes together thus establishing more MCS.

      on several TEM images, some pictures illustrating different conditions look very similar, as if they were serial cuts: Fig 1B (Day 1 and Day 14), Fig 4D (Rh1 and Rh1>dEsytCABM::GFP), Fig 6B Day 1 and Day 14 and Fig 6C Day 1. Could the authors check if there was a mistake with these pictures?

      The images are not taken from serial sections of the same TEM block as is evident from the arrangement of nucleus of each photoreceptor cell. As mentioned in the figure legends, all experiments are carried out using 3 independent blocks (N=3 fly heads) prepared from each genotype and 10 photoreceptors from each block/ fly retinae are used for quantification of contact site density/ contact site distance. Aside from the arrangement of the accessory cells and cellular nuclei, the TEM images will appear very similar since Drosophila photoreceptor neurons are symmetrically arranged, with around 700–800 ommatidia per eye each comprising 8 photoreceptors.

      Minor comments:

      • lines 84-88 : the sentence is not clear. Besides, the authors should precise what they mean by "extra-cellular Ca2+ influx enhance ER-PM contact sites". Which parameter exactly has been shown to be regulated by Ca2+?

      The paper by Idevall-Hagren et al. proposes that following store operated Ca2+ influx, Esyt1 translocates to ER-PM junctions and the number of ER-PM contact sites increases. Please refer to this section of the publication from Idevall-Hagren et al. (2015) (PMID: 26202220):

      “As detected by TIRF microscopy, the depletion of Ca2+ from the lumen of the ER occurring under these conditions led to a progressive accumulation of ER‐anchored STIM1 at the PM, where it activates Orai Ca2+ channels (Fig 4C). Subsequent addition of 1–10 mM Ca2+ to the extracellular medium, either in the absence or in the presence of SERCA inhibitors, caused a massive increase in cytosolic Ca2+ (SOCE) through the activated Ca2+ channels (Figs 4A and EV4D–G). Such increase induced a very robust translocation of E‐Syt1 to the PM (Figs 4B and EV4D–G), which, in the absence of SERCA inhibition (i.e., when a reversible inhibitor of the SERCA pump had been washed out), preceded the dissociation of STIM1 and the inactivation of SOCE (Fig 4D). Inspection of TIRF microscopy images during the manipulation showed that E‐Syt1 does not form new contacts but populates and expands contacts previously occupied by STIM1.”

      • lines 108-110: can you give the reference?

      Reference for the localization of dEsyt to ER-PM MCS is Nath et.al PMID PMID: 32716137

      Reference for the localization of TRP and TRPL at the microvillar plasma membrane: Numerous primary research papers have shown this- for example see review PMID: 11557987, PMID: 22487656

      • line 189: the authors should summarize the findings in one sentence. "Functional activity" would refer to lipid transfer.

      The text will be modified as per the suggestion.

      Reviewer #3 (Significance (Required)):

      General assessment

      The work relies on a model system that enables the exploration of the role of Esyt in vivo, in a fundamental process highly regulated during development. The data clearly show the effect of Esyt mutant during development of photoreceptors in Drosophila but as discussed before, some experimental evidences are missing to completely prove the statements.

      Advance

      This work brings new insights in the functional role of lipid transfer during development and explores how the dialog between lipid transfer and Ca2+ flux can influence MCS organization. The interesting points that could be explored in the paper are the effects of a Ca2+ influx on Esyt and EsytCABM localization, and on their lipid transfer activity.

      Audience

      This work would be of interest for the membrane contact sites community and for the Developmental biology community.

      We thank the reviewer for highlighting the significance of our work and the clarity of the data. Additional data to address the points they have raised will be provided.

      __Reviewer #4 __

      (Evidence, reproducibility and clarity (Required)):

      In this study, Nath et al., aim at understanding the role of dESyt Ca2+ binding activity on ER-PM MCS in D. melanogaster photoreceptors. Using a combination of transmission electron microscopy and fluorescence microscopy, the authors explore the ability of a dESyt mutant, supposedly unable to bind Ca2+ (based on homology with the human ortholog hESyt2), to recapitulate the function of the wild type version of the protein in establishing ER-PM MCS and modulating their density.

      Findings:

      1) MCS density depends on the activity of TRP and TRPL channels in aging photoreceptors.

      2) Mutation of dESyt Ca2+ binding residues (dEsytCaBM::GFP) leads to a gross mis-localization of the protein, even in the presence of the endogenous protein.

      3) Overexpression of the mutant affects the structure of photoreceptors upon constant illumination.

      4) After 6 days of continuous illumination, RDGB is mis-localized in cells overexpressing dEsytCaBM::GFP.

      5) Overexpressed dEsytCaBM::GFP fails to reduce the distance between ER and PM, meaning it fails to establish ER-PM contract sites, while overexpressed dEsyt::GFP show reduced MCS distance. Overexpressed dEsyt::GFP also leads to a 10% increase in MCS density compared to WT or cells expressing dEsytCaBM::GFP.

      6) dEsytCaBM::GFP is not able to rescue the light dependent retinal degeneration of dESytKO, although it slightly delays the onset, but is able to rescue RDGB localization at day 6 of constant illumination.

      7) Examining MCS density in dESytKO cells, rescues with dEsyt::GFP and dEsytCaBM::GFP show a slightly higher MCS density than dESytKO at day 1. At day 14, ER-PM MCS were non-existent in dESytKO, unchanged in dEsyt::GFP and reduced by 20% in dEsytCaBM::GFP compared to day1.

      Specific comments:

      My field of expertise is biochemistry and structural biology (including cellular cryo-electron tomography), but I have no experience with drosophila biology, so I am not able to judge the drosophila work per se.

      While I find the confocal microscopy experiments compelling, I have some reservations regarding the quantification of the TEM images (MCS distances and density) as it was done manually, and therefore, to some extent subjective, especially, when differences between conditions are in the order of 10%. I would have found the quantification more convincing if done systematically, i.e. segmenting the MCS and computationally measuring distances and densities. Otherwise, the authors could expand a little bit on how their methodology is accurate.

      As the reviewer correctly mentions, the quantification will be more convincing if done systematically, i.e. segmenting the MCS and computationally measuring distances and densities. For MCS measurements, we have experimented with the segmentation method using ImageJ and Imaris. As mentioned in the answer to Q4 of reviewer 3, we used fixation methods that allow enhanced membrane preservation and better visualization of membranes and MCS (Matsumoto‐Suzuki et al, 1989). However, this staining method does not selectively stain the ER which is part of the MCS but all the ER. Due to this, automated segmentation poses significant challenges.

      The primary drawback of the segmentation method is that, in the process of training the software to predict/detect distinct cellular compartments, it recognizes all ER membranes, including SMC as well as the ER that is not part of the MCS. As a result, the software's minimum distance calculation may be between PM and SMC or PM and generic ER, which does not help the analysis we wish to perform. Similarly, to determine the contact site distance in images with obscure ER and PM boundaries, the software uses the border it can identify—which is typically inside the rhabdomere rather than at its edge. For the contact site density measurements, software is not able to distinguish between ER and pigment granules close to the rhabdomere as the gray scale value for both these compartments are comparable.

      Advantages of manual approach:

      To account for potential effects of photoreceptor depth on contact site density and distance, we have analyzed TEM sections obtained directly from the nuclear plane of the photoreceptors to calculate both contact site density and distance. Additionally, by utilizing the freehand line tool, manual analysis enables us to define the length of each little section of the MCS and the base of the rhabdomere. The entire length of the MCS at the base is then calculated by adding each segment together. An illustration of how the manual analysis is done will be included as part of methods in the revision.

      Another point is whether the levels of expression of dESyt proteins (dESyt-GFP and dESytCABM-GFP) are comparable. In the overexpression experiments, what are the expression levels of the constructs compared to the endogenous protein? The authors should provide e.g. a Western blot.

      As per the suggestion, western blot analysis will be conducted to compare the expression levels of the constructs utilized to the endogenous protein.

      Concerning the modelling, while I do think that the identification of dESyt Ca2+ binding residues is correct (the sequence alignment is convincing and the sequence identity is very high), and that most likely the structural arrangement will be conserved, homology modelling (using MODELLER with a single reference) leads to models highly similar to the input reference (in particular when the sequence identity is very high). Therefore, rmsd will necessarily be low and the side chain arrangement of conserved residues will be identical. This is unlikely to happen, as protein structures will not be identical despite high sequence conservation. In addition, a crystal structure is a snapshot of a protein conformation that is favorable for crystal formation. It would have been more interesting to use an AlphaFold model and show that the arrangement on the residues is compatible with Ca2+ binding (i.e., the C positions are similar).

      We agree with the reviewer that the data presented to demonstrate the inability of dEsytCaBM to bind Ca2+ is inadequate as is also pointed out by other reviewers. It would be crucial to prove this using multiple approaches. As suggested AlphaFold model will be used to answer the same.

      Minor comments:

      Line 102: indicate what PI and PA stand for (I don't think that there is a need for acronyms when they are not reused in the text later on).

      Changes will be incorporated as per the suggestion.

      Line 217-219: "When the same experimental set was examined for MCS density, we discovered that the density enhanced by 10% in Rh1>dEsyt::GFP while being comparable between wild type and dEsytCaBM::GFP flies." The authors don't comment on this finding. Does that imply that increase in the protein levels leads to increase in MCS density?

      Yes. Increase in wild type dEsyt protein levels can establish more contact sites as well as reduce the contact site distance which further elucidates the protein's role in functional tethering as mentioned in line 215 as proposed by previous studies in other models (PMID: 23791178; PMID: 27065097; PMID: 29222176).

      Lines 298-302: "...implying that dEsytCaBM exerts a dominant negative effect on wild type dEsyt. One possible mechanism for the phenotypes exhibited by dEsytCaBM expression in wild type cells is suggested by the findings of a structural and mass spectrometry investigation of hEsyt2 that reveals that the SMP domain dimerizes to create a 90Å long cylinder to facilitate the transfer of lipids (Schauder et al., 2014)." It is not clear to me what the authors suggest here: because of the dimerisation between wild type and mutant, the mutant has a negative effect or that the SMP dimerization is somehow impaired in dEsytCaBM?

      SMP domain of Esyt proteins have previously been shown to dimerize (PMID: 23791178, PMID: 24847877). They are known to form either homodimers or heterodimers in mammalian system where there are three genes that code for the protein (Esyt1, 2 and 3). In Drosophila, since it is just one gene that codes for the protein, our hypothesis is that one copy of the functional wild type gene dimerizes with the CaBM mutant and thereby render the wild type gene product nonfunctional.

      Line 304-305: "...protein expression was restricted to the cell body rather than the presynaptic terminals...". I am not sure that this is correct. The fact that a protein is localizing to a compartment does not mean that its expression is restricted to that compartment (one should measure mRNA levels to conclude this).

      The statement is based on the findings made by Kikuma et al, 2017 (PMID: 28882990) when they tried to understand the role of dEsyt at the NMJs.

      In figure 1B legend, indicate what SMC stands for (the acronym should be indicated in figure 1A legend).

      The text will be added as suggested.

      In figure 2A legend Ca binding in black box but in red boxes in figure.

      Changes will be incorporated as per the suggestion.

      **Referees cross-commenting**

      I agree with the other reviewers that one of the premise of this study relies on the loss of calcium binding by the dESyt mutant and this is not experimentally proven by the authors. However, I find that this will be difficult to prove in vivo. Only measurements of dESyt calcium binding affinity would constitute a direct proof (which requires protein purification. Any in vivo or cellular experiment would be an indirect proof. I believe that based on the high sequence conservation with ESyt proteins, the calcium binding residues have been correctly identified.

      Reviewer #4 (Significance (Required)):

      ESyt proteins are known ER-PM tethers involved in lipid transfer at MCS in a Ca2+ dependent manner. Contrary to yeast and mammals, that have several ESyt orthologs, D. melanogaster has only one ESyt, making it an ideal model to study ESyt function in vivo. It has been previously shown that proper localization of ESyt at MCS depends on Ca2+ concentration: ESyts are anchors to the ER but translocate to the PM in response to elevation of Ca2+ levels in the cytosol (Fernández-Busnadiego et al., 2015). The finding that an ESyt mutant unable to bind calcium is not localized properly is therefore not surprising. The link between RDGB, a protein known to localize at MCS, and ESyt has been shown before but to my knowledge Nath et al., show for the first time that RDBG localization at MCS is directly dependent on the Ca2+ binding activity of ESyt. In addition, the authors convincingly demonstrate that the Ca2+ binding activity of dESyt is necessary to maintain the structure of aging photoreceptors.

      The main finding of this study is that the Ca2+ binding activity of dESyt regulates the density of ER-PM MCS in photoreceptors. If true (see my comment below), that would be a novel finding, although the authors don't propose any mechanistic explanation for this.

      3. Description of the revisions that have already been incorporated in the transferred manuscript

      Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

      We haven't made any changes to the manuscript yet. However, we will be able to implement the changes mentioned in the pointwise response to reviewers above.

      4. Description of analyses that authors prefer not to carry out

      Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

      • *

      We feel that experiments to directly determine the calcium binding of dEsyt and the loss of this in dEsytCaBM are beyond the scope of this study. This is because of the huge work to heterologously express and purify the protein. We have proposed alternate ways to strengthen this conclusion.

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      Referee #4

      Evidence, reproducibility and clarity

      In this study, Nath et al., aim at understanding the role of dESyt Ca2+ binding activity on ER-PM MCS in D. melanogaster photoreceptors. Using a combination of transmission electron microscopy and fluorescence microscopy, the authors explore the ability of a dESyt mutant, supposedly unable to bind Ca2+ (based on homology with the human ortholog hESyt2), to recapitulate the function of the wild type version of the protein in establishing ER-PM MCS and modulating their density.

      Findings:

      1. MCS density depends on the activity of TRP and TRPL channels in aging photoreceptors.
      2. Mutation of dESyt Ca2+ binding residues (dEsytCaBM::GFP) leads to a gross mis-localization of the protein, even in the presence of the endogenous protein.
      3. Overexpression of the mutant affects the structure of photoreceptors upon constant illumination.
      4. After 6 days of continuous illumination, RDGB is mis-localized in cells overexpressing dEsytCaBM::GFP.
      5. Overexpressed dEsytCaBM::GFP fails to reduce the distance between ER and PM, meaning it fails to establish ER-PM contract sites, while overexpressed dEsyt::GFP show reduced MCS distance. Overexpressed dEsyt::GFP also leads to a 10% increase in MCS density compared to WT or cells expressing dEsytCaBM::GFP.
      6. dEsytCaBM::GFP is not able to rescue the light dependent retinal degeneration of dESytKO, although it slightly delays the onset, but is able to rescue RDGB localization at day 6 of constant illumination.
      7. Examining MCS density in dESytKO cells, rescues with dEsyt::GFP and dEsytCaBM::GFP show a slightly higher MCS density than dESytKO at day 1. At day 14, ER-PM MCS were non-existent in dESytKO, unchanged in dEsyt::GFP and reduced by 20% in dEsytCaBM::GFP compared to day1.

      Specific comments:

      My field of expertise is biochemistry and structural biology (including cellular cryo-electron tomography), but I have no experience with drosophila biology, so I am not able to judge the drosophila work per se. While I find the confocal microscopy experiments compelling, I have some reservations regarding the quantification of the TEM images (MCS distances and density) as it was done manually, and therefore, to some extent subjective, especially, when differences between conditions are in the order of 10%. I would have found the quantification more convincing if done systematically, i.e. segmenting the MCS and computationally measuring distances and densities. Otherwise, the authors could expand a little bit on how their methodology is accurate.

      Another point is whether the levels of expression of dESyt proteins (dESyt-GFP and dESytCABM-GFP) are comparable. In the overexpression experiments, what are the expression levels of the constructs compared to the endogenous protein? The authors should provide e.g. a Western blot.

      Concerning the modelling, while I do think that the identification of dESyt Ca2+ binding residues is correct (the sequence alignment is convincing and the sequence identity is very high), and that most likely the structural arrangement will be conserved, homology modelling (using MODELLER with a single reference) leads to models highly similar to the input reference (in particular when the sequence identity is very high). Therefore, rmsd will necessarily be low and the side chain arrangement of conserved residues will be identical. This is unlikely to happen, as protein structures will not be identical despite high sequence conservation. In addition, a crystal structure is a snapshot of a protein conformation that is favorable for crystal formation. It would have been more interesting to use an AlphaFold model and show that the arrangement on the residues is compatible with Ca2+ binding (i.e., the C positions are similar).

      Minor comments:

      Line 102: indicate what PI and PA stand for (I don't think that there is a need for acronyms when they are not reused in the text later on).

      Line 217-219: "When the same experimental set was examined for MCS density, we discovered that the density enhanced by 10% in Rh1>dEsyt::GFP while being comparable between wild type and dEsytCaBM::GFP flies." The authors don't comment on this finding. Does that imply that increase in the protein levels leads to increase in MCS density?

      Lines 298-302: "...implying that dEsytCaBM exerts a dominant negative effect on wild type dEsyt. One possible mechanism for the phenotypes exhibited by dEsytCaBM expression in wild type cells is suggested by the findings of a structural and mass spectrometry investigation of hEsyt2 that reveals that the SMP domain dimerizes to create a 90Å long cylinder to facilitate the transfer of lipids (Schauder et al., 2014)." It is not clear to me what the authors suggest here: because of the dimerisation between wild type and mutant, the mutant has a negative effect or that the SMP dimerization is somehow impaired in dEsytCaBM?

      Line 304-305: "...protein expression was restricted to the cell body rather than the presynaptic terminals...". I am not sure that this is correct. The fact that a protein is localizing to a compartment does not mean that its expression is restricted to that compartment (one should measure mRNA levels to conclude this).

      In figure 1B legend, indicate what SMC stands for (the acronym should be indicated in figure 1A legend).

      In figure 2A legend Ca binding in black box but in red boxes in figure.

      Referees cross-commenting

      I agree with the other reviewers that one of the premise of this study relies on the loss of calcium binding by the dESyt mutant and this is not experimentally proven by the authors. However, I find that this will be difficult to prove in vivo. Only measurements of dESyt calcium binding affinity would constitute a direct proof (which requires protein purification. Any in vivo or cellular experiment would be an indirect proof. I believe that based on the high sequence conservation with ESyt proteins, the calcium binding residues have been correctly identified.

      Significance

      ESyt proteins are known ER-PM tethers involved in lipid transfer at MCS in a Ca2+ dependent manner. Contrary to yeast and mammals, that have several ESyt orthologs, D. melanogaster has only one ESyt, making it an ideal model to study ESyt function in vivo. It has been previously shown that proper localization of ESyt at MCS depends on Ca2+ concentration: ESyts are anchors to the ER but translocate to the PM in response to elevation of Ca2+ levels in the cytosol (Fernández-Busnadiego et al., 2015). The finding that an ESyt mutant unable to bind calcium is not localized properly is therefore not surprising. The link between RDGB, a protein known to localize at MCS, and ESyt has been shown before but to my knowledge Nath et al., show for the first time that RDBG localization at MCS is directly dependent on the Ca2+ binding activity of ESyt. In addition, the authors convincingly demonstrate that the Ca2+ binding activity of dESyt is necessary to maintain the structure of aging photoreceptors.

      The main finding of this study is that the Ca2+ binding activity of dESyt regulates the density of ER-PM MCS in photoreceptors. If true (see my comment below), that would be a novel finding, although the authors don't propose any mechanistic explanation for this.

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      Referee #3

      Evidence, reproducibility and clarity

      Summary

      In the present work, the authors explore the role of Ca2+ binding to Esyt in the regulation of ER-PM contact sites using drosophila photoreceptors as a model system. By expressing in wild type or in EsytKO flies a mutated version of dEsyt which is predicted to lose Ca2+ binding, they highlight a potential role of Ca2+ binding to Esyt in the regulation of ER-PM contact sites density and the development of rhabdomeres. The data clearly show the effect of Esyt mutant during development of photoreceptors in Drosophila. However, as discussed below, one essential missing point is the experimental proof that the mutant has indeed lost its ability to bind Ca2+, and that PIP2 binding is not perturbed.

      Major comments

      • One major comment is the lack of experimental proof that the EsytCABM mutant is indeed unable to bind Ca2+. The MIB tool only gives a prediction and it is not sufficient to prove their statements throughout the manuscript on the requirement of Ca2+ binding for the regulation of MCS. Moreover, they should check experimentally the potential differences in the capacity of EsytCABM mutant to bind PI(4,5)P2, which can potentially perturb its subcellular localization.
      • Figure 1A: the legend on the right side of the scheme is missing. On the left, RDGB and dEsyt don't associate with the PM.
      • line 125: the authors should describe more precisely the Trp mutant that they used.
      • concerning the quantification of MCS density done throughout the paper, can the authors mention what they considered as an MCS, in other words, what distance they defined as the maximal distance between the ER and the PM.
      • Figure 3: the localization of Esyt and EsytCABM in S2R cells and in vivo is not precisely analyzed: a co-staining with PM and ER markers should be added in order to state the localization at ER-PM MCS or at apical PM.
      • line 181: the authors should precise in which membrane compartments Esyt is localized.
      • line 185-187: the conclusion here doesn't seem to fit the data, as the EsytCABM mutant looks enriched at ER-PM contact sites.
      • a paragraph on the production of Drosophila transgene mutants should be added to the Mat et Med section.
      • considering the phenotypes observed for the EsytCABM mutant in vivo, the authors should provide an analysis of the level of expression of the exogenous proteins Esyt and EsytCABM by western blot in the different backgrounds. EsytCABM seems to be expressed at lower levels in Figure 3C.
      • Fig 4D: considering the perturbation of RDGB localization observed at Day 6, the authors should analyze the organization of MCS by TEM at Day 6, in addition to Day 1.
      • the EsytCABM mutant exhibits strong dominant negative effects, but rescues completely or partially some of the phenotypes of Esyt KO: could the authors discuss and provide some hypothesis on this apparent discrepancy?
      • lines 230-233: the sentence is not clear. I don't see any consistency between data in Figure 5B, showing only very partial rescue by EsytCABM, and the data in Figure 5C (ii) showing complete rescue of RDGB localization by EsytCABM.
      • Figure 6D: could the authors comment the increase of MCS density observed in Esyt-GFP expressing flies.
      • on several TEM images, some pictures illustrating different conditions look very similar, as if they were serial cuts: Fig 1B (Day 1 and Day 14), Fig 4D (Rh1 and Rh1>dEsytCABM::GFP), Fig 6B Day 1 and Day 14 and Fig 6C Day 1. Could the authors check if there was a mistake with these pictures?

      Minor comments:

      • lines 84-88 : the sentence is not clear. Besides, the authors should precise what they mean by "extra-cellular Ca2+ influx enhance ER-PM contact sites". Which parameter exactly has been shown to be regulated by Ca2+?
      • lines 108-110: can you give the reference?
      • line 189: the authors should summarize the findings in one sentence. "Functional activity" would refer to lipid transfer.

      Significance

      General assessment

      The work relies on a model system that enables the exploration of the role of Esyt in vivo, in a fundamental process highly regulated during development. The data clearly show the effect of Esyt mutant during development of photoreceptors in Drosophila but as discussed before, some experimental evidences are missing to completely prove the statements.

      Advance

      This work brings new insights in the functional role of lipid transfer during development and explores how the dialog between lipid transfer and Ca2+ flux can influence MCS organization. The interesting points that could be explored in the paper are the effects of a Ca2+ influx on Esyt and EsytCABM localization, and on their lipid transfer activity.

      Audience

      This work would be of interest for the membrane contact sites community and for the Developmental biology community.

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      Referee #2

      Evidence, reproducibility and clarity

      Esyt is a C domain (a Ca2+ binding domain) containing protein that localizes to the ER-MCS, playing a role in ER-mitochondria tethering and lipid transfer. At the same time, proteins at the ER-MCS are well-positioned to sense changing levels of Ca2+. Previous studies reported that loss of Esyt in Drosophila causes a loss of ER-PM integrity and retinal degeneration. Here, the authors report the consequence of disrupting the Esyt C domain in Drosophila photoreceptor cells. They used in-silico strategies to identify the Ca2+ contacting residues within the C domain and generated transgenic flies containing either the wild type or the Esyt-CaBM mutants. They show that the wild type transgene rescues several Esyt KO phenotypes in the Drosophila photoreceptors. In some cases, they report dominant negative effects of Esyt-CaBM overexpression.

      This is a straightforward structure-function analysis of the Esyt C domain. Overall, the experiments are well executed. At the same time, a few aspects of the manuscript could be further improved. For example, the authors analyze multiple aspects of photoreceptor integrity. In some cases, they show that the mutant Esyt transgene shows dominant negative effects. In others, there is no evidence or even a partial function. Clarifying these points could be helpful. Below are a few specific points for the authors' consideration:

      Major

      1. RDGB is a protein that localizes to the ER-MCS. Esyt-CABM-GFP expression causes RDGB mis-localization even in the presence of wild type Esyt expression, suggestive of a dominant negative effect (Fig. 4C). But Esyt CaBM-GFP expression doesn't seem to have a dominant negative effect on contact site distance (Fig. 4D). Are the authors not seeing a dominant negative effect because they didn't examine older flies? Or, is there a distinct effect of Esyt CaBM on RDGB localization and contact site distance? If there is a distinct effect, what is the reason?
      2. Esyt-CABM-GFP partially rescues the Esyt KO phenotype in retinal degeneration (Fig 6). This is surprising since cellular assays in Fig 4 show a failure of Esyt-CaBM to localize to ER-MCS. The results here contrast with earlier data showing that Esyt-CABM has dominant negative effects. How will the authors interpret the results? Is it possible that Esyt-CAMB still has some residual Ca2+ binding activity? Alternatively, does this result imply that Esyt can still function (albeit at lower capacity) without binding Ca2+? Is there Esyt function unrelated to ER-MCS site maintenance when it comes to its role in retinal degeneration? A reasonable explanation is warranted.

      Minor:

      Figure legends refer to "SMC" (I am guessing they are referring to Sub microvillar cisternae) without defining it in the text.

      Significance

      This study will be of interest to those generally interested in the ER mitochondria contact sites. The main significance here is in dissecting the role of the C-domain within the Esyt protein. The authors demonstrate a physiological role using Drosophila photoreceptors as a model.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      This study builds on previous work from the same group, where they use Drosophila photoreceptors as a model system to investigate the role or ER-plasma membrane contact sites in an in vivo setting. The authors recently described a role of the ER-PM contact site protein dEsyt in regulating photoreceptor function in Drosophila. In this follow-up study, they explore whether this function of dEsyt is connected Ca2+ signaling downstream of photoreceptor activation. Using a dEsyt mutant that should be unable to bind Ca2+, they find that Ca2+ to some extent is required for dEsyt localization, membrane contact site formation and photoreceptor function.

      Major comments:

      The use of photoreceptor cells in Drosophila is an elegant model system that enable studies of membrane contact sites and associated proteins in a native condition. The data presented by the authors clearly shows that these structures are important for photoreceptor function, and that dEsyt plays a role at these sites. However, this was already known from previous studies by the same group. When it comes to whether these contacts are sensing Ca2+ changes and if these changes are acting through dEsyt, which is the focus of the current manuscript, the results are unclear to me and would need to be clarified by the authors both in text and with new experiments.

      1. What is the role of cellular Ca2+ signaling in the regulation of dEsyt function? There are several aspects here that needs to be clarified. 1) How is WT dEsyt localization regulated by Ca2+? This could for example be evaluated in the mutant flies used in Fig. 1 (trpl302; trp343), where lack of light-induced Ca2+ influx would be predicted to result in a localization of dEsyt that resembles that observed for dEsytCaBM. 2) Is Ca2+ important for dEsyt localization, lipid exchange or both? The authors express a version of dEsyt with mutation made in all three C2 domains. In mammalian E-Syts, Ca2+ binding to the C2A domain is important for lipid exchange while binding to C2C (in E-Syt1) is important for interactions with lipids in the plasma membrane. Using more carefully designed mutants will allow the authors to determine how Ca2+ regulates dEsyt function in vivo. In addition, the authors must show experimentally that the mutant dEsytCaBM is unable to bind Ca2+ (could e.g. be done by acute Ca2+ changes in the cell-based model used in Fig. 3). Writing that "This transgene carrying a total of nine mutations should render the protein unable to bind calcium" (p. 6, line 173) is not sufficient.
      2. The localization of dEsyt shown in Fig. 3B is a bit confusing. First of all, I would recommend including markers of the ER and the plasma membrane, because without these it is difficult to make statements about the localization of dEsyt to these structures. Second, it appears that WT dEsyt localize to the reticular ER, and that the CaBM version localize to the plasma membrane. This is somewhat opposite to mammalian ESyts, where mutations that prevent Ca2+ binding either had no effect (for ESyt2) or prevented (for ESyt1) the interaction with the plasma membrane. It also appears different from the localization in vivo (Fig. 3C). Clarifying this will be important. It will also be important to connect this localization to changes in Ca2+ and not just to the localization of a mutant that may or may not be deficient in Ca2+ binding (see comment above).
      3. I don't fully understand the time course of events. The authors show that dEsytCaBM is mislocalized already at day 1 in dark-reared flies (Fig. 3C) but this mislocalization is not accompanied by a change in MCS density or gap distance, and consistently does not influence the localization of RDGB. The authors next expose the flies to constant light illumination to trigger Ca2+ dependent signaling, and this leads to mislocalization of RDGB, perhaps indicating changes in MCS (this is not shown). From these results it is difficult to know what the role of dEsyt is. It would be necessary to also show a control where Ca2+ signaling is not induced, e.g. a parallel dark-control (same number of days but no illumination). This is particularly important given that the authors show in Fig. 1 that preventing Ca2+ influx had a dramatic impact on MCS density even at day 1 (which is in sharp contrast to dEsytCaBM-expressing flies, that show normal morphology at day 1, which rather implies that dEsyt is not a major Ca2+ effector).
      4. The experiments done in dEsyt KO flies are important, and here the authors show that dEsyt1 could to some extent rescue all phenotypes. Some results are a bit puzzling. For example, dEsyt1CaBM localization in dEsyt1 KO flies is identical to that of WT dEsyt (Fig. 5C), which is in sharp contrast to the data shown in Fig. 3C. What is the reason for this? I would have anticipated the opposite (i.e. that in WT flies, dEsytCaBM can form dimers with endogenous dEsyt through SMP-domain interactions which may have an impact on its localization and the function of endogenous dEsyt, but that in the dEsyt KO cells, dEsytCaBM would show a different localization due to the lack of endogenous dEyt to interact with). It is important to clarify as one of the major observations here is that dEsytCaBM no longer localize to MCS. Since the CaBM version of dEsyt could rescue, to some extent, MCS density and delay photoreceptor degeneration, this implies that Ca2+ may not be required for regulation of dEsyt function or that the mutant is still able to partially bind to Ca2+. One experiment that would help the authors determining the function of dEsyt in vivo would be to use a mutant that lacks functional SMP domain (ideally also with and without mutations in the C2-domains).
      5. PLC activation typically couples to rapid signaling and involved hydrolysis of PIP2 and release of Ca2+ from the ER. Mammalian Esyts also require PIP2 for plasma membrane binding (through interactions with C2-domains), so constitutive PLC activity would be expected to impair ESyt localization to MCS. Here, the authors expose flies for days of constant illumination. How does this influence plasma membrane PIP2 levels and could this be of relevance for how data is interpreted? Do the authors know whether the CaBM mutant has reduced affinity for PIP2?

      Minor comments:

      1. The overexpression of WT dEsyt had a dramatic impact on MCS density and gap distance, while expression of dEsytCaBM did not. If these contacts are important for photoreceptor function, is it not surprising that such a dramatic change in photoreceptor structure was without effect on function? This should be further discussed.
      2. How is quantification of MCS density and gap distance influenced by retinal degeneration (e.g. induced by dEsyt KO)?
      3. The graphical abstract is a bit confusing. It seems to suggest that changes in dEsyt is a consequence of ageing and does not show any role of this protein in photoreceptor function. I think that the abstract could be improved to more clearly highlight the findings in the manuscript. For example, it doesn't at all show the difference in localization between WT and CaBM.
      4. P. 5, line 135 the authors state that "The tethering and lipid transfer activity of mammalian Esyts are reported to be influenced by Ca2+". This is a massive understatement. Ca2+ is a critical regulator of Esyt function in mammalian cells.
      5. In figure legend 1B and C: correct µM to µm.
      6. In figure legend 2A: should be red rectangles and not black rectangles.
      7. In Fig. 2B: specify which isoform of human ESyt that is shown.
      8. In Fig. 2C: do the authors mean D374 or D384 (as indicated in Fig. 2A)?

      Significance

      Light-induced signal transduction in photoreceptor cells involves Ca2+ influx and signaling and also depends on correct formation of ER-plasma membrane contact sites. In mammalian cells, the Esyts (esp. Esyt1 and Esyt2) localize to ER-PM contacts in a Ca2+-dependent manner, and the ion has dual effects in both enriching the protein at the membrane contact sites and in promoting lipid transport. Mammalian Esyts form homo- and heterodimers, and the properties of the dimers depends on their composition (PMID: 26202220). Drosophila only have one Esyt (dEsyt) which is structurally most similar to mammalian Esyt2, and the authors have previously shown how this protein is required for photoreceptor function (PMID: 32716137), although the role of Ca2+ was not investigated in that study. However, an earlier study has shown that mutations of all Ca2+-coordinating residues in dEsyt impairs protein function in Drosophila neurons (PMID: 28882990), so a similar Ca2+-dependence in the retina would be expected. The results from the present study confirm the requirement of Ca2+ signaling for dEsyt function, and extends this Ca2+-dependent regulation to also involve photoreceptor-induced Ca2+ signaling, which corroborates many other studies showing the requirement of Ca2+ signaling for the regulation of Esyt function in mammalian cells (e.g. PMID: 23791178; PMID: 27065097; PMID: 29222176; PMID: 26202220; PMID: 24183667; PMID: 30589572). As such, the results from this study represent an incremental step towards understanding Esyt function in vivo. These results would be of greatest interest to researchers working of photoreceptor function, and of some interest to a broader audience working on membrane contact sites and signal transduction. My own background is in mammalian cell biology, with a focus on lipid and Ca2+ signaling and inter-organelle communication. I have limited understanding of the model system used here (Drosophila photoreceptor cells).

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      Reply to the reviewers

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

      Summary In this study, Raja et al. found cytoplasmic condensates formed by the treatment of INFγ, investigated components of these condensates and identified p62, NBR1 and PARP14 as their components. INFγ treatment induced PARP14 expression, and PAPR14 inhibitor treatment inhibited condensation formation, suggesting that the amount of PARP14 and its enzymatic activity are important for the condensate formation. The ADPr-positive p62 condensates were independent of autophagic degradation, and proteasomal activity was required for their formation.

      Major comment 1. The finding that the ubiquitin-proteasome, but not autophagy activity, is indispensable for the formation of p62 condensates is of interest. However, the molecular mechanism by which the ubiquitin-proteasome system (UPS) is involved in the regulation of the PARP14-p62 condensate is still unclear. Which step(s) is the UPS involved?

      We appreciate the reviewer's acknowledgment of the novelty of our studies on the requirement of the ubiquitin-proteasome system (UPS) in the formation of ADPr-containing PARP14/p62 condensates. We have demonstrated that condensation formation requires the first and last steps of the UPS using two distinct classes of inhibitors: (1) TAK243 inhibits the E1 enzyme by forming a covalent adduct with ubiquitin that mimics the ubiquitin-adenylate complex, thereby blocking the initial step of ubiquitin conjugation (Fig. 6F-G). (2) Three different proteasome inhibitors with varying degrees of selectivity—MG132, epoxomicin, and Bortezomib—block the final step of the UPS by inhibiting the 26S proteasome (Fig. 6B, S6D). Given that blocking the early steps of the ubiquitin conjugation pathway or the late stages of the UPS inhibits the formation of ADPr condensates, we deduce that an active UPS is required. We will explore the involvement of additional steps in the UPS.

      The p62 condensate serves as a scaffold for autophagosome formation through the assembling autophagy receptors including NBR1 and TAX1BP1, followed by recruiting ATG proteins such as FIP200. While ADPr-positive p62 condensates also contain NBR1 and polyubiquitinated proteins, they are unrelated to autophagic degradation. It is unclear what factors govern autophagy-independent function.

      As we have identified the requirement of active UPS in regulating these condensates, determining the factors that govern autophagy-independent functions, though interesting, is beyond the scope of this manuscript. Our data indicate that the formation of ADPr-containing condensates, which include p62, other autophagy receptors such as NBR1, and polyubiquitinated proteins, but lack the autophagasome membrane protein LC3B (Fig. 3B, 5E-I, and S5D). Notably. this condensate formation is not inhibited by treatment with Bafilomycin A1 and chloroquine, which target the final step of autophagy involving lysosome interaction (Fig. 6A). In response to the reviewer's comments, we will further investigate whether these condensates also include other autophagy receptors, such as TAX1BP1, as well as the downstream autophagosome protein FIP200. Additionally, we will genetically deplete the critical autophagy factor ATG5 to confirm orthogonally that the formation of these condensates is indeed independent of autophagy.

      The authors claim that the amount of PARP14 and its MAR activity are essential for the condensate formation. However, all experiments were performed only with PARP14 inhibitors, and further validation is needed. If the importance of PARP14 activity is to be directly demonstrated, experiments in which an enzyme activity mutant is introduced into PARP14 KO cells are needed.

      We would like to clarify that we have not only used PARP14 chemical inhibitors to reduce MAR activity but also employed PROTAC to reduce the amount of PARP14 (Fig. 1H). Both approaches demonstrated that the inhibition of either the amount or MAR activity of PARP14 is critical for condensate formation. Additionally, we demonstrated that condensate formation is reduced upon PARP14 knockdown using siRNA and shRNA, as well as CRISPR-mediated knockout (Fig. 1G and S1C-H).

      Furthermore, we showed that transient transfection of a PARP14 mutant deficient in ADP-ribosylhydrolase activity into U2OS cells leads to the formation of ADPr condensates that colocalize with PARP14, independent of IFNγ treatment. Notably, a subset of condensates—particularly the larger ones—that contain both PARP14 and ADPr showed strong colocalization with p62 (Fig. 4G). Treatment with PARP14 MAR activity inhibitor under these conditions resulted in the disappearance of ADPr/PARP14 condensates while p62 bodies remained (Fig. 4H), further indicating that ADPr enrichment in p62 bodies depends on the MAR activity of PARP14. To further confirm the dependence on MAR activity, we have now repeated the experiment using a PARP14 mutant deficient in MAR activity. PARP14 and ADPr condensates were not observed upon expression of this mutant, indicating that condensate formation depends on PARP14 MAR activity.

      In Figure 2a, the heatmap alone is insufficient. Neither errors nor statistical comparisons are indicated.

      We will incorporate our statistical data presented in Fig. S2A-D into Fig. 2A.

      The statistical analysis of Figure S2 is inappropriate; instead of t-tests, multiple comparisons should be used to compare three or more groups.

      We will perform multiple comparison analyses, as suggested.

      Minor comment 1. What percentage of p62 condensates upon INFγ treatment are ADPr positive? Are all p62 bodies seen with INFγ stimulation unrelated to autophagy?

      We will perform the quantification, as suggested.

      Is ADPr condensation a PARA14-specific phenomenon? PARP9 and PARP12 were also upregulated by INFγ treatment. Are these factors also involved in condensate formation?

      Amongst all catalytically active PARPs, ADPr condensation requires only PARP14. Russo et al., J Biol Chem 2021, have shown that genetic knockout of PARP9 affects the formation of ADPr condensates; however, PARP9 is catalytically inactive as an ADP-ribosyltransferase. Ribeiro et al., EMBO 2024, have further confirmed the requirement of PARP9 by siRNA knockdown and have also shown that condensate formation does not require PARP12. Based on the reviewers' comments, we will independently confirm this observation by performing knockdown experiments.

      Figure 4D appears to be immunoprecipitation (IP) under non-denaturing conditions. If so, it is not possible to distinguish whether the MAR signal is derived from p62 or from the p62 interacting proteins (the associated ubiquitinated substrates). IP experiments should be performed under denaturing conditions.

      We will perform denaturing IP or other experiments to confirm the p62 modification upon IFNγ treatment. Additionally, we would like to note that following our submission, Kubon et al. reported in a bioRxiv preprint that p62 is ADP-ribosylated in a PARP14-dependent manner upon treatment with type I interferon, IFNβ. This finding is consistent with our study involving type II interferon, IFNγ.

      In Figure 5B, which band is HO1, the upper or lower?

      Both bands are HO1, as shown by Biswas et al., J Biol Chem 2014. One band appears at 28 kDa and the other at 32 kDa. The 32-kDa isoform is predominantly constitutive in the cytoplasm, whereas the 28-kDa HO-1 is predominant and primarily localized to the nucleus.

      There is no image for ubiquitin in S5D.

      Our original statement, “However, when inhibited with the mTOR inhibitor Torin-1, autophagy is induced, leading to increased autophagosome formation marked by LC3B on the membranes, which facilitates the recruitment of p62 and ubiquitinated proteins (Fig. S5D),” contained a misplaced figure citation. The correct statement should be: “However, when inhibited with the mTOR inhibitor Torin-1, autophagy is induced, leading to increased autophagosome formation marked by LC3B on the membranes (Fig. S5D), which facilitates the recruitment of p62 and ubiquitinated proteins.” Our intention was to show that there are conditions, such as Torin-1 treatment, where p62 and LC3B colocalize.

      Right panel in Figure 4F shows only IFγ + RBN, which should show all data sets in the same panel.

      Given the complexity of the three conditions with extensive data points and error bars on the FRAP experiments, we aim to present the data clearly. Instead of merging the panel into one figure, we initially provided a summary table in Figure 4F. However, in response to the reviewer's comments, we will provide the composite image that includes all data sets in the same panel.

      Reviewer #1 (Significance (Required)):

      Liquid droplets, which have continuously being identified in cells, are a hot topic in cell biology. Droplet formation, structure, molecular dynamics, and degradation, as well as their abnormalities and disease development due to genetic mutation and stress, are of wide-ranging interest from basic to pathological aspects. Therefore, this research has the potential to attract interest from a wide range of fields.

      General assessment Overall, the data are clear and the phenomenon is of interest. However, the molecular mechanism and biological significance of the condensate formation is unknown; It is unclear why proteasome activity is required for the formation of PARP14-mediated ADP ribosylation. It is also unclear what the consequences are for the cell if the ADPr-positive condensates are not formed. Thea authors should address these general and important issues and provide the data If not all.

      We thank the reviewer for acknowledging that our condensate investigation is timely and important in cell biology and for recognizing that “data are clear and the phenomenon is of interest”. As mentioned in the Discussion, these condensates can be reversed by the SARS-CoV-2 macrodomain in lung A549 cells, whose activity to remove ADP-ribosylation is critical for viral replication and pathogenesis, indicating the biological significance of these condensates. In addition, similar IFNγ conditions can induce PARP14 expression in melanoma, where PARP14 inhibition resensitizes these cancers to immunotherapy. Given that these ADPr condensates are also observed in A375 melanoma cells beyond lung cells (Fig. S3B), this provides additional context to investigate their biological significance in the future.

      We would like to note that we have already made significant advances by (1) revealing the identity of these condensates as related to p62 bodies (Fig. 3-5), (2) defining the responsible ADP-ribosyltransferase as PARP14 (Fig. 1-2), and (3) determining the requirements for condensation through ubiquitin-proteasome system (Fig. 6). The proposed exploration of the functional consequences and significance is beyond the scope of this manuscript. However, we will further define the mechanistic involvement of which step of ubiquitin-proteasome system.

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

      This manuscript investigates the formation of a novel cellular structure or condensate, similar to p62 bodies, that includes PARP14 and p62. The interferon-induced PARP14-mediated ADP-ribosylation of p62 in these condensates depends on an active ubiquitin-proteasome system. These condensates are characterized by the presence of PARP14 and ADPr and include some, but not all, components of the p62 bodies. Furthermore, their formation depends on both ubiquitin activation and proteasome activity, but it is unaffected by autophagy inhibition, unlike conventional p62 bodies.

      The Introduction provides a well-delineated context of condensates, highlighting the importance of post-translational modifications in responding to environmental changes.

      Although the manuscript is well-organized with apparent logical development, there are weaknesses that diminish the impact of the reported data. A more accurate review of the structures, both from a morphological and quantitative perspective, would strengthen the conclusions and the overall impact of this work. Additionally, while the authors have analyzed the contribution of PARP14 to condensate formation, the biological significance of these structures remains unclear. For instance, performing MS (mass spectrometry) analysis on the described structures could help identify their composition and functions.

      The methodologies used in this study are standard for molecular and cellular biology research, including immunofluorescence assays, transient transfections, immunoprecipitations, and fluorescence recovery after photobleaching (FRAP) assays. These methods are described in detail and can be reproduced.

      Below, please find a list of comments and suggestions to enhance the robustness of the data:

      We thank the reviewer for acknowledging the logical progression of the manuscript and the detailed, reproducible methods. As detailed below, we will perform super-resolution microscopy experiments to examine morphology, improve data quantification, and conduct proteomics experiments to identify how the p62 interactome changes upon IFNγ treatment.

      Major Points

      1. The IF analyses are central to the conclusions reported and are employed for each of the inhibitors or other tools used to investigate the formation of these condensates. The quality of the IF images needs to be improved; the shape and contacts of the condensates should be analyzed using either super-resolution or EM microscopy, or preferably both. The lack of morphometry and quantification from cell populations needs to be addressed for all experiments. These analyses are needed to support the claim that the condensates presented in this study are indeed novel structures, rather than being transient aggregates of a different nature.

      We believe the reviewer may be referring to the size of the images rather than their quality, as they are of high resolution when zoomed in. However, we agree that larger images would enhance clarity. We will be discreet in choosing the figures to present, given that we have over 550 panels in the main figures and over 250 in the supplemental figures. We will resize our figures to ensure the images are clearly visible.

      We will perform Airyscan imaging to provide super-resolution images for a better understanding of the morphology of these condensates. We will perform the morphometry quantification (circularity and ellipticity). For quantification, we would like to point out that nearly all of our experiments were analyzed from at least 4 fields, each containing 20-50 cells (depending on the magnification of 20x or 40x). In response to the reviewer's comment, we will also provide quantification on a per-cell basis.

      Our data indicate that these are novel ADPr-containing condensates that colocalize with PARP14, p62, NBR1, and ubiquitin, but not LC3B (Fig. 1F, 3B, 5E-F, 5I). These structures are inducible by IFN treatment and can be inhibited by even 1 hour of PARP14 inhibition (Fig. 1A-B, 2D) They are dependent on PARP14 induction and its ADP-ribosyltransferase activity (Fig. 1G, 2B, 2D). These structures are not protein aggregates, as evidenced by their lack of staining with ProteoStat Dye (Fig. S6A), which stains for unfolded proteins.

      The claim that PARP14 is essential for the formation of condensates requires support by the analyses indicated above. Minor points regarding Fig. 1 are indicated below. I suggest performing KD of PARP9 and/or PARP12 (whose expression is increased upon IFN treatment) and checking ADPr condensates to validate the central role of PARP14.

      ADPr condensation requires PARP14, as demonstrated by multiple genetic depletion techniques (siRNA/shRNA/CRISPR; Fig. 1G, S1C-H) and chemical inhibitors (catalytic and PROTAC; Fig. 1H, 2B, 2D). We will provide additional image analyses to support the claim. In addition, Russo et al., J Biol Chem 2021, have shown that genetic knockout of PARP9 affects the formation of ADPr condensates; however, PARP9 is catalytically inactive as an ADP-ribosyltransferase. Ribeiro et al., EMBO 2024, have further confirmed the requirement of PARP9 by siRNA knockdown and have also shown that condensate formation does not require PARP12. Based on the reviewers' comments, we will independently confirm this observation by performing knockdown experiments.

      According to the text, "PARP14 was pulled down by ADP-ribose binding Af1521 macrodomain following IFNγ treatment (Fig. 2H)", but the legend to the figure says otherwise. A Pan-ADPr binding reagent (MABE1016) is reported in the figure. Although the conclusion is similar for the results obtained with these two tools (but they must be described and reported properly), it is still insufficient to claim that PARP14 is ADP-ribosylated. This point should be at least discussed.

      We apologize for the confusion. The Pan-ADPr binding reagent (MABE1016) is a His-tagged recombinant Af1521 macrodomain that binds to ADP-ribosylated protein (Gibson et al., Biochemistry 2017). Therefore, we used Ni-NTA resin to pull down His-tagged AF1521 for the subsequent analysis of PARP14. We will revise the text and figure legend for Fig. 2H to clarify this. We will further probe the eluted PARP14 is indeed ADP-ribosylated by western blot. Consistent with our studies, Kar et al. and Ribeiro et al. (EMBO J. 2024) also recently reported that PARP14 is ADP-ribosylated upon IFNγ treatment in A549 cells. Additionally, Higashi et al. (J. Proteome Res. 2019) reported PARP14 ADP-ribosylation in IFNγ-treated macrophage cells. We will include these references in our Discussion.

      I have difficulties analyzing the colocalization with the different organelles, even enlarging the images as much as possible. In most cases, only one condensate per image is shown. Continuities with the nuclear envelope appear in some cases: has this been investigated?

      We have provided images of at least two cells containing multiple cytoplasmic condensates in Figure S3A. We believe part of the confusion arises from the staining pattern of ADPr in the nucleus, which colocalizes with splicing speckles. However, this nuclear staining was not altered by IFNγ treatment. Therefore, we have focused on the cytoplasmic condensates in this study and will clarify this focus in the main text. However, in response to the reviewer’s question, we will also visit the possibilities of enrichment of signals at the nuclear envelope. For each colocalization study, we have analyzed at least four fields, each containing 20-30 cells. To further strengthen our claim for colocalization analyses, we will now provide quantification on a per-cell basis.

      Minor Points

      1. Fig. 1A: The DAPI images at 3 and 6 hours are reversed. Additionally, for Fig. S1a and Fig. 1A, please include quantifications.

      We apologize for the oversight and will provide quantification.

      1. Fig. 1B: Check PARP14 levels (and other IFN-PARPs) under the same experimental conditions.

      As suggested, we will assess PARP9, PARP12, and PARP14 levels.

      Fig. 1H: Explain why PARP14 IF staining is still visible upon RBN012811 treatment, while it is completely lost in WB analysis or upon PARP14 siRNA treatment (Fig. 1G). In addition, please include IF quantifications.

      To clarify, for Figure 1H, the images provided correspond to those from IFNγ-treated cells while the western blot data include both with and without IFNγ treatment. We would like to point out that RBN012811 treatment indeed shows a similar dose-dependent signal with increasing hours of treatment, comparable to the western blot results. Specifically, we observed a small amount of PARP14 remaining at the 1-hour timepoint on western blots and IF images, with the highest intensity observed compared to other timepoints. In addition, we believe part of the discrepancy is due to background staining by PARP14 antibodies. Therefore, we will examine the level of background staining in PARP14 KO cells and provide corresponding IF quantification.

      Fig. 2C: Please include quantifications.

      We will provide quantification.

      1. Fig. 2E: The RBN treatment time is not indicated. Please include this information in the figure legend.

      We apologize for the oversight and will add the treatment time (24 h) to the figure legend.

      Fig. 2G: I am not convinced about the PARP14 staining. IF images do not show an increase in PARP14 levels, while WB analysis shows a strong increase in PARP14 protein levels (see Fig. 2E). Moreover, the RBN treatment time was not indicated; please include it in the figure legend. Does RBN alone affect PARP14 localization? The reported picture shows only 2 cells, each with a different subcellular localization of PARP14. As previously suggested, quantifications are required.

      When presenting the data, our aim was to show the pattern rather than the relative intensity difference. Therefore, we used the autocontrast image function across different conditions, which resulted in an apparent change in pattern even with weak signals in control or RBN-treated samples. To address this, we will ensure the images presented across different conditions have the same exposure and are shown with consistent image contrast parameters. We will also include quantification of the condensates. Additionally, we apologize for the oversight and will add the RBN treatment time to the figure legend.

      Fig. 3B: Pearson's correlation coefficient (PCC) is reported for n=3. The images show one condensate per cell. Under these conditions, the number of cells analyzed should be at least 100 for each experiment. Additionally, the PCC between PARP14 and p62 at steady state is shown to be 60% (which is quite high). However, the IF pictures do not support this quantification. Can the authors provide higher-resolution pictures? Does PARP14 always co-localize with p62? Lines 207-208 state: "these findings suggest that PARP14 is localized to p62 bodies upon IFNγ treatment when ADP-ribosylation occurs." According to the PCC value, the two proteins co-localize even in the absence of IFN. Can the authors clarify this aspect?

      We apologize for the inaccurate description. The data should be n=4, representing different fields, each containing 20-30 cells (as indicated by the number of dots in the original graph panels in Fig. 3B). The Pearson's correlation coefficient was calculated across the cells, instead of focusing on the condensates—we will provide additional analyses on condensate colocalization analyses. We will also provide larger images and quantification to indicate the level of PARP14 colocalization with p62. For PARP14, we did not see a significant number of PARP14 condensates in control cells; PARP14 condensates were seen only after IFNγ treatment. A fraction of PARP14 condensates did not colocalize with p62. We will provide detailed quantification analyses.

      Fig. S3B: Please include quantifications.

      Quantification will be provided

      Fig. S3C: How was the condensate size quantified? It would be useful to show a quantification mask.

      We apologize for the omission in the Method Section. The condensate size quantification was performed with ImageJ. The nuclei were first identified with DAPI staining and masked out from the ADPr channel. The image was then thresholded with the “Maximum Entropy” method from ImageJ and the “Analyze Particles” function was used to identify condensates with size larger than 1 pixel. Quantification mask will be provided.

      Fig. 3D: Does p62 KD affect PARP14 localization? The reported picture shows only 2 cells, each with different staining of PARP14.

      p62 KD reduced the number of PARP14 condensates but did not change their localization. We will provide a representative image with more cells to illustrate this effect more clearly and provide quantification on the change in number of condensates.

      Fig. 4A: Please quantify the PARP14 co-IP signal with p62, normalized to PARP14 total levels. In the reported WB, it is difficult to see the interaction between PARP14 and p62 in untreated conditions. Please provide clearer WB.

      As suggested, we will quantify the PARP14 co-IP signal by normalizing it with PARP14 input levels. Additionally, we will provide a clearer WB in the revised manuscript.

      Additionally, I would expect an increased interaction between PARP14 and p62 upon IFN treatment due to PARP14 recruitment to p62 condensates, not just because of increased PARP14 levels. Since the authors show that PARP14 is not recruited to ADPr condensates upon RBN treatment (Fig. 2G), why is the interaction between p62 and PARP14 so high under RBN treatment?

      RBN treatment inhibits PARP14 catalytic activity but simultaneously increases PARP14 levels, as first described by Schenkel et al., Cell Chem Biol 2021. Western blot data indicate that the interaction between PARP14 and p62 is independent of this activity and instead depends on PARP14 protein levels. However, the formation of ADPr/PARP14-containing condensates requires catalytically active PARP14. Based on these data, we conclude that the colocalization of p62 and PARP14 depends on the catalytic activity of PARP14, which is reflected by its ADP-ribosylation.

      Fig. 4C: Please quantify WB signals of ADP-ribosylated p62 for the different conditions analyzed. ADP-ribosylation of p62 is still present in cells lacking PARP14. Are there other enzymes that can modify p62? Moreover, the authors state: "We observed an increased MARylation of p62 upon IFNγ treatment" (line 230); is this dependent on the increase in PARP14 levels or the translocation of PARP14 to ADPr condensates? Quantifications should help clarify this aspect.

      WB signals will be quantified. We agree with the reviewer's observation regarding the presence of ADP-ribosylated p62 in PARP14 KO cells. The basal levels of ADP-ribosylated p62 may be due to other PARP enzymes. However, PARP14 is critical for the increase in ADP-ribosylation under IFNγ treatment, as the increase was not observed in PARP14 KO cells. Given that PARP14 inhibitors increase PARP14 levels, we interpret that the increase in p62 MARylation requires an increase in active PARP14 levels, not just its total level. Since PARP14 activity is crucial for the localization of PARP14 to p62 condensates and its enrichment of ADPr signals, it is possible, as suggested by the reviewer, that the increase in MARylation of p62 is dependent on the translocation of PARP14 to the structure. However, the field currently lacks the tools to disrupt p62 bodies without knocking down p62 to definitively test whether colocalization is required for the MARylation increase.

      Fig. 4G: Quantificationsare required.

      Quantification will be provided

      Reviewer #2 (Significance (Required)): The role of the PARP family in cellular processes is a very active and rapidly growing field. New information about the organization of PARPs in the nucleus, cytosol, or different types of bodies/structures is certainly relevant to the field. However, the present study is too preliminary at the moment to be considered highly relevant. Both the data analysis and conclusions need to be carefully reviewed. After major revisions, the manuscript might be of general interest if well contextualized within the fields of post-translational modification and protein degradation processes. It would remain in any case interesting for the field of ADP ribosylation. We thank the reviewer for recognizing the significance of our work in the rapidly evolving field of PARP biology. We apologize for the lack of clarity that we indeed quantified over 100 cells across at least 4 fields of images for the data reported. To further address the concerns raised, we will provide additional cell-based quantification to strengthen our claims. Furthermore, we will enhance the contextualization of our findings within the broader frameworks of post-translational modification and protein degradation processes in the Introduction and Discussion sections.

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

      In this manuscript, titled "Interferon-Induced PARP14-Mediated ADP-Ribosylation in p62 Bodies Requires an Active Ubiquitin-Proteasome System", Raja et al. perform fluorescence microscopy assays and molecular analyses on cultured cells ex vivo to further our understanding of ADP-ribose accumulations that form in the cytoplasm in response to IFγ stimulation. Guided by the operon-like linkage and co-expression patterns of PARP14, PARP9, and DTX3L and recent reports describing a SARS-CoV-2-dissolved cytoplasmic body induced by interferon-induced that is rich in ADP-ribose and the PARP9/DTX3L heterodimer form following IFγ stimulation, the authors provide clarity in this manuscript regarding two knowledge gaps - (i) what catalyzes mono(ADP-ribosyl)ation within these structures (as PARP9 lacks ADP-ribosyltransferase activity) and (ii) how these foci/condensates relate to similarly composed autophagy-associate "p62 bodies" that have been previously described. Using a combination of genetic depletion and inhibitor-based approaches, the authors show that these ADPr-condensates rely on the catalytic activity of PARP14. The authors also show that while these ADPr-condensates share componentry with "p62 bodies" like ubiquitin and p62 itself, these foci are distinct accumulations, as they lack both LC3B and sensitivity to autophagy inhibitors and require an active ubiquitn-mediated proteosomal degradation system.

      While this report represents a more incremental advance in our understanding of these cell signaling structures, especially considering a pair of very recently published and similar reports (Kar et al., EMBO J [2024] and Chaves Ribiero et al EMBO J [2024]), the work here is well-written and reasoned and complements these works with some novelty and distinction to that reported literature. The experiments are definitive and of high quality and the authors interpretations/conclusions are largely well-supported by the results. Thus, it is my opinion that this work is appropriate for publication with predominantly minor revisions (outlined below) and a few more substantive experimental additions.

      We thank the reviewer for recognizing the high quality of our work and for acknowledging that our interpretations are well-supported by the results. We appreciate that the reviewer deemed our work ready for publication with minor revisions. We believe the reviewer’s perception of our work as incremental arises because two related studies were published in June, after we submitted our work to Review Commons in May. According to the Scooping Protection Policy, our work should still be considered novel. The publication of these studies in EMBO J, which reported the discovery of PARP14 in ADPr-containing condensate formation, highlights the significance of our research. However, we further contribute to this discovery by demonstrating the critical role of PARP14 using multiple genetic manipulation techniques (siRNA, shRNA, and CRISPR-Cas9) and chemical inhibitors (catalytic and PROTAC), indicating the rigor of our studies. Moreover, we not only investigate PARP14 but also define the identity of these condensates related to p62 bodies and establish the requirement of an active ubiquitin-proteasome system for their formation.

      Major Comment:

      A major claim and novelty reported here is that the ADPr condensates are distinct from "p62 bodies". The evidence to support this rely largely on differences in their sensitivity to pharmacological treatments as well as somewhat subtle differences in FRAP recovery in p62 condensates after IFNgamma treatment. But, this claim would be better supported with more comprehensive mapping of differences in the componentry or functional outcomes of these condensates. The authors might consider:

      -Mass spectrometry against p62 (a common component) in standard "p62 bodies" and ADPr Condensates, followed by IF to confirm significantly different composition in, what is argued here, these distinct structures. -Fine mapping of concentration dependence of components that give rise to these distinct condensates as has been demonstrated in papers like Riback et al Nature 2020 and others. -Methodology of the author's choosing to decipher functional outcomes from these condensates followed by demonstration that components unique to ADPr condensates are dispensable for functioning "p62 bodies" and, vice versa, components unique to "p62 bodies" are dispensable for ADPr Condensate function.

      As rightly pointed out by the reviewer, our studies indicate the alteration in the composition and dynamics of p62 bodies upon IFNγ treatment. This was assessed using immunofluorescence against various known components of p62 bodies (Fig. 3B, 5E-I), quantification of the condensate size (Fig. S3C), and p62 mobility assessment by photokinetic experiments (Fig. 3C, 4F). In considering reviewer’s suggestions, we will perform p62 interactome studies with and without IFNγ treatment to identify potential changes. Additionally, we will analyze the concentration dependence of ADPr for condensate formation. However, we believe that investigating the functional outcomes is beyond the scope of this manuscript.

      Minor Comments:

      Overall, the representative microscopy images are far too small. For the benefit of future readers, please consider enlarging these images.

      More of the quantitation of microscopy images, with accompanying statistics, that are found in abundance in the supplemental material should find their way into the main figures of the manuscript. This will give room for larger and more reader-friendly representative microscopy images in the main figures/text as discussed briefly above.

      We appreciate the reviewer’s suggestions and rightly pointed out that our quantification and statistics were in supplementary materials. Given that we have provided over 800 image panels, we will restructure the manuscript so that the cell biology information is more readily available. We will move our quantification data and statistics currently in the supplementary materials to the main figures. Additionally, we will provide larger and more reader-friendly representative microscopy images in the main text as suggested.

      Can the authors test whether or not the condensates are purely driven by mono(ADP-ribosyl)ation? Or does poly(ADP-ribose) co-occupy these condensates and play a substantive role?

      We have tested for the presence of poly(ADP-ribose) in the condensates and found it is not present. We will provide the supporting data.

      The manuscript would benefit from discussing very recent and related reports (Kar et al., EMBO J [2024] and Chaves Ribiero et al EMBO J [2024]), that I suspect were not available at the time of submission.

      Yes, the reviewer is correct that our submission preceded the publication of these related reports. In light of the co-discovery, we will add a section to discuss their findings.

      IFNalpha and IFNbeta, which are used in Figure S1, do not appear as reagents in Table 1.

      We apologize for the oversight and will add the information on IFNa and IFNb to Table 1.

      On lines 113-114, it would seem more appropriate to describe the increase of PARP-14 as statistically significant and largest in magnitude. "most significant" would just mean lowest p-value, which I expect is different that the authors intend here.

      We thank the reviewer's suggestion will modify the text as follows:

      "PARP9, PARP12, and PARP14 were statistically significantly upregulated at 6 and 24 hours post-treatment, with PARP14 showing the largest increase in mRNA expression levels (Fig. 1D and S1B)."

      In Figure S1, better care should be taken to crop and align the western blots.

      We thank the reviewer for pointing this out, and we will properly align and crop the western blots in Figure S1.

      On line 154, it may be more appropriate to describe ITK as a "weaker" inhibitor of PARP14 relative to PARP11. It certainly is effective as an inhibitor (Figs. S2A and S2G) and its unclear how the authors (or anyone would) define what qualities make it "weak".

      We thank the reviewer's suggestion and will modify the text as follows:

      “…—specifically RBN012579 (hereafter RBN) and ITK7 (a potent PARP11 inhibitor with inhibitory effects on PARP14 that are weaker than RBN)—…"

      The multiple bands for PARP14 in Figure 3E should be addressed. Why does this differ from other blots from the same cells?

      We believe that the multiple bands seen can be due to insufficient blocking and using a different lot of PARP14 antibodies. We will address the issue by performing a new experiment with proper blocking conditions and using the same lot of PARP14 antibody as other blots. It should be noted that that variation is also observed in the reagent website: https://www.scbt.com/p/parp-14-antibody-c-1

      Reviewer #3 (Significance (Required)):

      I expect the advances in this work will appeal more to specialists who are interested in ADP-ribosylation as a signaling molecule and to those engaged in biotechnological efforts to drug immunological responses.

      The advances reported here are incremental. The ADPr condensates that form in response to IFNgamma, the involvement of PARP9/DTX3L, and very recently the involvement of PARP14 and its MARylation activity are all known. Less known is the notion that this condensate is distinct from other kinds of "bodies", which is a clear point of novelty, especially if buttressed by the authors as suggested in this review.

      We agree with the reviewer that our work is significant for multiple fields, including ADP-ribosylation and immunology. The perception of our work as incremental likely stems from the publication of two related recent studies in June, after our submission in May. According to the Scooping Protection Policy in Review Commons, our work should remain novel in editorial consideration. More importantly, the back-to-back EMBO J studies highlight the importance of reporting the critical role of PARP14 in ADPr-containing condensate formation. We further contribute to this discovery in three aspects: (1) we rigorously demonstrate the critical role of PARP14 through multiple genetic techniques (siRNA, shRNA, and CRISPR-Cas9) and chemical inhibitors (catalytic and PROTAC), (2) we reveal the identity of these condensates as related to p62 bodies, and (3) we define their requirement for an active ubiquitin-proteasome system.

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

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      Referee #3

      Evidence, reproducibility and clarity

      In this manuscript, titled "Interferon-Induced PARP14-Mediated ADP-Ribosylation in p62 Bodies Requires an Active Ubiquitin-Proteasome System", Raja et al. perform fluorescence microscopy assays and molecular analyses on cultured cells ex vivo to further our understanding of ADP-ribose accumulations that form in the cytoplasm in response to IFγ stimulation. Guided by the operon-like linkage and co-expression patterns of PARP14, PARP9, and DTX3L and recent reports describing a SARS-CoV-2-dissolved cytoplasmic body induced by interferon-induced that is rich in ADP-ribose and the PARP9/DTX3L heterodimer form following IFγ stimulation, the authors provide clarity in this manuscript regarding two knowledge gaps - (i) what catalyzes mono(ADP-ribosyl)ation within these structures (as PARP9 lacks ADP-ribosyltransferase activity) and (ii) how these foci/condensates relate to similarly composed autophagy-associate "p62 bodies" that have been previously described. Using a combination of genetic depletion and inhibitor-based approaches, the authors show that these ADPr-condensates rely on the catalytic activity of PARP14. The authors also show that while these ADPr-condensates share componentry with "p62 bodies" like ubiquitin and p62 itself, these foci are distinct accumulations, as they lack both LC3B and sensitivity to autophagy inhibitors and require an active ubiquitn-mediated proteosomal degradation system.

      While this report represents a more incremental advance in our understanding of these cell signaling structures, especially considering a pair of very recently published and similar reports (Kar et al., EMBO J [2024] and Chaves Ribiero et al EMBO J [2024]), the work here is well-written and reasoned and complements these works with some novelty and distinction to that reported literature. The experiments are definitive and of high quality and the authors interpretations/conclusions are largely well-supported by the results. Thus, it is my opinion that this work is appropriate for publication with predominantly minor revisions (outlined below) and a few more substantive experimental additions.

      Major Comment:

      A major claim and novelty reported here is that the ADPr condensates are distinct from "p62 bodies". The evidence to support this rely largely on differences in their sensitivity to pharmacological treatments as well as somewhat subtle differences in FRAP recovery in p62 condensates after IFNgamma treatment. But, this claim would be better supported with more comprehensive mapping of differences in the componentry or functional outcomes of these condensates. The authors might consider:

      • Mass spectrometry against p62 (a common component) in standard "p62 bodies" and ADPr Condensates, followed by IF to confirm significantly different composition in, what is argued here, these distinct structures.
      • Fine mapping of concentration dependence of components that give rise to these distinct condensates as has been demonstrated in papers like Riback et al Nature 2020 and others.
      • Methodology of the author's choosing to decipher functional outcomes from these condensates followed by demonstration that components unique to ADPr condensates are dispensable for functioning "p62 bodies" and, vice versa, components unique to "p62 bodies" are dispensable for ADPr Condensate function.

      Minor Comments:

      Overall, the representative microscopy images are far too small. For the benefit of future readers, please consider enlarging these images.

      More of the quantitation of microscopy images, with accompanying statistics, that are found in abundance in the supplemental material should find their way into the main figures of the manuscript. This will give room for larger and more reader-friendly representative microscopy images in the main figures/text as discussed briefly above.

      Can the authors test whether or not the condensates are purely driven by mono(ADP-ribosyl)ation? Or does poly(ADP-ribose) co-occupy these condensates and play a substantive role?

      The manuscript would benefit from discussing very recent and related reports (Kar et al., EMBO J [2024] and Chaves Ribiero et al EMBO J [2024]), that I suspect were not available at the time of submission.

      IFNalpha and IFNbeta, which are used in Figure S1, do not appear as reagents in Table 1.

      On lines 113-114, it would seem more appropriate to describe the increase of PARP-14 as statistically significant and largest in magnitude. "most significant" would just mean lowest p-value, which I expect is different that the authors intend here.

      In Figure S1, better care should be taken to crop and align the western blots.

      On line 154, it may be more appropriate to describe ITK as a "weaker" inhibitor of PARP14 relative to PARP11. It certainly is effective as an inhibitor (Figs. S2A and S2G) and its unclear how the authors (or anyone would) define what qualities make it "weak".

      The multiple bands for PARP14 in Figure 3E should be addressed. Why does this differ from other blots from the same cells?

      Significance

      I expect the advances in this work will appeal more to specialists who are interested in ADP-ribosylation as a signaling molecule and to those engaged in biotechnological efforts to drug immunological responses.

      The advances reported here are incremental. The ADPr condensates that form in response to IFNgamma, the involvement of PARP9/DTX3L, and very recently the involvement of PARP14 and its MARylation activity are all known. Less known is the notion that this condensate is distinct from other kinds of "bodies", which is a clear point of novelty, especially if buttressed by the authors as suggested in this review.

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      Referee #2

      Evidence, reproducibility and clarity

      This manuscript investigates the formation of a novel cellular structure or condensate, similar to p62 bodies, that includes PARP14 and p62. The interferon-induced PARP14-mediated ADP-ribosylation of p62 in these condensates depends on an active ubiquitin-proteasome system. These condensates are characterized by the presence of PARP14 and ADPr and include some, but not all, components of the p62 bodies. Furthermore, their formation depends on both ubiquitin activation and proteasome activity, but it is unaffected by autophagy inhibition, unlike conventional p62 bodies.

      The Introduction provides a well-delineated context of condensates, highlighting the importance of post-translational modifications in responding to environmental changes.

      Although the manuscript is well-organized with apparent logical development, there are weaknesses that diminish the impact of the reported data. A more accurate review of the structures, both from a morphological and quantitative perspective, would strengthen the conclusions and the overall impact of this work. Additionally, while the authors have analyzed the contribution of PARP14 to condensate formation, the biological significance of these structures remains unclear. For instance, performing MS (mass spectrometry) analysis on the described structures could help identify their composition and functions.

      The methodologies used in this study are standard for molecular and cellular biology research, including immunofluorescence assays, transient transfections, immunoprecipitations, and fluorescence recovery after photobleaching (FRAP) assays. These methods are described in detail and can be reproduced.

      Below, please find a list of comments and suggestions to enhance the robustness of the data:

      Major Points

      1. The IF analyses are central to the conclusions reported and are employed for each of the inhibitors or other tools used to investigate the formation of these condensates. The quality of the IF images needs to be improved; the shape and contacts of the condensates should be analyzed using either super-resolution or EM microscopy, or preferably both. The lack of morphometry and quantification from cell populations needs to be addressed for all experiments. These analyses are needed to support the claim that the condensates presented in this study are indeed novel structures, rather than being transient aggregates of a different nature.
      2. The claim that PARP14 is essential for the formation of condensates requires support by the analyses indicated above. Minor points regarding Fig. 1 are indicated below. I suggest performing KD of PARP9 and/or PARP12 (whose expression is increased upon IFN treatment) and checking ADPr condensates to validate the central role of PARP14.
      3. According to the text, "PARP14 was pulled down by ADP-ribose binding Af1521 macrodomain following IFNγ treatment (Fig. 2H)", but the legend to the figure says otherwise. A Pan-ADPr binding reagent (MABE1016) is reported in the figure. Although the conclusion is similar for the results obtained with these two tools (but they must be described and reported properly), it is still insufficient to claim that PARP14 is ADP-ribosylated. This point should be at least discussed.
      4. I have difficulties analyzing the colocalization with the different organelles, even enlarging the images as much as possible. In most cases, only one condensate per image is shown. Continuities with the nuclear envelope appear in some cases: has this been investigated?

      Minor Points

      1. Fig. 1A: The DAPI images at 3 and 6 hours are reversed. Additionally, for Fig. S1a and Fig. 1A, please include quantifications.
      2. Fig. 1B: Check PARP14 levels (and other IFN-PARPs) under the same experimental conditions.
      3. Fig. 1H: Explain why PARP14 IF staining is still visible upon RBN012811 treatment, while it is completely lost in WB analysis or upon PARP14 siRNA treatment (Fig. 1G). In addition, please include IF quantifications.
      4. Fig. 2C: Please include quantifications.
      5. Fig. 2E: The RBN treatment time is not indicated. Please include this information in the figure legend.
      6. Fig. 2G: I am not convinced about the PARP14 staining. IF images do not show an increase in PARP14 levels, while WB analysis shows a strong increase in PARP14 protein levels (see Fig. 2E). Moreover, the RBN treatment time was not indicated; please include it in the figure legend. Does RBN alone affect PARP14 localization? The reported picture shows only 2 cells, each with a different subcellular localization of PARP14. As previously suggested, quantifications are required.
      7. Fig. 3B: Pearson's correlation coefficient (PCC) is reported for n=3. The images show one condensate per cell. Under these conditions, the number of cells analyzed should be at least 100 for each experiment. Additionally, the PCC between PARP14 and p62 at steady state is shown to be 60% (which is quite high). However, the IF pictures do not support this quantification. Can the authors provide higher-resolution pictures? Does PARP14 always co-localize with p62? Lines 207-208 state: "these findings suggest that PARP14 is localized to p62 bodies upon IFNγ treatment when ADP-ribosylation occurs." According to the PCC value, the two proteins co-localize even in the absence of IFN. Can the authors clarify this aspect?
      8. Fig. S3B: Please include quantifications.
      9. Fig. S3C: How was the condensate size quantified? It would be useful to show a quantification mask.
      10. Fig. 3D: Does p62 KD affect PARP14 localization? The reported picture shows only 2 cells, each with different staining of PARP14.
      11. Fig. 4A: Please quantify the PARP14 co-IP signal with p62, normalized to PARP14 total levels. In the reported WB, it is difficult to see the interaction between PARP14 and p62 in untreated conditions. Please provide clearer WB. Additionally, I would expect an increased interaction between PARP14 and p62 upon IFN treatment due to PARP14 recruitment to p62 condensates, not just because of increased PARP14 levels. Since the authors show that PARP14 is not recruited to ADPr condensates upon RBN treatment (Fig. 2G), why is the interaction between p62 and PARP14 so high under RBN treatment?
      12. Fig. 4C: Please quantify WB signals of ADP-ribosylated p62 for the different conditions analyzed. ADP-ribosylation of p62 is still present in cells lacking PARP14. Are there other enzymes that can modify p62? Moreover, the authors state: "We observed an increased MARylation of p62 upon IFNγ treatment" (line 230); is this dependent on the increase in PARP14 levels or the translocation of PARP14 to ADPr condensates? Quantifications should help clarify this aspect.
      13. Fig. 4G: Quantifications are required.

      Significance

      The role of the PARP family in cellular processes is a very active and rapidly growing field. New information about the organization of PARPs in the nucleus, cytosol, or different types of bodies/structures is certainly relevant to the field.

      However, the present study is too preliminary at the moment to be considered highly relevant. Both the data analysis and conclusions need to be carefully reviewed. After major revisions, the manuscript might be of general interest if well contextualized within the fields of post-translational modification and protein degradation processes. It would remain in any case interesting for the field of ADP ribosylation.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary

      In this study, Raja et al. found cytoplasmic condensates formed by the treatment of INFγ, investigated components of these condensates and identified p62, NBR1 and PARP14 as their components. INFγ treatment induced PARP14 expression, and PAPR14 inhibitor treatment inhibited condensation formation, suggesting that the amount of PARP14 and its enzymatic activity are important for the condensate formation. The ADPr-positive p62 condensates were independent of autophagic degradation, and proteasomal activity was required for their formation.

      Major comment

      1. The finding that the ubiquitin-proteasome, but not autophagy activity, is indispensable for the formation of p62 condensates is of interest. However, the molecular mechanism by which the ubiquitin-proteasome system (UPS) is involved in the regulation of the PARP14-p62 condensate is still unclear. Which step(s) is the UPS involved?
      2. The p62 condensate serves as a scaffold for autophagosome formation through the assembling autophagy receptors including NBR1 and TAX1BP1, followed by recruiting ATG proteins such as FIP200. While ADPr-positive p62 condensates also contain NBR1 and polyubiquitinated proteins, they are unrelated to autophagic degradation. It is unclear what factors govern autophagy-independent function.
      3. The authors claim that the amount of PARP14 and its MAR activity are essential for the condensate formation. However, all experiments were performed only with PARP14 inhibitors, and further validation is needed. If the importance of PARP14 activity is to be directly demonstrated, experiments in which an enzyme activity mutant is introduced into PARP14 KO cells are needed.
      4. In Figure 2a, the heatmap alone is insufficient. Neither errors nor statistical comparisons are indicated.
      5. The statistical analysis of Figure S2 is inappropriate; instead of t-tests, multiple comparisons should be used to compare three or more groups.

      Minor comment

      1. What percentage of p62 condensates upon INFγ treatment are ADPr positive? Are all p62 bodies seen with INFγ stimulation unrelated to autophagy?
      2. Is ADPr condensation a PARA14-specific phenomenon? PARP9 and PARP12 were also upregulated by INFγ treatment. Are these factors also involved in condensate formation?
      3. Figure 4D appears to be immunoprecipitation (IP) under non-denaturing conditions. If so, it is not possible to distinguish whether the MAR signal is derived from p62 or from the p62 interacting proteins (the associated ubiquitinated substrates). IP experiments should be performed under denaturing conditions.
      4. In Figure 5B, which band is HO1, the upper or lower?
      5. There is no image for ubiquitin in S5D. Right panel in Figure 4F shows only IFγ + RBN, which should show all data sets in the same panel.

      Significance

      Liquid droplets, which have continuously being identified in cells, are a hot topic in cell biology. Droplet formation, structure, molecular dynamics, and degradation, as well as their abnormalities and disease development due to genetic mutation and stress, are of wide-ranging interest from basic to pathological aspects. Therefore, this research has the potential to attract interest from a wide range of fields.

      General assessment

      Overall, the data are clear and the phenomenon is of interest. However, the molecular mechanism and biological significance of the condensate formation is unknown; It is unclear why proteasome activity is required for the formation of PARP14-mediated ADP ribosylation. It is also unclear what the consequences are for the cell if the ADPr-positive condensates are not formed. Thea authors should address these general and important issues and provide the data If not all.

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      Reply to the reviewers

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

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      Referee #3

      Evidence, reproducibility and clarity

      The manuscript by Balachandra and Amodeo presents Bellymount-Pulsed Tracking as a technique for continuous long-term imaging of Drosophila oogenesis. This approach modifies the existing Bellymount technique by exposing restrained female flies to pulses of CO2 anesthesia in combination with image acquisition. Flies that survived the restraint were kept alive for many hours by addition of a liquid diet in the restraint apparatus. This allowed for imaging and tracking of egg chamber development over longer time periods than capable with ex vivo culturing methods. However, the authors did report a 40% mortality rate and decreased fecundity compared to unrestrained flies. Using this method the authors were able to image and measure the growth rate of developing egg chambers in living flies, and capture events like vitellogenesis which relies on the interactions of multiple organ systems.

      This technique is a notable contribution to the fly community, as it could be useful for studying processes that require interactions between multiple tissues and organs, as well as for long-term imaging of other internal structures in the adult fly. The significance is somewhat reduced due to the relatively high mortality rate and the decreased fecundity and egg chamber growth rate reported. However, the authors should be commended for their diligence in documenting the limitations of the procedure, as this now provides a strong jumping off point to improve the technique if it becomes widely adopted by the fly community. Overall, the experiments appear to have been carefully performed and the manuscript is clearly written. However, there are several issues that should be addressed prior to publication.

      Major concerns

      1. The movies of egg chamber development are challenging to interpret. They could be improved by the addition of timestamps and other annotations. Having multiple example movies of the same process would also be valuable. It could be helpful to potential users of this technique to show the process the authors used for identifying the same egg chamber between such long time points.
      2. Figure 4 - Given that the Bellymount PT technique slows oogenesis and reduces egg chamber growth in vitellogenic stages (Figure 3E), it is possible that Bellymount PT slows yolk protein uptake. It would be important to establish a baseline for how much to expect yolk protein levels to change across stages to compare to measurements obtained with Bellymount PT. It would be a relatively simple experiment to show the change in yolk protein uptake across stages in fixed samples. This could also be performed for His2Av dynamics during nurse cell dumping.
      3. Movie 11 - The authors propose that Bellymount-PT can be used to visualize the process of border cell migration. However, there is no obvious movement of the cluster relative to the nurse cell nuclei over the course of the 3 hour long movie. The authors should either show a better movie of border cell migration, or remove this claim from the manuscript.
      4. Movie 13 - The authors claim that they see egg chamber rotation continue in stage 9 and 10 egg chambers. This movie is not convincing. There is also very strong evidence in the literature that egg chamber rotation ends at stage 8. Chen et al., Cell Reports, 2017 showed using a method that tracks follicle cell migration in vivo that rotational migration ends during stage 8. The only movement of follicle cells after stage 8 is due to the epithelial reorganization that occurs during the posterior movement of the follicle cells as the stretch cells flatten. Additionally, after stage 8 follicle cells lose their circumferentially oriented actin protrusions that drive rotation. This claim should be removed from the manuscript.

      Minor comments

      1. Line 104 - The authors mention that CO2 affects fertility in flies. They should also reference Sustar et al., Genetics, 2023 and Zimmerman and Berg, PLoS One, 2024 for wider ranging effects of CO2 on oogenesis.
      2. Line 244 - Although it is true that the original paper describing egg chamber rotation reported that it starts at 5, subsequent studies from multiple labs have confirmed that it begins much earlier. First shown by Cetera et al., Nature Communications, 2014 but later confirmed by Bilder, Dahmann, and Mirouse labs. Chen et al., Cell Reports, 2016 has even published a movie of an egg chamber initiating rotation as it buds from the germarium.
      3. Figures of egg chambers are generally oriented anterior on the left and posterior on the right. Reorienting all the figures would be challenging, so the recommendation is to be clear in the figure legends the orientation of the images. This is important given they are shown in different orientations in Figure 1 than throughout the rest of the paper, and also will be helpful for readers who may not be familiar with the structure of the ovary/egg chambers.
      4. Figure 1B and Methods line 334 - Should "Rely" be "Relay"?
      5. Figure 1E - Oocyte nuclei are missing from the diagrams of stage 7, 13 and 14 egg chambers. Also, "G" looks like a figure panel label, could just say Germarium
      6. Figure 3F-H - "Stagee" should be "Stage"
      7. Figure 4B - Why is the fluorescence for egg chamber #6 so much higher than the others? It makes the slopes of the other samples hard to see.
      8. Figure 4D,E,G - For clarity, the labeled boxes should be the same color as the lines on the associated graphs. In line 790 "Note the steady increase of H2Av in all three regions as it exits the nurse cell nuclei" - this is not actually shown without the nurse cell nuclei average intensity being on the graph as well.
      9. Line 787 - "Note the flow of H2Av" - "flow" is not actually shown in these static images. Consider a more precise description.

      Referee Cross-commenting

      The other reviewers make several excellent points. We personally feel that it is beyond the scope of this initial report to ask the authors to show that they can see all aspects of oogenesis with this technique. If the method becomes widely adopted by the oogenesis community, individual researchers can optimize it to suit the exact process they want to study. If the authors want to claim they can see a particular process, it needs to be well documented and convincing. For example, we agree that the movies that claim to show egg chamber rotation (both during established stages and later) and border cell migration need to be improved or the claims need to be removed. However, we feel that the authors have documented enough other interesting processes to make the study worthy of publication. Likewise, asking the authors to determine the minimal time window that can be used for imaging could take months of open-ended work and is something that could be better tackled by subsequent users depending on the requirements of the biological process they want to study. It seems better to get the work out into the public sooner rather than later so that improvements can be crowd sourced.

      Finally, although Flp-out clones were used for cell tracking in the original Belly mount paper, this technique will be less effective during the first half of oogenesis when the egg chamber is rotating, as the clone is likely to rotate into and out of sight between imaging time points.

      Significance

      This technique is a notable contribution to the fly community, as it could be useful for studying processes that require interactions between multiple tissues and organs, as well as for long-term imaging of other internal structures in the adult fly. The significance is somewhat reduced due to the relatively high mortality rate and the decreased fecundity and egg chamber growth rate reported. However, the authors should be commended for their diligence in documenting the limitations of the procedure, as this now provides a strong jumping off point to improve the technique if it becomes widely adopted by the fly community. Overall, the experiments appear to have been carefully performed and the manuscript is clearly written. However, there are several issues that should be addressed prior to publication.

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      Referee #2

      Evidence, reproducibility and clarity

      Summary:

      The authors describe an improvement of the Bellymount imaging method for internal tissues of the fly's abdomen. They are able to increase the total duration of the imaging by introducing pulsed anesthesia. This allows the immobilized flies to take up food in between the imaging; this increases survival rate and allows for longer total imaging times. The authors illustrate the technique by tracking the development of egg chambers.

      Major Points

      • The Bellymount PT method results in decreased fecundity, which might affect the processes (oogenesis) the authors looked at. Indeed, the authors conclude that "oogenesis is not completely stalled under the Bellymount-PT protocol" (line 140). The authors do provide some data indicating that egg chambers develop (Fig. 2G,H; Fig. 3F,H), in particular a stage 10 egg chamber proceeding to a stage where dorsal appendages seem to form. However, for early stage egg chambers this is less convincing. The egg chambers show an increase in (cross-sectional) area, however, what is the evidence that they also mature? For example, during egg chamber maturation, the ratio of oocyte/nurse cell volume changes, follicle cells re-arrange, etc. The authors should test whether any of these characteristics can be observed in egg chambers imaged using Bellymount PT. This may include the imaging of egg chambers in which both nuclei and plasma membranes are visualized.
      • A potential advantage of the Bellymount PT method is the ability to follow the dynamics of processes. A current drawback, however, is the rather low temporal resolution as the fly needs to wake up between single images. The authors should provide an estimate for the minimal possible cycle time and should test whether flies imaged at 10 minutes interval show lower survival/fecundity than flies imaged at 2 hours interval.
      • The authors claim that they can track on a cellular level (based on nuclei), but it is unclear how accurate the tracking is. Especially cell tracking over very long times might be challenging here, as the time delay between two time points is big. The authors should test the accuracy of their tracking, potentially by creating Flip-out clones and using them as a control.
      • The authors show that they can visualize cell membranes (Moesin-GFP, Fig. 2C). Tracking cells over time based on their membranes would greatly widen the applicability of the method as it would enable to analyze the complex cellular dynamics during egg chamber maturation. The authors should test whether cells can be tracked over time (e.g. using Moesin-GFP) using their technique.
      • Movie 11. The authors claim that they can capture border cell migration. However, it is unclear whether the border cells actually migrate towards posterior. The authors should track and quantitatively analyze the migration path of the border cells in their movies.
      • Movie 12. The authors claim that they can observe egg chamber rotation. However, it is unclear whether the egg chambers actually rotate. The authors should track cells and quantify the angular velocity of movement.

      Minor Points

      • Please move the labels of the scale bars to the legends.
      • The figures (especially 2 and 3) would benefit from a clearer structuring. Moving part of them to supplementary figures would also help.
      • "stage" typo in figure 3

      Significance

      The authors describe here an improvement of an existing technique. The advantage of the improved technique is the longer imaging time, which potentially allows users to track cells/organelles/proteins over time. However, tracking requires the user to connect single time points with each other, which is somewhat unclear at this time. Moreover, the potential applicability (and significance) of the technique would be widened if visualization and tracking of cell membranes/organelles/vesicles would be possible. With these further optimizations, the technique would add a useful tool to the Drosophila community.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary

      The Drosophila ovary is an established model system for many aspects of development and cell biology. In vitro culture of live ovaries has provided valuable insight, yet these methods do not accurately mimic oogenesis in vivo for some stages. Here the authors develop a new method that allows for sustained imaging of ovaries in intact flies, maintaining normal physiology.

      The method provides a valuable addition to the field. Processes such as growth, cell migration, egg chamber rotation, yolk uptake and nurse cell dumping can be observed in the intact fly. Time lapse and 3D reconstruction provide valuable tools. While the detail/resolution of the images is not as good as ex vivo or fixed samples, the ability to maintain normal development and homeostasis provides a novel advantage. The figures and movies are well-presented and sufficient detail is provided in the methods.

      Major comments

      1. Why do the authors think that growth is slowed? The imaging process or the trapping/anesthesia of the fly? For example, if the frequency of imaging was varied, it could reveal whether it was the actual imaging that affected development. Did the length of time the fly had been in the trap make a difference? The sentence on lines 190-191 is not clear.
      2. In Movie 6, the nurse cell nuclear shape does not look normal - more ovoid than round. Perhaps some settings are off in the 3D reconstruction.
      3. Movie 11 - why do the border cells seem stalled?
      4. There is no discussion of the earliest stages of oogenesis. Is it possible to see egg chambers forming from the germarium?

      Minor comments

      1. It would be helpful to mention if the egg chambers stay in similar locations or move around - is it challenging to locate the same egg chamber after 2 hours?
      2. Are any egg chambers degenerating? This could indicate stress in the fly.
      3. In Figure 4D, release of HisAV into the cytoplasm is described. Similar release of nuclear proteins was described by Cooley et al. 1992 so this paper could be cited.
      4. At 321 minutes in Figure 4D, a large nucleus is apparent in the oocyte. Is this an oocyte nucleus or evidence for nurse cell translocation to the oocyte as described in Ali-Murthy et al. 2021?

      Significance

      The technique provides a significant advance to the field, extending the time period currently possible to image ovaries through the Belly Mount method. It will immediately benefit researchers working on the ovary but could be extended to many other tissues in the fly abdomen such as the gut and tumor models.

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      Reply to the reviewers

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

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      Referee #3

      Evidence, reproducibility and clarity

      Summary:

      Parkin, a E3 ubiquitin ligase, is involved in the clearance of damaged mitochondrial via mitophagy. Upon mitochondrial damage, the activated Parkin ubiquitinates many mitochondrial substrates, leading to the recruitment of mitophagy effectors. However, the mechanism of substrate recognition by Parkin is still not known.

      In this manuscript, Koszela et al. utilized diverse biochemical assays and biophysical approaches, combined with AlphaFold prediction, to identify a conserved region in the flexible linker between the Ubl and RING0 domains of Parkin that recognizes mitochondrial GTPase Miro1 via a stretch of hydrophobic residues and is critical for its ubiquitination activity on Miro1. This manuscript reveals the mechanisms by which Parkin recognizes and ubiquitinates substrate Miro1, providing a biochemical explanation for the presence of Parkin at the mitochondrial membrane prior to activation by mitochondrial damage. This study also provides insights into mitochondrial homeostasis and may facilitate new therapeutic approaches for Parkinson's disease.

      Major Comments:

      • The authors should expand the background introduction to include the biological function of Miro1, the domain architecture of Miro1 and more context of Miro1 K572 ubiquitination in mitophagy.
      • Figure 1B is confusing. Due to the presence of various bands, it is hard to assign specific bands in each lane. In addition, there are various unlabeled bands that makes things unclear. The authors should include loading controls to clearly discern pParkin, Ube1, Ube2L3, and all substrates.
      • In Figure 1B, it was not possible to identify the ubiquitination bands of E2 enzyme UBE2L3 and the E1 enzyme UBE1. Please indicate these bands on the gel.
      • Since ubiquitinated Miro1 and Mfn1 are similar in molecular weight (Fig. 1b), the authors should show a western blot against the Miro1 and Mfn1 tag as done in the supplementary information, At least for the competition assays involving both Miro1 and Mfn1.
      • The conclusion that Miro1 is pParkin's preferred substrate is not convincing. In the competition assay used to show substrate preference, Miro1 is at a five-fold higher concentration than the other substrates and 25-fold higher than FANCI/D2. This would ultimately drive pParkin's interaction with Miro1. This is further highlighted by the fact that it adding Mfn1 in excess has a similar effect. The competition assay should be done at equimolar concentrations of Miro1 and substrate. More convincing would be a competition assay where substrate ubiquitination is quantified at several different concentrations of Miro1.
      • In Figure 1F, it is unclear what is defined as "high" or "low" ubiquitination levels statistically. Some of the changes in ubiquitination levels are extremely subtle (ex. mitoNEET and FancI/D2 in the presence and absence of Miro1 and Mfn1). In some cases, I find it extremely difficult to tell if there is any change in the ubiquitination levels when comparing lanes containing excess of different substrates. I would like to see band quantifications of this experiment in triplicate to support the conclusions drawn from the competition assay.
      • The authors used both unmodified and phosphorylated Parkin for the crosslinking experiments and observe no difference in the intensity of the bands. However, this is not sufficient to draw any conclusion about the affinity between phosphorylated Parkin and Miro1 (which was done in lines 341-343). The authors should comment on why they did not test pParkin binding with Miro1, especially given the statement:

      "In our assays in the absence of pUb, pParkin must interact with its substrates without the action of pUb, likely through 158 transient, low affinity interactions" - The reference to Parkin115-124 as a "Substrate Targeting Region (STR)" is misleading. This would imply that this motif in Parkin is responsible for general substrate recognition when there is no direct evidence of this. In Figure 5F, the authors create a synthetic peptide based off the STR sequence. Although this sequence was effective in inhibiting the ubiquitination of Miro1, it was ineffective against Mfn1. This would indicate that Mfn1 relies on a completely different set of interactions for ubiquitination by Parkin. I suggest that the authors tone down the language in describing this region and rename this region (perhaps "Miro1 Targeting Region (MTR)"?). - The authors appear to confuse plDDT and PAE scores in Figure 5B. The PAE describes the expected positional error of each residue in the model. The plot should be colored in terms of Expected Position Error (Ångstrom), not plDDT scores.

      Minor Comments:

      • Figure 1A would benefit from a schematic showing the domain architecture. If the goal is to appreciate the length of the linker, then showing the actual amino acid length would be beneficial.
      • In Supplementary Figure 2D, the authors performed the MST experiment with His6-Smt3-tagged Parkin. The group had previously shown that the presence of the tag artificially interferes with autoubiquitination, potentially by forming intramolecular interactions. The SEC, Native Page, and ITC data of untagged Parkin with Miro1 provide sufficient evidence that the interaction between the two are weak. The authors should consider removing the MST data, since they are not congruent with the other experiments.
      • The ITC data in Supplementary Figure 2C look promising. It would be nice if the authors could try to quantify the Kd of their STR peptides to Miro1
      • Are STR peptides 1 and/or 2 unable to inhibit ubiquitination of other Parkin substrates besides Mfn1? Do these other substrates utilize the STR for recognition? AlphaFold modeling may provide some insight on Parkin recognition of other substrates.
      • The authors shold consider using AlphaFold3 to model the interaction of pParkin with Miro1 compares to unmodified Parkin.
      • Please label the protein names in Figure 4A for a better presentation.
      • Page 2, line 37. "...by a 65-residue flexible region (linker) to a unique to Parkin RING0 domain..." should be "...by a 65-residue flexible region (linker) to a unique Parkin RING0 domain...". The second "to" should be omitted.
      • Page 3, Line 48: "fulfill", not "fulfil"
      • Page 5, line 110. In sentence, "...phosphorylation at Ser65 of Parkin...", it is better to explicitly state that this phosphorylation happens on the Parkin Ubl domain.
      • Page 7, line151. Figure 1F should be Figure 1G.
      • Page 11, line 241. In sentence "...Miro1 residues R263, R265 and D228...", do the authors mean R261 and not R265?

      Significance

      Parkin is an E3 ubiquitin ligase that is activated to ubiquitinate diverse substrates on the mitochondrial membrane in response to mitochondrial damage, thereby recruiting mitophagy effectors. This study reveals the mechanisms by which Parkin recognizes and ubiquitinates Miro1, providing insights into mitochondrial homeostasis and facilitating new therapeutic approaches for Parkinson's disease.

      Readers with a background in protein ubiquitination and mitochondrial homeostasis might be interested in this study. My expertise includes protein ubiquitination and structural biology. However, I do not have sufficient expertise to evaluate the NMR experiments in this manuscript.

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      Referee #2

      Evidence, reproducibility and clarity

      Koszela et al. have submitted this manuscript demonstrating the molecular mechanism of interaction between Parkin and one of its known substrates, Miro1. While the interaction and ubiquitination of Miro1 by Parkin (and it's role in mitochondrial quality control) has been known since 2011, as demonstrated by the Schwarz group and others, the mechanism of action has remained unknown. The ability of Parkin to ubiquitinate multiple proteins upon mitochondrial damage has indeed led many groups to speculate that Parkin is a promiscuous E3 ligase upon activation; this manuscript tries to provide a rationale for the interaction with one of its known substrates through a combination of biochemical and biophysical studies.

      The authors demonstrate that Miro1 is efficiently ubiquitinated in in vitro biochemical assays in comparison to a few mitochondrial and non-mitochondrial proteins in an attempt to show that Miro1 is a preferred substrate for Parkin. Cross-linking coupled with mass spectrometry, SAXS and NMR experiments were used to provide compelling evidence for a direct and specific interaction between Parkin and Miro1. Molecular modelling using Colabfold and biochemical assays with mutants of the proposed interaction site were then used to provide further proof for the specificity of the interaction. This interaction is shown to occur between the conserved a.a.115-122 (referred to in this study as STR; located in the linker connecting the Ubl to RING0) and the EF domain of Miro1. Interestingly, the authors show that peptides corresponding to 115-122 competitively inhibit ubiquitination of Miro1 by Parkin. Overall, this article constitutes an important addition to our understanding of Parkin's mechanism of action. However, some of the key claims remain unsubstantiated, as described below.

      Major issues:

      1. In line 151 the authors claim, 'these data strongly support the hypothesis that Miro1 is the preferred substrate of pParkin...'. Arguably, the biggest issue with this study is the lack of substantial proof that Miro1 is the preferred parkin substrate in a cellular or physiological context. This claim cannot be made based on a biochemical assay with three other proteins. The Harper group has performed in-depth proteomics studies on the kinetics of Parkin-mediated ubiquitination and proposed that VDACs and Mfn2 (among a few others) are most efficiently ubiquitinated upon mitochondrial damage in induced neurons (Ordureau et al, 2018,2020). Interestingly, neither of these papers have been mentioned by the authors in this manuscript. The Trempe group has shown that Mfn2 is efficiently targeted by Parkin through mitochondrial reconstitution assays and proximity ligation assays (Vranas et al, 2022). The authors need to substantiate their claim through cellular or mitochondrial assays to prove that Miro1 is the preferred physiological substrate of Parkin. Cellular experiments also account for cellular abundance and proximity of Parkin to the substrate, which is not possible in biochemical assays of the kind presented here. In the absence of strong experimental proof for this claim, these claims should be tampered down to Miro1 being "the preferred substrate compared to the other proteins in this assay", and the manuscript should focus more on the molecular mechanism of interaction between Miro1 and Parkin.
      2. In addition to the point above, the authors do not describe the rationale for specifically choosing Mfn1 and MitoNEET for their comparison with Miro1 as substrates. Interestingly, Miro1, MitoNEET and Mfn1 are not among the most efficiently ubiquitinated substrates of Parkin (Ordureau et al, 2018). Additionally, the authors have used a construct of Mfn1 that lacks the full HR1 domain for their assays. Previously, it has been shown that the HR1 of mitofusins is targeted by Parkin (McLelland et al. 2018). Can the authors prove that their Mfn1 construct is as efficiently ubiquitinated as full-length Mfn1 by Parkin? If it is not possible to obtain soluble full-length Mfn1 or other membrane proteins for these assays, then I strongly recommend the authors should perform mitochondrial reconstitution assays as others have performed previously (Vranas et al, 2022) and use this opportunity to also report the ubiquitination kinetics of multiple mitochondrial substrates compared to Miro1 to make a more compelling case for substrate preference.
      3. The authors show that both pParkin-Miro1 and Parkin-Miro1 complexes can be captured by chemical cross-linking. It is well-established in the field that pUbl binds to RING0 (Gladkova et al, 2018) (Sauve et al, 2018) while non-phosphorylated Ubl binds RING1 (Trempe et al, 2013). The Komander group has also shown that the ACT (adjacent to the STR) element binds RING2 in the activated Parkin structure (Gladkova et al, 2018). This suggests that STR could occupy different positions in the Parkin and pParkin. The authors have only reported the cross-link/MS data and model of the Parkin-Miro1 complex. Arguably, the pParkin-Miro1 data is just as, if not more, relevant given that pParkin represents the activated form the ligase. The authors need to robustly establish that Miro1 binds to the STR element in both cases by demonstrating the following:

      A. Mass spectrometry data from cross-linked pParkin-Miro1 complex suggesting the same interaction site.

      B. Colabfold modelling with the pParkin structure to show that Miro1 would bind to the same element. 4. Does Parkin only bind to Miro1, or can it bind to Miro2 as well? Are there differences between the binding site and Ub target sites between the two proteins? The author should also show experimentally if both proteins get ubiquitinated as efficiently by Parkin and if the STR element is involved in recognizing both proteins. Interestingly, the Harper group reports that Miro2 gets more efficiently ubiquitinated than Miro1 (Ordureau et al, 2018). 5. In Figure 5D, the level of unmodified Miro1 seems to be similar in assays with WT or I122Y Parkin, though the former seems to form longer chains while the latter forms shorter chains. Is there an explanation for this? Perhaps, the authors need to perform this assay at shorter time points to show that there is more unmodified Miro1 remaining when treated with I122Y Parkin (and similarly for the L221R mutant of Miro1)? Also, why is the effect of Miro1 L221R and Parkin I122Y not additive?

      Minor comments:

      1. The authors should report the full cross-linking/MS data report from Merox including the full peptide table and decoy analysis report.
      2. The authors should report statistics for the fit of the Colabfold model to the experimental SAXS curve.
      3. Why is the Parkin-Miro1 interaction only captured by NMR and not by ITC? The authors should at least attempt to show the interaction of the STR peptide with Miro1 by an orthogonal technique like ITC.
      4. The authors should report the NMR line broadening data quantitatively i.e. reporting the reduction in signal intensity for the peaks upon peptide Miro1 binding to quantitatively demonstrate that the 115-122 peak intensity reduction is more significant than other regions.
      5. Figure 4 (structure figure) and B (PAE plot) should be annotated with the names of domains and elements in Parkin and Miro1 to make these figures clearer and more informative.

      Referees cross-commenting

      I am in agreement with reviewers 1 and 2. Both of them raise valid and interesting points in their reviews.

      Specifically, I would like to highlight the following:

      1. Reviewer 1 makes a very good point (5/6) highlighting that L119A does not impair Parkin recruitment in the previously reported study. I second this concern and believe that the authors need to re-frame their discussion and make it much more nuanced with regards to the role of Miro1-Parkin interaction in mitophagy (if any at all). Additionally, the authors should also note that previous studies in the field from the Youle group (Narendra et al, 2008) and multiple other groups have shown a complete absence of Parkin recruitment to healthy mitochondria. Parkin recruitment to healthy mitochondria hence remains a controversial idea at best, with no evidence for it outside of Parkin overexpression systems (Safiulina et al, 2018) which can also lead to artifacts. The discussion should take all major studies/observations into account to propose a more nuanced picture of the role of Parkin-Miro1 interaction. Perhaps, this interaction plays more of a role in mitochondrial quarantine (Wang et al. 2011) as suggested by the Schwarz group than in Parkin recruitment?
      2. Reviewer 3 raises a valid concern about the lack of quantification in ubiquitination assays and alludes to the difficulty in visualizing ubiquitination of multiple proteins. That was a concern I also had but did not include in my review. Perhaps, the authors should also show western blots for each of the protein (in a time course experiment) demonstrating the difference in ubiquitination kinetics of each of proteins instead of busy SDS-PAGE gels for the assay.

      Significance

      The key strength of this study is the strong biophysical evidence of a direct interaction between Parkin and Miro1 and the discovery of the Miro1 binding site on Parkin. The biophysical and biochemical experiments in this study have been well-designed and executed. The evidence for a specific interaction between Parkin and Miro1 has been provided through multiple approaches. The authors should be commended for this effort. The biggest limitation of this study is the lack of proof that Miro1 is the preferred Parkin substrate in a cellular/physiological context since in biochemical assays Parkin can ubiquitinate multiple proteins non-specifically. Substrate preference claims need to be established in more physiologically relevant experimental settings.

      Overall, the study represents a mechanistic advance in terms of our understanding of the interaction between Parkin and one of its substrates i.e. Miro1, showing that Parkin can indeed specifically bind its substrates before targeting them for ubiquitination. This might also inspire others to investigate the molecular mechanism of action of Parkin with other substrates. This paper would likely appeal specialized audiences i.e. biochemists and structural biologists studying Parkin in mitochondrial quality control.

      Reviewer expertise: Expert biochemist and biophysicist with a number highly cited works in the field of mitochondrial quality control and Parkin.

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      Referee #1

      Evidence, reproducibility and clarity

      The manuscript by Koszela et al. explores the substrate preference of the Parkinson's disease associated ubiquitin E3-ligase, Parkin. They conclude that Miro1 is a preferred substrate of Parkin and go on to further characterize a binding site of Parkin to Miro1 using a range of biochemical approaches. This site is identical to previously reported (see point 2). The experimental work is strong with many high-quality assays supporting their ideas; however, there are several major points that should be considered:

      1. The majority (perhaps all) of their biochemical work on Miro1 uses a truncated form of Miro1 lacking the first GTPase domain. It isn't at all clear why this is the case, as no justification is given. Moreover, functional full-length Miro1 has been purified in several papers (e.g. PMID: 33132189). If ubiquitination kinetics are different between the full-length and truncated form of Miro1, this would call into question the significance of the findings in vivo, where the truncation does not exist.
      2. As the manuscript is currently written, there are areas which do not do justice to previous work. Firstly, the authors state throughout the manuscript that no previous work has identified a binding interface between Parkin and one of its substrates, e.g., in the abstract "no substrate interaction site in Parkin has been reported". This is not true as a recent paper already described the binding interface (DOI: 10.1038/s44318-024-00028-1). "we identify a conserved region in the flexible linker", again this interface is identical to that identified previously. Therefore, this study does not "identify" this interface. Given the timing, it is likely that this discovery has been "scooped" by the previous study, but since the present study goes much further in the biochemical characterization of the interface, it would not diminish the paper's importance to rewrite it, giving proper credit where due. Secondly, the authors spend a large part of their discussion speculating on the significance of non-activated Parkin being able to bind Miro e.g., "Importantly, our results suggest that Parkin can interact with Miro1 independently of its activation state, as Parkin phosphorylation does not detectably increase its interaction with Miro1...". Again, this was already known as Parkin has been shown to be recruited to mitochondria upon Miro1 overexpression in the absence of PINK1 (DOI: 10.15252/embj.201899384 and DOI: 10.15252 /embj. 2018100715). The further biochemical characterisation of the Parkin-Miro1 interaction is important and therefore, in both cases the work contained within the manuscript is still a significant contribution, which should, however, be properly discussed in the light of published work.
      3. The Miro L221R mutation is used to disrupt Miro-Parkin interaction. Yet, this non-conservative mutation in the midst of a folded domain might have other effects, like affecting calcium binding or preventing the folding of the domain. This is not tested. The complementary Parkin-I122Y used for the same purpose decreases but does not abolish Parkin-Miro1 binding. Parkin-L119A is proposed to abolish the Parkin-Miro1 interaction. The inclusion of this mutant might be important to fully ascertain the role of Parkin-Miro1 binding in Miro1 ubiquitination.
      4. The effect of Miro competition on other substrates' ubiquitylation is marginal and its reproducibility is questionable (whether mitoNEET ubiquitylation is affected at all in figure 1G is unclear. This blot is anyway over processed with an unnaturally uniform grey background). If the authors wish to make a point about it, these experiments should be repeated and quantified. Moreover, since the model is that the specific Miro-Parkin interaction is involved, the mutants above should be used in the same competition experiments and shown to be unable to compete.
      5. Related to the previous point, one important factor about the kinetics that the authors do not discuss is how any of it relates to mitophagy in vivo. There very well might be a slight intrinsic preference at a given concentration of substrate and Parkin; however, how this plays out in the cell is not clear, e.g., Miro1 may be many times more, or less, abundant than Mfn1, and so a preference might not have much of an effect. So ubiquitination kinetics would need to be considered in a broader cellular context.
      6. Related to the above point, the authors state "Parkin translocation was diminished upon L119A mutation, supporting the importance of the Parkin Miro1-interacting site in mitophagy.". However, the study (not cited but which this reviewer assumes to be DOI: 10.1038/s44318-024-00028-1 since the L119A mutation has only ever been used here) finds no change in Parkin recruitment upon damage. So, it cannot be used to support "the importance of the Parkin Miro1-interacting site in mitophagy".

      Referees cross-commenting

      The reviews align well together with many overlaping point and similar assessment of the significance. Reviewer 2 brings in interesting points pertaining to literature that we were not aware of, explaining why we didn't make these points.

      One comment on reviewer's 3 last major points

      It does not appear that there is a confusion between pIDDT and PAE scores. The plot is coloured according to PAE (which is a residue x residue 2D matrix, figure 4B), while the protein ribbon is coloured according to pIDDT, which is a 1D per-residue confidence score.

      Significance

      This study provides an in-depth in vitro assessment of a specific binding interface between the E3-ligase Parkin and one of its substrate Miro1. Although this interface has been recently described, this study goes well beyond previous knowledge by showing that the interface is important for complete Miro ubiquitylation by Parkin, therefore showing that interactions involving unstructured linkers participate in substrate recognition by the E3-ligase. The importance of this interaction remains to be assessed in vivo. This study is of interest to basic mitochondrial dynamics, quality control and mitophagy researcher as well as translational Parkinson's Disease researchers.

      The reviewer's expertise is in mitochondrial membrane dynamics.

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      Reply to the reviewers

      Manuscript number: RC- 2024-02497

      Corresponding author(s): Tourriere, Hélene and Maraver, Antonio

      1. General Statements [optional]

      We sincerely thank the Editors and Reviewers for the time devoted to our manuscript. We found their critiques interesting and very helpful. After careful examination and thanks to a large collaborative effort, we will be able to answer to all the reviewers’ comments by adding significantly new experimental data.

      We are also encouraged by the positive comments of the Reviewers:

      “This manuscript will likely engage oncologists who investigate the chemotherapy-resistant mechanisms of platinum compounds in NSCLC treatment” (Reviewer 1);

      “Overall, the authors have conducted experiments that sufficiently elucidate their claims, and the description of the experiments is detailed.”; and “Overall, this work unveils a novel mechanism for Notch activation in response to platinum chemotherapy, providing a renewed outlook on overcoming chemotherapy resistance in NSCLC” (Reviewer 2).

      We are also aware that both reviewers agreed that there is room for improvement, and we are sure that upon accomplishment of all proposed experiments both reviewers will be fully satisfied.

      Please bear in mind that although it was known that platinum-based chemotherapy induced the Notch pathway in lung cancer cells, the underlying molecular mechanism was largely unknown. Thanks to the molecular dissection we performed in our study, we propose an innovative treatment for patients with lung cancer, the main cause of death by cancer in the world. Hence, we agree with both reviewers that our study will be appealing for a large number of cancer researchers, and we feel it will be also the case for those interested in DNA damage, Notch and MDM2 pathways.

      2. Description of the planned revisions

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

      Summary: This manuscript from Maraver and co-authors investigates the putative resistance mechanisms that hinder the efficacy of platinum-based therapies (e.g., carboplatin) against non-small cell lung carcinoma (NSCLC). Using in vitro lung cancer cell lines, shRNA-based knockdown, and exogenous overexpression systems, the research describes a DNA damage-induced resistance mechanism involving the NOTCH signaling pathway and the E3 ligase MDM2. The authors show that carboplatin treatment induces DNA damage and promotes ATM activation, which in turn activates the NOTCH signaling pathway via ubiquitination and stabilization of the Notch Intracellular Domain (NICD). New findings include the MDM2-mediated ubiquitination and stabilization of NICD. Using in vivo NSCLC-PDX models, they demonstrate that combining carboplatin with Notch and MDM2 inhibitors can enhance tumor killing, suggesting that targeting the MDM2/NICD axis in conjunction with carboplatin may be a viable therapeutic alternative. Furthermore, they show that NICD and MDM2 levels are elevated among tumor samples from chemo-resistant patients. Consistent with these findings, high MDM2 levels correlate with poor progression-free survival (PFS) in NSCLC patients.

      [Authors] We thank this reviewer for her/his fair summary of our work that highlights our new findings.

      Major comments:

      Some of the key conclusions may not be convincing.

      [Authors] We understand the concerns that reviewer might have and we are sure that upon accomplishment of all experiments detailed below, she/he will be convinced that the manuscript will be ready for publication.

      1. One significant weakness of the manuscript is the lack of exploration into the underlying mechanism of how MDM2 mediates the stabilization of NICD. While the observation of MDM2-mediated NICD stabilization is intriguing, it is important to provide a more convincing explanation for the reviewers. This could be achieved by offering a detailed molecular mechanism, especially considering that MDM2 typically targets proteins for degradation.

      [Authors] After reading this reviewer’s comment, we realize we did a poor job discussing better the previous study demonstrating that MDM2 induced ubiquitination on NICD but not for degradative purposes (Pettersson et al., 2013). In particular, they performed it using a mutated form of ubiquitin in lysine 48, i.e., the K48R mutant. Like this, the authors of this seminal study demonstrated that MDM2 was still able to induce ubiquitination in NICD, and hence it was not degradative.

      Still, and to confirm that this is the case also upon DNA damage, we will perform experiments using same K48R mutant to formally prove that MDM2 upon DNA damage does not ubiquitinate NICD via lysine 48-linked polymers, and hence it is not degradative. Even more, upon discussion with Laetitia Linares, author of our study and long-lasting expert in ubiquitination (for instance see (Riscal et al., 2016) and (Arena et al., 2018)), we will use another ubiquitin mutant in lysine 63. This different type of ubiquitination does not mark proteins for degradation but promote an association of the targeted protein with DNA helping for DNA repair (Liu et al., 2018). Using a ubiquitin mutated in this lysine, i.e., K63R, this type of ubiquitination cannot occur. Taking into account that we observe NICD increase ubiquitination upon DNA damage, the use of K63R will be very informative.

      Hence, we will repeat experiments of current Figure 3A with the same WT ubiquitin as before, and now also with K48R and K63R mutants. Even more, we will also include mutant forms of ubiquitin which can only form ubiquitin chains on lysine 48 (K48 only) or lysine 63 (K63 only) and we anticipate that in the presence of K48 only mutant, NICD will not be ubiquitinated upon DNA damage, while the use of K63 only mutant will be very useful. All these data will be part of the new Figure 3A.

      Of note, Dr Linares has all tools required to perform these experiments and hence we will start them soon.

      Another weakness lies in the unclear role and the underlying mechanism of ATM in the MDM2-mediated NICD stabilization. While the data presented (Fig. 3B, 3C) suggest that carboplatin could elevate MDM2 levels for NICD stabilization, a more precise method to induce MDM2 overexpression specifically for targeting NICD is required. It appears that ATM plays a crucial role in this regulatory process. The following questions must be addressed: Does ATM induce the phosphorylation of MDM2 for its protein stabilization and/or E3 ligase activity?

      [Authors] There are several points here.

      For the first one, the use of a more precise method to induce MDM2 overexpression, it is exactly what we did in Figure 4A, i.e., ectopic expression of MDM2 to demonstrate that MDM2 is sufficient to increase NICD levels.

      For the second one, i.e., the phosphorylation status of MDM2 by ATM in our system, we will perform different experiments. There are up to six proposed residues in MDM2 to be phosphorylated by ATM upon DNA damage: S386, S395, S407, T419, S425, and S429 (Cheng et al., 2011). Among all of them, S395 is the most well-known and again Dr Linares has interesting tools we will use to answer to this specific reviewer’s point. We will use an MDM2 mutant harboring an aspartate instead of the serine in this position, i.e., S395D, that mimics the serine 395 phosphorylation induced by ATM upon DNA damage. We will use this mutant together with the WT and 464A MDM2 proteins already used, and if this residue is important in our phenotype, total levels of NICD will be even higher and/or localize more in the nuclei when compared with WT MDM2. All these new data will appear as the new Figure 4A __and new Figure 4B__.

      Furthermore, we will also use an antibody that recognizes this phosphorylation site by WB after carboplatin treatment and it will be part of the new Figure 3B.

      Finally, we will also express WT MDM2 and purify it by immunoprecipitation in different experimental conditions: steady state, upon carboplatin treatment and also in combination of carboplatin and ATM inhibitor, to perform phospho-proteomics analysis upon all these conditions. Of note, and to show the feasibility of this approach, the proteomic platform at Biocampus in Montpellier has experience using this technique (Kassouf et al., 2019).

      The combination therapy of carboplatin with MDM2 and NICD inhibitors may lack compelling rationale (see below).

      [Authors] This is a very important point but we discuss it below, where more information is provided by the reviewer. Still, we anticipate we will perform a new in vivo experiment to answer to this point.

      In lines 275-276, the authors stated that their preclinical data establish the enhancement of carboplatin's therapeutic effect in NSCLC in vivo through MDM2-NICD axis inhibition. However, it's important to note that this finding remains preliminary at this stage.

      [Authors] We consider that our statement is not exaggerated, but we will tone down the message as proposed by the reviewer in the next submission.

      Minor comments:

      1. The observed loss of NICD during ATMi + carboplatin treatment in Figures 2A and 2B raises the question of whether ATM regulates the gene transcription of NOTCH. In addition to the CHX assay conducted in Figures 2C and 2D, quantifying NOTCH mRNA upon ATM inhibition could provide further insights. Alternatively, referencing relevant studies on this topic may strengthen the discussion.

      [Authors] This is an interesting experiment and we will perform it.

      In Figures 4A and 4B, the noticeable discrepancy between the exogenous expression of wild-type (WT) MDM2 and catalytically inactive MDM2-464A raises concerns. It is essential to consider if the reduced ubiquitination and stability of NICD might be attributed to varying levels of MDM2-464A in the cells rather than its catalytic inactivity. While p53 ubiquitination was utilized as a control, ensuring comparable levels of MDM2 and MDM2-464A expression could enhance the experimental rigor. Compared to the smear poly-ubiquitination bands observed for MDM2 in Figure 4B, the ubiquitination of NICD appears simpler. What distinguishes the feature of MDM2-mediated NICD ubiquitination? Could it potentially involve mono-ubiquitination?

      [Authors] The point of the reviewer is well taken, and importantly, as mentioned above in main point 2, we will repeat these experiments and will appear as new Figure 4A and new Figure 4B.

      Regarding the type of ubiquitination, as explained in detail in major point 1 to same reviewer, we will fully characterize the type of ubiquitination on NICD induced by DNA damage, and we will confirm that MDM2 is required for this specific ubiquitination in future new Figure 4C where we will overexpress the required ubiquitin forms and WT MDM2.

      In Figure 5A, the authors need to consider conducting additional NOTCH-associated factors to definitively demonstrate the activation of NOTCH signaling beyond HES1. Alternatively, in Figure 5B, the NICD Western blot could be complemented by detecting HES1 or other NOTCH-associated factors.

      [Authors] To answer to this particular point, we will test for other downstream targets of Notch as NRARP and it will appear as part of new Figure 5C.

      In Figures 5C and 5D, crucial control groups are missing, specifically mice treated solely with SP141+DBZ, carboplatin+SP141, and SP141+DBZ. It is essential to include these groups to demonstrate that the enhanced tumor killing results from the combination of carboplatin with SP141 and/or DBZ, rather than from SP141 and DBZ alone. Furthermore, in addition to the currently used NSCLC-PDX model harboring the p53 (P151R) mutation, it would be informative to include a NSCLC-PDX model expressing WT p53.

      [Authors] This is a crucial point in this rebuttal as mentioned before in major point 3 and we detail it in here.

      We did only 3 groups because preliminary data indicated that SP141 in combination with carboplatin was not showing any benefit compared to carboplatin alone while upon combination of carboplatin with Notch inhibition there was only a slight increase in therapeutic carboplatin benefit but otherwise not very potent, and for simplicity we preferred to don’t show these data. But, after reading this point from Reviewer 1, even if we will propose later only the triple combination for patients, we clearly need to demonstrate that the other combinations are not potent enough or not at all.

      The reviewer asked to include: “SP141+DBZ, carboplatin+SP141, and SP141+DBZ”. We imagine that she/he meant: SP141+DBZ, carboplatin+SP141, and carboplatin +DBZ, that together with the vehicle, carboplatin and carboplatin+SP141+DBZ makes 6 groups of treatments. Putting together the 8 mice devoted for tumor growth and survival, plus 4 mice for the acute treatment for IHC and WB purposes (for current Figures 5A and 5B) makes a total of 72, that is a substantial number of mice. Of note, since we performed the in vivo experiment presented in the current manuscript, a new Notch inhibitor called nirogacestat, appear in the market being the first in class Notch inhibitor to treat solid cancer patients (desmoid tumors) after demonstrating a significant therapeutic effect in clinical trials (Gounder et al., 2023).

      Hence, we will take advantage of the repetition of this experiment to substitute this new molecule instead of DBZ, that is an interesting molecule for preclinical research, but without any clinical relevance. Therefore, the use of nirogacestat will further increase the medical impact of our data. Importantly, nirogacestat is better tolerated than DBZ, meaning that mice can be treated for longer periods of time and we propose in here to treat up to 12 weeks. Finally, after discussion with Quentin Thomas, author of the manuscript and clinical researcher in the lab, we will provide 4 carboplatin cycles as it is proposed today to NSCLC patients in an attempt of getting closer to the clinical setting. In particular we will provide carboplatin to mice on weeks 1, 4, 7 and 10, while treating with MDM2 inhibitor (SP141) and Notch inhibitor (nirogacestat) from Monday to Friday for the 12 weeks.

      This experiment will be long and will require an important use of resources both human and financial, but we are sure that the effect in tumor growth and survival will be more dramatic than the one presented now.

      On the contrary and as explained in the 4th subheading part of this “revision plan”, including another 72 mice to treat a p53 proficient NSCLC PDX, when we already demonstrated in vitro that p53 is not required for the phenotype described in this study, for us it is totally unfeasible by ethical reasons, i.e., the use of animals in research (please see below for further details).

      All the new data will appear as new Figure 5 (B to E). For new Figure 5A please see below the major comment 2 of Reviewer 2.

      Though beyond the current study's scope, in the discussion section, the authors may want to propose or hypothesize on how MDM2-mediated NICD stabilization contributes to carboplatin resistance. This could provide valuable insights for future research directions.

      [Authors] We will discuss this part as proposed by the reviewer.

      In the Western blot results, the total ATM and ATR controls were absent.

      [Authors] The reviewer is totally right and we will repeat experiments to include all the totals as requested.

      Authors may choose to include a graphical abstract at the end of their study to visually illustrate the mechanisms they have described.

      [Authors] Very good idea thanks, we will do it.

      Reviewer #1 (Significance (Required)):

      Advance: The authors aim to present a novel perspective on the resistance mechanisms to platinum compounds in NSCLC therapy. They explore platinum compounds-induced DNA damage, ATM activation, and MDM2-mediated stabilization of the active form of NOTCH (NICD). However, to strengthen their claims, they must provide more conclusive results.

      Audience: This manuscript will likely engage oncologists who investigate the chemotherapy-resistant mechanisms of platinum compounds in NSCLC treatment, as well as scientists specializing in NOTCH and MDM2 pathways. However, the manuscript's central claims lack robust support from the available data, and the current approaches employed are not sufficiently thoughtful and rigorous; there is room for improvement.

      My expertise is molecular medicine, cancer biology, and epigenetics.

      [Authors] We want to thank again this reviewer for her/his helpful comments that will increase the impact and the relevance of our study while keeping the original message.

      We are also very satisfied when she/he said: “This manuscript will likely engage oncologists who investigate the chemotherapy-resistant mechanisms of platinum compounds in NSCLC treatment”.

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

      In this manuscript, Sara Bernardo et al. investigated the molecular mechanisms underlying the activation of the Notch signaling in response to DNA damage induced by platinum-based chemotherapeutic agents in non-small cell lung cancer (NSCLC). They demonstrated that carboplatin treatment induces DNA double-strand breaks (DSBs) and stabilizes NICD, a process dependent on ATM and mediated by MDM2. In vivo experiments in patient-derived xenografts (PDX) showed that inhibition of NICD and MDM2 enhanced platinum effectiveness. Furthermore, clinical analysis revealed a correlation between MDM2 expression and poor prognosis in NSCLC patients treated with platinum compounds, emphasizing the clinical relevance of the MDM2-NICD axis in platinum resistance.

      [Authors] We thank this reviewer for her/his nice synopsis of our study.

      Major comments:

      Overall, the authors have conducted experiments that sufficiently elucidate their claims, and the description of the experiments is detailed. However, there is still room for the improvement.

      [Authors] We are very pleased that reviewer finds our experimental work “…sufficiently elucidate their claims, and the description of the experiments is detailed.” And we are sure that after all the new experiments we are proposing in here, she/he will be fully satisfied.

      1.The finding that MDM2 promoted NICD stability through non degradative ubiquitination is interesting and in line with a previous study. As it is also known that NICD is regulated by various post-translational modifications, including ubiquitination that promotes NICD degradation. It is unclear what's the potential difference between these two types of ubiquitination. For example, do these two differ in specific ubiquitination sites? Can the authors provide some discussion?

      [Authors] We agree with the reviewer and hence we will perform a new set of experiments to determine the role of 2 key lysine residues in the ubiquitin protein promoting either degradation or DNA binding. As explained in detail in major point 1 from reviewer 1, we will determine if DNA damage promotes ubiquitination in position 48, i.e., to degrade, or in position 63, i.e., to facilitate the binding to DNA for repairing upon DNA damage, or in any of these 2 positions. And as mentioned above, we will then confirm that MDM2 is responsible of the specific ubiquitination type we will uncover. We are sure that the reviewer will be satisfied by these new data once is generated.

      As for the specific ubiquitination sites in NICD, there are up to 17 lysine residues susceptible of being ubiquitinated. Hence unveiling what residues are targeted by MDM2 and if they differ from others inducing degradation as those promoted by the E3 ligase FBXW7, we feel is out of the scope of the current manuscript. Still, we will discuss all this part as kindly proposed by the reviewer.

      Could the overexpression of MDM2 or NICD lead to carboplatin resistance in A549 or H358 cells?

      [Authors] This is a very interesting experiment and prompted by the reviewer’s comment we started the subcloning of inducible NICD into lentiviral vectors to generate stable cells and test the carboplatin sensitivity in presence of different levels of NICD. These new data will be the new Figure 5A.

      The trends observed in the western blot data within the manuscript appear inconsistent. While the authors propose that NICD levels increased upon incubation with carboplatin, the discrepancy arises when considering the NICD levels without cycloheximide (CHX) treatment in Figure 1E, where no significant elevation is observed (Lane 6 vs. Lane 1).

      [Authors] The point of the reviewer is well taken. Please bear in mind that in here we are handling several signaling pathways that interact among them while having each one different kinetics. Our finding of increased NICD upon carboplatin treatment is highly consistent in vitro and in vivo, but it is true that in the experiment mentioned by the reviewer is not obvious, probably due to some kinetic issue. We are repeating this experiment to have the increased in NICD upon carboplatin as it is in the rest of the manuscript (up to 9 times only in main figures).

      The quality of western blots needs to be improved, especially Fig. 1C and S1C, also Figure 3B. Moreover, the NICD western blot sometimes appears as one band and sometimes as two bands. Please provide an explanation. If possible, please quantify the bands in western blots.

      [Authors] We agree with the reviewers that not all WB have the same quality and we will repeat some of them to homogenize the quality all over the manuscript, and particularly, we will repeat the ones kindly pointed out by the reviewer.

      The two bands it is something we also noticed and we will pay attention while reproducing the WB, since it might be related to discrepancies in the percentage of acrylamide. If this is not the case, i.e., upon repetition we still observe in some conditions and not in others, we will provide explanations for this in the new submission as kindly proposed by the reviewer.

      Finally, and also as proposed by the reviewer we will quantify the WB bands.

      Please provide a necessary discussion on whether the targeted treatment approach towards the MDM2-NICD axis is applicable to all patients or only to those with high expression of MDM2/NICD.

      [Authors] In the discussion of the current manuscript, we focused into the MDM2 high expression subset of patients for this issue, but in the next submission we will enlarge to patients with high levels of NICD also.

      How to interpret the significance of the simultaneous increase in NICD ubiquitination and stability mediated by MDM2? Please provide a relevant discussion.

      [Authors] We will provide strong experimental data to go beyond discussion (please see above the experiments with ubiquitin mutants), but we will also provide discussion of this particular point.

      In Figure 5B, please also check the level of MDM2. In Figure 5C, carboplatin appears to have little impact on tumor growth. How to explain the increase of Ki-67 in the carboplatin treatment group in Figure 5A?

      [Authors] We will measure also levels of MDM2 in the future new Figure 5C as requested by the reviewer.

      As for the interesting observation of the Ki67, since we will repeat the whole experiment, we will pay special attention to this point if ever it is repeated. Should be this the case, we will elaborate an explanation.

      Minor comments:

      1.Please include scale bars in Figure 1B and Supplemental Figure 1B.

      [Authors] We thank the reviewer for this comment. We will include the scale bars where required.

      2.Figure 5D, the P values of the survival curve should be indicated in the figures.

      [Authors] We will include the P values in the future new Figure 5E.

      3.The presentation of survival curve data in Figures 5D and 6A should be consistent.

      [Authors] The point of the reviewer is well taken and we will use Prism to draw the PFS for patients in Figure 6A as we did for the mice in current Figure 5D.

      4.It seems that supplemental figure 2 is missing.

      [Authors] We actually jumped from supplemental figure 1 to 3 because we do not have any associated supplemental figure to main Figure 2. We will clarify this point in the next submission.

      5.Please carefully check the spelling of the entire text, for example, on page 20, line 426 it should be 'western'. Also, please spell out the abbreviations DDR and ATM.

      [Authors] We will double check all spelling and provide the abbreviations kindly suggested by the reviewer.

      6.The abbreviation for Cleaved caspase 3 should be CC3.

      [Authors] We thank the reviewer for this information, we will use CC3 in the next submission.

      Reviewer #2 (Significance (Required)):

      Notch signaling is associated with the occurrence and development of non-small cell lung cancer (NSCLC). Previous study indicates that the expression of Notch protein is significantly higher in NSCLC tissues compared to normal tissues (PMID: 31170211). Additionally, the upregulation of Notch1 is correlated with higher tumor grades, lymph node metastasis, tumor-node-metastasis (TNM) staging, and poor prognosis (PMID: 25996086). Abnormal activation of Notch signaling pathway is frequently observed in chemotherapy-resistant NSCLC, and some studies have aimed to address NSCLC drug resistance via modulating Notch signaling (PMID: 30087852, 38301911). This manuscript firstly proposes that MDM2-mediated stabilization of NICD upon DNA damage plays a major role in NSCLC response to platinum chemotherapy. It further suggests that targeting the MDM2-NICD axis could prove to be an effective therapeutic strategy. Overall, this work unveils a novel mechanism for Notch activation in response to platinum chemotherapy, providing a renewed outlook on overcoming chemotherapy resistance in NSCLC. This manuscript will attract those interested in the mechanisms of chemotherapy resistance and novel treatment approaches.

      [Authors] We sincerely thank the reviewer for finding that our “…work unveils a novel mechanism for Notch activation in response to platinum chemotherapy, providing a renewed outlook on overcoming chemotherapy resistance in NSCLC”. We are also very satisfied when she/he says: “This manuscript will attract those interested in the mechanisms of chemotherapy resistance and novel treatment approaches.”

      Finally, we are convinced that the reviewer will appreciate all the new proposed experimental data, and also that upon finishing all experiments, she/he will think that the manuscript will be suitable for publication.

      3. Description of the revisions that have already been incorporated in the transferred manuscript

      For simplicity, we decided to introduce all changes in next submission upon conclusion of all experimental approaches proposed above.

      4. Description of analyses that authors prefer not to carry out

      While we will perform almost all experiments proposed by reviewers, there is one we feel is not possible to do due to ethical reasons. Reviewer 1 wanted us to perform a new in vivo experiment with the same PDX using up to 6 treatment groups. We use 8 mice per condition (for tumor growth and survival) plus 4 for the “acute” treatment for WB and IHC purposes, hence 12 mice x 6 groups = 72 mice, and we will perform this experiment as indicated above and proposed by the reviewer.

      On the contrary, the reviewer asked us also to repeat the same experiment with a PDX p53 proficient. While we understand the possible interest, since we demonstrated in vitro that p53 is not required for the protective phenotype of MDM2 and Notch upon DNA damage, we honestly believe that using another 72 mice to confirm this aspect in vivo, is against the rational use of animals in research going against the 3Rs rule. Hence, we will not perform this experiment unless Editors believe is strictly required.

      REFERENCES

      Arena, G., Cisse, M. Y., Pyrdziak, S., Chatre, L., Riscal, R., Fuentes, M., Arnold, J. J., Kastner, M., Gayte, L., Bertrand-Gaday, C., et al. (2018). Mitochondrial MDM2 Regulates Respiratory Complex I Activity Independently of p53. Mol Cell 69, 594-609 e598.

      Cheng, Q., Cross, B., Li, B., Chen, L., Li, Z., and Chen, J. (2011). Regulation of MDM2 E3 ligase activity by phosphorylation after DNA damage. Mol Cell Biol 31, 4951-4963.

      Gounder, M., Ratan, R., Alcindor, T., Schoffski, P., van der Graaf, W. T., Wilky, B. A., Riedel, R. F., Lim, A., Smith, L. M., Moody, S., et al. (2023). Nirogacestat, a gamma-Secretase Inhibitor for Desmoid Tumors. N Engl J Med 388, 898-912.

      Kassouf, T., Larive, R. M., Morel, A., Urbach, S., Bettache, N., Marcial Medina, M. C., Merezegue, F., Freiss, G., Peter, M., Boissiere-Michot, F., et al. (2019). The Syk Kinase Promotes Mammary Epithelial Integrity and Inhibits Breast Cancer Invasion by Stabilizing the E-Cadherin/Catenin Complex. Cancers (Basel) 11.

      Liu, P., Gan, W., Su, S., Hauenstein, A. V., Fu, T. M., Brasher, B., Schwerdtfeger, C., Liang, A. C., Xu, M., and Wei, W. (2018). K63-linked polyubiquitin chains bind to DNA to facilitate DNA damage repair. Sci Signal 11.

      Pettersson, S., Sczaniecka, M., McLaren, L., Russell, F., Gladstone, K., Hupp, T., and Wallace, M. (2013). Non-degradative ubiquitination of the Notch1 receptor by the E3 ligase MDM2 activates the Notch signalling pathway. Biochem J 450, 523-536.

      Riscal, R., Schrepfer, E., Arena, G., Cisse, M. Y., Bellvert, F., Heuillet, M., Rambow, F., Bonneil, E., Sabourdy, F., Vincent, C., et al. (2016). Chromatin-Bound MDM2 Regulates Serine Metabolism and Redox Homeostasis Independently of p53. Mol Cell 62, 890-902.

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      Referee #2

      Evidence, reproducibility and clarity

      In this manuscript, Sara Bernardo et al. investigated the molecular mechanisms underlying the activation of the Notch signaling in response to DNA damage induced by platinum-based chemotherapeutic agents in non-small cell lung cancer (NSCLC). They demonstrated that carboplatin treatment induces DNA double-strand breaks (DSBs) and stabilizes NICD, a process dependent on ATM and mediated by MDM2. In vivo experiments in patient-derived xenografts (PDX) showed that inhibition of NICD and MDM2 enhanced platinum effectiveness. Furthermore, clinical analysis revealed a correlation between MDM2 expression and poor prognosis in NSCLC patients treated with platinum compounds, emphasizing the clinical relevance of the MDM2-NICD axis in platinum resistance.

      Major comments:

      Overall, the authors have conducted experiments that sufficiently elucidate their claims, and the description of the experiments is detailed. However, there is still room for the improvement.

      1.The finding that MDM2 promoted NICD stability through non degradative ubiquitination is interesting and in line with a previous study. As it is also known that NICD is regulated by various post-translational modifications, including ubiquitination that promotes NICD degradation. It is unclear what's the potential difference between these two types of ubiquitination. For example, do these two differ in specific ubiquitination sites? Can the authors provide some discussion? 2. Could the overexpression of MDM2 or NICD lead to carboplatin resistance in A549 or H358 cells? 3. The trends observed in the western blot data within the manuscript appear inconsistent. While the authors propose that NICD levels increased upon incubation with carboplatin, the discrepancy arises when considering the NICD levels without cycloheximide (CHX) treatment in Figure 1E, where no significant elevation is observed (Lane 6 vs. Lane 1). 4. The quality of western blots needs to be improved, especially Fig. 1C and S1C, also Figure 3B. Moreover, the NICD western blot sometimes appears as one band and sometimes as two bands. Please provide an explanation. If possible, please quantify the bands in western blots. 5. Please provide a necessary discussion on whether the targeted treatment approach towards the MDM2-NICD axis is applicable to all patients or only to those with high expression of MDM2/NICD. 6. How to interpret the significance of the simultaneous increase in NICD ubiquitination and stability mediated by MDM2? Please provide a relevant discussion. 7. In Figure 5B, please also check the level of MDM2. In Figure 5C, carboplatin appears to have little impact on tumor growth. How to explain the increase of Ki-67 in the carboplatin treatment group in Figure 5A?

      Minor comments:

      1.Please include scale bars in Figure 1B and Supplemental Figure 1B. 2.Figure 5D, the P values of the survival curve should be indicated in the figures. 3.The presentation of survival curve data in Figures 5D and 6A should be consistent. 4.It seems that supplemental figure 2 is missing. 5.Please carefully check the spelling of the entire text, for example, on page 20, line 426 it should be 'western'. Also, please spell out the abbreviations DDR and ATM. 6.The abbreviation for Cleaved caspase 3 should be CC3.

      Significance

      Notch signaling is associated with the occurrence and development of non-small cell lung cancer (NSCLC). Previous study indicates that the expression of Notch protein is significantly higher in NSCLC tissues compared to normal tissues (PMID: 31170211). Additionally, the upregulation of Notch1 is correlated with higher tumor grades, lymph node metastasis, tumor-node-metastasis (TNM) staging, and poor prognosis (PMID: 25996086). Abnormal activation of Notch signaling pathway is frequently observed in chemotherapy-resistant NSCLC, and some studies have aimed to address NSCLC drug resistance via modulating Notch signaling (PMID: 30087852, 38301911). This manuscript firstly proposes that MDM2-mediated stabilization of NICD upon DNA damage plays a major role in NSCLC response to platinum chemotherapy. It further suggests that targeting the MDM2-NICD axis could prove to be an effective therapeutic strategy. Overall, this work unveils a novel mechanism for Notch activation in response to platinum chemotherapy, providing a renewed outlook on overcoming chemotherapy resistance in NSCLC. This manuscript will attract those interested in the mechanisms of chemotherapy resistance and novel treatment approaches.

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      Referee #1

      Evidence, reproducibility and clarity

      Summary:

      This manuscript from Maraver and co-authors investigates the putative resistance mechanisms that hinder the efficacy of platinum-based therapies (e.g., carboplatin) against non-small cell lung carcinoma (NSCLC). Using in vitro lung cancer cell lines, shRNA-based knockdown, and exogenous overexpression systems, the research describes a DNA damage-induced resistance mechanism involving the NOTCH signaling pathway and the E3 ligase MDM2. The authors show that carboplatin treatment induces DNA damage and promotes ATM activation, which in turn activates the NOTCH signaling pathway via ubiquitination and stabilization of the Notch Intracellular Domain (NICD). New findings include the MDM2-mediated ubiquitination and stabilization of NICD. Using in vivo NSCLC-PDX models, they demonstrate that combining carboplatin with Notch and MDM2 inhibitors can enhance tumor killing, suggesting that targeting the MDM2/NICD axis in conjunction with carboplatin may be a viable therapeutic alternative. Furthermore, they show that NICD and MDM2 levels are elevated among tumor samples from chemo-resistant patients. Consistent with these findings, high MDM2 levels correlate with poor progression-free survival (PFS) in NSCLC patients.

      Major comments:

      Some of the key conclusions may not be convincing.

      1. One significant weakness of the manuscript is the lack of exploration into the underlying mechanism of how MDM2 mediates the stabilization of NICD. While the observation of MDM2-mediated NICD stabilization is intriguing, it is important to provide a more convincing explanation for the reviewers. This could be achieved by offering a detailed molecular mechanism, especially considering that MDM2 typically targets proteins for degradation.
      2. Another weakness lies in the unclear role and the underlying mechanism of ATM in the MDM2-mediated NICD stabilization. While the data presented (Fig. 3B, 3C) suggest that carboplatin could elevate MDM2 levels for NICD stabilization, a more precise method to induce MDM2 overexpression specifically for targeting NICD is required. It appears that ATM plays a crucial role in this regulatory process. The following questions must be addressed: Does ATM induce the phosphorylation of MDM2 for its protein stabilization and/or E3 ligase activity?
      3. The combination therapy of carboplatin with MDM2 and NICD inhibitors may lack compelling rationale (see below).
      4. In lines 275-276, the authors stated that their preclinical data establish the enhancement of carboplatin's therapeutic effect in NSCLC in vivo through MDM2-NICD axis inhibition. However, it's important to note that this finding remains preliminary at this stage.

      Minor comments:

      1. The observed loss of NICD during ATMi + carboplatin treatment in Figures 2A and 2B raises the question of whether ATM regulates the gene transcription of NOTCH. In addition to the CHX assay conducted in Figures 2C and 2D, quantifying NOTCH mRNA upon ATM inhibition could provide further insights. Alternatively, referencing relevant studies on this topic may strengthen the discussion.
      2. In Figures 4A and 4B, the noticeable discrepancy between the exogenous expression of wild-type (WT) MDM2 and catalytically inactive MDM2-464A raises concerns. It is essential to consider if the reduced ubiquitination and stability of NICD might be attributed to varying levels of MDM2-464A in the cells rather than its catalytic inactivity. While p53 ubiquitination was utilized as a control, ensuring comparable levels of MDM2 and MDM2-464A expression could enhance the experimental rigor. Compared to the smear poly-ubiquitination bands observed for MDM2 in Figure 4B, the ubiquitination of NICD appears simpler. What distinguishes the feature of MDM2-mediated NICD ubiquitination? Could it potentially involve mono-ubiquitination?
      3. In Figure 5A, the authors need to consider conducting additional NOTCH-associated factors to definitively demonstrate the activation of NOTCH signaling beyond HES1. Alternatively, in Figure 5B, the NICD Western blot could be complemented by detecting HES1 or other NOTCH-associated factors.
      4. In Figures 5C and 5D, crucial control groups are missing, specifically mice treated solely with SP141+DBZ, carboplatin+SP141, and SP141+DBZ. It is essential to include these groups to demonstrate that the enhanced tumor killing results from the combination of carboplatin with SP141 and/or DBZ, rather than from SP141 and DBZ alone. Furthermore, in addition to the currently used NSCLC-PDX model harboring the p53 (P151R) mutation, it would be informative to include a NSCLC-PDX model expressing WT p53.
      5. Though beyond the current study's scope, in the discussion section, the authors may want to propose or hypothesize on how MDM2-mediated NICD stabilization contributes to carboplatin resistance. This could provide valuable insights for future research directions.
      6. In the Western blot results, the total ATM and ATR controls were absent.
      7. Authors may choose to include a graphical abstract at the end of their study to visually illustrate the mechanisms they have described.

      Significance

      Advance: The authors aim to present a novel perspective on the resistance mechanisms to platinum compounds in NSCLC therapy. They explore platinum compounds-induced DNA damage, ATM activation, and MDM2-mediated stabilization of the active form of NOTCH (NICD). However, to strengthen their claims, they must provide more conclusive results.

      Audience: This manuscript will likely engage oncologists who investigate the chemotherapy-resistant mechanisms of platinum compounds in NSCLC treatment, as well as scientists specializing in NOTCH and MDM2 pathways. However, the manuscript's central claims lack robust support from the available data, and the current approaches employed are not sufficiently thoughtful and rigorous; there is room for improvement."

      My expertise is molecular medicine, cancer biology, and epigenetics.

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      Reply to the reviewers

      Manuscript number: RC-2024-02394

      Corresponding author(s): Altman, Brian J

      1. General Statements [optional]

      We thank all three Reviewers for their insightful and helpful feedback and suggestions. We strongly believe that addressing these comments has now resulted in a much-improved manuscript. We appreciate that the Reviewers found the manuscript "interesting" with "valuable insights and... obvious novelty", "an important study that is well-done", and "an important understanding of the crosstalk between cancer cells and immune cells as well as the understanding of how the TME disrupts circadian rhythms". All three Reviewers requested a significant revision, which we provide here. We carefully and completely responded to each Reviewer question or suggestion, in most cases with new experiments and text, and in a very few cases with changes or additions to the Discussion section. This includes new data in seven of the original Figures and Supplementary Figures, and one new main Figure and three new Supplementary Figures. Highlights of these new data include testing the role of low pH in cancer cell supernatant on macrophage rhythms, and analysis of single-cell RNA-sequencing data for heterogeneity in macrophage circadian gene expression. Additional experiments were also performed that were not included in the manuscript, and these data are presented in this Response. A detailed point-by-point response to each comment is included below with excerpts of the data and updated text for the reviewers. Please note that the PDF version of this Response includes images of the new Figures inserted in to the manuscript.

      2. Point-by-point description of the revisions

      __Reviewer #1 __

      Evidence, reproducibility and clarity

      The manuscript by Knudsen-Clark et al. investigates the novel topic of circadian rhythms in macrophages and their role in tumorigenesis. The authors explore how circadian rhythms of macrophages may be influenced by the tumor microenvironment (TME). They utilize a system of bone marrow-derived macrophages obtained from transgenic mice carrying PER2-Luciferase (PER2-Luc), a trackable marker of rhythmic activity. The study evaluates how conditions associated with the TME, such as polarizing stimuli (to M1 or M2 subtype), acidic pH, and elevated lactate, can each alter circadian rhythms in macrophages. The authors employ several approaches to explore macrophage functions in cancer-related settings. While the manuscript presents interesting findings and may be the first to demonstrate that tumor stimuli alter circadian rhythms in macrophages and impact tumor growth, it lacks a clear conclusion regarding the role of altered circadian rhythms in suppressing tumor growth. Several discrepancies need to be addressed before publication, therefore, the manuscript requires revision before publication, addressing the following comments:

      We thank Reviewer #1 for the comments regarding the quality of our work and are pleased that the Reviewer finds that this manuscript "presents interesting findings and may be the first to demonstrate that tumor stimuli alter circadian rhythms in macrophages and impact tumor growth". We have addressed all comments and critiques from Reviewer #1 below. To summarize, we added new data on how different macrophage polarization states affect media pH (Supplementary Figure 4), further characterized gene expression in our distinct macrophage populations (Supplementary Figure 1), provided clarity in the data and text on the universal nature of Clock Correlation Distance (CCD) across macrophage populations (Figure 6), included human tumor-associated macrophage (TAM) data for CCD (Figure 7) analyzed single-cell RNA-sequencing data of TAMs to demonstrate heterogeneity in circadian gene expression (Figure 9), and used tumor-conditioned media to show that low pH still affects macrophage rhythms in this context *Supplementary Figure 5". Thanks to the helpful suggestions of the Reviewer, we also made numerous clarifications and fixed a critical referencing error that the Reviewer identified.

      Major comments: 1. It is well known that pro-inflammatory macrophages primarily rely on glycolysis during inflammation, exhibiting dysregulated tricarboxylic acid (TCA) cycle activity. These pro-inflammatory macrophages are commonly referred to as 'M1' or pro-inflammatory, as noted in the manuscript. In contrast, M2 macrophages, or pro-resolution macrophages, are highly dependent on active mitochondrial respiration and oxidative phosphorylation (OXPHOS). Given that M1 macrophages favor glycolysis, they create an acidic environment due to elevated lactate levels and other acidifying metabolites. However, the study does not address this effect. The authors' hypothesis revolves around the acidic environment created by glycolytic tumors, yet they overlook the self-induced acidification of media when culturing M1 macrophages. This raises the question of how the authors explain the reduced circadian rhythms observed in pro-inflammatory macrophages in their study, while low pH and higher lactate levels enhance the amplitude of circadian rhythms. I would encourage the authors to incorporate the glycolytic activity of pro-inflammatory macrophages into their experimental setup. Otherwise the data look contradictory and misleading in some extent.

      We appreciate the important point Reviewer #1 made that macrophages polarized toward a pro-inflammatory phenotype such as those stimulated with IFNγ and LPS (M1 macrophages) prioritize metabolic pathways that enhance glycolytic flux, resulting in increased release of protons and lactate as waste products from the glycolysis pathway. In this way, polarization of macrophages toward the pro-inflammatory phenotype can lead to acidification of the media, which may influence our observations given that we are studying the effect of extracellular pH on rhythms in macrophages. To address this point, we have performed additional experiments in which we measured pH of the media to capture changes in media pH that occur during the time in which we observe changes in rhythms of pro-inflammatory macrophages.

      In line with the documented enhanced glycolytic activity of pro-inflammatory macrophages, the media of pro-inflammatory macrophages is acidified over time, in contrast to media of unstimulated or pro-resolution macrophages. Notably, while pH decreased over time in the pro-inflammatory group, the pH differential between the pH7.4, pH6.8, and pH6.5 sample groups was maintained over the period in which we observe and measure changes in circadian rhythms of pro-inflammatory macrophages. Additionally, media that began at pH 7.4 was acidified only to pH 7 by day 2, above the acidic pH of 6.8 or 6.5. As a result, there remained a difference in pH between the two groups (pH 7.4 and pH 6.5) out to 2 days consistent with the changes in rhythms that we observe between these two groups. This indicates that the difference in circadian rhythms observed in pro-inflammatory macrophages cultured at pH 7.4 compared to pH 6.5 were indeed due to the difference in extracellular pH between the two conditions. We have incorporated these data, shown below, into Supplementary Figure 4 and added the following discussion of these data to the Results section:

      "In line with their documented enhanced glycolytic capacity, pro-inflammatory macrophages acidified the media over time (Supplementary Figure 4C). Notably, while pH of the media the pro-inflammatory macrophages were cultured in decreased over time pH, the pH differential between the pH 7.4, pH 6.8, and pH 6.5 samples groups of pro-inflammatory macrophages was maintained out to 2 days, consistent with the changes in rhythms that we observe and measure between these groups."

      The article examines the role of circadian rhythms in tumor-associated macrophages, yet it lacks sufficient compelling data to support this assertion. Two figures, Figure 7 and Figure 9, are presented in relation to cancer. In Figure 7, gene expression analysis of Arg1 (an M2 marker) and Crem (a potential circadian clock gene) is conducted in wild-type macrophages, BMAL1-knockout macrophages with dysregulated circadian rhythms, and using publicly available data on tumor-associated macrophages from a study referenced as 83. However, it is noted that this referenced study is actually a review article by Geeraerts et al. (2017) titled "Macrophage Metabolism as Therapeutic Target for Cancer, Atherosclerosis, and Obesity" published in Frontiers in Immunology. This raises concerns about the reliability of the results. Furthermore, comparing peritoneal macrophages from healthy mice with macrophages isolated from lung tumors is deemed inaccurate. It is suggested that lung macrophages from healthy mice and those from mice with lung tumors should be isolated separately for a more appropriate comparison. Consequently, Figure 7B is further questioned regarding how the authors could compare genes from the circadian rhythm pathway between these non-identical groups. As a result, the conclusion drawn from these data, suggesting that tumor-associated macrophages exhibit a gene expression pattern similar to BMAL1-KO macrophages, is deemed incorrect, affecting the interpretation of the data presented in Figure 8.

      We thank Reviewer #1 for pointing out our error in the reference provided as the source of the TAM data used for CCD in Figure 7. While we took care to provide the GEO ID for the data set (GSE188549) in the Methods section, we mistakenly cited Geeraerts (2017) Front Immunol when we should have cited Geeraerts (2021) Cell Rep. We have corrected this citation error in the main text.

      We also appreciate Reviewer #1's concern that we are comparing circadian gene expression of peritoneal macrophages to tumor-associated macrophages derived from LLC tumors, which are grown ectopically in the flank for the experiment from which the data set was produced. To ensure an accurate comparison of gene expression, we downloaded the raw FASTQ files from each dataset and processed them in identical pipelines. Our main comparison between these cell types is Clock Correlation Distance (CCD), which compares the pattern of co-expression of circadian genes (Shilts et al PeerJ 2018). CCD was built from multiple mouse and human tissues to be a "universal" tool to compare circadian rhythms, and designed to compare between different tissues and cell types. Each sample is compared to a reference control built from these multiple tissues. To better convey this concept to readers to give confidence the suitability of CCD for comparing data sets across different tissues, we have added the reference control to Figure 7 (now Figure 6B), We have also expanded our analysis to include bone marrow-derived macrophages, to further demonstrate that the organization of clock gene co-expression is not specific to peritoneal macrophages; we have added this data to Figure 7 (now Figure 6C,D). Finally, we have included an abbreviated explanation of the points made above in the results section.

      Due to the universal nature of the CCD tool, we disagree with Reviewer #1's assertion that "the conclusion drawn from these data, suggesting that tumor-associated macrophages exhibit a gene expression pattern similar to BMAL1-KO macrophages, is deemed incorrect". Indeed, this finding mirrors findings in the original CCD paper, which showed that tumor tissues universally exhibit a disordered molecular clock as compared to normal tissue. Notably, the original CCD paper also compared across cell and tumor types.

      As an additional note to the review, we would like to clarify that nowhere in the manuscript do we propose that Crem is a potential circadian clock gene. We are clear throughout the manuscript that we are using Crem as a previously established biomarker for acidic pH-sensing in macrophages. Please see below for the modified Figure and text.

      "To understand the status of the circadian clock in TAMs, we performed clock correlation distance (CCD) analysis. This analysis has previously been used to assess functionality of the circadian clock in whole tumor and in normal tissue[102]. As the circadian clock is comprised of a series of transcription/translation feedback loops, gene expression is highly organized in a functional, intact clock, with core clock genes existing in levels relative to each other irrespective of the time of day. In a synchronized population of cells, this ordered relationship is maintained at the population level, which can be visualized in a heatmap. CCD is designed to compare circadian clock gene co-expression patterns between different tissues and cell types. To accomplish this, CCD was built using datasets from multiple different healthy tissues from mouse and human to be a universal tool to compare circadian rhythms. Each sample is compared to a reference control built from these multiple tissues (Figure 6B)[102]. To validate the use of this analysis for assessing circadian disorder in macrophages, we performed CCD analysis using publicly available RNA-sequencing data from bone marrow-derived macrophages and wild type peritoneal macrophages, as a healthy control for functional rhythms in a synchronized cell population, and BMAL1 KO peritoneal macrophages, as a positive control for circadian disorder[44]."

      And in the Discussion:

      "Interestingly, analysis of TAMs by clock correlation distance (CCD) presents evidence that rhythms are disordered in bulk TAMs compared to other macrophage populations (Figure 6). CCD is one of the most practical tools currently available to assess circadian rhythms due to its ability to assess rhythms independent of time of day and without the need for a circadian time series, which is often not available in publicly available data from mice and humans[102]."

      If the authors aim to draw a clear conclusion regarding the circadian rhythms of tumor-associated macrophages (TAMs), they may need to analyze single-sorted macrophages from tumors and corresponding healthy tissues. Such data are publicly available (of course not in #83)

      We agree with Reviewer #1 that while our interpretation of the data is that there may be heterogeneity in circadian rhythms of tumor-associated macrophages, we cannot prove this without assessing circadian rhythms at the single cell level. While single-cell RNA-sequencing data of freshly isolated tumor associated macrophages of sufficient read depth for circadian gene expression analysis has historically been unavailable, fortunately a dataset was released recently (May 2024) which we were able to use to address this point. We have analyzed publicly available single-cell RNAseq data of tumor-associated macrophages (GSE260641, Wang 2024 Cell) to determine whether there are differences in expression of circadian clock genes between different TAM populations. We have added these data as a new Figure 9. Please see the figure and updated text below.

      "Tumor-associated macrophages exhibit heterogeneity in circadian clock gene expression.

      __ Our findings suggested that heterogeneity of the circadian clock may lead to disorder in bulk macrophage populations, but did not reveal if specific gene expression changes exist in tumor-associated macrophages at the single-cell level. To determine whether heterogeneity exists within the expression of circadian clock genes of the tumor-associated macrophage population, we analyzed publicly available single-cell RNA sequencing data of macrophages isolated from B16-F10 tumors[107]. To capture the heterogeneity of macrophage subsets within the TAM population, we performed unbiased clustering (Figure 9A). We then performed differential gene expression to determine if circadian clock genes were differentially expressed within the TAM subpopulations. The circadian clock genes Bhlhe40 (DEC1), Bhlhe41 (DEC2), Nfil3 (E4BP4), Rora (RORα), Dbp (DBP), and Nr1d2 (REV-ERBβ) were significantly (adj.p We next sought to determine whether differences in circadian clock gene expression between TAM subpopulations were associated with exposure to acidic pH in the TME. To this end, we first assessed Crem expression in the TAM subpopulations that were identified by unbiased clustering. Crem expression was significantly higher in TAM clusters 4, 5, and 6 compared to TAM clusters 1-3 and 7-9 (Figure 9C). Clusters were subset based on Crem expression into Crem high (clusters 4-6) and Crem low (clusters 1-3, 7-9) (Figure 9D), and differential gene expression analysis was performed. The circadian clock genes Nfil3, Rora, Bhlhe40, and Cry1 (CRY1) were significantly (adj.p __And in the Discussion:

      "Supporting the notion that population-level disorder may exist in TAMs, we used scRNA-sequencing data and found evidence of heterogeneity between the expression of circadian clock genes in different TAM subpopulations (Figure 9A, B). Phenotypic heterogeneity of TAMs in various types of cancer has previously been shown[20, 21, 125, 126], and we have identified distinct TAM subpopulations by unbiased clustering (Figure 9A). Within those TAM subpopulations, we identified differential expression of circadian clock genes encoding transcription factors that bind to different consensus sequences: DEC1 and DEC2 bind to E-boxes, NFIL3 and DBP binds to D-boxes, and RORα and REV-ERBβ binds to retinoic acid-related orphan receptor elements (ROREs)[127, 128]. While little is known about regulation of macrophages by E-box and D-box elements beyond the circadian clock, aspects of macrophage function have been shown to be subject to transcriptional regulation through ROREs[129, 130]. Thus, we speculate that variations in these transcription factors may exert influence on expression of genes to drive diversity between TAM subpopulations. Differential expression of circadian clock genes between TAM subpopulations was also associated with Crem expression (Figure 9C-E), suggesting that exposure of TAMs to acidic pH within the TME can alter the circadian clock. However, there remained significant variation in expression of circadian clock genes within the Crem high and Crem low groups (Figure 9B), suggesting that acidic pH is not the only factor in the TME that can alter the circadian clock. Together, these data implicate the TME in driving heterogeneity in TAM circadian rhythms just as it drives heterogeneity in TAM phenotype.

      Interestingly, in contrast to our observations of circadian disorder in TAMs isolated from LLC tumors (Figure 6), rhythmicity in expression of circadian genes was observed in bulk TAMs isolated from B16 tumors[107]. This suggests that circadian rhythms of TAMs are maintained differently in different types of cancer. Notably, both of these observations were at the population level. Upon separation of the B16 TAM population into subsets by unbiased clustering of single-cell RNA sequencing data, we measured differences in expression of circadian clock genes between TAM subpopulations (Figure 9A,B). This suggests that even within a rhythmic TAM population, there is heterogeneity in the circadian clock of TAM subpopulations."

      Additionally, it is widely acknowledged that human and mouse macrophages exhibit distinct gene expression profiles, both in vitro and in vivo. While assuming that genes involved in circadian rhythms are conserved across species, the authors could consider extending their funding to include analyses of single-sorted macrophages from cancer patients, such as those with lung cancer or pancreatic ductal adenocarcinoma (PDAC). These experiments would provide relevant insights into TAM biology.

      We agree that with Reviewer #1 that ultimately, being able to relate findings in mice to humans is critical. It is important to assess if circadian disorder is observed in TAMs in human cancers as it is for LLC tumor-derived macrophages in mice. To address this point, we have performed CCD using a human data set (GSE116946; Garrido 2020 J Immunother Cancer) suitable for use with CCD (wherein macrophages were isolated from bulk tumor in humans, with a high enough samples size, and not cultured prior to sequencing). We have added these data as a new Figure 7, shown below. Please see the added data and updated text below.

      "We next assessed the status of the circadian clock in human TAMs from NSCLC patients. We performed CCD with publicly available RNA-seq data of tumor-adjacent macrophages and tumor-associated macrophages from NSCLC patients, using alveolar macrophages from healthy donors as a control[104, 105]. To assess the contribution of the acidic TME to circadian disorder, we subset TAM NSCLC patient samples into groups (Crem high TAMs and Crem low TAMs) based on median Crem expression. Notably, in macrophages from human NSCLC there was a trend toward disorder in Crem low but not Crem high TAM samples (Figure 7A,B). Additionally, the co-variance among core clock genes observed in alveolar macrophages from healthy donors was absent within Crem low and Crem high TAM samples (Figure 7C). In all, these data indicate that there is population-level disorder in the circadian rhythms of tumor-associated macrophages in humans and mice, suggesting that circadian rhythms are indeed altered in macrophages within the TME."

      And in the Discussion:

      "Indeed, we observed differences in the circadian clock of Crem low human TAM samples compared to Crem high human TAM samples, suggesting that acidic pH influences circadian disorder in TAMs (Figure 7). Interestingly, Crem low TAM samples exhibited a trend toward disorder while Crem high TAM samples did not. This is of particular interest, as we have observed that acidic pH can enhance circadian rhythms in macrophages, raising the question of whether acidic pH promotes or protects against circadian disorder."

      Minor comments: 1. Figure 2C needs clarification. It's unclear why pro-inflammatory macrophages treated with lactic acid would have a shorter amplitude and period, while acidic pH would increase amplitude and period in M2 macrophages.

      We thank Reviewer #1 for this important observation. Based on the comment, it is our understanding that the Reviewer is referring to the data in Figure 2 (low pH) compared to Figure 4 (lactate). We also find it very interesting that lactate alters rhythms in a manner distinct from the way in which acidic pH alters rhythms. Reviewer 3 asked for clarification on how lactate affected circadian gene expression in pH 7.4 or 6.5. We have added these data as Figure 4C (data and text below). It is notable that lactate opposing effects on circadian gene expression in pH 6.5, enhancing the effects of low pH in some cases (Nr1d1) while blunting them in other cases (Cry1). This is mentioned in the text.

      "Lactate was also observed to alter expression of the circadian clock genes Per2, Cry1, and Nr1d1 over time in BMDMs cultured at pH 6.5, while having more subtle effects at pH 7.4 (Figure 4C). Notably, lactate blunted the effect of pH 6.5 on Cry1 expression, while enhancing the effect of low pH on Nr1d1 expression."

      Why these two stimuli alter rhythms differently remains an open question that is discussed in the Discussion section and is prime to be a topic of future investigation. We have added to the Discussion section potential reasons why these conditions may alter rhythms differently, such as the different pathways downstream of sensing these two different conditions. Please see the updated text, below.

      "Although lactate polarizes macrophages toward a pro-resolution phenotype similar to acidic pH[30, 93], exposure to lactate had different effects on circadian rhythms - and in some cases, circadian clock gene expression - than exposure to acidic pH (Figure 4). Sensing of lactate occurs through different pathways than acid-sensing, which may contribute to the different ways in which these two stimuli modulate circadian rhythms of macrophages[111]. One previously published finding that may offer mechanistic insight into how phenotype can influence circadian rhythms is the suppression of Bmal1 by LPS-inducible miR-155[54]. It has also been observed that RORα-mediated activation of Bmal1 transcription is enhanced by PPARγ co-activation[112]. In macrophages, PPARγ expression is induced upon stimulation with IL-4 and plays a key role in alternative activation of macrophages, promoting a pro-resolution macrophage phenotype, and supporting resolution of inflammation[113-115]. Such observations prompt the question of whether there are yet-unidentified factors induced downstream of various polarizing stimuli that can modulate expression of circadian genes at the transcriptional and protein levels. Further work is required to understand the interplay between macrophage phenotype and circadian rhythms."

      The scale in Figure 2C should be equal for all conditions (e.g., -200).

      We appreciate Reviewer #1's preference for the axes to be scaled similarly to enable cross-comparison between graphs. However, due to the different amplitude of pro-inflammatory macrophages compared to the others, we feel that making all axes the same will make it hard to see the rhythms of pro-inflammatory macrophages, hindering the reader's ability to observe the data. Thus, we have put the matched-axis plots, shown below, in Supplementary Figure 4A.

      Absolute values of amplitude, damping, and period differ between Figure 1 and Figure 2A, B, C. The authors should explain these discrepancies.

      As with many experimental approaches, there is slight variation in absolute values between independent experiments, which Reviewer #1 correctly notes. However, while the absolute values vary slightly, the relationship between the values in each of these conditions remains the same across the panels mentioned by Reviewer #1.

      The authors should consider modulating the acidic environment of macrophages in settings more representative of cancer. For example, by adding conditioned media from tumor cells with pronounced glycolysis.

      We appreciate Reviewer #1's desire to more closely mimic the tumor microenvironment. To address Reviewer #1's point, we cultured macrophages in RPMI or cancer cell (KCKO) supernatant at pH 6.5 or pH-adjusted to pH 7.4 and assessed rhythms by measuring rhythmic activity of Per2-Luc with LumiCycle analysis. We then compared changes in rhythms between macrophages cultured normal media to cancer cell supernatant in pH-matched conditions to assess how cancer cell-conditioned media may influence circadian rhythms of macrophages, and the contribution of acidic pH. We have added these data, shown below, as a new Supplementary Figure 5, and included a discussion of these data in the manuscript. Please see the new Figure and updated text below.

      "Cancer cell supernatant alters circadian rhythms in macrophages in a manner partially reversed by neutralization of pH.

      We have observed that polarizing stimuli, acidic pH, and lactate can alter circadian rhythms. However, the tumor microenvironment is complex. Cancer cells secrete a variety of factors and deplete nutrients in the environment. To model this, we cultured BMDMs in RPMI or supernatant collected from KCKO cells, which are a murine model of pancreatic ductal adenocarcinoma (PDAC)[94, 95], at pH 6.5 or neutralized to pH 7.4 (Supplementary Figure 5). Circadian rhythms of BMDMs cultured in cancer cell supernatant at pH 7.4 or pH 6.5 exhibited increased amplitude and lengthened period compared to RPMI control at pH 7.4 or 6.5, respectively, indicating that cancer cell supernatant contains factors that can alter circadian rhythms of BMDMs. Notably, BMDMs cultured in cancer cell supernatant at pH 6.5 had increased amplitude and shortened period compared to BMDMs cultured in cancer cell-conditioned media at pH7.4, indicating that pH-driven changes in rhythms were maintained in BMDMs cultured in cancer cell supernatant. When the pH of cancer cell supernatant was neutralized to pH7.4, the increased amplitude was decreased, and the shortened period was lengthened, indicating that neutralizing acidic pH partially reverses the changes in rhythms observed in macrophages cultured in cancer cell supernatant at pH 6.5. These data further support our observations that acidic pH can alter circadian rhythms of macrophages both alone and in combination with various factors in the TME."

      And, in the Discussion:

      "We have shown that various stimuli can alter rhythms of macrophages in a complex and contributing manner, including polarizing stimuli, acidic pH, and lactate. TGFβ is produced by a variety of cells within the TME, and was recently identified as a signal that can modulate circadian rhythms[123, 124]. Additionally, when we exposed macrophages to cancer cell-conditioned media, rhythms were modulated in a manner distinct from acidic pH or lactate, with these changes in rhythms partially reversed by neutralization of the cancer cell-conditioned media pH (Supplementary Figure 5). It is conceivable that, in addition to acidic pH, other stimuli in the TME are influencing circadian rhythms to drive population-level disorder that we observed by CCD."

      Arg1 alone is not sufficient as an M2 polarization marker. The authors should include additional markers.

      We thank Reviewer #1 for bringing up this critical point in experimental rigor. While Arg1 is a commonly-used marker for M2 polarization, Reviewer #1 points out that polarization of macrophages is typically assessed by a full panel of markers characteristic of the M2 state. To address this point, we have expanded our panel to include several other markers of M2 polarization in mice such as Retnla, Ym1, MGL1, and CD206. In response to Reviewer 2's major point 2 and Reviewer 3's major point 4 below, we have also expanded our panel of markers used to assess the M1 polarization state with Tnfa, Il1b. and Il6. We have added these data, shown below, to Supplementary Figure 1 and updated the text appropriately. Please see the new Figure and updated text below.

      "Consistent with previous studies, we found that genes associated with anti-inflammatory and pro-resolution programming characteristic of IL-4 and IL-13-stimulated macrophages such as Arg1, Retnla, Chil3 (Ym1), Clec10a (MGL1), and Mrc1 (CD206) were induced in IL-4 and IL-13-stimulated macrophages, but not IFNγ and LPS-stimulated macrophages. In contrast, genes associated with pro-inflammatory activity characteristic of IFNγ and LPS-stimulated macrophages such as Nos2 (iNOS), Tnfa, Il1b, and Il6 were induced in IFNγ and LPS-stimulated macrophages, but not IL-4 and IL-13-stimulated macrophages (Supplementary Figure 1)[28, 30, 65, 71, 74, 75]. This indicates that macrophages stimulated with IL-4 and IL-13 were polarized toward a pro-resolution phenotype, while macrophages stimulated with IFNγ and LPS were polarized toward a pro-inflammatory phenotype."

      __ Significance__

      While the manuscript provides valuable insights and has obvious novelty, it requires a significant revision

      We thank Reviewer #1 for their deep read of our manuscript, and their helpful feedback and suggestions. As shown by the comments above, we are confident we have fully addressed each of the points that were made to result in a much-improved revised manuscript.

      __ Reviewer #2 __

      Evidence, reproducibility and clarity

      Knudsen-Clark et al. showed that the circadian rhythm of bone marrow-derived macrophages (BMDM) can be affected by polarization stimuli, pH of the microenvironment, and by the presence of sodium-lactate. Mechanistically, the acidic pH of cell microenvironment is partly regulated by intracellular cAMP-mediated signaling events in BMDM. The authors also showed that the circadian clock of peritoneal macrophages is also modified by the pH of the cell microenvironment. Using publicly available data, the authors showed that the circadian rhythm of tumor-associated macrophages is similar to that of Bmal1-KO peritoneal macrophages. In a murine model of pancreatic cancer, the authors showed that the tumor growth is accelerated in C57BL/6 mice co-injected with cancer cells and Bmal1-KO BMDM as compared to mice co-injected with cancer cell and wild type BMDM.

      We thank Reviewer #2 for their insightful and helpful comments and feedback. Their Review guided key clarifying experiments and additions to the Discussion and Methods. To summarize, we added new data to Supplementary Figure 1 to characterize distinct gene expression in our different polarized macrophage populations, showed in Supplementary Figure 2 that serum shock independently induces cAMP and Icer, discussed the limitations of the artificial polarization models more clearly, and updated our Methods to better explain how macrophages were isolated from the peritoneum. We also quantified multiple immunoblots of pCREB, provided clarity in the Methods and Reviewer-only data on how our protein-extraction protocol isolates nuclear protein, better introduced the BMAL1-KO mouse model, and showed in Supplementary Figure 6 that low pH can induce oscillations in the absence of a serum shock.

      Major points of criticism: 1. Nine main figures include different experimental models on a non-systematic manner in the manuscript, and only literature-based correlation is used to link the results each other. The authors used in vitro BMDM and peritoneal cell-based model systems to study the effects of IL4+IL13, IFNg+LPS, low pH, sodium-lactate, adenylate cyclase inhibitors on the circadian clock of macrophages. The link between these microenvironment conditions of the cells is still correlative with the tumor microenvironment: publicly available data were used to correlate the increased expression level of cAMP-activated signaling events with the presence of acidic pH of tumor microenvironment. Notably, the cell signaling messenger molecule cAMP is produced by not only low extracellular pH by activated GPCRs, but also starvation of the cell. The starvation is also relevant to this study, since the BMDM used in the in vitro culture system were starving for 24 hours before the measurement of Per2-Luc expression to monitor circadian rhythm.

              We agree with the important point that Reviewer #2 makes that our synchronization protocol of serum starvation followed by serum shock can impact the cAMP signaling pathway. Indeed, it has previously been shown that serum shock induces phosphorylation of CREM in rat fibroblasts, which is indicative of signaling through the cAMP pathway. To address this point, we have added a schematic of our synchronization protocol to Supplementary Figure 2B for additional clarity. We have also performed additional experiments to test whether cAMP signaling is induced in macrophages by our synchronization protocol. For this, we assessed downstream targets of the cAMP signaling pathway, Icer and pCREB, after serum starvation but before serum shock, and at several time points post-treatment with serum shock (Supplementary Figures 2D,E). We observed that Icer and phosphorylation of Creb are induced rapidly in macrophages upon exposure to serum shock, as early as 10 minutes for pCREB and 1 hour post-exposure for Icer. Notably, this signaling is transient and rapidly returns to baseline, with pCREB levels fully returned to baseline by 2 hours post-treatment, at which time media is replaced and the experiment begins (CT 0). These data, shown below, have been added to Supplementary Figure 2 and a discussion of these data has been added to the manuscript - please see the modified text below.
      

      "The synchronization protocol we use to study circadian rhythms in BMDMs involves a 24-hour period of serum starvation followed by 2 hours of serum shock. It has previously been shown that serum shock can induce signaling through the cAMP pathway in rat fibroblasts[98]. To determine whether the synchronization protocol impacts cAMP signaling in macrophages, we harvested macrophages before and after serum shock. We then assessed Icer expression and phosphorylation of cyclic AMP-response element binding protein (CREB), which occur downstream of cAMP and have been used as readouts to assess induction of cAMP signaling in macrophages[29, 96, 100]. Serum shock of macrophages following serum starvation led to rapid phosphorylation of CREB and Icer expression that quickly returned to baseline (Supplementary Figure 2D,E). This indicates that serum starvation followed by serum shock in the synchronization protocol we use to study circadian rhythms in BMDMs induces transient signaling through the cAMP signaling pathway. "

      The definition of pre-resolution macrophages (MF) used across the manuscript could be argued. The authors defined BMDM polarized with IL-4 and IL-13 as pre-resolution MF. Resolution is followed by inflammation, but the IL-4 secretion does not occur in every inflammatory setting. Moreover, IL-4 and IL-13 are secreted during specific tissue environment and immunological settings involving type 2 inflammation or during germinal center reactions of the lymph nodes. • What are the characteristics of pre-resolution macrophages (MF)? The authors indicated that IL-4 and IL-13 cytokines were used to model the pre-resolution macrophages. In which pathological context are these cytokines produced and induce pre-resolution macrophages? IL-4 polarized BMDM can also produce pro-inflammatory protein and lipid mediators as compared to LPS-stimulated BMDM, and IL-4 polarized BMDM still have potent capacity to recruit immune cells and to establish type 2 inflammation.

      • The authors showed Arg1 and Vegfa qPCR data from BMDM only. Based on the literature, these MFs are anti-inflammatory cells particularly. Resolution-related MFs followed by acute inflammation are a specific subset of MFs, and the phenotype of pre-resolution MF should be described, referred, and measured specifically.

      We thank Reviewer #2 for bringing up this important point that clarity is required in describing our in vitro macrophage models. We chose the most commonly used models of in vitro macrophage polarization in the tumor immunology field, M2 (IL-4+IL-13) and M1 (IFNγ+LPS). These polarization conditions have been used for over two decades in the field, and have been well-characterized to drive a pro-inflammatory (for M1) and pro-resolution or anti-inflammatory (for M2) macrophage phenotype (Murray 2017 Annu Rev Phys). Each of these cell states have similarities in phenotype to pro-inflammatory and pro-resolution (pro-tumorigenic) macrophages found in tumors. In fact, in the literature, pro-inflammatory and pro-resolution TAMs will frequently be categorized as "M1" or "M2", respectively, even though this is a gross oversimplification (Ding 2019 J Immunol, Garrido-Martin 2020 J Immunother Cancer).

      As Reviewer #2 points out, IL-4 and IL-13 play a role in inflammatory settings, mediating protective responses to parasites and pathological responses to allergens. Importantly, IL-4 and IL-13 are also key regulators and effectors of resolution and wound repair (Allen 2023 Annu Rev Immunol). In line with this, M2 macrophages show many of the characteristics of pro-resolution programming in their gene expression profile, expressing genes associated with wound healing (ex. Vegf) and immunoregulation (ex. Arg1) (Mantovani 2013 J Pathol). These cells have frequently been used as a model for studying TAMs in vitro, due to the similarity in pro-resolution programming that is dysregulated/hijacked in TAMs (Biswas 2006 Blood). M2 macrophages have also been referred to as anti-inflammatory, and this is in line with their role in the type 2 response driven by IL-4 and IL-13, as this is primarily a response induced by allergy or parasites where tissue damage drives an anti-inflammatory and pro-resolution phenotype in macrophages (Pesce 2009 Plos Pathogens and Allen 2023 Annu Rev Immunol).

      We do not assert that these in vitro models recapitulate the macrophage polarization cycle that Reviewer #2 astutely describes, and indeed, stimuli polarizing macrophages in tumor are much more diverse and complex (Laviron 2022 Cell Rep). We also fully agree with Reviewer #2 that, while IL4 and IL13 may exist in the tumor and be secreted by Th2 CD4 T cells (see Shiao 2015 Cancer Immunol Res), there may be multiple reasons why macrophages may be polarized to a pro-resolution, M2-like state in a tumor (in fact, exposure to low pH and lactate each independently do this, as we show in Supplementary Figure 2 and Figure 4, and was previously shown in Jiang 2021 J Immunol and Colegio 2014 Nature). Nonetheless, using the well-described M1 and M2 in vitro models allows our findings to be directly comparable to the vast literature that also uses these models, and to understand how distinct polarization states respond to low pH.

      We fully agree with Reviewer #2 that these cells must be defined more clearly in the text. We have taken care to discuss the limitations of using in vitro polarization models to study macrophages in our Limitations of the Study section. To better address Reviewer #2's concern, we have more thoroughly introduced the M2 macrophages as a model, and are clear that that these are type 2-driven macrophages that share characteristics of pro-resolution macrophages. We have also added additional citations to the manuscript, including those highlighted above in our response. Finally, we have expanded our panel to better characterize the IL-4/IL-13 stimulated macrophages using more markers that have been characterized in the literature, in line with both Reviewer #2's comments and that of Reviewer #1 and Reviewer #3. Please see the updated data and text, below.

      "As macrophages are a phenotypically heterogeneous population in the TME, we first sought to understand whether diversity in macrophage phenotype could translate to diversity in circadian rhythms of macrophages. To this end, we used two well-established in vitro polarization models to study distinct macrophage phenotypes[5, 60-63]. For a model of pro-inflammatory macrophages, we stimulated macrophages with IFNγ (interferon γ) and LPS (lipopolysaccharide) to elicit a pro-inflammatory phenotype[60, 64]. These macrophages are often referred to as 'M1' and are broadly viewed as anti-tumorigenic, and we will refer to them throughout this paper as pro-inflammatory macrophages[65, 66]. For a model at the opposite end of the phenotypic spectrum, we stimulated macrophages with IL-4 and IL-13[60, 67]. While these type 2 stimuli play a role in the response to parasites and allergy, they are also major drivers of wound healing; in line with this, IL-4 and IL-13-stimulated macrophages have been well-characterized to adopt gene expression profiles associated with wound-healing and anti-inflammatory macrophage phenotypes[68-71]. As such, these macrophages are often used as a model to study pro-tumorigenic macrophages in vitro and are often referred to as 'M2' macrophages; throughout this paper, we will refer to IL-4 and IL-13-stimulated macrophages as pro-resolution macrophages[66, 72, 73]. Consistent with previous studies, we found that genes associated with anti-inflammatory and pro-resolution programming characteristic of IL-4 and IL-13-stimulated macrophages such as Arg1, Retnla, Chil3 (Ym1), Clec10a (MGL1), and Mrc1 (CD206) were induced in IL-4 and IL-13-stimulated macrophages, but not IFNγ and LPS-stimulated macrophages. In contrast, genes associated with pro-inflammatory activity characteristic of IFNγ and LPS-stimulated macrophages such as Nos2 (iNOS), Tnfa, Il1b, and Il6 were induced in IFNγ and LPS-stimulated macrophages, but not IL-4 and IL-13-stimulated macrophages (Supplementary Figure 1)[28, 30, 65, 71, 74, 75]. This indicates that macrophages stimulated with IL-4 and IL-13 were polarized toward a pro-resolution phenotype, while macrophages stimulated with IFNγ and LPS were polarized toward a pro-inflammatory phenotype.

      In the Limitations of the Study section, we now write the following:

      "Our observations of rhythms in macrophages of different phenotypes are limited by in vitro polarization models. It is important to note that while our data suggest that pro-inflammatory macrophages have suppressed rhythms and increased rate of desynchrony, it remains unclear the extent to which these findings apply to the range of pro-inflammatory macrophages found in vivo. We use IFNγ and LPS co-treatment in vitro to model a pro-inflammatory macrophage phenotype that is commonly referred to as 'M1', but under inflammatory conditions in vivo, macrophages are exposed to a variety of stimuli that result in a spectrum of phenotypes, each highly context-dependent. The same is true for for 'M2'; different tissue microenvironment are different and pro-resolution macrophages exist in a spectrum."

      The authors used IFNg and LPS, or IL-4 and IL-13 and co-treatments to polarize BMDM in to type 1 (referred as pro-inflammatory MF) and type 2 (referred as pre-resolution MF) activation state. The comparison between these BMDM populations has limitations, since LPS induces a potent inflammatory response in MF. The single treatment with MF-polarizing cytokines enable a more relevant comparison to study the circadian clock in classically and alternatively activated MF.

      We thank Reviewer #2 for bringing up this important point to provide additional clarity on our polarization conditions. The use of IFNγ and LPS to polarize macrophages toward a pro-inflammatory, M1 phenotype, and the use of IL-4 an IL-13 to polarize macrophages toward a pro-resolution, M2 phenotype have been commonly used for over two decades, and thus are well-characterized in the literature (please see Murray 2017 Annu Rev Phys for an extensive review on the history of these polarization models, as well as Hörhold 2020 PLOS Computational Biology, Binger 2015 JCI, McWhorter 2013 PNAS, Ying 2013 J Vis Exp for more recent studies using these models). The use of LPS alone or in combination with IFNγ, and IL-13 along with IL-4, was introduced in 1998 (Munder 1998 J Immunol). This approach was originally designed to mimic what could happen when macrophages were exposed to CD4+ Th1 cells, which produce IFNγ, or Th2 cells, which produce IL-4 and IL-13 (Munder 1998 J Immunol, Murray 2017 Annu Rev Phys). As Reviewer #2 points out, these stimuli induce potent responses, driving macrophages to adopt pro-inflammatory or pro-resolution/anti-inflammatory phenotypes that are two extremes at opposite ends of the spectrum of macrophage phenotypes (Mosser 2008 Nat Rev Immunol). Since our goal was to study rhythms of distinct macrophage phenotypes in vitro, and how TME-associated conditions such as acidic pH and lactate affect their rhythms, these cell states were appropriate for our questions. Thus, the polarization models used in this paper allowed us to achieve this goal. We include a section in the Discussion on the limitations of in vitro polarization models.

      "A critical question in understanding the role of circadian rhythms in macrophage biology is determining how different polarization states of macrophages affect their internal circadian rhythms. This is especially important considering that tumor-associated macrophages are a highly heterogeneous population. Our data indicate that compared to unstimulated macrophages, rhythms are enhanced in pro-resolution macrophages, characterized by increased amplitude and improved ability to maintain synchrony; in contrast, rhythms are suppressed in pro-inflammatory macrophages, characterized by decreased amplitude and impaired ability to maintain synchrony (Figure 1). These agree with previously published work showing that polarizing stimuli alone and in combination with each other can alter rhythms differently in macrophages[80, 81]. In a tumor, macrophages exist along a continuum of polarization states and phenotypes[18-21, 24]. Thus, while our characterizations of rhythms in in vitro-polarized macrophages provide a foundation for understanding how phenotype affects circadian rhythms of macrophages, further experiments will be needed to assess macrophages across the full spectrum of phenotypes. Indeed, alteration of rhythms may be just as highly variable and context-dependent as phenotype itself."

      There are missing links between the results of showing the circadian rhythm of polarized BMDM, sodium-lactate treated BMDM, and tumor growth. Specifically, do the used pancreatic ductal adenocarcinoma cells produce IL-4 and sodium-lactate? In the LLC-based experimental in silico analysis of tumors, the LLC do not produce IL-4.

      Reviewer #2 raises important points about the source of lactate and IL-4 in tumors as relevance for our investigation of how these factors can alter rhythms in macrophages. Tumor-infiltrating Th2 CD4 T cells are potential sources of IL-4 and IL-13 in the tumor (see Shiao 2015 Cancer Immunol Res). Various cells in the tumor can produce lactate. We discuss this in both the Introduction and the Results: poor vascularization of tumors results in hypoxia areas, where cells are pushed toward glycolysis to survive and thus secrete increased glycolytic waste products such as protons and lactate. As lactate is lactic acid, ionized it is sodium l-lactate.

      How can the circadian rhythm affect the function of BMDM? The Authors should provide evidence that circadian rhythm affects the function of polarized MF.

      We agree with Reviewer #2 that the next step is to determine how altered rhythms influence function of macrophages. This will be the topic of future work, but is outside the scope of this paper. Our contribution with this paper is providing the first evidence that rhythms are altered in the TME and the TME-associated conditions can alter rhythms in macrophages. We have added what is currently known about how circadian rhythms influence macrophages function to the discussion section to facilitate a conversation about this important future direction. Please see the updated text below.

      "Considering our observations that conditions associated with the TME can alter circadian rhythms in macrophages, it becomes increasingly important to understand the relevance of macrophage rhythms to their function in tumors. It has been shown that acidic pH and lactate can each drive functional polarization of macrophages toward a phenotype that promotes tumor growth, with acidic pH modulating phagocytosis and suppressing inflammatory cytokine secretion and cytotoxicity[28, 30, 93]. However, how the changes in circadian rhythms of macrophages driven by these conditions contributes to their altered function remains unknown. Current evidence suggests that circadian rhythms confer a time-of-day-dependency on macrophage function by gating the macrophage response to inflammatory stimuli based on time-of-day. As such, responses to inflammatory stimuli such as LPS or bacteria are heightened during the active phase while the inflammatory response is suppressed during the inactive phase. An important future direction will be to determine how changes in circadian rhythms of macrophages, such as those observed under acidic pH or high lactate, influences the circadian gating of their function."

      In Figure 3, the authors show data from peritoneal cells. The isolated peritoneal cells are not pure macrophage populations. Based on the referred article in the manuscript, the peritoneal cavity contains more then 50% of lymphocytes, and the myeloid compartment contains 80% macrophages.

      Reviewer #2 raises important concerns about the purity of the peritoneal population used in our experiments. We enrich for peritoneal macrophages from the peritoneal exudate cells by removing non-adherent cells in culture. This is described in our Methods section and is a method of isolation that is commonly used in the field, as lymphocytes are non-adherent. In addition to the source cited in the paper within our Methods section (Goncalves 2015 Curr Prot Immunol), please see Layoun 2015 J Vis Exp, de Jesus 2022 STAR Protocols, and Harvard HLA Lab protocol - macrophages enriched in this manner have been shown to be over 90% pure. We have modified our Methods section to make this clear, and added the additional references in this response to this section of our Methods. Please see the modified text below.

      "Peritoneal exudate cells were harvested from mice as previously published[137]. To isolate peritoneal macrophages, peritoneal exudate cells were seeded at 1.2*106 cells/mL in RPMI/10% HI FBS supplemented with 100U/mL Penicillin-Streptomycin and left at 37⁰C for 1 hour, after which non-adherent cells were rinsed off[136]. Isolation of peritoneal macrophages using this method has been shown to yield a population that is over 90% in purity[138, 139]. Peritoneal macrophages were then cultured in Atmospheric Media at pH 7.4 or 6.5 with 100μM D-luciferin, and kept at 37⁰C in atmospheric conditions."

      The figure legend of Figure 3 describes the effects of pH on the circadian rhythm of bone marrow-derived macrophages ex vivo. Peritoneal macrophages involve tissue resident peritoneal macrophages with yolk sac and fetal liver origin, and also involve small peritoneal MF with bone marrow origin. The altered description of results and figure legends makes confusion.

      We are very grateful to Reviewer #2 for pointing out our typo. We have fixed the caption of Figure 3 to properly describe the data as "peritoneal macrophages ex vivo".

      In Figure 6C, one single Western blot is shown with any quantification. The authors should provide data of the relative protein level of p-CREB from at least 3 independent experiments. In the Western-blot part of the methods, the authors described that the pellet was discarded after cell lysis. The p-CREB is the activated form of the transcription factor CREB and there is increased binding to the chromatin to regulate gene expression. By discarding the pellet after cell lysis, the chromatin-bond p-CREB could be also removed at the same time.

      We thank Reviewer 2 for bringing up this point. We agree that quantification is an important aspect of western blot. We have repeated the experiment again for n=3 and provide quantification of pCREB normalized to total protein. We have added these data, shown below, to Figure 5.

      Reviewer #2 also expressed concern that we may not be capturing all of the CREB due to nuclear localization and chromatin binding. We specifically chose the lysis buffer M-Per, which is formulated to lyse the nucleus and solubilize nuclear and chromatin-bound proteins. To demonstrate this, we show in the below Figure to the Reviewer that the nuclear protein p85 is solubilized and readily detectable by western blot using our protein extraction method.

      We have also added an additional sentence in the Methods section for clarity - please see the modified text below.

      "Cells were lysed using the M-Per lysis reagent (Thermo Scientific, CAT#78501), supplemented with protease and phosphatase inhibitor cocktail (1:100; Sigma, CAT#PPC1010) and phosphatase inhibitor cocktail 2 (1:50; Sigma, CAT#P5726), with 200μM deferoxamine (Sigma, CAT#D9533). M-Per is formulated to lyse the nucleus and solubilize nuclear and chromatin-bound proteins, allowing isolation of nuclear proteins as well as cytosolic proteins. Lysates were incubated on ice for 1 hour, then centrifuged at 17,000 xg to pellet out debris; supernatant was collected."

      It is confusing that adenylate-cyclase inhibitor MDL-12 elevated the phospho-CREB levels in BMDM. How can the authors exclude any other inducers of CREB phosphorylation?

      We agree with Reviewer #2 that it is surprising pCREB was elevated with MDL-12 treatment alone, and we do indeed think that there are other pathways contributing to this. We have addressed this point in the Discussion - please see the text below.

      "The mechanism through which acidic pH can modulate the circadian clock in macrophages remains unclear. Evidence in the literature suggests that acidic pH promotes a pro-resolution phenotype in macrophages by driving signaling through the cAMP pathway[29]. It has previously been shown that cAMP signaling can modulate the circadian clock[99]. However, our data indicated that cAMP signaling was not fully sufficient to confer pH-mediated changes in circadian rhythms of macrophages (Figure 5A,B). Treatment with MDL-12, commonly known as an inhibitor of adenylyl cyclase[29, 117], resulted in suppression of pH-induced changes in amplitude of circadian rhythms but did not inhibit signaling through the cAMP signaling pathway (Figure 5C,D). While MDL-12 is commonly used as an adenylyl cyclase inhibitor, it has also been documented to have inhibitory activity toward phosphodiesterases (PDEs) and the import of calcium into the cytosol through various mechanisms[118, 119]. This is of particular interest, as calcium signaling has also been shown to be capable of modulating the circadian clock[120]. Furthermore, while acid-sensing through GPCRs have been the most well-characterized pathways in macrophages, there remain additional ways in which acidic pH can be sensed by macrophages such as acid-sensing ion channels[121, 122]. Further work is required to understand the signaling pathways through which pH can influence macrophage phenotype and circadian rhythms."

      It is described in the methods that BMDM were starving for 24 hours in serum-free culture media followed by serum shock (50% FBS). The cAMP production can be induced during cell starvation which should be considered for the data representation.

      We appreciate that Reviewer #2 points out that our synchronization protocol of serum starvation followed by serum shock may impact the cAMP signaling pathway in macrophages, as serum shock has been shown to induce pCREB, a downstream mediator of cAMP signaling, in rat fibroblasts. Indeed, we show in additional experiments performed (in response to Reviewer #2's major comment 1) evidence that cAMP signaling is induced in macrophages following the serum shock phase of our synchronization protocol, as indicated by elevation of Icer and pCREB. As we note above, this induction is transient and returns to baseline by 2 hours post-serum shock, the time at which we replace media and begin our experiments (CT 0).

      Despite the transient nature of cAMP induction by our synchronization protocol, we agree wholeheartedly with Reviewer #2 that this must be considered in light of our experimental system in which we are studying the effect of acidic pH on circadian rhythms of macrophages, which in itself induces signaling through the cAMP signaling pathway. To address Reviewer #2's point, we have performed experiments in which we culture unstimulated BMDMs in neutral pH 7.4 or acidic pH 6.5, without prior serum starvation and serum shock (i.e. we do not submit these BMDMs to the synchronization protocol). We then observed circadian rhythms of Per2-Luc by LumiCycle to determine whether acidic pH alters circadian rhythms of BMDMs in the absence of prior serum starvation followed by serum shock. Similar to our observations in Figure 2, circadian rhythms of macrophages at pH 6.5 had increased amplitude and shortened period compared to rhythms of macrophages at pH 7.4. This indicates that pH-driven changes in circadian rhythms observed in our system are not due to the synchronization protocol. The data, shown below, have been placed in a new Supplementary Figure 6, and a discussion of these results has been added to the Results section - please see the updated text below.

      "As acidic pH induces signaling through the cAMP pathway, we sought to determine whether acidic pH independently contributed to the pH-driven changes in circadian rhythms we observe in BMDMs. To test this, we omitted the synchronization step and observed BMDM rhythms by LumiCycle when cultured in neutral pH 7.4 or acidic pH 6.8 or pH 6.5 (Supplementary Figure 6). Circadian rhythms of BMDMs cultured at pH 6.5 exhibited similar changes as previously observed, with enhanced amplitude and shortened period relative to BMDMs at pH 7.4. This indicates pH-driven changes observed in circadian rhythms of BMDMs occur in the absence of prior serum starvation and serum shock. "As acidic pH independently induces signaling through the cAMP pathway, we sought to determine whether acid pH could also independently contribute to the pH-driven changes in circadian rhythms we observe in BMDMs. To test this, we omitted the synchronization step and observed BMDM rhythms by LumiCycle when cultured in neutral pH 7.4 or acidic pH 6.8 or pH 6.5 (Supplementary Figure 6). Circadian rhythms of BMDMs cultured at pH 6.5 exhibited similar changes as previously observed, with enhanced amplitude and shortened period relative to BMDMs at pH 7.4. This indicates pH-driven changes observed in circadian rhythms of BMDMs occur in the absence of prior serum starvation and serum shock."

      How can the authors explain and prove that the wild type and Bmal1-KO BMDM co-injected with pancreatic cancer cells subcutaneously survive, present, and have effector functions at the same extent in the subcutaneous tissue, before and during tumor growth (Figure 9)? In other words, what kind of MF-derived parameters could be modified by disrupting the circadian rhythm of MF during tumor development? The production of MF-derived regulatory enzymes, cytokines, growth factors are affected by the disrupted circadian clock in MF?

              Review #2 poses the very important question of why we see differences in tumor growth in our co-injection model, and what might be driving it. Of note, co-injection models of tumor growth are commonly used to determine macrophage-specific roles in tumor growth (Colegio 2014 Nature, Mills 2019 Cell Rep, Lee 2018 Nat Comm). We observed that tumor growth is altered when macrophages with disrupted circadian rhythms (BMAL1 KO) are co-injected compared to when macrophages with intact circadian rhythms (WT) are co-injected in a murine model of pancreatic cancer using KCKO cells. Our observation is supported by a previously published paper in which they used a co-injection model of melanoma, which we cite in the manuscript(Alexander 2020 eLife). What drives this difference in tumor growth remains an open question that is the subject of future work and is outside the scope of this paper, which focuses on our discovery that factors associated with the tumor microenvironment can alter circadian rhythms in macrophages. We have included a discussion on what is currently known about how circadian rhythms alter macrophage function, acknowledging that we have yet to answer these important questions and identifying it as interest for future work. Please see the text below.
      

      "Considering our observations that conditions associated with the TME can alter circadian rhythms in macrophages, it becomes increasingly important to understand the relevance of macrophage rhythms to their function in tumors. It has been shown that acidic pH and lactate can each drive functional polarization of macrophages toward a phenotype that promotes tumor growth, with acidic pH modulating phagocytosis and suppressing inflammatory cytokine secretion and cytotoxicity[28, 30, 93]. However, how the changes in circadian rhythms of macrophages driven by these conditions contributes to their altered function remains unknown. Current evidence suggests that circadian rhythms confer a time-of-day-dependency on macrophage function by gating the macrophage response to inflammatory stimuli based on time-of-day. As such, responses to inflammatory stimuli such as LPS or bacteria are heightened during the active phase while the inflammatory response is suppressed during the inactive phase. An important future direction will be to determine how changes in circadian rhythms of macrophages, such as those observed under acidic pH or high lactate, influences the circadian gating of their function. Data from our lab and others suggest that disruption of the macrophage-intrinsic circadian clock accelerates tumor growth, indicating that circadian regulation of macrophages is tumor-suppressive in models of PDAC (our work) and melanoma [109]. This agrees with complementary findings that behavioral disruption of circadian rhythms in mice (through chronic jetlag) disrupts tumor macrophage circadian rhythms and accelerates tumor growth[56]. It remains unclear whether this is through the pro-tumorigenic functions of macrophages such as extracellular matrix remodeling or angiogenesis, through suppression of the anti-tumor immune response, or a combination of both functions. Further work will be needed to tease apart these distinctions."

      Minor points of criticism: 1. The figure legends of the graphs and diagrams are missing in Figure 2D,E,F

      We thank Reviewer #2 for pointing out that figure legends were missing. We have added legends for Figure 2D,E,F.

      The BMAL1-based in vivo murine model of circadian rhythm is not introduced in the manuscript.

      We thank Reviewer #2 for bringing to our attention that the BMAL1 KO macrophage model was not well-introduced in the manuscript. To address this point, we have modified the text to better introduce this model. Please see the modified text below.

      "As a positive control for circadian clock disruption, we used data from BMAL1 KO peritoneal macrophages [44]. BMAL1 KO macrophages have a genetic disruption of the circadian clock due to the loss of Bmal1, the central clock gene. As a result, circadian rhythms of BMAL1 KO macrophages are disrupted, lacking rhythmicity and downstream circadian regulation of macrophage function (Supplementary Figure 8)[45, 54]. "As a positive control for circadian clock disruption, we used data from BMAL1 KO peritoneal macrophages [44]. BMAL1 KO macrophages have a genetic disruption of the circadian clock due to the loss of Bmal1, the central clock gene. As a result, circadian rhythms of BMAL1 KO macrophages are disrupted, lacking rhythmicity and downstream circadian regulation of macrophage function (Supplementary Figure 8)[45, 54]."__ __

      Significance

      Knudsen-Clark et al. showed that the circadian rhythm of bone marrow-derived macrophages (BMDM) can be affected by polarization stimuli, pH of the microenvironment, and by the presence of sodium-lactate. Mechanistically, the acidic pH of cell microenvironment is partly regulated by intracellular cAMP-mediated signaling events in BMDM. The authors also showed that the circadian clock of peritoneal macrophages is also modified by the pH of the cell microenvironment. Using publicly available data, the authors showed that the circadian rhythm of tumor-associated macrophages is similar to that of Bmal1-KO peritoneal macrophages. In a murine model of pancreatic cancer, the authors showed that the tumor growth is accelerated in C57BL/6 mice co-injected with cancer cells and Bmal1-KO BMDM as compared to mice co-injected with cancer cell and wild type BMDM.

      We are grateful to Reviewer #2 for their very helpful comments and suggestions, which we believe have greatly enhanced the clarity and reproducibility of this manuscript.

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

      Review for Knudsen-Clark et al.

      "Circadian rhythms of macrophages are altered by the acidic pH of the tumor microenvironment"

      Knudsen-Clark and colleagues explore the impact of TME alterations on macrophage circadian rhythms. The authors find that both acidic pH and lactate modulate circadian rhythms which alter macrophage phenotype. Importantly, they define circadian disruption of tumor-associated macrophages within the TME and show that circadian disruption in macrophages promotes tumor growth using a PDAC line. This represents an important understanding of the crosstalk between cancer cells and immune cells as well as the understanding of how the TME disrupts circadian rhythms. The study is well-done, however, authors need to address several important points below.

      We thank Reviewer #3 for their in-depth and insightful comments and suggestions, which have resulted in a much-improved manuscript. We were pleased that Reviewer #3 found the work to be "an important study that is well-done" and that it "represents an important understanding of the crosstalk between cancer cells and immune cells as well as the understanding of how the TME disrupts circadian rhythms.". In response to Reviewer #3's comments, we have added several new key experiments and changes to the text. To summarize, we added new data to Supplementary Figure 1 to better characterize our macrophage polarization states, showed in Figure 3 that low pH affects peritoneal macrophage circadian gene expression in a similar fashion as bone marrow-derived macrophages, added new data in Figure 4 to show how lactate and low pH affect circadian gene expression over time, and new computational analysis to Figures 6, 7, and Supplementary Figure 9 to probe circadian gene covariance from publicly available data. We also made several key additions to the Discussion to discuss the functional implications of macrophage circadian rhythm disruption by low pH and potential mechanisms of this disruption. Finally, at the request of Reviewer #3, we consolidated several existing Figures and added new data, where appropriate, to existing figures, and we worked to describe new findings succinctly.

      Major comments:

      • In Figures 3 and 4, the authors can include additional clock genes that can be run by qPCR. This was done in Figure 2 and was a nice addition to the data.

      We agree with Reviewer #3's suggestion that an analysis of clock gene expression at the mRNA level would enhance our data in Figures 3 and 4. To address this point, we have performed short time course experiments to assess circadian clock gene expression over time in BMDMs cultured with or without lactate at neutral or acidic pH (for Figure 4). In line with the difference in circadian rhythms of Per2-Luc levels between BMDMs cultured in the presence or absence of lactate which we observed by Lumicycle analysis, we measured changes in expression of the circadian clock genes Per2, Nr1d1, and Cry1 between macrophages cultured with 25 mM sodium-L-lactate compared to those cultured with 0 mM sodium-L-lactate at pH 6.5. We have added these data, shown below, to Figure 4, and updated the manuscript accordingly to discuss these results. Please see below for the new Figure Panel and modified text.

      "Lactate was also observed to alter expression of the circadian clock genes Per2, Cry1, and Nr1d1 over time in BMDMs cultured at pH 6.5, while having more subtle effects at pH 7.4 (Figure 4C). Notably, lactate blunted the effect of pH 6.5 on Cry1 expression, while enhancing the effect of low pH on Nr1d1 expression. In all, these data indicate that concentration of lactate similar to that present in the TME can influence circadian rhythms and circadian clock gene expression of macrophages."

      As an additional measure to address Reviewer #3's point about Figure 3 (peritoneal macrophages), we have compared expression of circadian clock genes in peritoneal macrophages cultured at neutral pH 7.4 or acidic pH 6.8 for 24 hours using a publicly available RNA-seq data set from Jiang 2021 J Immunol (GSE164697). In line with previous observations in macrophages cultured under acidic compared to neutral pH conditions, including the clock gene expression data from Figure 2 in BMDMs and the Per2-Luc levels observed in peritoneal macrophages in Figure 3, we found that peritoneal macrophages exhibited differences in expression of circadian clock genes when cultured at acidic pH 6.8 compared to neutral pH 7.4. We have added these data, shown below, as Figure 3B, and have updated the manuscript accordingly - please see below for the new Figure panel and modified text.

      "To test whether pH-driven changes in circadian rhythms of peritoneal macrophages were reflected at the mRNA level, we compared expression of circadian clock genes in peritoneal macrophages cultured at neutral pH 7.4 or acidic pH 6.8 for 24 hours using publicly available RNA-sequencing data [30]. In line with altered circadian rhythms observed by Lumicycle, peritoneal macrophages cultured at pH 6.8 expressed different levels of circadian clock genes than peritoneal macrophages culture at pH 7.4 (Figure 3B). The trends in changes of gene expression in peritoneal macrophages cultured at pH 6.8 matched what we observed in BMDMs, where low pH generally led to higher levels of circadian clock gene expression (Figure 2D-F). These data support our observations by LumiCycle and indicate that acidic pH drives transcriptional changes in multiple components of the circadian clock. In all, these data are evidence that pH-dependent changes in circadian rhythms are relevant to in vivo-differentiated macrophages."

      We have also updated the Methods section appropriately

      "FASTQ files from a previously published analysis of peritoneal macrophages cultured under neutral pH 7.4 or acidic pH 6.8 conditions were downloaded from NCBI GEO (accession #GSE164697) [30]."

      2) There are far too many figures with minimal data in each. Please consolidate the figures. For example, Figures 1-3 can be fully combined, Figures 4-6 can be combined, and Figures 7-8 can be combined. Additionally, it is unclear if Figure 5 needs to be in the main, it can be moved to the supplement.

      We appreciate the preference of Reviewer #3 to see some of the figures consolidated. We have combined Figures 5 and 6 into a single new Figure 5. Additionally, we have added new data from revisions to current figures to increase the amount of data in each figure and minimize the amount of new figures generated. In all, despite the large amount of new data added to the paper in response to Reviewer comments and suggestions (including additional data in Figure 4 and new Figures 6 and 8), our manuscript now contains 10 main Figures, only one more than the initial submission.

      3) The observation that conditions like pH and lactate alter macrophage phenotype and rhythmicity are important. However, macrophage phenotype via gene expression does not always correlate to function. It is important for authors to demonstrate the effect of pH or lactate on macrophage function. This can be done using co-culture assays with cancer cells. If these experiments cannot be performed, it is suggested that authors discuss these limitations and consideration in the discussion.

      Reviewer #3 correctly points out that changes in phenotype does not always correlate to changes in function. Others have shown that acidic pH and lactate can each alter macrophage phenotype, and also alter macrophage function and the ability to promote tumor growth (please see El-Kenawi 2019 Br J Cancer, Jiang 2021 J Immunol, Colegio 2014 Nature). How changes in rhythms influence macrophage function remains unknown and we agree with Reviewer #3 that this is an important future direction, We have added a section in the Discussion to facilitate the discussion of this important future direction. Please see the text below.

      "Considering our observations that conditions associated with the TME can alter circadian rhythms in macrophages, it becomes increasingly important to understand the relevance of macrophage rhythms to their function in tumors. It has been shown that acidic pH and lactate can each drive functional polarization of macrophages toward a phenotype that promotes tumor growth, with acidic pH modulating phagocytosis and suppressing inflammatory cytokine secretion and cytotoxicity[28, 30, 93]. However, how the changes in circadian rhythms of macrophages driven by these conditions contributes to their altered function remains unknown. Current evidence suggests that circadian rhythms confer a time-of-day-dependency on macrophage function by gating the macrophage response to inflammatory stimuli based on time-of-day. As such, responses to inflammatory stimuli such as LPS or bacteria are heightened during the active phase while the inflammatory response is suppressed during the inactive phase. An important future direction will be to determine how changes in circadian rhythms of macrophages, such as those observed under acidic pH or high lactate, influences the circadian gating of their function."

      4) On line 119-122, authors describe a method for polarization of macrophages. They then reference one gene to confirm each macrophage polarization state. To more definitively corroborate proper macrophage polarization, authors should perform qPCR for additional target genes that are associated with each phenotype. For example, Socs3, CD68, or CD80 for M1, and CD163 or VEGF for M2. Alternatively, the authors should cite previous literature validating this in vitro polarization model.

      We appreciate Reviewer #3's suggestion to better the phenotypic identity of our polarization models with additional canonical markers. To address this point, we have expanded our panel using transcriptional markers commonly used in the murine polarization model for M1 macrophages such as Tnfa, Il6, and Il1b. As discussed in the response to Reviewer #1's minor point 5 and Reviewer #2's major point 2, we have also expanded our panel to include additional markers for M2 such as Vegf, Retnla, Ym1, Mgl1, and CD206. We have added these new data to Supplementary Figure 1. Finally, we have added additional citations for the in vitro polarization models. Please see the modified text and new data, below.

      "As macrophages are a phenotypically heterogeneous population in the TME, we first sought to understand whether diversity in macrophage phenotype could translate to diversity in circadian rhythms of macrophages. To this end, we used two well-established in vitro polarization models to study distinct macrophage phenotypes[5, 60-63]. For a model of pro-inflammatory macrophages, we stimulated macrophages with IFNγ (interferon γ) and LPS (lipopolysaccharide) to elicit a pro-inflammatory phenotype[60, 64]. These macrophages are often referred to as 'M1' and are broadly viewed as anti-tumorigenic, and we will refer to them throughout this paper as pro-inflammatory macrophages[65, 66]. For a model at the opposite end of the phenotypic spectrum, we stimulated macrophages with IL-4 and IL-13[60, 67]. While these type 2 stimuli play a role in the response to parasites and allergy, they are also major drivers of wound healing; in line with this, IL-4 and IL-13-stimulated macrophages have been well-characterized to adopt gene expression profiles associated with wound-healing and anti-inflammatory macrophage phenotypes[68-71]. As such, these macrophages are often used as a model to study pro-tumorigenic macrophages in vitro and are often referred to as 'M2' macrophages; throughout this paper, we will refer to IL-4 and IL-13-stimulated macrophages as pro-resolution macrophages[66, 72, 73]. Consistent with previous studies, we found that genes associated with anti-inflammatory and pro-resolution programming characteristic of IL-4 and IL-13-stimulated macrophages such as Arg1, Retnla, Chil3 (Ym1), Clec10a (MGL1), and Mrc1 (CD206) were induced in IL-4 and IL-13-stimulated macrophages, but not IFNγ and LPS-stimulated macrophages. In contrast, genes associated with pro-inflammatory activity characteristic of IFNγ and LPS-stimulated macrophages such as Nos2 (iNOS), Tnfa, Il1b, and Il6 were induced in IFNγ and LPS-stimulated macrophages, but not IL-4 and IL-13-stimulated macrophages (Supplementary Figure 1)[28, 30, 65, 71, 74, 75]. This indicates that macrophages stimulated with IL-4 and IL-13 were polarized toward a pro-resolution phenotype, while macrophages stimulated with IFNγ and LPS were polarized toward a pro-inflammatory phenotype.

      5) Several portions of the manuscript are unnecessarily long, including the intro and discussion. Please consolidate the text. The results section is also very lengthy, please consider consolidation.

      We appreciate Reviewer #3's preference for a shorter manuscript. The revised manuscript, in response to the many Reviewer comments and requests, contains many new pieces of data, and we have taken care to describe these new data as briefly and simply as possible. In preparation for this Revision, we also removed and shortened several sections of the Results and Discussion where we felt extra explanation was not necessary. We will work with the editor of the journal we submit to ensure the length of the manuscript sections is compliant with the journal's guidelines.

      6) The authors find that macrophage phenotype impacts rhythmicity. However, there is no mechanistic understanding of why this occurs. The authors should provide some mechanistic insight on this topic in the discussion.

      We agree with Reviewer #3 that while the mechanism by which macrophage phenotype alters rhythms remains unknown, this is an important topic of discussion. While there is some literature on how circadian rhythms modulate inflammatory response (and hints at how it may influence phenotype) in macrophages, there is very little on the converse: how phenotype may influence circadian rhythms. We address this point by expanding on our Discussion - please see the modified text below.

      "Elucidating the role of circadian rhythms in regulation of macrophage biology necessitates a better understanding of the crosstalk between phenotype and circadian rhythms. Although lactate polarizes macrophages toward a pro-resolution phenotype similar to acidic pH[30, 93], exposure to lactate had different effects on circadian rhythms - and in some cases, circadian clock gene expression - than exposure to acidic pH (Figure 4). Sensing of lactate occurs through different pathways than acid-sensing, which may contribute to the different ways in which these two stimuli modulate circadian rhythms of macrophages[111]. One previously published finding that may offer mechanistic insight into how phenotype can influence circadian rhythms is the suppression of Bmal1 by LPS-inducible miR-155[54]. It has also been observed that RORα-mediated activation of Bmal1 transcription is enhanced by PPARγ co-activation[112]. In macrophages, PPARγ expression is induced upon stimulation with IL-4 and plays a key role in alternative activation of macrophages, promoting a pro-resolution macrophage phenotype, and supporting resolution of inflammation[113-115]. Such observations prompt the question of whether there are yet-unidentified factors induced downstream of various polarizing stimuli that can modulate expression of circadian genes at the transcriptional and protein levels. Further work is required to understand the interplay between macrophage phenotype and circadian rhythms."

      7) The data presented in Figure 9 is very intriguing and arguably the strongest aspect of the paper. To strengthen the point, the authors could repeat this experiment with an additional cell model, another PDAC line or a different cancer line.

      We appreciate Reviewer #3's comment about the impact of tumor growth data. Indeed, our finding that deletion of Bmal1 in co-injected macrophages accelerated PDAC growth has been recapitulate by others in different cancer models. This lends strength to our observations. We discuss and cite complementary work on macrophage rhythms and tumor growth in other models of cancer the Discussion, please see below.

      "Data from our lab and others suggest that disruption of the macrophage-intrinsic circadian clock accelerates tumor growth, indicating that circadian regulation of macrophages is tumor-suppressive in models of PDAC (our work) and melanoma [109]. This agrees with complementary findings that behavioral disruption of circadian rhythms in mice (through chronic jetlag) disrupts tumor macrophage circadian rhythms and accelerates tumor growth[56]."

      Minor Comments:

      1) Data is Figure 2 is interesting and the impact on circadian rhythms is clear based on changes in amplitude and period. However, though the impact on period and amplitude is clear from Figures 2A-C, the changes in circadian gene expression are less clear. For instance, though amplitude is up in 2B, amplitude is suppressed in 2C. However, that does not appear to be reflected in the gene expression data in Figures 2E and F. The authors should comment on this.

      Reviewer #3 correctly points out that there appear to be discrepancies between the LumiCycle data in Figure 2 and the circadian gene expression data in Figure 2. This discrepancy is perhaps unsurprising given that the gene expression data is only a short time course over 12 hours, while the LumiCycle data are collected over a course of 3 days. The gene expression data do not allow us to determine changes in period or rhythm. Another point of interest is that it's been shown that circadian regulation occurs on many different levels (transcriptional, post-transcriptional, translational, post-translational). As result of this, circadian patterns observed in gene transcripts don't always match those of their encoded proteins; just the same, circadian patterns of proteins aren't always reflected in their encoding gene transcripts (Collins 2021 Genome Res). Due to this multi-level regulation, we propose that the results of the LumiCycle analysis, which measures PER2-Luc levels, are a more robust readout of rhythms because they are further downstream of the molecular clock than transcriptional readouts. That said, observing changes at both the protein (by Lumicycle) and transcriptional level confirm that all components of the clock are altered by acidic pH, even if the way in which they are altered appears to differ. We have incorporated the points we raised above into the Results section.

      Please see the modified text below.

      "Low pH was also observed to alter the expression of the circadian clock genes Per2, Cry1, and Nr1d1 (REV-ERBα) over time across different macrophage phenotypes, confirming that multiple components of the circadian clock are altered by acidic pH (Figure 2D-F). Notably, the patterns in expression of circadian genes did not always match the patterns of PER2-Luc levels observed by LumiCycle. This is perhaps unsurprising, as circadian rhythms are regulated at multiple levels (transcriptional, post-transcriptional, translational, post-translational); as a result, circadian patterns observed in circadian proteins such as PER2-Luc do not always match those of their gene transcripts[77]."

      2) On line 156-158, authors describe damping rate. I believe the authors are trying to say that damping rate increases as the time it takes cells to desynchronize decreases and vice versa. However, this point needs to be better explained.

      We thank Reviewer #3 for bringing to our attention that this was not communicated clearly in the text. We have adjusted our explanation to be clearer. Please see the modified text below.

      "Damping of rhythms in most free-running cell populations (defined as populations cultured in the absence of external synchronizing stimuli) occurs naturally as the circadian clocks of individual cells in the population become desynchronized from each other; thus, damping can be indicative of desynchrony within a population[84]. The damping rate increases as the time it takes for rhythms to dissipate decreases; conversely, as damping rate decreases as the time it takes for rhythms to dissipate increases."

      3) Data presented in Figures 3 and 4 are different in terms of the impact of changing the pH. The source of the macrophages is different, but the authors could clarify this further.

      We thank Reviewer #3 for this comment. Our conclusion is that the impact of low pH is largely similar in Figure 3 (peritoneal macrophages) and Figure 4 (BMDMs exposed to low pH and lactate). In both Figures 3 and 4, exposure to acidic pH by culturing macrophages at pH 6.5 increased amplitude, decreased period, and increased damping rate compared to macrophages cultured at neutral pH 7.4.

      4) For heatmaps shown in Figures 7 and 8, please calculate covariance and display asterisks where P We thank Reviewer #3 for the excellent suggestion to use an additional approach to asses circadian clock status in samples by measuring co-variance in the circadian clock gene network. To address this point, we have performed weighted gene co-expression network analysis (WGCNA) to calculate covariance, as was originally performed in Chun and Fortin et al Science Advances 2022. For the samples analyzed in Figure 7 (now Figure 6), we have added these data to the figure. We have applied this analysis to a new set of human data that we analyzed and added it to the new Figure 7. Finally, for the samples analyzed in Figure 8, we have added these data as a new Supplementary Figure 9. Please see the data and modified text below.

      Figure 6

      "Weighted gene co-expression network analysis (WGCNA) has been used as an alternate approach to measure the co-variance between clock genes and thus assess bi-directional correlations among the core clock gene network in healthy tissue and tumor samples [103]. In line with the circadian disorder observed by CCD, while many bi-directional correlations among the core clock gene network were significant and apparent in wild type peritoneal macrophages, these relationships were altered or abolished within BMAL1 KO peritoneal macrophages and TAM samples, and in some cases replaced by new relationships (Figure 6E). This indicates that there is population-level disorder in the circadian rhythms of tumor-associated macrophages in murine lung cancer."

      Figure 7

      "We next assessed the status of the circadian clock in human TAMs from NSCLC patients. We performed CCD with publicly available RNA-seq data of tumor-adjacent macrophages and tumor-associated macrophages from NSCLC patients, using alveolar macrophages from healthy donors as a control[104, 105]. To assess the contribution of the acidic TME to circadian disorder, we subset TAM NSCLC patient samples into groups (Crem high TAMs and Crem low TAMs) based on median Crem expression. Notably, in macrophages from human NSCLC there was a trend toward disorder in Crem low but not Crem high TAM samples (Figure 7A,B). Additionally, the co-variance among core clock genes observed in alveolar macrophages from healthy donors was absent within Crem low and Crem high TAM samples (Figure 7C). In all, these data indicate that there is population-level disorder in the circadian rhythms of tumor-associated macrophages in humans and mice, suggesting that circadian rhythms are indeed altered in macrophages within the TME."

      Supplementary Figure 9

      "CCD score worsened as populations became increasingly desynchronized, with the 12hr desynchronized population having a significantly worse CCD score than synchronized, homogenous macrophage population (Figure 8C). This indicates that as circadian rhythms of individual macrophages within a population become more different from each other, circadian disorder increases at the population-level. This is further supported by WGCNA, which revealed that the significant co-variance of circadian clock genes in the synchronized population was progressively altered and lost as the population is increasing desynchronized to 12 hours (Supplementary Figure 9)."

      Reviewer #3 (Significance (Required)):

      This is an important study that is well-done. It is the feeling of the reviewer that the study warrants a revision, at the discretion of the editor. The study represents an important understanding of the crosstalk between cancer cells and immune cells as well as the understanding of how the TME disrupts circadian rhythms.

      We thank Reviewer #3 for their comments regarding the impact and significance of our work. As shown by the comments above, we are confident we have fully addressed each of the points that were made to result in a much-improved revised manuscript.




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      Referee #3

      Evidence, reproducibility and clarity

      Review for Knudsen-Clark et al. "Circadian rhythms of macrophages are altered by the acidic pH of the tumor microenvironment"

      Knudsen-Clark and colleagues explore the impact of TME alterations on macrophage circadian rhythms. The authors find that both acidic pH and lactate modulate circadian rhythms which alter macrophage phenotype. Importantly, they define circadian disruption of tumor-associated macrophages within the TME and show that circadian disruption in macrophages promotes tumor growth using a PDAC line. This represents an important understanding of the crosstalk between cancer cells and immune cells as well as the understanding of how the TME disrupts circadian rhythms. The study is well-done, however, authors need to address several important points below.

      Major comments:

      1. In Figures 3 and 4, the authors can include additional clock genes that can be run by qPCR. This was done in Figure 2 and was a nice addition to the data.
      2. There are far too many figures with minimal data in each. Please consolidate the figures. For example, Figures 1-3 can be fully combined, Figures 4-6 can be combined, and Figures 7-8 can be combined. Additionally, it is unclear if Figure 5 needs to be in the main, it can be moved to the supplement.
      3. The observation that conditions like pH and lactate alter macrophage phenotype and rhythmicity are important. However, macrophage phenotype via gene expression does not always correlate to function. It is important for authors to demonstrate the effect of pH or lactate on macrophage function. This can be done using co-culture assays with cancer cells. If these experiments cannot be performed, it is suggested that authors discuss these limitations and consideration in the discussion.
      4. On line 119-122, authors describe a method for polarization of macrophages. They then reference one gene to confirm each macrophage polarization state. To more definitively corroborate proper macrophage polarization, authors should perform qPCR for additional target genes that are associated with each phenotype. For example, Socs3, CD68, or CD80 for M1, and CD163 or VEGF for M2. Alternatively, the authors should cite previous literature validating this in vitro polarization model.
      5. Several portions of the manuscript are unnecessarily long, including the intro and discussion. Please consolidate the text. The results section is also very lengthy, please consider consolidation.
      6. The authors find that macrophage phenotype impacts rhythmicity. However, there is no mechanistic understanding of why this occurs. The authors should provide some mechanistic insight on this topic in the discussion.
      7. The data presented in Figure 9 is very intriguing and arguably the strongest aspect of the paper. To strengthen the point, the authors could repeat this experiment with an additional cell model, another PDAC line or a different cancer line.

      Minor Comments:

      1. Data is Figure 2 is interesting and the impact on circadian rhythms is clear based on changes in amplitude and period. However, though the impact on period and amplitude is clear from Figures 2A-C, the changes in circadian gene expression are less clear. For instance, though amplitude is up in 2B, amplitude is suppressed in 2C. However, that does not appear to be reflected in the gene expression data in Figures 2E and F. The authors should comment on this.
      2. On line 156-158, authors describe damping rate. I believe the authors are trying to say that damping rate increases as the time it takes cells to desynchronize decreases and vice versa. However, this point needs to be better explained.
      3. Data presented in Figures 3 and 4 are different in terms of the impact of changing the pH. The source of the macrophages is different, but the authors could clarify this further.
      4. For heatmaps shown in Figures 7 and 8, please calculate covariance and display asterisks where P < 0.001. This will more clearly demonstrate the loss of co-variance between the clock network as a result of clock disruption, the TME, and cell desynchrony.

      Significance

      This is an important study that is well-done. It is the feeling of the reviewer that the study warrants a revision, at the discretion of the editor. The study represents an important understanding of the crosstalk between cancer cells and immune cells as well as the understanding of how the TME disrupts circadian rhythms.

    3. 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

      Knudsen-Clark et al. showed that the circadian rhythm of bone marrow-derived macrophages (BMDM) can be affected by polarization stimuli, pH of the microenvironment, and by the presence of sodium-lactate. Mechanistically, the acidic pH of cell microenvironment is partly regulated by intracellular cAMP-mediated signaling events in BMDM. The authors also showed that the circadian clock of peritoneal macrophages is also modified by the pH of the cell microenvironment. Using publicly available data, the authors showed that the circadian rhythm of tumor-associated macrophages is similar to that of Bmal1-KO peritoneal macrophages. In a murine model of pancreatic cancer, the authors showed that the tumor growth is accelerated in C57BL/6 mice co-injected with cancer cells and Bmal1-KO BMDM as compared to mice co-injected with cancer cell and wild type BMDM.

      Major points of criticism: 1. Nine main figures include different experimental models on a non-systematic manner in the manuscript, and only literature-based correlation is used to link the results each other. The authors used in vitro BMDM and peritoneal cell-based model systems to study the effects of IL4+IL13, IFN+LPS, low pH, sodium-lactate, adenylate cyclase inhibitors on the circadian clock of macrophages. The link between these microenvironment conditions of the cells is still correlative with the tumor microenvironment: publicly available data were used to correlate the increased expression level of cAMP-activated signaling events with the presence of acidic pH of tumor microenvironment. Notably, the cell signaling messenger molecule cAMP is produced by not only low extracellular pH by activated GPCRs, but also starvation of the cell. The starvation is also relevant to this study, since the BMDM used in the in vitro culture system were starving for 24 hours before the measurement of Per2-Luc expression to monitor circadian rhythm. 2. The definition of pre-resolution macrophages (MF) used across the manuscript could be argued. The authors defined BMDM polarized with IL-4 and IL-13 as pre-resolution MF. Resolution is followed by inflammation, but the IL-4 secretion does not occur in every inflammatory setting. Moreover, IL-4 and IL-13 are secreted during specific tissue environment and immunological settings involving type 2 inflammation or during germinal center reactions of the lymph nodes. • What are the characteristics of pre-resolution macrophages (MF)? The authors indicated that IL-4 and IL-13 cytokines were used to model the pre-resolution macrophages. In which pathological context are these cytokines produced and induce pre-resolution macrophages? IL-4 polarized BMDM can also produce pro-inflammatory protein and lipid mediators as compared to LPS-stimulated BMDM, and IL-4 polarized BMDM still have potent capacity to recruit immune cells and to establish type 2 inflammation. • The authors showed Arg1 and Vegfa qPCR data from BMDM only. Based on the literature, these MFs are anti-inflammatory cells particularly. Resolution-related MFs followed by acute inflammation are a specific subset of MFs, and the phenotype of pre-resolution MF should be described, referred, and measured specifically. 3. The authors used IFN and LPS, or IL-4 and IL-13 and co-treatments to polarize BMDM in to type 1 (referred as pro-inflammatory MF) and type 2 (referred as pre-resolution MF) activation state. The comparison between these BMDM populations has limitations, since LPS induces a potent inflammatory response in MF. The single treatment with MF-polarizing cytokines enable a more relevant comparison to study the circadian clock in classically and alternatively activated MF. 4. There are missing links between the results of showing the circadian rhythm of polarized BMDM, sodium-lactate treated BMDM, and tumor growth. Specifically, do the used pancreatic ductal adenocarcinoma cells produce IL-4 and sodium-lactate? In the LLC-based experimental in silico analysis of tumors, the LLC do not produce IL-4. 5. How can the circadian rhythm affect the function of BMDM? The Authors should provide evidence that circadian rhythm affects the function of polarized MF. 6. In Figure 3, the authors show data from peritoneal cells. The isolated peritoneal cells are not pure macrophage populations. Based on the referred article in the manuscript, the peritoneal cavity contains more then 50% of lymphocytes, and the myeloid compartment contains 80% macrophages. 7. The figure legend of Figure 3 describes the effects of pH on the circadian rhythm of bone marrow-derived macrophages ex vivo. Peritoneal macrophages involve tissue resident peritoneal macrophages with yolk sac and fetal liver origin, and also involve small peritoneal MF with bone marrow origin. The altered description of results and figure legends makes confusion. 8. In Figure 6C, one single Western blot is shown with any quantification. The authors should provide data of the relative protein level of p-CREB from at least 3 independent experiments. In the Western-blot part of the methods, the authors described that the pellet was discarded after cell lysis. The p-CREB is the activated form of the transcription factor CREB and there is increased binding to the chromatin to regulate gene expression. By discarding the pellet after cell lysis, the chromatin-bond p-CREB could be also removed at the same time. 9. It is confusing that adenylate-cyclase inhibitor MDL-12 elevated the phospho-CREB levels in BMDM. How can the authors exclude any other inducers of CREB phosphorylation? 10. It is described in the methods that BMDM were starving for 24 hours in serum-free culture media followed by serum shock (50% FBS). The cAMP production can be induced during cell starvation which should be considered for the data representation. 11. How can the authors explain and prove that the wild type and Bmal1-KO BMDM co-injected with pancreatic cancer cells subcutaneously survive, present, and have effector functions at the same extent in the subcutaneous tissue, before and during tumor growth (Figure 9)? In other words, what kind of MF-derived parameters could be modified by disrupting the circadian rhythm of MF during tumor development? The production of MF-derived regulatory enzymes, cytokines, growth factors are affected by the disrupted circadian clock in MF?

      Minor points of criticism: 1. The figure legends of the graphs and diagrams are missing in Figure 2D,E,F 2. The BMAL1-based in vivo murine model of circadian rhythm is not introduced in the manuscript.

      Significance

      Knudsen-Clark et al. showed that the circadian rhythm of bone marrow-derived macrophages (BMDM) can be affected by polarization stimuli, pH of the microenvironment, and by the presence of sodium-lactate. Mechanistically, the acidic pH of cell microenvironment is partly regulated by intracellular cAMP-mediated signaling events in BMDM. The authors also showed that the circadian clock of peritoneal macrophages is also modified by the pH of the cell microenvironment. Using publicly available data, the authors showed that the circadian rhythm of tumor-associated macrophages is similar to that of Bmal1-KO peritoneal macrophages. In a murine model of pancreatic cancer, the authors showed that the tumor growth is accelerated in C57BL/6 mice co-injected with cancer cells and Bmal1-KO BMDM as compared to mice co-injected with cancer cell and wild type BMDM.

      Major points of criticism:

      1. Nine main figures include different experimental models on a non-systematic manner in the manuscript, and only literature-based correlation is used to link the results each other. The authors used in vitro BMDM and peritoneal cell-based model systems to study the effects of IL4+IL13, IFN+LPS, low pH, sodium-lactate, adenylate cyclase inhibitors on the circadian clock of macrophages. The link between these microenvironment conditions of the cells is still correlative with the tumor microenvironment: publicly available data were used to correlate the increased expression level of cAMP-activated signaling events with the presence of acidic pH of tumor microenvironment. Notably, the cell signaling messenger molecule cAMP is produced by not only low extracellular pH by activated GPCRs, but also starvation of the cell. The starvation is also relevant to this study, since the BMDM used in the in vitro culture system were starving for 24 hours before the measurement of Per2-Luc expression to monitor circadian rhythm.
      2. The definition of pre-resolution macrophages (MF) used across the manuscript could be argued. The authors defined BMDM polarized with IL-4 and IL-13 as pre-resolution MF. Resolution is followed by inflammation, but the IL-4 secretion does not occur in every inflammatory setting. Moreover, IL-4 and IL-13 are secreted during specific tissue environment and immunological settings involving type 2 inflammation or during germinal center reactions of the lymph nodes.
        • What are the characteristics of pre-resolution macrophages (MF)? The authors indicated that IL-4 and IL-13 cytokines were used to model the pre-resolution macrophages. In which pathological context are these cytokines produced and induce pre-resolution macrophages? IL-4 polarized BMDM can also produce pro-inflammatory protein and lipid mediators as compared to LPS-stimulated BMDM, and IL-4 polarized BMDM still have potent capacity to recruit immune cells and to establish type 2 inflammation.
        • The authors showed Arg1 and Vegfa qPCR data from BMDM only. Based on the literature, these MFs are anti-inflammatory cells particularly. Resolution-related MFs followed by acute inflammation are a specific subset of MFs, and the phenotype of pre-resolution MF should be described, referred, and measured specifically.
      3. The authors used IFN and LPS, or IL-4 and IL-13 and co-treatments to polarize BMDM in to type 1 (referred as pro-inflammatory MF) and type 2 (referred as pre-resolution MF) activation state. The comparison between these BMDM populations has limitations, since LPS induces a potent inflammatory response in MF. The single treatment with MF-polarizing cytokines enable a more relevant comparison to study the circadian clock in classically and alternatively activated MF.
      4. There are missing links between the results of showing the circadian rhythm of polarized BMDM, sodium-lactate treated BMDM, and tumor growth. Specifically, do the used pancreatic ductal adenocarcinoma cells produce IL-4 and sodium-lactate? In the LLC-based experimental in silico analysis of tumors, the LLC do not produce IL-4.
      5. How can the circadian rhythm affect the function of BMDM? The Authors should provide evidence that circadian rhythm affects the function of polarized MF.
      6. In Figure 3, the authors show data from peritoneal cells. The isolated peritoneal cells are not pure macrophage populations. Based on the referred article in the manuscript, the peritoneal cavity contains more then 50% of lymphocytes, and the myeloid compartment contains 80% macrophages.
      7. The figure legend of Figure 3 describes the effects of pH on the circadian rhythm of bone marrow-derived macrophages ex vivo. Peritoneal macrophages involve tissue resident peritoneal macrophages with yolk sac and fetal liver origin, and also involve small peritoneal MF with bone marrow origin. The altered description of results and figure legends makes confusion.
      8. In Figure 6C, one single Western blot is shown with any quantification. The authors should provide data of the relative protein level of p-CREB from at least 3 independent experiments. In the Western-blot part of the methods, the authors described that the pellet was discarded after cell lysis. The p-CREB is the activated form of the transcription factor CREB and there is increased binding to the chromatin to regulate gene expression. By discarding the pellet after cell lysis, the chromatin-bond p-CREB could be also removed at the same time.
      9. It is confusing that adenylate-cyclase inhibitor MDL-12 elevated the phospho-CREB levels in BMDM. How can the authors exclude any other inducers of CREB phosphorylation?
      10. It is described in the methods that BMDM were starving for 24 hours in serum-free culture media followed by serum shock (50% FBS). The cAMP production can be induced during cell starvation which should be considered for the data representation.
      11. How can the authors explain and prove that the wild type and Bmal1-KO BMDM co-injected with pancreatic cancer cells subcutaneously survive, present, and have effector functions at the same extent in the subcutaneous tissue, before and during tumor growth (Figure 9)? In other words, what kind of MF-derived parameters could be modified by disrupting the circadian rhythm of MF during tumor development? The production of MF-derived regulatory enzymes, cytokines, growth factors are affected by the disrupted circadian clock in MF?

      Minor points of criticism:

      1. The figure legends of the graphs and diagrams are missing in Figure 2D,E,F
      2. The BMAL1-based in vivo murine model of circadian rhythm is not introduced in the manuscript.