- Mar 2023
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The Kim et al. paper titled "PRMT5 links lipid metabolism to contractile function of skeletal muscles" reports how the arginine methyltransferase PRMT5 affects lipid metabolism in myofibers by stabilizing the mSREBP1 protein and repressing the expression of the PNPLA2 gene. The genetic deletion of PRMT5 in muscle results in the loss of lipid droplets in myofibers and a loss in muscle strength. Additionally, there is a change in muscle fiber types, moving from an oxidative state to a more glycolytic one. While the authors present compelling data on PRMT5's role in muscle metabolism, there are some concerns on the mouse model used and the sequencing data.
Major concerns:
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The mouse model used in this study is PRMT5fl/fl , Myl1cre in order to genetically delete PRMT5 in skeletal muscle. While there is no issue with the KO mice, the WT mice are PRMT5fl/fl , Myl1+ which is not an acceptable control. It is known that Cre itself can have a phenotype, and additionally Myl1 is very highly expressed. Thereby, there is a large amount of Cre in the KO mice, but none in the WT which may contribute to the differences seen between WT and KO mice. The appropriate WT control is PRMT5+/+ Myl1cre and the experiments would need to be repeated using this mouse genotype as the WT.
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We appreciated the comment and have analyzed many mice from the various control groups (WT, Myl1Cre, Prmt5f/f, and Myl1Cre/Prmt5f/+). Long story short, we have maintained and used Myl1Cre for multiple projects and in several previous publications (PMID: 25794679; PMID: 27644105), and never observed a phenotype of the Myl1Cre In the current study during the development of the Myl1Cre-Prmt5KO mouse model, we had to first breed Myl1Cre with Prmt5f/f to generate the Myl1Cre/Prmt5f/+ mice, and then breed Myl1Cre/Prmt5f/+ with Prmt5f/fmice to generate the Myl1Cre/Prmt5f/f mice. During the breeding we had generated many Myl1Cre/Prmt5f/+ mice (at least 10). We only observed phenotypes in the Myl1Cre/Prmt5f/f mice but not in the Myl1Cre/Prmt5f/+ (heterozygous KO) mice. In line with our observation, no phenotypes were described in the original report on the generation of the Myl1Cre mice by Steve J. Burden and his colleagues (Bothe, Genesis, 2000, PMID: 10686620). Also, in consistent to our choice of the floxed mice as control, Pereira et al (EMBO Molecular Medicine, 2020, PMC7005622 ) used the Ndufsf/+/Myl1Cre-/- or Ndufsf/f/Myl1Cre-/- as control for their Ndufs3f/f/Myl1Cre+/- KO mice.
- Given the situation, we trust that the reviewer will agree that the Prmt5f/f mice are appropriate controls and repeating all the experiments with a new control model will not only require years of work but also violate IACUC’s and NIH’s 3R policy in reducing unnecessary use of animals. We added a sentence to state that the Prmt5f/f are phenotypically identical to Myl1Cre/Prmt5f/+ mice in the revised manuscript.
In the scRNA-Seq the authors claim that PRMT5 is not expressed in quiescent muscle stem cells. However, the data set that is used only has approximately 250 muscle stem cells, which would not provide much coverage. It would be necessary to validate this claim by using other data sets, such as Tabula Muris or publicly available bulk RNA-Seq.
- As suggested, we queried Tabula Muris on Prmt5 expression in skeletal muscles based on scRNA-seq. The results showed that Prmt5 is expressed at very low levels in various mononuclear cell populations in the skeletal muscle. Specifically, only 8% of satellite cells had detectable levels of Prmt5, while 92% satellite cells had no detectable levels of Prmt5 (Table 1). We included the results in the revised Supplemental Table S1.
The ChIP-Seq data shown was performed on 3T3-L1 cells and is not appropriate for a muscle paper. The ChIP-Seq must be performed on muscle cells in order to confirm their conclusion.
- We trust that the reviewer understand that ChIP-seq only represents a discovery tool that needs to be experimentally validated. Although the ChIP-Seq data and identification of the PRMT5 binding peak at the Pnpla2 gene was based on 3T3-L1 cells, we have validated enrichment of PRMT5 on the potential binding region through ChIP-qPCR experiments. Repeating the ChIP-seq on muscle cells will not add additional support to the conclusion.
The authors claim that loss of PRMT5 leads to a gradual loss of muscle fiber size but has no effect on myogenesis. The evidence to support that claim is shallow, being based solely on CSA and total number of myofibers, along with a loss of lean body mass. To confirm this statement, it would be best to quantify the CSA and # of myofibers in EDL and TA at P7 and P21. Further, a regeneration assay would also demonstrate if myogenesis is compromised or not.
- Thank you for this suggestion. As Myl1Cre is only expressed in post-differentiation myocytes and myofibers (Bi et al, 2016, eLife, PMID: 27644105), we do not expect the Myl1Cre/Prmt5f/f to impact muscle development. Nevertheless, we now provide data on analysis of muscles at P7 and P21, as well postnatal muscle regeneration. The results are included in Supplementary Fig S2.
The data presented shows that there is fiber type switch from oxidative to glycolytic, along with a decrease in muscle strength in the PRMT5 KO mice. This seems counterintuitive to what is known in the field as glycolytic fibers are viewed as being capable of generating more force than oxidative, while having less endurance. The authors should clarify this point and elaborate more on their conclusion that the loss of strength is due to an altered metabolism.
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We agree with the reviewer that an increased abundance of glycolytic myofibers should increase muscle force under normal conditions. However, the increased glycolytic fibers in the Prmt5 mKO mice is associated with metabolic deficiencies. These fibers are atrophic (smaller than control fibers of the same myosin type), devoid of lipid droplets and had less force production. We added the following sentences to the discussion in this matter. Minor concerns:
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The term myocyte is not the most accurate word for describing skeletal muscle. Myofibers would be best for fully differentiated muscle, myotubes for in vitro differentiation and myocytes should be reserved for differentiated cells that have not fused yet (1-2 nuclei/cell). I would recommend changing all mentions of myocyte to myofiber and changing "myocyte specific" with regards to the mouse models as "skeletal muscle specific"
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Thank you for your suggestion. We updated the nomenclature accordingly.
Figure 1 Panel F and G would be clearer if they were labelled as 2 months old mice
We edited the Figure 1F, and 1G to include the mouse age. 3. Figure 2 Panel E, G and H the control line appears to be missing error bars
Error bars were in the original panels, but the variation was very small, making it hard to visualize the error bars. 4. Figure 2 legend should specify that these mice are 2 months old for the sake of clarity
We added mouse age to the Figure 2 legend. 5. Figure 3 Panel G and H are not informative and are misleading. The supplemental panels show that when normalized to body mass there is no difference in O2 consumption or CO2 production. These should be replaced with the supplemental panels
We reformatted the figure as suggested.
Figure 4 Panel E and F, are these separate experiments? The values do not match between the 2 panels. If these are separate it should be made more clear. a. Error bars appear to be missing in Panel E
Error bars were included (as it was obvious after FCCP) but the error bars are small for the rest of the time points. b. As this is an experiment where the state of the cell is incredibly important (metabolism of myoblast is much different to myotube), the authors must demonstrate that there is no defect in in vitro differentiation by showing the fusion index assay for these cells and a representative image of the myotubes.
The differentiation of the KO cells was normal as Myl1cre is only expressed after differentiation. we isolated myoblasts from WT and Prmt5MKO mice and differentiated for 3 days to stain MyoG and MF20 to measure fusion index. However, we did not see any change in fusion index from differentiated myotubes (Supplementary Fig. S4A)
c.The authors should mention in the legend that these are 3 DM myotubes
Figure legends are updated.
- Figure 5 Panel G, a qPCR to confirm the O/E of the PRMT5 and SREBP1a in the test samples would be necessary.
We added the PRMT5 and SREBP1 O/E data (Supplementary Fig S5C, D). a. The double O/E cells are marked as significantly different, but it is unclear to which group they are significantly different to.
We edited the figure to highlight the comparison. 8. Figure 7 Panel B, body weight would be more informative in g rather than percentage.
We reformatted the figure as suggested.
It would be interesting to test whether the KO of Pnpla2 also rescues the fiber type switch.
We added Fiber type staining in dKO muscles. Based on quantification in Sol and EDL muscles, increased Type IIB (glycolytic myofibers) in Prmt5MKO mice was significantly decreased in Prmt5/Pnpla2MKO mice (Supplementary Fig S6D-F).
Reviewer #1 (Significance (Required)):
Overall the manuscript provides insight into the role of PRMT5 in regulating the metabolism of skeletal muscle. While the paper provides some interesting data, it is severely hampered by the improper WT controls lacking the cre alleles. In order for the data to be reliable, all of the WT samples will need to be replaced with PRMT5+/+ Myl1 cre mice. There are other papers looking at the role of PRMT5 in skeletal muscle, however these are more focused on muscle stem cells than the myofibers. Therefore this paper does fill in a gap with regards to the metabolic role of PRMT5 and how this can affect skeletal muscle function. This paper would most likely be of interest to a specialized audience, mostly those in the skeletal muscle field.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In the manuscript "PRMT5 links lipid metabolism to contractile function of skeletal muscles", Kim et al., describe the role for the arginine methyl transferase PRMT5 in maintaining skeletal muscle homeostasis. The authors showed that myocyte-specific deletion of PRTM5 results in the loss of muscle mass, reduced motor-performance, a fiber type switch from oxidative to glycolytic fibers along with reduced lipid content in the myofibers. The authors reasoned that absence of PRMT5 results in reduced methylation and stability of mSREBP1 and an increase in the expression of adipose triglyceride lipase (ATGL).
Major Comments
- Experiments looking at the interaction between PRMT5 and mSREBP1a using overexpressed proteins are used to conclude that PRMT5 methylates SREBP1a. While the results are consistent with these conclusions, the finding remains correlative. Methylation assays using purified PRMT5 and SREBP1a would be required to make a definite conclusion that PRMT5 methylates SREBP1a. These should be performed. In the absence of such data, the authors would need to adjust their conclusions to say that in the presence of PRMT5, SREBP1a becomes methylated, and that it remains to be determined if this is directly mediated by PRMT5.
[response] We thank the reviewer for this comment and wished we could perform in vitro methylation assay to address whether SREBP1a is directly methylated by PRMT5. However, our co-author (Dr. Changdeng Hu) who is an expert of PRMT5 biochemistry unfortunately died recently, hampering the validation of SREBP1 as PRMT5 substrate. We would also like to mention that several other studies have reported SREBP1 as substrate of PRMT5 in cancer cells (Liu et al, 2016, Cancer Research, https://doi.org/10.1158/0008-5472.CAN-15-1766 ).We cited and discussed the paper in the manuscript. Our new results using enzymatic inhibitor of PRMT5 (BLL3.3) further supports that PRMT5 mediates methylation of SREBP1 (Supplementary Fig. S5A).
Stability studies in figure 5E have been performed in HEK293 cells using over-expressed proteins. While these results show that PRMT5 protects SREBP1a from degradation, the significance of this in muscle is less clear. Western blots of these proteins in C2C12 cells show that the over expression of PRMT5 does not stabilize SREBP1a (Flag) despite the appearance of increased methylation. To solidify the concept that PRMT5-dependent methylation of SREBP1 leads to its stabilization, cycloheximide experiments should be performed in myotubes generated in culture from the PRMT5mko mice. The stability of the endogenous SREBP1a gene could be monitored using antibodies.
[response] We performed that study as suggested. Consistent with the notion that PRMT5 stabilizes SREBP1, we found extremely low levels of SREBP1 proteins (nearly undetectable) in Prmt5 KO myotubes, in contrast to the robust expression of SREBP1 in WT myotubes (Supplementary Fig. S5B). This extremely low levels of SREBP1 precludes us from examining degradation after cycloheximide treatment
The measurement of methylation levels of SREBP1a are complicated by the fact that the protein levels are destabilized in the absence of PRMT5. The authors should use a PRMT5 inhibitor experiments in complement to these overexpression studies to measure the relative methylation of mSREBP1a (SMY10/mSREBP1).
[response] We used PRMT5 inhibitor, BLL 3.3, to support that mSREBP1a methylation is mediated by PRMT5 (Supplementary Fig. S5A).
Minor Comments 4. In figure 1H, there are more nuclei surrounding the myofibers. The authors should document the number of PAX7 cells per myofiber in the Control and Prmt5MKO mouse strains as it helps understand the additive effect of change in PAX7 cells during muscle atrophy.
[response] We quantified the number of Pax7+ cells in muscles and myofibers of WT and KO mice (Supplementary S2D,E).
In figure 5, the legend title mentioned ATGL. However the stability or methylation results of ATGL are not presented anywhere in the manuscript. Only in figure 6 did the authors show the differential expression of ATGL in the presence and absence of PRMT5. This title for Figure 5 should corrected.
[response] Thanks for clarifying. We fixed title of Figure 5 in the manuscript.
For better representation, the authors should consider moving the western blot panel (S3A) and lipid droplet staining data (S3E) to main figures and some of the data on force generation and body weights to supplementary. [response] We updated the figures as suggested.
Reviewer #2 (Significance (Required)):
This is an interesting manuscript that provides novel insight into the role for PRMT5 in muscle homeostasis. While previous studies have looked at the PRMT5 from a transcriptional standpoint during muscle differentiation, this work shows a role for PRMT5 in controlling the metabolic state of myofibers through transcriptional and potentially non-transcriptional mechanisms. Identification of the transcriptional regulation of Pnpla2 gene by PRMT5 is confirmed by mouse rescue experiments with the double KO mice. However the role for non-transcriptional control of SREBP1a stability through methylation by PRMT5 is not as clearly established. To strengthen this aspect of the manuscript, additional experiments are needed.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The lipid droplets represent an energy store and central hub of lipid metabolism in cells. In the skeletal muscle, abundant lipid droplets are present in myofibers (especially in oxidative Type 1 and IIA myofibers) and thought to play a role in supplying energy through fatty acid oxidation (FAO) to power muscle contraction. Increased abundance of lipid droplets in myofibers is associated with poor muscle function and insulin resistance in patients of type 2 diabetes. Paradoxically, myofibers of trained athletes also contain higher than normal levels of lipid droplets but with better contractile function and insulin sensitivity. The molecular mechanism underlying this "Athlete's Paradox" has been unclear, due to the lack of understanding of what controls biogenesis and metabolism of lipid droplets in the myofiber.
In this manuscript, Kuang and colleague provide compelling evidence to support a key role of PRMT5 in maintaining lipid droplets in the myofiber. They generated a conditional knockout mouse model to disrupt the Prmt5 gene in the myofibers. This leads to an astonishing depletion of lipid droplets in myofibers. The Prmt5 null myofibers also exhibited poor contractile function and classical signs of atrophy. To determine if the depletion of lipid droplets drives muscle atrophy or if muscle atrophy drives depletion of lipid droplets, the authors introduced a secondary lesion (ATGL-KO) in the Prmt5 null myofibers that would preserve the lipid droplets by preventing ATGL-mediated lipolysis. This restored lipid droplet content and largely rescued muscle contractile function, demonstrating that depletion of lipid droplets drives muscle atrophy and impairs muscle contractile function. The authors also performed a series of biochemical and molecular biology assays to show that PRMT5 stabilizes SREBP1a through dimethylation, enhancing the activity of this master transcriptional regulator of de novo lipogenesis. PRMT5 also methylates H4R3, and the methylated H4R3 represses the transcription of Pnpla2 (ATGL - which controls lipolysis), therefore inhibiting degradation of lipid droplets. These results together illustrate the dual role of PRMT5 in promoting lipid biogenesis and inhibiting lipid droplet degradation.
Reviewer #3 (Significance (Required)):
Collectively, this study identify PRMT5 as a key regulator of lipid metabolism in the muscle and establish a causal relationship between lipid droplet and muscle contractile function, and point to scarce lipid droplets as a driver of muscle atrophy. PRMT5 has previously been reported to regulate early myogenesis but its role in post-fusion myofibers has never been reported, therefore the conceptual novelty of this study is high. There are couple of minor points authors should consider: 1) While muscle-specific Prmt5-KO mice show reduced muscle mass, it is not clear whether this is a developmental effect or muscle atrophy. Authors should measure a few markers of muscle atrophy such as Atrogin1 and MuRF1 and overall levels of ubiquitination. Alternatively, authors can also subject the mice to conditions of muscle atrophy such as starvation and measure how various markers of atrophy are affected.
[response] Thank you for this suggestion. As the Myl1Cre is only expressed in post-differentiation myocytes and myotubes/myofibers, we did see any developmental defects during postnatal myogenesis (Supplementary Fig S2A-C). We also checked Atrogin-1 and MuRF1 in WT and KO muscle tissues based on your advice, but we did not find any significant difference (Supplementary Fig S1F). These two genes are muscle-specific E3 ubiquitin ligases involved in protein degradation by the ubiquitin proteasome pathway. This finding is consistent with the idea that there are multiple mechanisms that can lead to muscle atrophy, and our study clearly elaborates that dysregulation of lipid catabolism by PRMT5 is the main pathway associated with muscle wasting.
2) Please show representative EcoMRI images for body composition analysis.
[response] Thank you for your comments, but the EcoMRI equipment does not provide images of body composition. It only provides data of lean mass, fat mass and water in gram. We presented those data in the manuscript.
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Referee #3
Evidence, reproducibility and clarity
The lipid droplets represent an energy store and central hub of lipid metabolism in cells. In the skeletal muscle, abundant lipid droplets are present in myofibers (especially in oxidative Type 1 and IIA myofibers) and thought to play a role in supplying energy through fatty acid oxidation (FAO) to power muscle contraction. Increased abundance of lipid droplets in myofibers is associated with poor muscle function and insulin resistance in patients of type 2 diabetes. Paradoxically, myofibers of trained athletes also contain higher than normal levels of lipid droplets but with better contractile function and insulin sensitivity. The molecular mechanism underlying this "Athlete's Paradox" has been unclear, due to the lack of understanding of what controls biogenesis and metabolism of lipid droplets in the myofiber.
In this manuscript, Kuang and colleague provide compelling evidence to support a key role of PRMT5 in maintaining lipid droplets in the myofiber. They generated a conditional knockout mouse model to disrupt the Prmt5 gene in the myofibers. This leads to an astonishing depletion of lipid droplets in myofibers. The Prmt5 null myofibers also exhibited poor contractile function and classical signs of atrophy. To determine if the depletion of lipid droplets drives muscle atrophy or if muscle atrophy drives depletion of lipid droplets, the authors introduced a secondary lesion (ATGL-KO) in the Prmt5 null myofibers that would preserve the lipid droplets by preventing ATGL-mediated lipolysis. This restored lipid droplet content and largely rescued muscle contractile function, demonstrating that depletion of lipid droplets drives muscle atrophy and impairs muscle contractile function. The authors also performed a series of biochemical and molecular biology assays to show that PRMT5 stabilizes SREBP1a through dimethylation, enhancing the activity of this master transcriptional regulator of de novo lipogenesis. PRMT5 also methylates H4R3, and the methylated H4R3 represses the transcription of Pnpla2 (ATGL - which controls lipolysis), therefore inhibiting degradation of lipid droplets. These results together illustrate the dual role of PRMT5 in promoting lipid biogenesis and inhibiting lipid droplet degradation.
Significance
Collectively, this study identify PRMT5 as a key regulator of lipid metabolism in the muscle and establish a causal relationship between lipid droplet and muscle contractile function, and point to scarce lipid droplets as a driver of muscle atrophy. PRMT5 has previously been reported to regulate early myogenesis but its role in post-fusion myofibers has never been reported, therefore the conceptual novelty of this study is high.
There are couple of minor points authors should consider:
- While muscle-specific Prmt5-KO mice show reduced muscle mass, it is not clear whether this is a developmental effect or muscle atrophy. Authors should measure a few markers of muscle atrophy such as Atrogin1 and MuRF1 and overall levels of ubiquitination. Alternatively, authors can also subject the mice to conditions of muscle atrophy such as starvation and measure how various markers of atrophy are affected.
- Please show representative EcoMRI images for body composition analysis.
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Referee #2
Evidence, reproducibility and clarity
In the manuscript "PRMT5 links lipid metabolism to contractile function of skeletal muscles", Kim et al., describe the role for the arginine methyl transferase PRMT5 in maintaining skeletal muscle homeostasis. The authors showed that myocyte-specific deletion of PRTM5 results in the loss of muscle mass, reduced motor-performance, a fiber type switch from oxidative to glycolytic fibers along with reduced lipid content in the myofibers. The authors reasoned that absence of PRMT5 results in reduced methylation and stability of mSREBP1 and an increase in the expression of adipose triglyceride lipase (ATGL).
Major Comments
- Experiments looking at the interaction between PRMT5 and mSREBP1a using overexpressed proteins are used to conclude that PRMT5 methylates SREBP1a. While the results are consistent with these conclusions, the finding remains correlative. Methylation assays using purified PRMT5 and SREBP1a would be required to make a definite conclusion that PRMT5 methylates SREBP1a. These should be performed. In the absence of such data, the authors would need to adjust their conclusions to say that in the presence of PRMT5, SREBP1a becomes methylated, and that it remains to be determined if this is directly mediated by PRMT5.
- Stability studies in figure 5E have been performed in HEK293 cells using over-expressed proteins. While these results show that PRMT5 protects SREBP1a from degradation, the significance of this in muscle is less clear. Western blots of these proteins in C2C12 cells show that the over expression of PRMT5 does not stabilize SREBP1a (Flag) despite the appearance of increased methylation. To solidify the concept that PRMT5-dependent methylation of SREBP1 leads to its stabilization, cycloheximide experiments should be performed in myotubes generated in culture from the PRMT5mko mice. The stability of the endogenous SREBP1a gene could be monitored using antibodies.
- The measurement of methylation levels of SREBP1a are complicated by the fact that the protein levels are destabilized in the absence of PRMT5. The authors should use a PRMT5 inhibitor experiments in complement to these overexpression studies to measure the relative methylation of mSREBP1a (SMY10/mSREBP1).
Minor Comments
- In figure 1H, there are more nuclei surrounding the myofibers. The authors should document the number of PAX7 cells per myofiber in the Control and Prmt5MKO mouse strains as it helps understand the additive effect of change in PAX7 cells during muscle atrophy.
- In figure 5, the legend title mentioned ATGL. However the stability or methylation results of ATGL are not presented anywhere in the manuscript. Only in figure 6 did the authors show the differential expression of ATGL in the presence and absence of PRMT5. This title for Figure 5 should corrected.
- For better representation, the authors should consider moving the western blot panel (S3A) and lipid droplet staining data (S3E) to main figures and some of the data on force generation and body weights to supplementary.
Significance
This is an interesting manuscript that provides novel insight into the role for PRMT5 in muscle homeostasis. While previous studies have looked at the PRMT5 from a transcriptional standpoint during muscle differentiation, this work shows a role for PRMT5 in controlling the metabolic state of myofibers through transcriptional and potentially non-transcriptional mechanisms. Identification of the transcriptional regulation of Pnpla2 gene by PRMT5 is confirmed by mouse rescue experiments with the double KO mice. However the role for non-transcriptional control of SREBP1a stability through methylation by PRMT5 is not as clearly established. To strengthen this aspect of the manuscript, additional experiments are needed.
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Referee #1
Evidence, reproducibility and clarity
The Kim et al. paper titled "PRMT5 links lipid metabolism to contractile function of skeletal muscles" reports how the arginine methyltransferase PRMT5 affects lipid metabolism in myofibers by stabilizing the mSREBP1 protein and repressing the expression of the PNPLA2 gene. The genetic deletion of PRMT5 in muscle results in the loss of lipid droplets in myofibers and a loss in muscle strength. Additionally, there is a change in muscle fiber types, moving from an oxidative state to a more glycolytic one. While the authors present compelling data on PRMT5's role in muscle metabolism, there are some concerns on the mouse model used and the sequencing data.
Major concerns:
- The mouse model used in this study is PRMT5fl/fl , Myl1cre in order to genetically delete PRMT5 in skeletal muscle. While there is no issue with the KO mice, the WT mice are PRMT5fl/fl , Myl1+ which is not an acceptable control. It is known that Cre itself can have a phenotype, and additionally Myl1 is very highly expressed. Thereby, there is a large amount of Cre in the KO mice, but none in the WT which may contribute to the differences seen between WT and KO mice. The appropriate WT control is PRMT5+/+ Myl1cre and the experiments would need to be repeated using this mouse genotype as the WT.
- In the scRNA-Seq the authors claim that PRMT5 is not expressed in quiescent muscle stem cells. However, the data set that is used only has approximately 250 muscle stem cells, which would not provide much coverage. It would be necessary to validate this claim by using other data sets, such as Tabula Muris or publicly available bulk RNA-Seq.
- The ChIP-Seq data shown was performed on 3T3-L1 cells and is not appropriate for a muscle paper. The ChIP-Seq must be performed on muscle cells in order to confirm their conclusion.
- The authors claim that loss of PRMT5 leads to a gradual loss of muscle fiber size but has no effect on myogenesis. The evidence to support that claim is shallow, being based solely on CSA and total number of myofibers, along with a loss of lean body mass. To confirm this statement, it would be best to quantify the CSA and # of myofibers in EDL and TA at P7 and P21. Further, a regeneration assay would also demonstrate if myogenesis is compromised or not.
- The data presented shows that there is fiber type switch from oxidative to glycolytic, along with a decrease in muscle strength in the PRMT5 KO mice. This seems counterintuitive to what is known in the field as glycolytic fibers are viewed as being capable of generating more force than oxidative, while having less endurance. The authors should clarify this point and elaborate more on their conclusion that the loss of strength is due to an altered metabolism.
Minor concerns:
- The term myocyte is not the most accurate word for describing skeletal muscle. Myofibers would be best for fully differentiated muscle, myotubes for in vitro differentiation and myocytes should be reserved for differentiated cells that have not fused yet (1-2 nuclei/cell). I would recommend changing all mentions of myocyte to myofiber and changing "myocyte specific" with regards to the mouse models as "skeletal muscle specific"
- Figure 1 Panel F and G would be clearer if they were labelled as 2 months old mice
- Figure 2 Panel E, G and H the control line appears to be missing error bars
- Figure 2 legend should specify that these mice are 2 months old for the sake of clarity
- Figure 3 Panel G and H are not informative and are misleading. The supplemental panels show that when normalized to body mass there is no difference in O2 consumption or CO2 production. These should be replaced with the supplemental panels
- Figure 4 Panel E and F, are these separate experiments? The values do not match between the 2 panels. If these are separate it should be made more clear.
- a. Error bars appear to be missing in Panel E
- b. As this is an experiment where the state of the cell is incredibly important (metabolism of myoblast is much different to myotube), the authors must demonstrate that there is no defect in in vitro differentiation by showing the fusion index assay for these cells and a representative image of the myotubes.
- c. The authors should mention in the legend that these are 3 DM myotubes
- Figure 5 Panel G, a qPCR to confirm the O/E of the PRMT5 and SREBP1a in the test samples would be necessary.
- a. The double O/E cells are marked as significantly different, but it is unclear to which group they are significantly different to.
- Figure 7 Panel B, body weight would be more informative in g rather than percentage.
- It would be interesting to test whether the KO of Pnpla2 also rescues the fiber type switch.
Significance
Overall the manuscript provides insight into the role of PRMT5 in regulating the metabolism of skeletal muscle. While the paper provides some interesting data, it is severely hampered by the improper WT controls lacking the cre alleles. In order for the data to be reliable, all of the WT samples will need to be replaced with PRMT5+/+ Myl1 cre mice. There are other papers looking at the role of PRMT5 in skeletal muscle, however these are more focused on muscle stem cells than the myofibers. Therefore this paper does fill in a gap with regards to the metabolic role of PRMT5 and how this can affect skeletal muscle function. This paper would most likely be of interest to a specialized audience, mostly those in the skeletal muscle field.
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Reply to the reviewers
1. General Statements [optional]
We thank the reviewers for their comments and very helpful suggestions to improve the manuscript. All the reviewers address that further confirmation of the causality of activity-induced AMPK activation and AMPK-induced mitochondrial fission and mitophagy regulating dendritic outgrowth in immature neurons would strengthen the significance of this study. We believe that this is the first study demonstrating that AMPK mediates activity-dependent dendritic outgrowth of immature neurons, and that regulation of mitophagy is critical for dendrite development.
We can perform most of the experimentations and corrections requested by the reviewers. We have already made several revisions and are currently working on additional experiments. All experiments will be finished in several weeks and we expect to submit a full revision by the due date.
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 #1-1.- MMP alone is not a good indicator of mitochondrial health. For instance, ATPase inhibitor causes increase in MMP and complex I inhibition diminish MMP and in both cases mitochondrial function is impaired. On the other hand, authors use increased flickering and mitochondrial ROS production as an indicator of enhanced respiration but they could also be used as indicators of mitochondrial dysfunction. Other assays, such as oxygen consumption, are needed to assess the mitochondrial function.”
*Related comments by Reviewer #2-C. In figure 6 it is unclear what is the significance of the TMRM "flickering" parameter quantified and the difference between the control and knockdown condition is small on average. *
Increase in TMRM flickering and mitochondrial ROS production, which we used as indicators of enhanced mitochondrial respiration, can certainly also be caused by mitochondrial dysfunction. We think it difficult to adopt an oxygen consumption assay in our system, as the transfection efficiency in the primary hippocampal culture is low (~10%). Instead, we plan to assess the mitochondrial function in control and AMPK deficient cells by using an ATP FRET sensor targeted to mitochondria (Mito-ATeam, Imamura et al., PNAS, 2009; Yoshida et al., Methods Mol Biol 2017). Mito-ATeam will be transfected in neurons to compare mitochondrial ATP synthesis in control and AMPK deficient neurons.
*Reviewer #1-2.- It would be interesting to show a better characterization of the mitophagy flux and to test whether pharmacological or genetic stimulation of mitophagy could revert the effect of AMPK KD on dendritic outgrowth, ultimately linking AMPK, mitophagy and dendritic outgrowth. The latter experiments may be challenging but not impossible, for example see (PMID: 27760312). *
We understand that it is important to demonstrate more strongly the correlation of the AMPK-induced peripheral fission and subsequent mitophagy of fragmented mitochondria with dendritic outgrowth. We will attempt the suggested experiment to see if induction of autophagy could revert the dendritic hypoplasia by AMPK KD. However, because AMPK deficiency generates elongated mitochondria defective in fission rather than fragmented mitochondria that are failed to undergo mitophagy, we doubt that activating mitophagy will properly remove damaged mitochondria.
In parallel to the above experiments, we currently analyze if inhibition of mitochondrial fission or mitophagy would phenocopy the hypoplastic dendrites of AMPK-deficient neurons, and if the activation of fission would rescue the phenotypes of AMPK KD, to strengthen the causality of AMPK-dependent fission, autophagy and dendrite outgrowth. So far we have observed that inhibition of mitochondrial fission by MFF knockdown or inhibition of autophagy by bafilomycin treatment strongly suppress dendrite outgrowth. MFF knockdown also leads to the elongation of mitochondria with decreased association of p62-puncta, strikingly reminiscent of AMPK-deficient neurons. Please see attached figures. Completed analyses will be included in the full revision.
*Reviewer #1-4.- Results clearly indicate that AMPK enhances mitochondrial fission, and that AMPK is necessary for proper dendritic outgrowth. However, as indicated, the role of AMPK-dependent mitochondrial fission in promoting dendritic growth is not well demonstrated. A possible, and not very difficult experiment, would be the expression of non-phosphorylable MFF S155/172 mutant (perhaps is also needed to knock down the endogenous MFF). Use of this mutant would abolish AMPK-dependent mitochondrial fission while preserving its other functions. *
Related comments by Reviewer #3-3. The authors could further confirm the claim by examining how mutations in Mff and ULK2 which cannot be phosphorylated by AMPK can rescue defects in mitochondrial fission and spine density.
We will examine if the expression of non-phosphorylable MFF S155/172 mutant would cause defective autophagy and dendritic arbor growth similarly to AMPK KD neurons. In addition, we will test whether MFF S155/172 mutant would inhibit activity-induced mitochondrial fission to strengthen the link between activity-AMPK-MFF-autophagy axis and dendritic outgrowth.
*Reviewer #1-Minor 2.- It is intriguing that as shown in Fig. 2A, rather than an increase in pAMPK/AMPK at DIV5 seems there is less phosphorylation despite FRET analysis indicate more AMPK activation. On the other hand, most of the blots in Fig. 6 seem to be overexposed. *
The exposure time of WB in Fig. 2A was adjusted so that all lanes can be compared. We will fix the exposure time.
Reviewer#2-A. Most of the evidence on the role of AMPKa2 relies on a shRNA-based strategy. The authors have performed this approach with the best practice, including selecting 2 shRNA plasmids for each gene, and performing a rescue experiment with shRNA -resistant cDNA. Yet, it is critical to provide stronger evidence with all the tools available to demonstrate the role of AMPKa2 in dendritic development. This is especially important because the effect reported by the authors is a transient effect: indeed, dendritic development appears abnormal in very young neurons (P5) but largely normal afterwards (P10). Hence one cannot discard a non specific effect on cell viability or sampling effect. The number of neurons counted is fairly low (about 30 neurons per condition) and it is not clear if they come from several independent cultures. It is known that plasmid preparation can impact cell viability and performing the experiment with only one batch of plasmid prep could explain why one plasmid would produce a short-lived effect on cell morphology. Two shRNA constructs are presented in figure S2A but only one is used for morphological experiments quantified in S2D-E with again a very low N number. The specific experiments I would recommend would be to increase the N: at least 25-30 neurons counted per culture, 3 independent cultures, and presenting the results of the two shRNA plasmids for both AMPKa1 and AMPKa2. Furthermore, the immunofluorescence validation of knockdown provided in figure S2B is not really convincing, a nuclear marker is lacking to determine where cells are (it seems that many cells are present in the image, maybe some of them with low AMPKa2 expression as well). A quantification should be provided as well as evidence for shRNA #1 and #2. *
*
We thank the reviewer for valuable suggestions to improve our manuscript. All the knockdown analyses were done from three independent experiments using different mouse litters and multiple batches of plasmid prep. N number was low because of a low transfection efficiency in the primary culture. We will repeat experiments and increase the sample number. We will also present results of the two shRNA constructs. We will redo the immunofluorescence for validation of shRNA knockdown and replace Extended Data Fig. 2B which was pointed out as not being clear.
*Reviewer #2-C. The observation, in vivo, that dendritic development is normal at P10 is intriguing but this reconciles the observation of altered dendritic development with previous studies demonstrating that AMPK knockout has little effect on brain development, as well as previous studies (Mairet-Coello et al. Neuron 2013, Lee et al. Nat commun 2022) targeting AMPKa2 in the hippocampus of AD mouse models by in utero electroporation. This is a critical aspect of the paper and as stated in the discussion, the previous studies only looked at the end product (neuronal morphology appears normal after development) but not the process of neuronal development and maturation. The in vitro experiment offer the possibility to study dendritic development over time in the same population of neurons, either through selected time points, or through time lapse imaging. This would strengthen one of the most original aspect of this work. *
We thank the reviewer for an important suggestion. We will analyze if dendritic morphology and mitochondria would recover in later stages in culture. However, the dendritic growth defects in AMPK KD neurons are apparently more severe in culture and our preliminary results have shown that dendritic growth defects and mitochondrial elongation persist until 10DIV. We anticipate that AMPK deficiency is complemented by certain compensation mechanisms in vivo that are not present in culture, such as chemical signals or synaptic inputs from correct afferents. We will confirm the recovery of dendritic outgrowth in vivo using an AMPK alpha2 knockout mouse. We will include the results in vivo and in vitro in the revised manuscript.
* The authors use a FRET probe to witness AMPK activity, and this part raises a lot of questions. A lot of the signal matches the regularly spaced activity peaks suggesting that FRET response is a coincidence detector of calcium waves. Hence, is the FRET signal influenced by intracellular calcium concentration, or changes in pH? To address this question, the proper control would be to use a FRET biosensor with a mutated AMPK phosphorylation site and demonstrating the absence of response to calcium waves. *
We think it unlikely that the FRET probe detects calcium concentration or pH change, as its kinetics and timing are different from calcium spikes. For confirmation, we will examine a FRET probe lacking phosphorylation sites to negate that calcium waves directly activate the FRET probe.
* Also, the parameter used for quantification is a so-called "number of FRET peaks over 3 minutes" for which the biological significance is unknown. On average there are 1-2 such "peaks" in control conditions (figure 4). These peaks have low amplitude, sometimes around 0.05-0.1 of the YFP/CFP ratio, which is about what is expected even in AMPKa2 knockdown cells (figure S4C). Are there changes in the baseline of FRET signal? *
We monitor FRET at 3-5 sec intervals and is set to 3 minutes due to gradual photobleaching. Although the event frequency is 0-4 times per 3 minutes observation, it is nearly absent in AMPK KD (1 small peak in 3 cells out of 40 cells) or activity deprivation, which we consider a significant difference. We have replaced Figure 4B, 4D, 4I, 4J andExtended Data Fig.4E. The basal FRET signal is lowered in AMPK KD cells, but also varies depending on the expression level of the probe. For comparision of the results shown in Figure 4 and Extended Data Fig.4, we have changed the y-axis to the normalized FRET signal {FRET/FRETbaseline} and jRGECO signals (DF/F0) in Fig. 4F, Extended Data Fig.4C, 4D.
*
*
*Finally, given that calcium peaks and AMPK activity peaks overlap, one key observation is the continued presence of calcium peaks upon AMPKa2 knockdown in figure S4D. Yet, the scale for jRGECO1 intensity in figure S4D differs from the scale in figure 4, making it difficult to interpret. It seems that on average the delta (peak-baseline) is 2000 in wild-type cells (figure 4), compared to 500 in AMPKa2 knockdown cells, which suggests a strong reduction in calcium signal amplitude upon knockdown of AMPK. This should be clarified to demonstrate that the FRET probe peaks are really due to AMPK activity. Also, the effect of STO-609 should be added to this figure. *
We think that the presence of calcium transients in AMPK KD cells supports our conclusion that AMPK is downstream of calcium signaling. The amplitude of calcium spikes was actually lowered in AMPK KD cells. We think it is due to the reduction of the cell size and complexity in KD cells. To negate that AMPK inhibition affects calcium influx, we will examine if acute inhibition by an AMPK inhibitor will suppress only FRET signals but not calcium waves. In addition, we will monitor calcium waves and FRET signals in neurons treated with STO-609 or AICAR. STO-609 and AICAR should decrease and increase FRET signals without affecting calcium influx.
- Other comments by Reviewer #2*
- Similarly, the number of events in figure 5F-G is really low. Is a difference between 0.02 in the control group and 0.01 in the knockdown group physiologically relevant?*
Since p62 puncta contact only a small mitochondrial region, the overlap area of mitochondria with p62 in the total mitochondrial area is small. We will analyze the number of p62 puncta associated with mitochondria per unit dendritic area.
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- Lines 339-350, the authors discuss about a putative regulatory loop involving AMPK dephosphorylation. Since this part of the discussion is based on the FRET signal, the authors should consider if an alternative explanation could be the kinetics of the biosensor dephosphorylation.* We will revise Discussion to argue about alternative possibilities of dynamic oscillation of the FRET signal when we get data from the above experiments.
*In terms of significance, I would have two major criticisms. The first is that it appears that many of the findings by the authors are redundant with observations of the roles of CAMKK2-AMPK-MFF-ULK1 in AD model mice, see for example the work by Polleux (Mairet-Coello et al. Neuron 2013, Lee et al., Nat commun 2022). As said above, my opinion is that the paper should put more emphasis on the transient effect of AMPK, which would be a novel observation and, as the authors rightfully discuss, a phenotype potentially overlooked in previous studies of AMPK KO mice. The second is that many points in the discussion seem to be over reached and are not entirely supported by the data. As an example lines 298-299 "leading to mitochondrial dysfunction with low respiratory activity" (not addressed in this manuscript), lines 312-313 "multiple signatures of mitochondrial dysfunction such as reduced delta-Psi-m and ROS production" (biological significance of these parameters?), lines 332-334 "AMPK phosphorylation dynamically oscillates in dendrites, depending on Ca2+ influx and CAMKK2 activity, while it is independent of LKB1" (the authors don't study AMPK phosphorylation, and the experimental data has many limitations that need addressing), etc. *
We thank reviewer’s guidance. We think this is the first study showing AMPK function in dendritic arbor growth in immature neurons before synaptogenesis. We will rewrite the manuscript to emphasize that neuronal activity in immature neurons regulates dendrite formation via AMPK in a short time window during brain development. Discussion will be revised according to the data of the ongoing additional experiments.
Reviewer#3-1. All these studies are done in invitro neuronal culture modal with transfection of ShRNAs to Knockdown AMPK. An alternative possibility is that authors could use an AMPK Conditional Knockout mouse models Conditional deletion of (AMPKα1/α2 (AMPKα1−/−; AMPKα2F/F; Emx1-Cre) derived neurons for this study.
We showed the effect of AMPK knockdown in hippocampal neurons in culture and in vivo (Fig. 2). For validation, we also examined CRISPR interference (Extended data Fig.2). We will examine in vivo phenotypes in pyramidal neurons in AMPK alpha2 knockout mice to further validate our observation.
Description of the revisions that have already been incorporated in the transferred manuscript
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*Reviewer #1-1.- Authors use mitochondrial membrane potential (MMP), MMP flickering and mitochondrial ROS production as indicators of mitochondrial function, but this is not convincing. To analyze MMP, authors use TMRM fluorescence normalized by mitochondria area. This is not correct, using this strategy would mean that a symmetric fission would instantly double MMP and fusion would half MMP. The analysis must be made by tracing ROIs of the same surface in different mitochondria and determining TMRM fluorescence in these ROIs. *
We have reanalyzed TMRM fluorescence using the method indicated. As a result, TMRM fluorescence show a slight but significant decrease (p=0.0071) in AMPK KD cells. Extended Data Fig. 5C has been replaced accordingly. We thank the Reviewer for kind guidance!
Reviewer #1-3.- The authors treat neurons with glutamate to support the view that synaptic activity activates AMPK and promotes mitochondrial fission. However, the concentration used (100 mM) may be excitotoxic. Synaptic activity can be induced by electric field stimulation, although this require equipment that may not be available in the authors' lab. Another alternative is network disinhibition with bicuculine or to use lower concentrations of glutamate. In any case, since neurons are immature and may respond differently from mature neurons, it would be worth to verify synaptic activity by analyzing Ca2+ transients.
*Reviewer #1-Minor 3.- It is necessary more explanation about spontaneous Ca2+ transients in immature cultures. What percentage of neuros experience it? Is it synchronized? *
*Related comments by Reviewer#2-D. It is well established and thus not surprising that AMPK activity increases in response to synaptic activity. It is more surprising to witness such an effect of activity in very immature neurons, where presumably synapses are sparse and not well developed. For example dendritic segments in Figure 1E and 3A don't have dendritic spines. Western-blot and/or immunofluorescence of synaptic markers with comparison to fully mature neurons would complete figure 1 and make the case whether the reported effects are marginal or a strong driver for dendritic development and AMPK regulation. *
We thank the reviewers’ point that we failed to emphasize in the original manuscript.
We focus on AMPK function during activity-dependent dendritic outgrowth in immature neurons before the onset of synaptogenesis. It has been shown that synaptogenesis occurs in dissociated hippocampal cultures between 7-12 DIV (eg, Renger et al., Neuron 2001) and that developing dendrites at 5 DIV are activated by ambient glutamate which is spontaneously released from nearby immature axon terminals and undergo spontaneous Ca2+ transients, and this non-synaptic activity is important for dendritic outgrowth (Andreae and Burrone, Cell Rep 2015). We have observed that Ca2+ transients in individual neurons are variable in frequency and magnitude and are not synchronized in consistent with previous studies. We have performed immunofluorescence with a synaptic marker PSD95 and confirmed that dendritic spines are not yet differentiated and PSD95 is sparsely distributed along the dendritic shaft in DIV5 hippocampal neurons. We describe the nature of Ca2+ transients in the Results more clearly and provide high magnified images and immunofluorescence with a synaptic marker PSD95 of the neurons at DIV5 and DIV13 as a new Fig. 1A. We believe that this is the first indication of AMPK function in non-synaptic neuronal activity during dendritogenesis.
We have observed induction of mitochondrial fission in neurons treated with 1 µM glutamate. Extended Data Fig. 1E has been replaced accordingly. Since GABA is known to induce depolarization in immature neurons (Soriano et al., PNAS 2008), we would like to exclude bicuculine treatment from this analysis.
*Reviewer #1-5.- The statistical analysis seems appropriate, but it is confusing that sometimes non-parametric and sometimes parametric tests are used. It is not indicated which test is used to determine normality since the methods section lacks a statistical analysis section.
*
We have revised Methods and have described statistical analysis in detail.
*Reviewer #1-Minor 1.- Authors should double check the analysis shown in Fig. 1A. As it is shown, Ca2+ transients are 2-3% higher than basal, when the video shown in video 1 seem to indicate much more. *
Thank you for pointing this out. In the original version, the percentile change was erroneously measured across the entire visual field, including areas without neurons. We have replaced Fig. 1B (original Fig. 1A) with reanalyzed data in the proximal region of the apical dendrite.
*Reviewer #1-Minor 4.- It is interesting that AMPK KD in vivo impairs dendritic architecture at P5, however at P10 the defect seem to be somehow compensated. This result apparently detracts from the relevance of the findings, however last year was published a paper in which in an animal model of Huntington's disease dendritic architecture is delayed during the first week but normalizes thereafter. Despite later normalization in dendritic architecture, this early defect in maturation has effects in adulthood as pharmacological restoration of arborization during the neonatal period suppresses some phenotypes observed in adulthood (PMID: 36137051). I believe that discussing this paper would help the reader to recognize the potential relevance of the findings. *
*Related comments by Reviewer #2: Nonetheless let aside the technical concern, if their findings hold true, this is an intriguing mechanism. There are interesting parallels to be made with observations of altered morphology and excitability of neurons in Huntington's disease model mice during the first postnatal week. These changes spontaneously reverts and are undetectable in the second week (Braz et al. Science 2022). Thus, precedent suggests that indeed dendritic development can take a slow course, and this study also suggests that this is important later since normalization of abnormal excitability during the first week in HTT mice prevents some of the phenotypes later in life. Here again, an interesting parallel could be made with the known role of AMPK in synaptic loss in AD models. *
We thank the reviewers for the supportive comments. We will refer this paper and discuss about potential significance of the transient defects in early dendrite morphology in AMPK deficient neurons.
*Reviewer#2-B. The Crispr method lacks validation which should be provided somehow. The drug-based experiment relies on compound C, a notoriously non specific AMPK inhibitor (see for example Bain et al. Biochem J 2007, or Vogt et al. Cell Signal 2011). Data obtained with Compound C is hard to interpret given the number of kinases that are affected by the drug and should be removed from the manuscript. *
We have added immunofluorescence images for validation of AMPK deletion by CRISPRi (Extended Data Fig. 2F).
We think the results of Compound C treatment support our conclusion in combination with KD and CRISPRi, but will delete the results in accordance with this comment.
- Other comments by Reviewer#2*
- Figure 5A-C relies on the quantification of fission events that appear very rare (0.4 event per 20 minutes). The difference between the two groups is between 0.1 and 0.2 events on average. Since this was quantified on a fairly low number of cells (N=14), it is hard to appreciate exactly how many events have been observed and the actual physiological relevance. Furthermore individual datapoints should be added to the figure to estimate variability.*
The number of fission events was counted in mitochondria in a unit length of dendrite of similar diameter, and normalized by the number of mitochondria. The values were thus small as they represent average number of events in one mitochondrion in 20 minutes. We have replaced the Fig. 1K, 3F, 5B and 5C to show the number of fission events in mitochondria included in a unit length of dendrites of similar diameter. Individual data points have been included.
Reviewer #3-4. Authors showed activity-dependent calcium signaling controls mitochondrial homeostasis and dendritic outgrowth via AMP-activated protein kinase (AMPK) in developing hippocampal neurons do the cortical mitochondria respond the same way as the hippocampal neurons?
Thank you for the comment. As pyramidal neurons in the cerebral cortex and hippocampus are basically the same origin, it is likely that they share the same signaling. We use hippocampal neurons in this study to perform quantitative analysis of dendritic morphology in the same type of neurons. Primary cultures of cortical neurons contain multiple different cell types, making it difficult to analyze the same cell type.
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: If activity is observed in only a portion of the neurons, taking advantage of the stablished long-term live imaging protocol in the authors' lab, it would be interesting to study in the same culture whether neurons that experience spontaneous activity develop more than those that do not. *
We prefer not to carry out this analysis, as activity-dependent dendritic growth has already been well described in previous papers. It will take considerable time to observe the number of neurons for analysis of correlation between Ca2+ transients and dendrite morphology. We would like to focus our effort to demonstrate AMPK signaling during activity-dependent dendritic growth.
Reviewer#3-2. Another technical issue here, most of the experiments are carried out on Neurobasal media, which has a lot of glucose plus substitution of glutamax might be not the perfect conditions for AMPK. Authors could not obtain evidence supporting the regulation of mitochondria biogenesis by PGC1α phosphorylation and expression. This surprise me, if you could reduce the glucose concentration if might change.
We observed little or no changes in phosphorylation of PGC1alpha by enhancing or suppressing neuronal activity or AMPK activity. As mitochondrial biogenesis is very active in growing neurons, we surmise that PGC1alpha and mitochondrial biogenesis is regulated by multiple mechanisms during neuronal differentiation and AMPK activation/inhibition might not induce visible changes. We agree the reviewer that there is room to seek the conditions under which changes in PGC1alpha can be detected, but we do not see why Neurobasal plus glutamax is not suitable for this study. Multiple papers studying AMPK function in cultured neurons use similar culture media (Sample et al., Mol. Cell. Biol., 2015; Muraleedharan et al., Cell. Rep., 2020; Lee et al., Nat. Commun., 2022). We might see PGC1 phosphorylation by glucose deprivation, as it decreases glycolysis-derived ATP and thereby activates AMPK. Since we focus on AMPK activation by calcium signals, we are afraid that it would be difficult to distinguish AMPK activation by ATP deficiency or calcium signaling in glucose deficient condition. In addition, glucose deprivation would affect neuronal activity (which consumes large amount of ATP) and neuronal differentiation including dendritic outgrowth.
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Referee #3
Evidence, reproducibility and clarity
The manuscript by Hatsuda and colleagues builds on previous work from their group and others, to further investigate the activity-dependent dendritic arbor development and AMPK-dependent mitochondrial quality control. It recently been illustrated that over-activation of the CAMKK2-AMPK kinase dyad mediates synaptic loss through coordinated phosphorylation of MFF-dependent mitochondrial fission and ULK2-dependent mitophagy (Aβ42 oligomers trigger synaptic loss through CAMKK2-AMPK-dependent effectors coordinating mitochondrial fission and mitophagy). Though this is progress is modest, present study showed neuronal activity induces activation of two downstream effectors of AMPK, MFF and ULK1, which are the key regulators of mitochondrial fission and mitophagy.
Major Concerns:
- All these studies are done in invitro neuronal culture modal with transfection of ShRNAs to Knockdown AMPK. An alternative possibility is that authors could use an AMPK Conditional Knockout mouse models Conditional deletion of (AMPKα1/α2 (AMPKα1−/−; AMPKα2F/F; Emx1-Cre) derived neurons for this study.
- Another technical issue here, most of the experiments are carried out on Neurobasal media, which has a lot of glucose plus substitution of glutamax might be not the perfect conditions for AMPK. Authors could not obtain evidence supporting the regulation of mitochondria biogenesis by PGC1α phosphorylation and expression. This surprise me, if you could reduce the glucose concentration if might change.
- The authors could further confirm the claim by examining how mutations in Mff and ULK2 which cannot be phosphorylated by AMPK can rescue defects in mitochondrial fission and spine density.
- Authors showed activity-dependent calcium signaling controls mitochondrial homeostasis and dendritic outgrowth via AMP-activated protein kinase (AMPK) in developing hippocampal neurons do the cortical mitochondria respond the same way as the hippocampal neurons?
Significance
It recently been illustrated that over-activation of the CAMKK2-AMPK kinase dyad mediates synaptic loss through coordinated phosphorylation of MFF-dependent mitochondrial fission and ULK2-dependent mitophagy (Aβ42 oligomers trigger synaptic loss through CAMKK2-AMPK-dependent effectors coordinating mitochondrial fission and mitophagy). Though this is progress is modest, present study showed neuronal activity induces activation of two downstream effectors of AMPK, MFF and ULK1, which are the key regulators of mitochondrial fission and mitophagy.
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Referee #2
Evidence, reproducibility and clarity
The manuscript 'Calcium signals tune AMPK activity and mitochondrial homeostasis in dendrites of developing neurons' by Hatsuda and collaborators aims at studying the interrelationship between neuronal activity, mitochondria dynamics (ie. fusion and fission mechanisms) and dendritic development. The authors provide evidence linking activity-dependent activation of a CAMKK2-AMPK pathway and the regulation of mitochondria fission and autophagy. Based on the literature, they focus on the roles of the mitochondria fission factor MFF and the autophagy regulator ULK1, both previously known targets of AMPK.
This work parallels previous observations in the context of Alzheimer's disease and as such the discovery of a molecular link between CAMKK2-AMPK, MFF/ULK1 and the regulation of dendritic mitochondria is not surprising. The change of biological context raises interesting question although the relevance of these observations is not addressed in this manuscript.
As a general comment, the work is well structured, reads easily. Iconography and figures organization are good. Major criticisms would concern the tools used to study AMPK and challenge some of the observations, as such I believe these are essential to address to validate the findings.
Major comments
- A. Most of the evidence on the role of AMPKa2 relies on a shRNA-based strategy. The authors have performed this approach with the best practice, including selecting 2 shRNA plasmids for each gene, and performing a rescue experiment with shRNA -resistant cDNA. Yet, it is critical to provide stronger evidence with all the tools available to demonstrate the role of AMPKa2 in dendritic development. This is especially important because the effect reported by the authors is a transient effect: indeed, dendritic development appears abnormal in very young neurons (P5) but largely normal afterwards (P10). Hence one cannot discard a non specific effect on cell viability or sampling effect. The number of neurons counted is fairly low (about 30 neurons per condition) and it is not clear if they come from several independent cultures. It is known that plasmid preparation can impact cell viability and performing the experiment with only one batch of plasmid prep could explain why one plasmid would produce a short-lived effect on cell morphology. Two shRNA constructs are presented in figure S2A but only one is used for morphological experiments quantified in S2D-E with again a very low N number. The specific experiments I would recommend would be to increase the N: at least 25-30 neurons counted per culture, 3 independent cultures, and presenting the results of the two shRNA plasmids for both AMPKa1 and AMPKa2. Furthermore, the immunofluorescence validation of knockdown provided in figure S2B is not really convincing, a nuclear marker is lacking to determine where cells are (it seems that many cells are present in the image, maybe some of them with low AMPKa2 expression as well). A quantification should be provided as well as evidence for shRNA #1 and #2.
- B. To complete the shRNA-based experiments, the authors use a single cell Crispr approach, as well as a pharmacological approach. The Crispr method lacks validation which should be provided somehow. The drug-based experiment relies on compound C, a notoriously non specific AMPK inhibitor (see for example Bain et al. Biochem J 2007, or Vogt et al. Cell Signal 2011). Data obtained with Compound C is hard to interpret given the number of kinases that are affected by the drug and should be removed from the manuscript.
- C. The observation, in vivo, that dendritic development is normal at P10 is intriguing but this reconciles the observation of altered dendritic development with previous studies demonstrating that AMPK knockout has little effect on brain development, as well as previous studies (Mairet-Coello et al. Neuron 2013, Lee et al. Nat commun 2022) targeting AMPKa2 in the hippocampus of AD mouse models by in utero electroporation. This is a critical aspect of the paper and as stated in the discussion, the previous studies only looked at the end product (neuronal morphology appears normal after development) but not the process of neuronal development and maturation. The in vitro experiment offer the possibility to study dendritic development over time in the same population of neurons, either through selected time points, or through time lapse imaging. This would strengthen one of the most original aspect of this work.
- D. It is well established and thus not surprising that AMPK activity increases in response to synaptic activity. It is more surprising to witness such an effect of activity in very immature neurons, where presumably synapses are sparse and not well developed. For example dendritic segments in Figure 1E and 3A don't have dendritic spines. Western-blot and/or immunofluorescence of synaptic markers with comparison to fully mature neurons would complete figure 1 and make the case whether the reported effects are marginal or a strong driver for dendritic development and AMPK regulation. Furthermore the authors use a FRET probe to witness AMPK activity, and this part raises a lot of questions. A lot of the signal matches the regularly spaced activity peaks suggesting that FRET response is a coincidence detector of calcium waves. Hence, is the FRET signal influenced by intracellular calcium concentration, or changes in pH? To address this question, the proper control would be to use a FRET biosensor with a mutated AMPK phosphorylation site and demonstrating the absence of response to calcium waves. Also, the parameter used for quantification is a so-called "number of FRET peaks over 3 minutes" for which the biological significance is unknown. On average there are 1-2 such "peaks" in control conditions (figure 4). These peaks have low amplitude, sometimes around 0.05-0.1 of the YFP/CFP ratio, which is about what is expected even in AMPKa2 knockdown cells (figure S4C). Are there changes in the baseline of FRET signal? Finally, given that calcium peaks and AMPK activity peaks overlap, one key observation is the continued presence of calcium peaks upon AMPKa2 knockdown in figure S4D. Yet, the scale for jRGECO1 intensity in figure S4D differs from the scale in figure 4, making it difficult to interpret. It seems that on average the delta (peak-baseline) is 2000 in wild-type cells (figure 4), compared to 500 in AMPKa2 knockdown cells, which suggests a strong reduction in calcium signal amplitude upon knockdown of AMPK. This should be clarified to demonstrate that the FRET probe peaks are really due to AMPK activity. Also, the effect of STO-609 should be added to this figure.
Other comments
- A. Figure 5A-C relies on the quantification of fission events that appear very rare (0.4 event per 20 minutes). The difference between the two groups is between 0.1 and 0.2 events on average. Since this was quantified on a fairly low number of cells (N=14), it is hard to appreciate exactly how many events have been observed and the actual physiological relevance. Furthermore individual datapoints should be added to the figure to estimate variability.
- B. Similarly, the number of events in figure 5F-G is really low. Is a difference between 0.02 in the control group and 0.01 in the knockdown group physiologically relevant?
- C. In figure 6 it is unclear what is the significance of the TMRM "flickering" parameter quantified and the difference between the control and knockdown condition is small on average. Rather, the data presented in figure S5 would suggest that there is no difference in TMRM signal.
- D. Lines 339-350, the authors discuss about a putative regulatory loop involving AMPK dephosphorylation. Since this part of the discussion is based on the FRET signal, the authors should consider if an alternative explanation could be the kinetics of the biosensor dephosphorylation.
Significance
The manuscript by Hatsuda and collaborator studies the roles of neuronal AMPK in the development of hippocampal neurons, specifically the authors describe a transient effect on dendritic development. To this reviewer's opinion, this is the major findings of this paper. Although the physiological implications of this finding are unknown, this is beyond the scope of this paper.
Yet in terms of significance, I would have two major criticisms. The first is that it appears that many of the findings by the authors are redundant with observations of the roles of CAMKK2-AMPK-MFF-ULK1 in AD model mice, see for example the work by Polleux (Mairet-Coello et al. Neuron 2013, Lee et al., Nat commun 2022). As said above, my opinion is that the paper should put more emphasis on the transient effect of AMPK, which would be a novel observation and, as the authors rightfully discuss, a phenotype potentially overlooked in previous studies of AMPK KO mice. The second is that many points in the discussion seem to be over reached and are not entirely supported by the data. As an example lines 298-299 "leading to mitochondrial dysfunction with low respiratory activity" (not addressed in this manuscript), lines 312-313 "multiple signatures of mitochondrial dysfunction such as reduced delta-Psi-m and ROS production" (biological significance of these parameters?), lines 332-334 "AMPK phosphorylation dynamically oscillates in dendrites, depending on Ca2+ influx and CAMKK2 activity, while it is independent of LKB1" (the authors don't study AMPK phosphorylation, and the experimental data has many limitations that need addressing), etc.
Nonetheless let aside the technical concern, if their findings hold true, this is an intriguing mechanism. There are interesting parallels to be made with observations of altered morphology and excitability of neurons in Huntington's disease model mice during the first postnatal week. These changes spontaneously reverts and are undetectable in the second week (Braz et al. Science 2022). Thus, precedent suggests that indeed dendritic development can take a slow course, and this study also suggests that this is important later since normalization of abnormal excitability during the first week in HTT mice prevents some of the phenotypes later in life. Here again, an interesting parallel could be made with the known role of AMPK in synaptic loss in AD models.
Reviewer expertise: I have expertise in neuronal metabolism
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, Hatsuda et al study the role of synaptic activity-dependent Ca2+ signals in activating AMPK and regulating mitochondrial homeostasis and dendritic outgrowth in developing neurons. Using cultures of immature primary hippocampal neurons, the authors found that Ca2+ transients activate AMPK, which regulates mitochondrial fission and dendritic growth. AMPK KD and pharmacological manipulation of AMPK activity confirmed a role of AMPK in mitochondrial morphology that correlated with impaired mitophagy and mitochondrial function. These findings led the authors to conclude that activity-dependent activation of AMPK promotes mitochondrial fission, which facilitates removal of dysfunctional mitochondria and thus contributes to maintaining a healthy mitochondrial pool that is necessary in the intense energetic effort that requires dendritic outgrowth.
Major comments:
Meanwhile the activation of AMPK and its role in mitochondrial fission and dendritic outgrowth is in general well demonstrated, the conclusion that AMPK is necessary for proper dendritic outgrowth because by promoting asymmetric mitochondrial fission facilitates mitophagy of dysfunctional mitochondria and thus ensures adequate generation of energy for dendritic outgrowth still seems preliminary.
- Authors use mitochondrial membrane potential (MMP), MMP flickering and mitochondrial ROS production as indicators of mitochondrial function, but this is not convincing. To analyze MMP, authors use TMRM fluorescence normalized by mitochondria area. This is not correct, using this strategy would mean that a symmetric fission would instantly double MMP and fusion would half MMP. The analysis must be made by tracing ROIs of the same surface in different mitochondria and determining TMRM fluorescence in these ROIs. But even in the case that there were changes in MMP, that it does not seem to be the case, MMP alone is not a good indicator of mitochondrial health. For instance, ATPase inhibitor causes increase in MMP and complex I inhibition diminish MMP and in both cases mitochondrial function is impaired. On the other hand, authors use increased flickering and mitochondrial ROS production as an indicator of enhanced respiration but they could also be used as indicators of mitochondrial dysfunction. Other assays, such as oxygen consumption, are needed to assess the mitochondrial function.
- It would be interesting to show a better characterization of the mitophagy flux and to test whether pharmacological or genetic stimulation of mitophagy could revert the effect of AMPK KD on dendritic outgrowth, ultimately linking AMPK, mitophagy and dendritic outgrowth. The latter experiments may be challenging but not impossible, for example see (PMID: 27760312).
- The authors treat neurons with glutamate to support the view that synaptic activity activates AMPK and promotes mitochondrial fission. However, the concentration used (100 M) may be excitotoxic. Synaptic activity can be induced by electric field stimulation, although this require equipment that may not be available in the authors' lab. Another alternative is network disinhibition with bicuculine or to use lower concentrations of glutamate. In any case, since neurons are immature and may respond differently from mature neurons, it would be worth to verify synaptic activity by analyzing Ca2+ transients.
- Results clearly indicate that AMPK enhances mitochondrial fission, as previously reported, and that AMPK is necessary for proper dendritic outgrowth. However, as indicated, the role of AMPK-dependent mitochondrial fission in promoting dendritic growth is not well demonstrated. For example, AMPK could regulate dendritic outgrowth through its role on cytoskeletal dynamics. A possible, and not very difficult experiment, would be the expression of non-phosphorylable MFF S155/172 mutant (perhaps is also needed to knock down the endogenous MFF). Use of this mutant would abolish AMPK-dependent mitochondrial fission while preserving its other functions.
- The statistical analysis seems appropriate, but it is confusing that sometimes non-parametric and sometimes parametric tests are used. It is not indicated which test is used to determine normality since the methods section lacks a statistical analysis section.
Minor comments:
- Authors should double check the analysis shown in Fig. 1A. As it is shown, Ca2+ transients are 2-3% higher than basal, when the video shown in video 1 seem to indicate much more.
- It is intriguing that as shown in Fig. 2A, rather than an increase in pAMPK/AMPK at DIV5 seems there is less phosphorylation despite FRET analysis indicate more AMPK activation. On the other hand, most of the blots in Fig. 6 seem to be overexposed.
- It is necessary more explanation about spontaneous Ca2+ transients in immature cultures. What percentage of neuros experience it? Is it synchronized? If activity is observed in only a portion of the neurons, taking advantage of the stablished long-term live imaging protocol in the authors' lab, it would be interesting to study in the same culture whether neurons that experience spontaneous activity develop more than those that do not.
- It is interesting that AMPK KD in vivo impairs dendritic architecture at P5, however at P10 the defect seem to be somehow compensated. This result apparently detracts from the relevance of the findings, however last year was published a paper in which in an animal model of Huntington's disease dendritic architecture is delayed during the first week but normalizes thereafter. Despite later normalization in dendritic architecture, this early defect in maturation has effects in adulthood as pharmacological restoration of arborization during the neonatal period suppresses some phenotypes observed in adulthood (PMID: 36137051). I believe that discussing this paper, and others with similar message (if they exist, I do not know), would help the reader to recognize the potential relevance of the findings.
I believe that all the proposed experiments would strongly help to support the claims of the paper and are perfectly feasible during the time given for a revision and economically affordable.
Significance
As authors already cite in their work, several groups have shown that mitochondrial fission is necessary for proper dendritic growth. Here, the authors have proposed that synaptic activity in immature neurons induce mitochondrial fission via AMPK activation and subsequent MFF phosphorylation. Many of the findings here are confirmations of previous work, for instance activity-dependent activation of AMPK (PMID: 25698741, PMID: 27012879) and induction of mitochondrial fission by AMPK via MFF phosphorylation (PMID: 26816379). The novelty of the work is in studying these processes in immature neurons and how this affects dendritic growth, which is of interest for cellular neuroscientist, but I do not think it represents a conceptual breakthrough. A more detailed understanding of the mechanism proposed, i.e. mitochondrial fission facilities removal of dysfunctional mitochondria to maintain the high energy demands of growing dendrites, would greatly enhance the significance of the study.
This reviewer specializes in neuronal cell biology, specifically the study of the mechanisms by which mitochondrial function regulates aspects of neuronal physiology, including neuritic outgrowth.
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Reply to the reviewers
Point-by-point response to reviewer comments
General statement
Several studies have previously demonstrated functional links between the death receptors (DR) TRAIL-R1/2 and the Unfolded protein response (UPR). In this manuscript, we describe the previously unrecognized IRE1-dependent dual regulation of the expression of another DR, CD95, and CD95L-induced cell death. Our work therefore adds to the current knowledge on the functional links existing between UPR and DR signaling and provides novel mechanistic insights on a dual regulation involving both transcriptional and post-transcriptional control of the expression of CD95 mRNA expression by IRE1. To demonstrate this, we have used both genetic (overexpression of XBP1s or dominant-negative forms of IRE1) and pharmacologic (IRE1 RNase inhibitor) approaches and cellular models of glioblastoma (GB) and triple-negative breast cancer (TNBC). We show that IRE1 RNase activity promotes CD95 expression and CD95-mediated cell death via the transcription factor XBP1s whilst IRE1 RNase limits CD95 expression and cell death via its ability to cleave RNAs (through RIDD, for Regulated IRE1-dependent decay of RNAs, activity). Furthermore, we report that IRE1-mediated control of CD95 expression is active in vivo, using a model of CD95-mediated fulminant hepatitis in mice. Lastly, we correlate these results to the pathology by showing that CD95 expression is decreased in RIDD high or XBP1s low human GB and TNBC tumors.
We thank the reviewers for their fair assessment of our manuscript and for their insightful comments. Below, we describe the experiments we plan to carry out to address the reviewers’ comments.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): Summary: Here the authors argue that IRE1 activation has opposite effects on Fas/CD95 expression/stability in a number of contexts, via either RIDD-dependent degradation of Fas mRNA or XBP-1-mediated induction of Fas expression, which led to either increased or decreased sensitivity to Fas-induced apoptosis in a number of settings. Major issues: The study is somewhat preliminary and inconclusive in that it is not clear why the RIDD function of XBP-1 appears to predominate in vitro in the cell lines examined, leading to modest increases in Fas expression levels (Figure 1) when IRE1 DN versus IRE1 WT constructs are overexpressed, which is at odds with the latter part of the paper which suggests that inhibition of RIDD led to reduced Fas expression levels. However, this could be due to supraphysiological levels of IRE1 being expressed under overexpression conditions, leading to confounding results. Similarly, when XBP-1s is overexpressed in vitro (Figure 5) the modest increases in CD95/Fas expression and sensitization to Fas-induced cell death may not be fully representative of what would be observed at physiological levels of XBP-1s activation. The in vivo results obtained using an IRE1 RNase inhibitor (MKC8866) contradict the earlier part of the study (as Fas levels decreased and there was protection from Fas-induced liver toxicity) and this could be due to a multitude of reasons. There is no doubt that impacting on IRE1 activity has interesting effects on CD95/Fas expression, which can be up- or -down-regulated, with consequences for cell death induced via engagement of the latter receptor, however, the manuscript does not offer a lot of clarity on which outcome is the predominant one in the context of engagement of the UPR. I have the following suggestions for improvement.
We thank the reviewer for this overall positive assessment.
- The authors should induce ER stress using Thaps, Brefeldin A and Tunicamycin, and explore the effects of doing this on Fas expression levels in the context of silencing endogenous IRE1, XBP-1 and PERK.
We do agree with this reviewer that the proposed experiments might further highlight which of the IRE1-dependent control of CD95 expression dominates upon ER stress induction. Therefore, we will perform the requested experiment in the various cell lines already used in the manuscript.
We propose to evaluate the expression of CD95 (at the mRNA and total protein levels) under ER stress induction (by different ER stressors) upon knock-down of IRE1 or XBP1. Other DRs (TRAIL-R1 and 2) have been shown to be induced by PERK activation and it is also demonstrated that PERK and IRE1 signaling pathways coregulate each other. As such, we also propose to assess whether PERK could also control CD95 expression in this setting.
- The authors should explore the effects of silencing of IRE1, XBP-1 and PERK on constitutive Fas expression and the outcome of Fas/CD95-induced apoptosis in cells not experiencing an overt activation of the UPR (i.e. in the absence of Thaps, Brefeldin A or other UPR inducer).
We thank the reviewer for their suggestion and will perform the requested experiments as proposed.
- The specificity of MKC8866 at the concentration used (30 uM) is unclear. What effect does MKCC have on sensitivity towards Fas-induced apoptosis, similar to the type of experimental set up presented in Figure 5A, 5B?
Regarding the specificity of MKC8866, this drug has been optimized and refined from a family of IRE1-specific endoribonuclease inhibitors initially obtained from a chemical library screen [1-3]. This salicylaldehyde analog has already shown to be effective in multiple cancer models including breast [4, 5] and prostate [2] cancers. We have recently demonstrated its efficacy in a GB mouse model [6]. It is therefore a widely used IRE1 inhibitor, including in the dose range 10-30 mM used in this study (e.g [4, 5]). We therefore do not think it is in the scope of this manuscript to re-assess it specificity. However, we will aim at testing an additional IRE1 inhibitor to assess whether similar effects can be observed on CD95 expression in cells. To do so, we propose to use a novel IRE1 kinase inhibitor developed in the laboratory (DOI: 10.26434/chemrxiv-2022-2ld35 – Accepted iScience) and shown to efficiently blunt IRE1 activity in GB. As also suggested by the reviewer, we will assess whether the use of MKC-8866 can affect CD95L-induced cell death in cell lines.
- Similarly, what effects does MKC8866 (at 30 uM) have on key Fas pathway determinants, such as Fas, FLIPL, FLIPs, Caspase-8, FADD, RIPK1, A20, CYLD, cIAP-1, cIAP-2 and Bid? There are many points at which MKC8866 could influence the outcome of Fas receptor engagement beyond the receptor itself.
In the present manuscript, we have shown that MKC-8866 reduces CD95 expression in mouse liver (IHC depicted in Figure 4B and S3B) in vivo and that, when used at 30 mM in vitro, it prevents the loss of CD95 expression induced by tunicamycin or thapsigargin in U87 cells (Fig 1C-F). We do agree with the reviewer that IRE1 may impact CD95-induced cell death beyond modulating CD95 expression, as also already discussed in the present manuscript. Therefore, and as suggested, we will assess whether MKC-8866, used at 30 mM, also impacts on the basal cellular expression of the various components of CD95 signaling mentioned by this reviewer.
Minor issues:
- For the Fas mRNA cleavage experiments presented in Figure 2, there are no irrelevant control mRNAs to allow the reader to judge whether the effects presented are specific to Fas mRNA or are commonly observed for many mRNAs at these amounts of IRE1 (1 ug, 0.5 ug, which appear high).
The expression of Fas mRNA was already normalized to GAPDH (which does not seem to vary upon incubation with IRE1). We nevertheless will test the expression of additional “irrelevant” RNAs as suggested by the reviewer.
Reviewer #1 (Significance (Required)): General assessment: this is an interesting study, as there is little knowledge currently concerning how the UPR influences Fas expression or Fas-dependent outcomes. However, the impact of this work is limited by the overexpression approaches used, which could produce artifactual results, as well as the contradictory message of the study.
Although we think that the message of the manuscript is indeed complex, the work presented herein does not rely exclusively on overexpression approaches as our genetic-based results are also comforted by the use of pharmacologic inhibitors of IRE1.
Advance: the advance reported here is relatively modest and limited in scope due to the inconclusive nature of the data presented.
Audience: this study will be of interests to specialists in the UPR and cell death communities.
We thank the reviewer for acknowledging the overall novelty of our work. We do hope that the experiments proposed will address her/his remaining concerns.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The authors address here for the first time the connection between CD95, which is known as Fas, and ER stress. The role of another DR, TRAIL-R2 has been already reported, but this is the first study uncovering the link between Cd95 system and ER stress. The study is performed on the high level and supported by all necessary controls. They find the connection between IRE1 and CD95 and show that it might play a role in Cd95 signaling and attenuate CD95-mediated cell death.
Further, the correlation between CD95 expression and IRE is found in tumors. Importantly the authors find out the connection between XBP1 and CD95 expression, which was not reported to date. Hence, it is a very important and highly essential piece of research.
We thank the reviewer for these very positive comments and the acknowledging of the novelty and importance of our study.
However, I would like to clarify the several issues:
1: Figure 1. Tunicamycin obviously leads to deglycosylation of CD95, which is indicated by the appearance of 35 Kda band. This should be highlighted and commented.
We agree, this will be commented on in the text.
- Figure 2c, d. The piece of mRNA structure, which is synthesized, might have the different secondary structure and might be not cleaved by IRE, accordingly. More detailed comments have to be provided in this regard.
The model depicted in Figure 2B is a predicted computational secondary structure of CD95 mRNA. In the experiments performed in Figure 2A, C and D the mRNA was extracted from U87 cells prior to incubation with recombinant IRE1 and the resulting products analyzed using RT-qPCR with primers flanking different portions of the CD95 mRNA sequence. For Figures 2C and D, the primers used flank the two sites which were predicted to be cleaved by IRE1 based on previous work from our lab [7]. Even though we cannot exclude that additional sites can be targeted beyond these two, the fact that the amplification of CD95 sequence is reduced in samples pre-incubated with recombinant IRE1 strongly suggests that IRE1 is indeed able to cleave CD95 mRNA in these regions in vitro. We will modify the main text to further explain this point.
- Figure 3. Caspase-8-3 western blots show beautiful effects but did authors see some effects further downstream, eg on PARP1 cleavage? Was cell death (not viability) measured as well? Can you comment on this?
This is absolutely right, we will test PARP-1 cleavage in this setting as suggested. Given the morphology of the cells we observed in the viability experiments, we would expect a similar trend using cell death assays. However, we do agree with the reviewer that this should be proven experimentally, so we will perform these experiments again using cell death assays as a read out.
- Did the authors looked at the DISC assembly? Did they detect some differences there?
No, we did not. We would expect some difference given the impact we have observed on CD95 expression, caspase-8 activation and cell death of expressing dominant negative forms of IRE1, but this of course needs to be actually tested. We are in the process of optimizing CD95 DISC experiments in our lab and we therefore hope to be able to address this reviewer’s comment in a revised version of the manuscript.
Reviewer #2 (Significance (Required)):
This is an excellent study. The authors address here for the first time the connection between CD95, which is known as Fas, and ER stress. The role of another DR, TRAIL-R2 has been already reported, but this is the first study uncovering the link between Cd95 system and ER stress. The study is performed on the high level and supported by all necessary controls. This is an important advance for the death receptor field.
Thank you again for these very positive comments and your insightful appreciation of our work.
References
- Volkmann, K., Lucas, J. L., Vuga, D., Wang, X., Brumm, D., Stiles, C., Kriebel, D., Der-Sarkissian, A., Krishnan, K., Schweitzer, C., Liu, Z., Malyankar, U. M., Chiovitti, D., Canny, M., Durocher, D., Sicheri, F. & Patterson, J. B. (2011) Potent and selective inhibitors of the inositol-requiring enzyme 1 endoribonuclease, J Biol Chem. 286, 12743-55.
- Sheng, X., Nenseth, H. Z., Qu, S., Kuzu, O. F., Frahnow, T., Simon, L., Greene, S., Zeng, Q., Fazli, L., Rennie, P. S., Mills, I. G., Danielsen, H., Theis, F., Patterson, J. B., Jin, Y. & Saatcioglu, F. (2019) IRE1α-XBP1s pathway promotes prostate cancer by activating c-MYC signaling, Nat Commun. 10, 323.
- Langlais, T., Pelizzari-Raymundo, D., Mahdizadeh, S. J., Gouault, N., Carreaux, F., Chevet, E., Eriksson, L. A. & Guillory, X. (2021) Structural and molecular bases to IRE1 activity modulation, Biochem J. 478, 2953-2975.
- Logue, S. E., McGrath, E. P., Cleary, P., Greene, S., Mnich, K., Almanza, A., Chevet, E., Dwyer, R. M., Oommen, A., Legembre, P., Godey, F., Madden, E. C., Leuzzi, B., Obacz, J., Zeng, Q., Patterson, J. B., Jager, R., Gorman, A. M. & Samali, A. (2018) Inhibition of IRE1 RNase activity modulates the tumor cell secretome and enhances response to chemotherapy, Nat Commun. 9, 3267.
- Almanza, A., Mnich, K., Blomme, A., Robinson, C. M., Rodriguez-Blanco, G., Kierszniowska, S., McGrath, E. P., Le Gallo, M., Pilalis, E., Swinnen, J. V., Chatziioannou, A., Chevet, E., Gorman, A. M. & Samali, A. (2022) Regulated IRE1α-dependent decay (RIDD)-mediated reprograming of lipid metabolism in cancer, Nat Commun. 13, 2493.
- Le Reste, P. J., Pineau, R., Voutetakis, K., Samal, J., Jégou, G., Lhomond, S., Gorman, A. M., Samali, A., Patterson, J. B., Zeng, Q., Pandit, A., Aubry, M., Soriano, N., Etcheverry, A., Chatziioannou, A., Mosser, J., Avril, T. & Chevet, E. (2020) Local intracerebral Inhibition of IRE1 by MKC8866 sensitizes glioblastoma to irradiation/chemotherapy in vivo, 841296.
- Voutetakis, K. D., D.; Vlachavas, E-I., Leonidas, DD.; Chevet, E.; Chatzioannou, A. (In preparation) RNA sequence motif and structure in IRE1-mediated cleavage.
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Referee #2
Evidence, reproducibility and clarity
The authors address here for the first time the connection between CD95, which is known as Fas, and ER stress. The role of another DR, TRAIL-R2 has been already reported, but this is the first study uncovering the link between Cd95 system and ER stress.The study is performed on the high level and supported by all necessary controls. They find the connection between IRE1 and CD95 and show that it might play a role in Cd95 signaling and attenuate CD95-mediated cell death.
Further, the correlation between CD95 expression and IRE is found in tumors. Importantly the authors find out the connection between XBP1 and CD95 expression, which was not reported to date. Hence, it is a very important and highly essential piece of research.
However, I would like to clarify the several issues:
1: Figure 1. Tunicamycin obviously leads to deglycosylation of CD95, which is indicated by the appearance of 35 Kda band. This should be highlighted and commented. 2.Figure 2c, d. The piece of mRNA structure, which is synthesized, might have the different secondary structure and might be not cleaved by IRE, accordingly. More detailed comments have to be provided in this regard. 3. Figure 3. Caspase-8-3 western blots show beautiful effects but did authors see some effects further downstream, eg on PARP1 cleavage? Was cell death ( not viability) measured as well? Can you comment on this? 4. Did the authors looked at the DISC assembly? Did they detect some differences there?
Significance
This is an excellent study. The authors address here for the first time the connection between CD95, which is known as Fas, and ER stress. The role of another DR, TRAIL-R2 has been already reported, but this is the first study uncovering the link between Cd95 system and ER stress.The study is performed on the high level and supported by all necessary controls. This is an important advance for the death receptor field.
-
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Referee #1
Evidence, reproducibility and clarity
Summary:
Here the authors argue that IRE1 activation has opposite effects on Fas/CD95 expression/stability in a number of contexts, via either RIDD-dependent degradation of Fas mRNA or XBP-1-mediated induction of Fas expression, which led to either increased or decreased sensitivity to Fas-induced apoptosis in a number of settings.
Major issues:
The study is somewhat preliminary and inconclusive in that it is not clear why the RIDD function of XBP-1 appears to predominate in vitro in the cell lines examined, leading to modest increases in Fas expression levels (Figure 1) when IRE1 DN versus IRE1 WT constructs are overexpressed, which is at odds with the latter part of the paper which suggests that inhibition of RIDD led to reduced Fas expression levels. However, this could be due to supraphysiological levels of IRE1 being expressed under overexpression conditions, leading to confounding results. Similarly, when XBP-1s is overexpressed in vitro (Figure 5) the modest increases in CD95/Fas expression and sensitization to Fas-induced cell death may not be fully representative of what would be observed at physiological levels of XBP-1s activation. The in vivo results obtained using an IRE1 RNase inhibitor (MKC8866) contradict the earlier part of the study (as Fas levels decreased and there was protection from Fas-induced liver toxicity) and this could be due to a multitude of reasons. There is no doubt that impacting on IRE1 activity has interesting effects on CD95/Fas expression, which can be up- or -down-regulated, with consequences for cell death induced via engagement of the latter receptor, however, the manuscript does not offer a lot of clarity on which outcome is the predominant one in the context of engagement of the UPR. I have the following suggestions for improvement.
- The authors should induce ER stress using Thaps, Brefeldin A and Tunicamycin, and explore the effects of doing this on Fas expression levels in the context of silencing endogenous IRE1, XBP-1 and PERK.
- The authors should explore the effects of silencing of IRE1, XBP-1 and PERK on constitutive Fas expression and the outcome of Fas/CD95-induced apoptosis in cells not experiencing an overt activation of the UPR (i.e. in the absence of Thaps, Brefeldin A or other UPR inducer).
- The specificity of MKC8866 at the concentration used (30 uM) is unclear. What effect does MKCC have on sensitivity towards Fas-induced apoptosis, similar to the type of experimental set up presented in Figure 5A, 5B?
- Similarly, what effects does MKC8866 (at 30 uM) have on key Fas pathway determinants, such as Fas, FLIPL, FLIPs, Caspase-8, FADD, RIPK1, A20, CYLD, cIAP-1, cIAP-2 and Bid? There are many points at which MKC8866 could influence the outcome of Fas receptor engagement beyond the receptor itself
Minor issues:
- For the Fas mRNA cleavage experiments presented in Figure 2, there are no irrelevant control mRNAs to allow the reader to judge whether the effects presented are specific to Fas mRNA or are commonly observed for many mRNAs at these amounts of IRE1 (1 ug, 0.5 ug, which appear high).
Significance
General assessment: this is an interesting study, as there is little knowledge currently concerning how the UPR influences Fas expression or Fas-dependent outcomes. However, the impact of this work is limited by the overexpression approaches used, which could produce artifactual results, as well as the contradictory message of the study.
Advance: the advance reported here is relatively modest and limited in scope due to the inconclusive nature of the data presented.
Audience: this study will be of interests to specialists in the UPR and cell death communities.
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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
Overview:
This manuscript addresses the emerging nexus linking the machinery associated with clathrin endocytosis (clathrin-coated pits; CCPs), flat clathrin lattices (FCLs) and the recently discovered Reticular Adhesions (RAs). This is timely work, reflecting recent foci on the relationship between these structures and systems. Initially clearly identifying reductions in FCL and RA formation on fibronectin, the authors sought to clarify the mechanisms that suppress or prevent FCL / RA formation on this matrix. Knock-down of integrin avb5 (core RA component) suppressed both RA and FCL formation, suggesting a dependence of FCLs on this integrin. This was supported by acute avb5 inhibition via cilengitide (avb5 and avb3 inhibitor) which caused disassembly of existing RAs and FCLs.
Notably, the inverse relationship also appears true, with suppression of core clathrin endocytic machinery (AP2 complex components) being sufficient to greatly deplete RA formation. Supporting this finding, overexpression of a dominant negative-acting protein fragment (AP180 c-terminal fragment) blocked both AP2 localisation to the plasma membrane and RA formation.
To unmix this bi-directional dependence further, the authors used acute cilengitide treatment followed by washout and post-washout incubation to first deplete RAs (cillengitide) and then allow monitoring of en masse RA formation after cilengitide washout. This is an effective experiment, however, the analysis would benefit from greater depth, particularly relating to the order of events. Analysis of this aspect seems central to the thrust of the paper, and some statistical analysis of either static co-occurrence or dynamic ordering in large numbers of FCL / RA structures (i.e. hundreds) would be of value.
The authors next focused on the observation that fibronectin suppressed both FCL and RA structures, by assessing the role of fibronectin-receptor integrin b1. Acute antibody mediated integrin b1 inhibition (mab13) and integrin b1 knock down both confirmed that in cells on fibronectin, suppression of integrin b1 is sufficient to permit massive upregulation of both FCL and RA formation. This is surprising and very interesting. It raises questions about the actual ECM requirements for avb5-mediated reticular adhesion formation. It would seem that fibronectin per se can support very efficient RA / FCL formation, but that normally concurrent integrin b1 activities would suppress this. Given this implication, it would be especially important to clarify the purity of FN ECM coating (as explored in questions 1-3 below) at the time of imaging. The discussion addresses a number of topics, and proposes a mechanistic model to explain the results presented. I don't find the mechanism very convincing, as the directionality of the dependence between FCLs and RAs is not clearly delineated by the experiments presented, in my opinion. That there is co-dependence is convincingly shown, but whether there is directionality, and what order of events underpins FCL then RA or RA then FCL formation, is unclear. Nonetheless, the evidence presented does generally support the idea of a shift in the way we consider the role of endocytic machinery in adhesion regulation, from a disassembly only related function to additional functions associated with adhesion formation and maintenance. Ideally, the mechanisms around this new assembly / maintenance function would be further delineated here, but regardless, this work does point in the direction of important new questions in this area. Further discussion about the potential role of this interdependent regulatory process in, for example, mitosis, seems unwarranted and should probably be removed.
Questions:
- A technical question on the replating experiments onto specific matrix proteins; after coating surfaces with the purified ECM components or controls, what media were the cells replated in? Ideally this should be serum-free media, to ensure that the ECM components of FBS / FCS are not immediately added to the purified ECM components. This should be clarified in the methods.
- Related to above, I cannot see how long cells were plated onto the different ECM conditions. This would be relevant to know and should be clarified because cells will secrete ECM over time and thus the purity of the ECM components addressed is dependent on the length of time cells are incubated and imaged for after attachment.
- Similarly, it is noted that cells plated on 'glass' support RA formation. It should be clarified what ECM component is then actually responsible for cell adhesion and adhesion complex (RA, FA or other) formation
- since this requires an ECM component of some type. Presumably, 'on glass' means whatever ECM is either derived from the media used during cell attachment / incubation (if that media contains serum, which is vitronectin rich), or whatever ECM is secreted by the cells themselves over the attachment / incubation period prior to imaging.
- In the cilengitide washout experiments, the evidence shown in figures seems to suggest that AP2-positive FCLs form in locations where avb5 (probably RAs) are already present, whereas avb5 positive structures do not form from AP2-only structures. Statistical analysis of this pattern (i.e. which protein is present first) would be valuable to address directionality. Notably, in Figure 3G, it appears that avb5 is present and increasing prior to the subsequent arrival of AP2.
- a. I would suggest that the cilengitide experimental results(3E-G) be shown in a separate figure from the endocytosis inhibition results (3A-D).
- The integrin b1 inhibition and knock down results are clear and interesting. Clarifying the ECM components present during these experiments would be valuable to interpretation of the paper.
Significance
see above
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Referee #2
Evidence, reproducibility and clarity
Summary:
Hakanpää and colleagues report on the relationship between flat clathrin lattices (FCLs) and reticular adhesions, with FCLs being preposed to nucleate reticular adhesions. Overall the experimental work is high quality and the data are generally well presented.
Major comments:
The Introduction is very brief and doesn't cover the information required to understand the paper. There are three cellular structures to be understood: focal adhesions, reticular adhesions and FCLs. The intro jumps straight into the FCLs (the paper is written from a FCL point of view) but there is no information about the other two structures really particularly the differences between them. Furthermore, there is nothing in the intro about cellular adhesion or why this is even worth studying. The authors should fully revise this Intro, there is much room for improvement!
Fig 4D I could not understand this plot and the legend did not describe it properly. What are the units of FCL frequency? I guess it is FCLs per some distance (10µm?), the images need a scale bar. OK, I read the description in the methods and now I see it is the proportion of total CCSs that are FCLs; so frequency is the wrong term. The legend says that there were 32 videos and there are 32 points on the plot but what we need to know is: where n = 1 cell, what did the FCL frequency do over time? A line is drawn on the graph, no info on what the line is and the fit is poor (R2 < 0.5). The authors should take their series of data points from individual cells and fit curves to each and describe the summary statistics of the parameters of these fits OR average the data and fit to that, using the 1 SD of the data for weighting the fit. Probably more data is required to do any meaningful fitting here. To my eye it looks like FCL frequency goes from 0.3 to a plateau of 0.5 at 10 min and that more timepoints between 0 and 10 min would have been useful.
Fig 3F/G is a nice expt. It looks as though the ITGB5 signal is already creeping up when the AP2 arrives. I agree that they accelerate together, but the prior accumulation of integrin is at odds with the conclusion that AP2/clathrin nucleates the adhesion. This experiment is missing two controls: what is the behaviour of ITGB5 in AP2 negative regions? What happens to both signals in the continued presence of cilengitide? These controls are needed to conclude that AP2 is nucleating the adhesion.
Minor comments:
Fig 6 - several typos - "adaptor proteins" "engagement" "containing"
Significance
Previously, endocytosis (clathrin-mediated) was thought to decrease cellular adhesion by removal of integrins. This paper suggests that the same machinery can be used to build adhesions. This is a surprising conclusion that will be of interest to many cell biologists; the topic of clathrin and adhesion is being actively explored by several labs either from the adhesion or the endocytosis sides. I have been following this topic from a distance and don't know the details of all the published papers, but this paper does seem to add something new over the recent work from Taraska, Sonnenberg, Montagnac, Strömblad.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, Hakanpää et al explored the connection between flat clathrin lattices and reticular adhesions and the regulatory mechanism underlying the formation of these two structures in the U2OS cells. The author provided evidence that the composition of the extracellular matrix plays critical roles in their formation and concluded that fibronectin and its receptor, β1 integrin, inhibit the assembly of FCLs and RAs. The author depleted several components of the clathrin mediated endocytosis machinery and could show that it blocked the formation of reticular adhesions.
Major comments
- In Fig. 1, the author plated U2OS cells on surfaces coated with different ECM components and then measured the frequency of FCLs. How long were the cells allowed to attach to the surfaces before they were imaged? Were the cells serum-starved before seeding? Given the fact that cells attached well even on BSA-coated dishes, I guess the cells were allow to attach and spread for at least overnight. In this case, the ECM components (vitronectin is very abundant in the serum in a concentration of 200-400 ug/mL, fibronectin is another one) in the culture medium would coat the glass surface and this has profound effects on the adhesion status of the cells. Thus, more details of this experiment need to be included and more attention should be pay regarding the data interpretation. In Fig. 1C, it seems like the mere glass surface induced the most FCL formation. However, if the cells are grown on the glass overnight or for days, the major component of the surface would actually be vitronectin and fibronectin (maybe more) rather than glass, thus it is not accurate to say that 'VTN reduced FCL frequency to some extent compared to glass' (Line 67).
- Line 91-93. It is not accurate to claim that the reticular adhesions are the only type of cellular adhesion maintained during mitosis. In several studies, active integrin β1 are found along the retraction fibers (Dix et al, Dev Cell, 2018; Chen et al, NCB, 2022). The importance of αVβ5 integrin in the spatial memory during mitosis was only shown in the in vitro cell culture. In fact, mice lacking αVβ5 integrin or its ligand vitronectin are both viable and show no major defects during embryonic development (Zheng et al, PNAS, 1995; Huang et al, Mol Cell Biol, 2000), suggesting reticular adhesions are dispensable in cell division in vivo. I advise to change it into'RAs are composed of αVβ5 integrin and are maintained during mitosis in culture'.
- It has been shown that fibronectin and laminin coating inhibit formation of reticular adhesions (Lock et al, NCB, 2018, Fig. S7). This study should be cited in Fig. 1. I suggest to also include laminin in Fig. 1C to make the list of ECM components more complete.
- Fig. 5C, the fluorescent intensity of αVβ5 integrin is increased dramatically when integrin β1 was depleted compared to the control shRNA. Although the images were collected in the TIRF mode, it is important to measure αVβ5 and β1 integrin level by immunoblot to confirm the knockdown efficiency of β1 integrin and exclude the possibility that the increase of RA formation is not due to the compensation by upregulation of αVβ5.
- Antibody-blocking or depletion of β1 integrin both lead to accumulation of FCL and RA formation, indicating that the activation of β1 integrin is critical in the inhibition of FCL and RA. Activation of β1 integrin depends on talin and kindlin, which bind β5 integrin with a much lower affinity. Would depletion of talin or kindlin cause FCL and RA formation similar to inhibition of β1 integrin?
Minor comments
- In most of the quantifications, only the number of the cells measured were mentioned in the legend. The number of replicate experiments is missing. It should be included in the legend as well.
- A recent study (https://doi.org/10.1242/jcs.259465) demonstrated the molecular mechanism underlying the localization of αVβ5 integrin in flat clathrin lattices. It should be mentioned in the introduction.
Significance
Although it is not novel that FCLs and RAs share same localization and might actually be the different parts of the same structure (Zuidema et al, JCS, 2022), the observation that inhibiting β1 integrin stimulates FCL and RA assembly is interesting as it indicates the counter-balance between the αVβ5 and α5β1 integrins. It is a pity that the author did not dig deeper into the mechanism underlying this interesting finding, which should greatly increase the impact of this study.
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Reply to the reviewers
Reviewer 1:
We would like to thank you for taking the time to review our manuscript. Your thoughtful and insightful comments have greatly improved the quality of our work. We appreciate your thoroughness in evaluating our study and providing valuable feedback.
Your constructive criticism and suggestions have helped us identify areas that needed further clarification and improvement, and we are grateful for your efforts in guiding us towards a stronger manuscript.
Thank you again for your time and expertise in reviewing our work. We hope that you find our revisions satisfactory and look forward to hearing your thoughts on the revised manuscript.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): *
In this manuscript by Sharma and colleagues, the authors investigate the transcriptional regulation of the TAL1 isoforms - that derive from differential promoter usage and/or alternative splicing - and the contribution of TAL1 long and TAL1 short protein isoforms in normal haematopoietic development and disease.
The study suggests that TAL1 transcript isoforms are fine-tuned regulated. By using CRISPR/Cas9 techniques, the authors show that the enhancer -8 (MuTE) and enhancer -60 differentially regulate the TAL1 isoforms. Whether the remaining enhancers at the TAL1 locus (see Zhou Y et al, Blood 2013) also differentially regulate TAL1 transcription remains to be elucidated.
The authors found that TAL1 short isoform interacts strongly with T-cell specific transcription factors such as TCF3 and TCF12, as compared to TAL1 long isoform. TAL1 short shows an apoptotic transcription signature and it fails in rescuing cell growth as compared to TAL1 long in T-ALL. In addition, TAL1 short promotes erythropoiesis.
Lastly, the authors suggest that altering TAL1 long and TAL1 short protein isoforms ratio could have a potential therapeutic application in disease, but further studies are needed. *
We would like to thank you for your time and effort in reviewing our manuscript. Your constructive feedback and insightful comments have been immensely valuable in improving the quality of our work. Your expertise in the field has undoubtedly contributed to the credibility and accuracy of this research. In addition, your dedication and attention to detail have been instrumental in shaping the final version of the manuscript.
* I have a number of comments: Figure 1 It was not mentioned that MOLT4 cells also have MuTE. Do Jurkat and MOLT4 share a similar profile in terms of TAL1 transcript isoforms? It would have been very interesting to see whether the TAL1 transcript isoforms are similar in SIL-TAL1+ cells (e.g RPMI-8402). In these cells, TAL1 activation results from a deletion that fuses the 5' non-coding region of SIL with TAL1. *
Thank you for your comment. We apologize for the confusion regarding the MOLT4 cells in our analysis. We have now updated the manuscript to explicitly mention the presence of MuTE in MOLT4 cells (Line 127). Additionally, we agree that it would be interesting to investigate whether the TAL1 transcript isoforms are similar in SIL-TAL1+ cells, such as RPMI-8402. To address this point, we have included the CCRF-CEM cell line that harbors the SIL-TAL1 recombination in our analysis. We have updated the manuscript with these new findings (Fig. 1C&D and S1A&B). Thank you for bringing this to our attention.
Figure 2 * It is not very clear how the expression of the short isoform delta exon 3 is quantified. Detailed information and a schematic of the primer location could be helpful. *
Thank you for your comment. We apologize for any confusion regarding the quantification of the expression of the short isoform (delta exon 3). The detailed information and schematic of the primer location can be found in Supplementary Figure 2B. We have included the location of each primer used in real-time PCR analysis for the quantification of all TAL1 isoforms. We hope this additional information will address your concerns.
* The results on Figure 2 derive from complex Cas9/CRISPR experiments. A schematic representation showing the location of the following elements is missing: CTCF sites, CTCF gRNA target region, dCas9-p300 gRNA target region and -60 enhancer. *
We agree that providing a schematic representation of the Cas9/CRISPR experiments would be helpful for better understanding the data in Figure 2. We have now included a detailed schematic of the location of the CTCF sites, CTCF gRNA target region, dCas9-p300 gRNA target region and -60 enhancer in Supplementary Figure 2E. We believe this new figure will provide a clearer overview of the experiments performed and will aid in the interpretation of the results.
* Are the levels of dCas9-p300 WT and dCas9-p300 MUT comparable in transfected HEK 293 cells? Were those possibly measured by qPCR or Western Blot? Why the authors chose to use 293T cells for the CTCF del as the enhancer usage around the locus must be so different from haematopoietic cells. *
Thank you for your question. We have added Western Blot analysis to compare the levels of dCas9-p300 WT and dCas9-p300 MUT in transfected HEK293T cells, as suggested. The results are presented in Supp. Fig. S2H.
Regarding the choice of HEK293T cells for the CTCF deletion experiment, we selected this cell line for its low expression of TAL1, which contributes to a high dynamic range when tethering p300 core to a closed chromatin region. We have added a clarification of our rationale for using HEK293T cells in the revised manuscript (Lines 177-8). Thank you for your valuable feedback.
* Is CPT - camptothecin? A control gene that is sensitive to CPT treatment would ensure the inhibitor is working. *
Thank you for your comment. Indeed, CPT stands for camptothecin, and this information is already included in the methods section. We have also added this information to the results section (Line 221) to make it clearer.
Regarding the suggestion to use a control gene sensitive to CPT treatment, we agree that this could be a useful addition to our experimental design. To address this, we have quantified the amount of TAL1 transcript to an endogenous control which is not transcribed by RNA Polymerase II (RNAPII) (18s rRNA). As a positive control, we compared Cyclo A, our endogenous control, to 18s rRNA and observed a reduction (Supp. Fig. S2K). This allows us to confidently conclude that the inhibitor is working as intended.
Thank you for bringing up this point, and we hope that our response addresses your concern.
*
In supplementary Figure 2D, the reduction in expression in Jurkat Del-12 is restricted to TSS2. There is no reduction in TAL1 TSS1 and TAL1 TSS4 (this is not clear from the result description section). As seen, these isoforms are upregulated and that could suggest a compensatory mechanism mediated by alternative promoter activation. The fact that Jurkat Del-12 express TAL1 from MSCV-TAL1 could also suggest that TSS1 and TSS4 are upregulated by TAL1 or indirectly, by other members of the TAL/LMO complex (see Sanda T et al, Cancer Cell 2012) *
Certainly, we appreciate your feedback. Supplementary Figure 2D indeed shows that the MuTE enhancer has a differential effect on the promoters, and we have now included this in the text of the manuscript. Regarding the TAL1-long isoform, while MSCV-TAL1 in the Jurkat Del-12 cell line does give rise to this isoform, our results from Figure 3A did not find TAL1-long to have a differential effect on TAL1 promoters. It is important to note that the experiment conducted was an exogenous construct in HEK293T cells, which has its limitations. Thus, the speculation that TAL1-long drives the result in supplementary Figure 2D is possible, and we have added this to the text. Thank you for bringing up this important point (Lines 167-9).
Figure 3 * A. Are the levels of TAL1 short cDNA and TAL1 long cDNA comparable in the co-transfection luciferase experiments? The overexpression of the isoforms does not reflect the endogenous expression levels in cell lines where one of the isoforms is more predominantly expressed (e.g Jurkat cells express low levels of TAL1 short). *
Thank you for your comment. To address your concern, we have added real time (Supp. Fig. S3A) as well as Western blot in a new figure (Supp. Fig. S3B) to show that the levels of TAL1-short and TAL1-long cDNA are comparable in the co-transfection luciferase experiments. Additionally, we observed a very low amount of endogenous TAL1 isoforms in the cell line (Supp. Fig. S3A&B), which was below detection using these methods. This suggests that the effect of the endogenous TAL1 in this cell line is low. We appreciate your feedback, and we hope this additional information addresses your concern.
* Figure 4 Are the levels of flag-TAL1 long and flag-TAL1 short comparable? The levels of expression could explain the low intensity signal for TAL1 long. *
Thank you for your insightful comment. Indeed, the issue of isoform quantification is critical in understanding the functional differences between TAL1-short and TAL1-long. To address this concern, we performed careful quantification of the isoforms and made sure that the amount was equal or slightly in favor of TAL1-long before conducting the experiments in this manuscript. We have also added a Western blot in Supp. Fig. S3A and real time in Supp. Fig. S3B showing the similar amount of the two isoforms. Furthermore, in Figure 4A, we provided the amount of each isoform in the input section, showing a higher amount of TAL1-long. This strengthens our result, which shows that TAL1-short binds stronger to TCF-3 and 12. Protein levels for ChIP-seq experiment (Fig. 4B-H) is now in Supp. Fig. S4B. We thank you for bringing up this important point, and we hope that our additional data and clarifications have addressed your concern
*Is there any reason for not performing a depletion of endogenous TAL1 prior to the ChIP seq flag experiment? *
Thank you for your comment. In our experience, infecting Jurkat cells with shRNA or an expressing vector systems can induce some cellular stress, and we did not want to add additional stress to the cells by depleting endogenous TAL1. Since we immunoprecipitated using a Flag-tagged protein, we did not see a need to deplete the endogenous TAL1 protein. However, in our RNA-seq experiment, depletion of endogenous TAL1 was critical, and we have added this additional step in this experiment.
* Could the authors speculate about MAF motif enrichment in both isoforms and not in TAL1-total? *
Thank you for bringing up this interesting point. It is worth noting that while all ChIP-seq experiments were performed in Jurkat cells, not all of them were conducted by us. In particular, ChIP-seq of TAL1 total was performed by Sanda et al., 2012, using an endogenous antibody against both isoforms, whereas we conducted ChIP-seq for TAL1-short and TAL1-long using a FLAG tag antibody in cells expressing each of the isoforms. Therefore, the different conditions of these experiments may have contributed to the observed MAF motif enrichment in both isoforms and not in TAL1-total. While we cannot provide a definitive explanation, we speculate that the overexpression of the isoforms or the presence of the FLAG tag may have facilitated the detection of the MAF motif. We have added this discussion to the manuscript to acknowledge and address this interesting observation (Lines: 307-8).
- Sanda et al., Core transcriptional regulatory circuit controlled by the TAL1 complex in human T cell acute lymphoblastic leukemia. Cancer Cell 22, 209-221 (2012).
* Do TAL1 long and TAL1 short recognise the same DNA motif? *
This is indeed a very interesting question but a difficult one to answer since TAL1 does not bind to the DNA alone but in a complex. In this situation, the ChIP-seq de-novo binding results suggest motifs that could be recognized by TAL1 or any of its complex partners. Using previous data, TAL1’s binding motif is CAGNTG (Hsu et al., 1994), while this motif was not identified in our analysis of the TAL1-total or FLAG-TAL1-long ChIP-seq results, we did, however, identify this sequence in FLAG-TAL1-short ChIP-seq results (p value=1e-93). We predict that this discrepancy is due to the complex nature of transcription factors binding and the fact that the ChIP-seq results were not all done in the same way. We have now added this to the discussion (Lines: 419-25).
- L. Hsu et al., Preferred sequences for DNA recognition by the TAL1 helix-loop-helix proteins. Mol Cell Biol 14, 1256-1265 (1994).
* Figure 6 In A and B, are the levels of flag-TAL1 long and flag-TAL1 short in transduced K562 comparable? In C and D, are the TAL1 levels reduced at the protein level?*
Thank you for your question. To answer your question, we added Western Blot analysis to show the comparable levels of flag-TAL1-long and flag-TAL1-short in transduced K562 cells (Supp. Fig. S6C). In Figure 6C and D, we also added Western Blot analysis to show the reduction in TAL1 protein levels upon shRNA-mediated knockdown(Supp. Fig. S6B).
* Minor points: Figure 1 A. Include a scale bar *
To address this, we included coordinates of the components of the gene marked in the figure.
* C. Loading control such as GAPDH is missing in the Western Blot. Are CUTLL cells the same as CUTTL-1? *
We added loading controls as requested now supplementary Fig. 1C, S2C, S3A, S4B, S6B&C. Yes, CUTLL is the same as CUTLL-1 we have now fixed this in the text (Line 120).
D. Adjust scale of the CHIP seq tracks in K562 cells in order to see the peak summit. *Include genome build *
Thank you for your comment. We have adjusted the scale of the ChIP-seq tracks in K562 cells as suggested to improve the visualization of the peak summit. However, one of the peaks still had a much higher signal and the summit is still missing from this particular peak. To address this, we have added a new figure in the supp. Fig. S1C materials where we adjusted the peak to show the summit. Please note that in this track, the chromatin structure at the enhancers is missing, and therefore, we did not include it in the main figure. Thank you for bringing this to our attention.
We have added a genome build hg19 to the figure legend.
* In supplementary Figure 1B, the symbol scheme is not clear *
Thank you for this note, we have replaced the figure and added text to make it clearer.
* Figure 2 A & C. Remove 'amount' from the Y axis. Is the total mRNA amount calculated as % of the reference genes? It could be specified on the y axis or figure legend. *
We have removed the word "amount" from the Y axis as requested. Total mRNA amount is normalized relative to the reference genes (∆∆Cq) by Bio-Rad's CFX Maestro software (version 2.3) according to the formula:
where:
- RQ = Relative Quantity of a sample
- Ref = Reference target in a run that includes one or more reference targets in each sample
- GOI = Gene of interest (one target)
* In supplementary Figure 2C, a loading control is missing.*
We have added alpha-tubulin to this figure.
* Figures 4, 5 and 6 Size of the figures should be increased. *
We have increased the figure size as suggested. *
Reviewer #1 (Significance (Required)): The study from Sharma and colleagues is novel and it extends the knowledge on TAL1 regulation and the role of TAL1 in development and disease. Although the study suggests that there is a correlation between enhancers, chromatin mark deposition at exons and regulation of alternative splicing, the mechanistic link is not fully elucidated.*
To further elucidate the mechanistic link between the MuTE enhancer, broad H3K4me3 modification spanning 7.5 Kbp from TAL1 promoter 1 to promoter 5 (as shown in Fig. 1D), and alternative splicing, we conducted experiments where we manipulated KMT2B, a component of the SET1/COMPASS complexes responsible for methylating H3K4. Our findings indicate that silencing KMT2B in Jurkat cells led to a significant 30% increase in TAL1-∆Ex3 (Fig. 2H and Supp. Fig. S2I&J). These results contribute to a more comprehensive understanding of the molecular mechanisms underlying TAL1 alternative splicing regulation.
The findings on TAL1 short protein are interesting but the data on TAL1 long lacks some refinement so then robust conclusions can be drawn. * The experimental data lacks a few controls. The text is clear and prior studies could be better referenced. *
We have made an effort to better reference out manuscript.
* As TAL1 is a very crucial transcription factor oncogene in T-ALL, the study is important as it addresses a very relevant question in the field that is the regulation of the transcription of TAL1 and the functional relevance of both TAL1 short and TAL1 long isoforms. *
Reviewer 2: *
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: Sharma et al. thoroughly characterized the regulation of TAL1 by mapping the use of its five promoters and enhancers, which together transcribe five transcripts, coding for two protein isoforms. For that purpose the authors used few cell lines: Jurkat as a T-ALL cell line, chronic myeloid leukemia (CML) cell line K562 and HEK293T with low TAL1 expression, as well as CutLL and MOLT4. They profiled the chromatin marks H3K27ac and H3K4me3 at the TAL1 locus, and show that when a the -8 enhancer is compromised tha chromatin marks change, and not only the expression level of TAL1 is reduced, the level of exon 3 skipping is increased. When the -60 enhancr was activated, TAL1 expression increased, and exon 3 skipping was reduced. Those findings indicate that in tal1, transcription and alternative splicing are co-regulated, independent of RNAPII. The authors also show that as an autoregulator, TAL1-short has a preference to TSS1-3 of TAL1, which is not shared by TAL1-long, and that each of the 5' UTR affect Tal1 expression differently. TAL1-short binds E-proteins more strongly than TAL1-long, binds many more sites than TAL1-long and stronger, and each isoform has unique set of targets. Finally, the authors set to identify the different functions of the TAL1 isoforms, and showed that Tal1-short slows cell growth and leads to TAL1-short but not TAL1-long leads to exhaustion of hematopoietic stem cells and promotes differentiation into erythroids. This paper used for the first time TAL1 isoform specific ChIP-seq, which enable accurate definition of isoform-specific targets in Jurkat cells. They demonstrated an interaction between choice of TSS and alternative splicing, and isoform specific functions. Given the clinical importance of TAL1 and the meticulous work performed to characterize its isoform specific regulation and function, I find this manuscript of interest, and only have minor suggestions to improve readability. *
Thank you for taking the time to carefully review our manuscript on the regulation and function of TAL1 isoforms. We appreciate your positive feedback on our comprehensive characterization of TAL1 regulation using chromatin profiling and isoform-specific ChIP-seq. We are glad that you found our findings on the co-regulation of transcription and alternative splicing, as well as the isoform-specific functions of TAL1, to be of interest.
We also appreciate your suggestions to improve the readability of the manuscript and have made the necessary revisions accordingly. Your feedback has been invaluable in strengthening the quality of our work, and we are grateful for your contribution to the scientific community.
* Minor comments: Add explicitly the motivation for choosing the cell line in each part. *
We have added motivation (Lines: 157-8, 177-8, 192-194, 235-6 text that was on the previous version: 192-194, 379-80).
* Figure 1 - Consider marking the promoter numbers and the enhancers names in the same names as in text (-8,-60 etc.), to make it easier for the readers to understand which enhancers is being discussed. *
This in a very important point. We have added the numbering to Figure 1D and Supp. Fig. S2A, B & E.
*P5, P18 - ProtParam is only a prediction tool, and does not supply an experimental measurement, as may be assumed from text. Please rephrase accordingly. *
The words “prediction tool” were added in the indicated paragraphs (Lines 115 and 427).
* Figure 2B/D - y axis label unclear, not explained in text. In accordance, unclear if the change is in the amount of RNA, or the ratio between the long and short variants. *
Thank you for this comment. We greatly appreciate your feedback and suggestions. To make our calculations, which are the norm in the splicing field, clearer, we have now added text to Figure 4 and provided more detailed explanations in lines 670-73. We hope that these modifications will improve the clarity and comprehensiveness of our manuscript.
*Consider removing the bars and increasing the dots, to make the graphs cleaner. *
We removed the bars throughout the manuscript for a cleaner look.
* P8 - The term '5C' may require more explanation, depending on target audience. *
We have added text to explain the technique (Lines 179-81).
* Figure 3 - the trend is that TAL1-short promotes transcription from all five TSSs. However, only in TSS1-3 is the difference significant, but the difference between the long and short forms is not significant. It is unclear if "The mean of three independent experiments done with three replicates" means overall there are three replicates per condition or nine. Please rephrase to clarify. *
Thank you for your comment. To clarify, we want to state that each biological experiment was done in three technical replicates, resulting in a total of nine replicates for each condition. We apologize for any confusion and have now rephrased to: The mean was calculated from three independent biological experiments, each performed with three technical replicates (Lines: 696 and 699).
*Fig 4 A - it seems that many of the sites bound by Tal1 total are not bind by either Tal1-short or Tal1-long. Indeed very little overlap between Tal1-short and Tal-1-total is seen in Fig 4I as well. It seems Tal1-long has very few peaks. Consider adding a discussion of possible reasons. *
We agree that these findings are noteworthy and warrant further discussion. We added text to the discussion section to explore potential reasons for these observations (Lines 416-25).
* Fig 4c - it is hard to distinguish the different lines. Consider a more clear visualization. Also, some text is in a font size too small to read. *
We have changed the format of the figure and took out the input data from the main figure to help the visualization. The input data appear in the Supp. Fig. S4C.
* Fig 4 D-H - will be useful to see the numbers, not just the % divided by %. *
A table with the specific numbers can be found in Supp Figure 4F-J.
* Fig 4 legend - 'I&L' possibly means 'I-L'. P14 - refer to where the results of the 'validation using real-time PCR' are shown. P16 - symbol replaced by an empty rectangle 20 M *
Thank you for these valuable comments, we have fixed/added these in the manuscript.
* Figure 6D - Y axis value seem strange (fold change relative to day 0 should be 1 at day 0). Consider different Y axis label for C and D to clarify. *
Thank you for this comment, we have changed the y-axis to: Fold-change relative to day 1.
* P18 - It is unclear which "two isoforms with posttranslational modifications which affected the migration rate of the protein (Fig. 1C)" were shown. Only two isoforms are mentioned throughout the paper. *
We have added text to clarify we are referring to TAL1-short and long (Lines 409-10).
*
P18 - "Our ChIP-seq results suggest that the isoforms bind at the same location (Fig. 4B)." - in 4B it seems most of TAL1-short bound positions are not bound by TAL1 long. Please clarify. *
* Worth mentioning that the Total TAL1 is taken from Jurkat cells but from a different experiment. * We have changed the statement and added the text referring to the experiments done independently (Lines 422-3).
*
Reviewer #2 (Significance (Required)): This paper used for the first time TAL1 isoform specific ChIP-seq, which enable accurate definition of isoform-specific targets in Jurkat cells. They demonstrated an interaction between choice of TSS and alternative splicing, and isoform specific functions. Given the clinical importance of TAL1 and the meticulous work performed to characterize its isoform specific regulation and function, I find this manuscript of interest, and only have minor suggestions to improve readability. *
- Sanda et al., Core transcriptional regulatory circuit controlled by the TAL1 complex in human T cell acute lymphoblastic leukemia. Cancer Cell 22, 209-221 (2012).
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Referee #2
Evidence, reproducibility and clarity
Summary:
Sharma et al. thoroughly characterized the regulation of TAL1 by mapping the use of its five promoters and enhancers, which together transcribe five transcripts, coding for two protein isoforms. For that purpose the authors used few cell lines: Jurkat as a T-ALL cell line, chronic myeloid leukemia (CML) cell line K562 and HEK293T with low TAL1 expression, as well as CutLL and MOLT4.
They profiled the chromatin marks H3K27ac and H3K4me3 at the TAL1 locus, and show that when a the -8 enhancer is compromised tha chromatin marks change, and not only the expression level of TAL1 is reduced, the level of exon 3 skipping is increased. When the -60 enhancr was activated, TAL1 expression increased, and exon 3 skipping was reduced. Those findings indicate that in tal1, transcription and alternative splicing are co-regulated, independent of RNAPII. The authors also show that as an autoregulator, TAL1-short has a preference to TSS1-3 of TAL1, which is not shared by TAL1-long, and that each of the 5' UTR affect Tal1 expression differently. TAL1-short binds E-proteins more strongly than TAL1-long, binds many more sites than TAL1-long and stronger, and each isoform has unique set of targets.
Finally, the authors set to identify the different functions of the TAL1 isoforms, and showed that Tal1-short slows cell growth and leads to TAL1-short but not TAL1-long leads to exhaustion of hematopoietic stem cells and promotes differentiation into erythroids.
This paper used for the first time TAL1 isoform specific ChIP-seq, which enable accurate definition of isoform-specific targets in Jurkat cells. They demonstrated an interaction between choice of TSS and alternative splicing, and isoform specific functions. Given the clinical importance of TAL1 and the meticulous work performed to characterize its isoform specific regulation and function, I find this manuscript of interest, and only have minor suggestions to improve readability.
Minor comments:
Add explicitly the motivation for choosing the cell line in each part.
Figure 1 - Consider marking the promoter numbers and the enhancers names in the same names as in text (-8,-60 etc.), to make it easier for the readers to understand which enhancers is being discussed.
P5, P18 - ProtParam is only a prediction tool, and does not supply an experimental measurement, as may be assumed from text. Please rephrase accordingly.
Figure 2B/D - y axis label unclear, not explained in text. In accordance, unclear if the change is in the amount of RNA, or the ratio between the long and short variants. Consider removing the bars and increasing the dots, to make the graphs cleaner.
P8 - The term '5C' may require more explanation, depending on target audience.
Figure 3 - the trend is that TAL1-short promotes transcription from all five TSSs. However, only in TSS1-3 is the difference significant, but the difference between the long and short forms is not significant. It is unclear if "The mean of three independent experiments done with three replicates" means overall there are three replicates per condition or nine. Please rephrase to clarify.
Fig 4 A - it seems that many of the sites bound by Tal1 total are not bind by either Tal1-short or Tal1-long. Indeed very little overlap between Tal1-short and Tal-1-total is seen in Fig 4I as well. It seems Tal1-long has very few peaks. Consider adding a discussion of possible reasons.
Fig 4c - it is hard to distinguish the different lines. Consider a more clear visualization. Also, some text is in a font size too small to read.
Fig 4 D-H - will be useful to see the numbers, not just the % divided by %.
Fig 4 legend - 'I&L' possibly means 'I-L'.
P14 - refer to where the results of the 'validation using real-time PCR' are shown.
P16 - symbol replaced by an empty rectangle 20 M
Figure 6D - Y axis value seem strange (fold change relative to day 0 should be 1 at day 0). Consider different Y axis label for C and D to clarify.
P18 - It is unclear which "two isoforms with posttranslational modifications which affected the migration rate of the protein (Fig. 1C)" were shown. Only two isoforms are mentioned throughout the paper.
P18 - "Our ChIP-seq results suggest that the isoforms bind at the same location (Fig. 4B)." - in 4B it seems most of TAL1-short bound positions are not bound by TAL1 long. Please clarify. Worth mentioning that the Total TAL1 is taken from Jurkat cells but from a different experiment.
Significance
This paper used for the first time TAL1 isoform specific ChIP-seq, which enable accurate definition of isoform-specific targets in Jurkat cells. They demonstrated an interaction between choice of TSS and alternative splicing, and isoform specific functions. Given the clinical importance of TAL1 and the meticulous work performed to characterize its isoform specific regulation and function, I find this manuscript of interest, and only have minor suggestions to improve readability.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript by Sharma and colleagues, the authors investigate the transcriptional regulation of the TAL1 isoforms - that derive from differential promoter usage and/or alternative splicing - and the contribution of TAL1 long and TAL1 short protein isoforms in normal haematopoietic development and disease.
The study suggests that TAL1 transcript isoforms are fine-tuned regulated. By using CRISPR/Cas9 techniques, the authors show that the enhancer -8 (MuTE) and enhancer -60 differentially regulate the TAL1 isoforms. Whether the remaining enhancers at the TAL1 locus (see Zhou Y et al, Blood 2013) also differentially regulate TAL1 transcription remains to be elucidated.
The authors found that TAL1 short isoform interacts strongly with T-cell specific transcription factors such as TCF3 and TCF12, as compared to TAL1 long isoform. TAL1 short shows an apoptotic transcription signature and it fails in rescuing cell growth as compared to TAL1 long in T-ALL. In addition, TAL1 short promotes erythropoiesis.
Lastly, the authors suggest that altering TAL1 long and TAL1 short protein isoforms ratio could have a potential therapeutic application in disease, but further studies are needed.
I have a number of comments:
Figure 1
It was not mentioned that MOLT4 cells also have MuTE. Do Jurkat and MOLT4 share a similar profile in terms of TAL1 transcript isoforms? It would have been very interesting to see whether the TAL1 transcript isoforms are similar in SIL-TAL1+ cells (e.g RPMI-8402). In these cells, TAL1 activation results from a deletion that fuses the 5' non-coding region of SIL with TAL1.
Figure 2
It is not very clear how the expression of the short isoform delta exon 3 is quantified. Detailed information and a schematic of the primer location could be helpful.
The results on Figure 2 derive from complex Cas9/CRISPR experiments. A schematic representation showing the location of the following elements is missing: CTCF sites, CTCF gRNA target region, dCas9-p300 gRNA target region and -60 enhancer. Are the levels of dCas9-p300 WT and dCas9-p300 MUT comparable in transfected HEK 293 cells? Were those possibly measured by qPCR or Western Blot? Why the authors chose to use 293T cells for the CTCF del as the enhancer usage around the locus must be so different from haematopoietic cells.
Is CPT - camptothecin? A control gene that is sensitive to CPT treatment would ensure the inhibitor is working.
In supplementary Figure 2D, the reduction in expression in Jurkat Del-12 is restricted to TSS2. There is no reduction in TAL1 TSS1 and TAL1 TSS4 (this is not clear from the result description section). As seen, these isoforms are upregulated and that could suggest a compensatory mechanism mediated by alternative promoter activation. The fact that Jurkat Del-12 express TAL1 from MSCV-TAL1 could also suggest that TSS1 and TSS4 are upregulated by TAL1 or indirectly, by other members of the TAL/LMO complex (see Sanda T et al, Cancer Cell 2012)
Figure 3
A. Are the levels of TAL1 short cDNA and TAL1 long cDNA comparable in the co-transfection luciferase experiments? The overexpression of the isoforms does not reflect the endogenous expression levels in cell lines where one of the isoforms is more predominantly expressed (e.g Jurkat cells express low levels of TAL1 short).
Figure 4
Are the levels of flag-TAL1 long and flag-TAL1 short comparable? The levels of expression could explain the low intensity signal for TAL1 long. Is there any reason for not performing a depletion of endogenous TAL1 prior to the ChIP seq flag experiment? Could the authors speculate about MAF motif enrichment in both isoforms and not in TAL1-total? Do TAL1 long and TAL1 short recognise the same DNA motif?
Figure 6
In A and B, are the levels of flag-TAL1 long and flag-TAL1 short in transduced K562 comparable? In C and D, are the TAL1 levels reduced at the protein level?
Minor points:
Figure 1
A. Include a scale bar C. Loading control such as GAPDH is missing in the Western Blot. Are CUTLL cells the same as CUTTL-1? D. Adjust scale of the CHIP seq tracks in K562 cells in order to see the peak summit. Include genome build In supplementary Figure 1B, the symbol scheme is not clear
Figure 2
A & C. Remove 'amount' from the Y axis. Is the total mRNA amount calculated as % of the reference genes? It could be specified on the y axis or figure legend.
In supplementary Figure 2C, a loading control is missing.
Figures 4, 5 and 6
Size of the figures should be increased.
Significance
The study from Sharma and colleagues is novel and it extends the knowledge on TAL1 regulation and the role of TAL1 in development and disease. Although the study suggests that there is a correlation between enhancers, chromatin mark deposition at exons and regulation of alternative splicing, the mechanistic link is not fully elucidated. The findings on TAL1 short protein are interesting but the data on TAL1 long lacks some refinement so then robust conclusions can be drawn.
The experimental data lacks a few controls. The text is clear and prior studies could be better referenced.
As TAL1 is a very crucial transcription factor oncogene in T-ALL, the study is important as it addresses a very relevant question in the field that is the regulation of the transcription of TAL1 and the functional relevance of both TAL1 short and TAL1 long isoforms.
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Reply to the reviewers
We would like to thank the reviewers for their extensive review of our manuscript and constructive criticism. We have attempted to address the points raised in the reviewer's comments and have performed additional experiments and have edited the text of the manuscript to explain these points. Please see below, our point-by-point response to the reviewer’s comments. In the submitted revised manuscript, some figure numbers have changed from the prior reviewed version.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In this MS, Mrj - a member of the JDP family of Hsp70 co-chaperones was identified as a regulator of the conversion of Orb2A (the Dm ortholog of CPEB) to its prion-like form.
In drosophila, Mrj deletion does not cause any gross neurodevelopmental defect nor leads to detectable alterations in protein homeostasis. Loss of Mrj, however, does lead to altered Orb2 oligomerization. Consistent with a role of prion-like characteristics of Orb2 in memory consolidation, loss of Mrj results in a deficit in long-term memory.
Aside from the fact that there are some unclarities related to the physicochemical properties of Orb2 and how Mrj affects this precisely, the finding that a chaperone could be important for memory is an interesting observation, albeit not entirely novel.
In addition, there are several minor technical concerns and questions I have that I feel the authors should address, including a major one related to the actual approach used to demonstrate memory deficits upon loss of Mrj.
Reviewer #1 (Significance (Required)):
Figure 1 (plus related Supplemental figures): • There seem to be two isoforms of Mrj (like what has been found for human DNAJB6). I find it striking to see that only (preferentially?) the shorter isoform interacts with Orb2. For DNAJB6, the long isoform is mainly related to an NLS and the presumed substrate binding is identical for both isoforms. If this is true for Dm-Mrj too, the authors could actually use this to demonstrate the specificity of their IPs where Orb2 is exclusively non-nuclear?
According to Flybase, Mrj has 8 predicted isoforms of which four are of 259 amino acids (PA, PB, PC, and PD), 3 are of 346 amino acids (PE, PG, and PH) and one is of 208 amino acids (PF) length (Supplementary data 1). We isolated RNA from flyheads and used this in RT-PCR experiments to check which Mrj isoforms express in the brain. Since both the 346 amino acid (1038 nucleotide long) and 259 amino acids (777 nucleotides long) form, which we refer to as the long and middle isoform, has the same N and C terminal sequences we used the same primer pair for this, but on RT-PCR the only amplicon we got corresponds to the 259 amino acid form. For the 208 amino acids (624 nucleotides long) form we designed a separate forward primer and attempted to amplify this using RT-PCR but were unable to detect this isoform also. This data is now presented in Supplemental Figure 4B. Since the only isoform detected from fly head cDNA corresponded to the 259 amino acid form, we think this is the predominant isoform of Mrj expressing in Drosophila and this is what is in our DnaJ library and what we have used in all our experiments here. This is also the same isoform described in previous papers on Drosophila Mrj (Fayazi et al, 2006; Li et al, 2016b). For this 259 amino acid Mrj isoform, we see its expression in both the nucleus and cytoplasm (Supplemental Figure 4C). As the long 346 AA fragment was undetectable in the brain, it was not feasible to address the reviewer’s point of using the long and short forms of Mrj for IP with Orb2. However, we have performed IP of human CPEB2 (hCPEB2) with the long and short isoforms of human DnaJB6 and have detected interaction of hCPEB2 with both the long and short isoforms of DnaJB6 (Supplemental Figure 6E).
- I would be interested to know a bit more about the other 5 JDPs that are interactors with Orb2: are the human orthologs of those known? It is striking that these other 5 JDPs interact with Orb2 in Dm (in IPs) but have no impact on Sup35 prion behavior. Importantly, this does not imply they may not have impact on the prion-like behavior of other Dm substrates, including Dm-Orb2.
We have performed BlastP analysis of CG4164, CG9828, CG7130, DroJ2, and Tpr2 protein sequences against Human proteins. Based on this we have listed the highest-ranking candidate identified here for each of these genes.
Drosophila Gene
Human gene
Query cover
Percent identity
E value
CG4164
dnaJ homolog subfamily B member 11 isoform 1
98 %
62.96%
2e-150
CG9828
dnaJ homolog subfamily A member 2
92%
39.41%
3e-84
CG7130
dnaJ homolog subfamily B member 4 isoform d
56%
69.44%
2e-30
Tpr2
dnaJ homolog subfamily C member 7 isoform 1
93%
46.22%
6e-139
DroJ2
dnaJ homolog subfamily A member 4 isoform 2
98%
60.60%
2e-169
In the context of the chimeric Sup35-based assay where Orb2A’s Prion-like domain (PrD) is coupled with the C-terminal domain of Sup35, the only protein which could convert Orb2A PrD-Sup35 C from its non-prion state to prion state was Mrj. Within the limitations of this heterologous-system based assay, the other 5 DnaJ domain proteins as well as the Hsp70’s were unable to convert the Orb2A PrD from its non-prion to prion-like state. What these other 5 interacting JDP proteins are doing through their interaction with Orb2A and if they are even expressing in the Orb2 relevant neurons will need to be tested separately and will be the subject of our future studies.
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The data in panels H, I indeed suggest that Mrj1 alters the (size of) the oligomers. It would be important to know what is the actual physicochemical change that is occurring here. The observed species are insoluble in 0.1 % TX100 but soluble in 0.1% SDS, which suggest they could be gels, but not real amyloids such as formed by the polyQ proteins that require much higher SDS concentrations (~2%) to be solubilized. This is relevant as Mrj1 reduces polyQ amyloidogenesis whereas is here is shown to enhance Orb2A oligomerization/gelidification. In the same context, it is striking to see that without Mrj the amount of Orb2A seems drastically reduced and I wonder whether this might be due to the fact that in the absence of Mrj a part of Orb2A is not recovered/solubilized due to its conversion for a gel to a solid/amyloid state? In other words: Mrj1 may not promote the prion state, but prevents that state to become an irreversible, non-functional amyloid?
On the reviewer’s point to address what is the actual physicochemical change occurring here, we will need to develop methods to purify the Orb2 oligomers in significant quantities to examine and distinguish if they are of gel or real amyloid-like nature. Currently, within the limitations of our ongoing work, this has not been possible for us to do and we can attempt to address this in our future work. Cryo-EM derived structure of endogenous Orb2 oligomers purified from a fly head extract from 3 million fly heads, made in the TritonX-100 and NP-40 containing buffer, the same buffer as what we have used here for the first soluble fraction, showed these oligomers as amyloids (Hervas et al, 2020). If the oligomers extracted using 0.1% and 2% SDS are structurally and physicochemically different, within the limitations of our current work, had not been possible to address.
The other point raised by the reviewer is, if in the absence of Mrj (in the context of Figure 4 of our previously submitted manuscript), a part of Orb2 is not solubilized due to us using a lower 0.1% SDS for extraction. To address this, we attempted to see how much of leftover Orb2 is remaining in the pellet after extraction with 0.1 % SDS. Towards this, according to the reviewers’ suggestion, we used a higher 2% SDS containing buffer to resuspend the leftover pellet after 0.1% SDS extraction, and post solubilisation ran all the fractions in SDD-AGE. We did this experiment with both wild-type and Mrj knockout fly heads. Under these different extractions, we first observed while there is more Orb2 in the soluble fraction (Triton X-100 extracted) of Mrj knockout, this amount is reduced in both the 0.1% SDS solubilized and 2% SDS solubilized fractions. So, even though there is leftover Orb2 after 0.1% SDS extraction, which can be extracted using 2% SDS, this amount is reduced in Mrj knockout. The other observation here is the Orb2 extracted using 2% SDS shows a longer smear in comparison to the 0.1% SDS extracted form suggesting a possibility of more and higher-sized oligomers present in this fraction. Since we do not have the exact physicochemical characterization of these oligomers detected with 0.1% and 2% SDS-containing buffer, we are not differentiating them by using the terms gels and real amyloids, but refer to them as 0.1% SDS soluble Orb2 oligomers and 2% SDS soluble Orb2 oligomers. Overall, our observations here suggest in absence of Mrj, both of these kinds of Orb2 oligomers are decreased and so Mrj is most likely promoting the formation of Orb2 oligomers. It is possible that the 0.1% SDS soluble Orb2 oligomers gradually accumulate and undergo a further transition to the 2% SDS soluble Orb2 oligomers, so if in absence of Mrj, the formation of the 0.1% SDS soluble Orb2 oligomers is decreased, the next step of formation of 2% SDS soluble Orb2 oligomers also be decreased. This data is now presented in Figure 5H, I and J).
On the other possibility raised by the reviewer that Mrj can prevent the oligomeric state of Orb2 to become an irreversible non-functional amyloid, we think it is still possible for Mrj to do this but this could not be tested under the present conditions.
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It may be good for clarity to refer to the human Mrj as DNAJB6 according to the HUGO nomenclature. Also, the first evidence for its oligomerization was by Hageman et al 2010.
We have now changed mentions of human Mrj to DNAJB6. We apologize for missing the Hageman et al 2010 reference and have now cited this reference in the context of Mrj oligomerization.
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It is striking to see that Mrj co-Ips with Hsp70AA, Hsp70-4 but not Hsp70Cb. The fact that interactions were detected without using crosslinking is also striking given the reported transient nature of J-domain-Hsp70 interactions Together, this may even suggest that Mrj-1 is recognized as a Hsp70 substrate (for Hsp70AA, Hsp70-4 but not Hsp70Cb) rather than as a co-chaperone. In fact, a variant of Mrj-1 with a mutation in the HPD motif should be used to exclude this option.
In IP experiments we notice Mrj interacts with Hsp70Aa and Hsc70-4 but not with Hsc70-1 and Hsc70Cb. In our previously submitted manuscript, we realized we made a typo on the figure, where we referred to Hsp70Aa as Hsc70Aa. We have corrected this in the current revised manuscript. On the crosslinking point raised by the reviewer, we reviewed the published literature for studies of immunoprecipitation experiments which showed an interaction between DnaJB6 and Hsp70. We noted while one of the papers (Kakkar et al, 2016) report the use of a crosslinker in the experiment which showed an interaction between GFP-Hsp70 and V5-DnaJB6, in another two papers the interaction between endogenous Mrj and endogenous Hsp/c70 (Izawa et al, 2000) and Flag-Hsp70 and GFP-DnaJB6 (Bengoechea et al, 2020) could be detected without using any crosslinker. Our observations of detecting the interaction of Mrj with Hsp70Aa and Hsc70-4 in the absence of a crosslinker are thus similar to the observations reported by (Izawa et al, 2000; Bengoechea et al, 2020).
On the point of if Mrj is a substrate for Hsp70aa and Hsc70-4 and not a co-chaperone, we feel in the context of this manuscript, since we are focussing on the role of Mrj in the regulation of oligomerization of Orb2 and in memory, the experiment with HPD motif mutant is probably not necessary here. However, if the reviewers suggest this experiment to be essential, we can attempt this experiment by making this HPD motif mutant.
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The rest of these data reconfirm nicely that Mrj/DNAJB6 can suppress polyQ-Htt aggregation. Yet note that in this case the oligomers that enter the agarose gel are smaller, not bigger. This argues that Mrj is not an enhancer of oligomerization, but rather an inhibitor of the conversion of oligomers to a more amyloid like state.
Figure 2 and Supplemental Figure 4 discuss the effect of Mrj on Htt aggregation. We have used 2 different Htt constructs here. For Figure 2I, we used only Exon1 of Htt with the poly Q repeats. Here in SDD-AGE, for the control lane, we see the Htt oligomers as a smear for the control. For Mrj, we see only a small band at the bottom which can be interpreted most likely as either a monomer or as small oligomers since we do not observe any smear here. However, for the 588 amino acid fragment of HttQ138 in the SDD-AGE we do not see a difference in the length of the smear but in the intensity of the smear of the Htt oligomers (Supplemental Figure 4E). Based on this we are suggesting in presence of Mrj, there are lesser Htt oligomers. On the point of Mrj is not an enhancer of oligomerization, but rather an inhibitor of the conversion of oligomers to a more amyloid-like state, our experiments with the Mrj knockout show reduced Orb2 oligomers (both for 0.1% and 2% SDS soluble forms), suggesting Mrj plays a role in the conversion of Orb2 to the oligomeric state. If Mrj inhibits the conversion of oligomers to a more amyloid-like state, this is possible but we couldn’t test this hypothesis here. However, for Htt amyloid aggregates, previous works done by other labs with DnaJB6 as well as our experiments with Mrj suggest this as a likely possibility.
Figure 3: • The finding that knockout of DNAJB6 in mice is embryonic lethal is related to a problem with placental development and not embryonic development (Hunter et al, 1999; Watson et al, 2007, 2009, 2011) as well recognized by the authors. Therefore, the finding that deletion of Dm-Mrj has no developmental phenotype in Drosophila may not be that surprising.
We agree with the reviewer’s point that DNAJB6 mutant mice have a problem with placental development. However, one of the papers cited here (Watson et al, 2009) suggests DNAJB6 also plays a crucial role in the development of the embryo independent of the placenta development defect. The mammalian DNAJB6 mutant embryos generated using the tetraploid complementation method show severe neural defects including exencephaly, defect in neural tube closure, reduced neural tube size, and thinner neuroepithelium. Due to these features seen in the mice knockout, and the lack of such developmental defects in the Drosophila knockout, we interpreted our findings in Drosophila as significantly different from the mammals.
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It is a bit more surprising that Mrj knockout flies showed no aggregation phenotype or muscle phenotype, especially knowing that DNAJB6 mutations are linked to human diseases associated with aggregation (again well recognized by the authors). However, most of these diseases are late-onset and the phenotype may require stress to be revealed. So, while important to this MS in terms of not being a confounder for the memory test, I would like to ask the authors to add a note of caution that their data do not exclude that loss of Mrj activity still may cause a protein aggregation-related disease phenotype. Yet, I also do think that for the main message of this MS, it is not required to further test this experimentally.
We agree with the reviewer and have added this suggestion in the discussion that loss of Mrj may still result in a protein aggregation-related disease phenotype, probably under a sensitized condition of certain stresses which is not tested in this manuscript.
Figure 4:
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IPs were done with Orb2A as bite and clearly pulled down substantial amounts of GFP-tagged Mrj. For interactions with Orb2B, a V5-tagged Mrj was use and only a minor fraction was pulled down. Why were two different Mrj constructs used for Arb2A and Orb2b?
In the previously submitted manuscript, we have used HA-tagged Mrj (not V5) for checking the interaction with full-length Orb2B tagged with GFP. This was done with the goal of using the same Mrj-HA construct as that used in the initial Orb2A immunoprecipitation experiment. Since this has raised some concern as in the IPs to check for interaction between truncated Orb2A constructs (Orb2A325-GFP and Orb2AD162-GFP) and Mrj (Mrj-RFP), we used a different GFP and RFP tag combination. To address this, we have now added the same tag combinations for the IPs (Mrj-RFP with Orb2A-GFP and Orb2B-GFP). In these immunoprecipitation experiments where Mrj-RFP was pulled down using RFP Trap beads, we were able to detect positive interaction with GFP-tagged Orb2A and Orb2B. This data is now added in Figure 4F and 4I. We also have added the IP data for interaction between Mrj-HA and untagged Orb2B in Figure 4K, similar to the combination of initial experiment between Mrj-HA and untagged Orb2A.
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In addition, I think it would be important what one would see when pulling on Mrj1, especially under non-denaturing conditions and what is the status of the Orb2 that is than found to be associated with Mrj (monomeric, oligomeric and what size).
We have now performed IP from wild-type fly heads using anti Mrj antibody and ran the immunoprecipitate in SDS-PAGE and SDD-AGE followed by immunoblotting them with anti-Orb2 antibody. Our experiments suggest that immunoprecipitating endogenous Mrj brings down both the monomeric and oligomeric forms of Orb2. This data is now added in Figure 4L, M and N.
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This also relates to my remark at figure 1 and the subsequent fractionation experiments they show here in which there is a slight (not very convincing) increase in the ratio of TX100-soluble and insoluble (0.1% SDS soluble) material. My question would be if there is a remaining fraction of 0.1% insoluble (2% soluble) Orb2 and how Mrj affects that? As stated before, this is (only) mechanistically relevant to understanding why there is less oligomers of Orb2 in terms of Mrj either promoting it or by preventing it to transfer from a gel to a solid state. The link to the memory data remains intriguing, irrespective of what is going on (but also on those data I do have several comments: see below).
We have addressed this in response to the reviewer’s comments on Figure 1. We find in both wild type and Mrj knockout fly heads, there are Orb2 oligomers that can be detected using 0.1% SDS extraction and with further extraction with 2% SDS. The 2% SDS soluble Orb2 oligomers were previously insoluble during 0.1% SDS-based extraction. However, the amounts of both of these oligomers are reduced in Mrj knockout fly heads. Since we do not have the physicochemical characterization of both of these kinds of oligomers, we are not using the terms gel or solid state here but referring to these oligomers as 0.1% SDS soluble Orb2 oligomers and 2% SDS soluble Orb2 oligomers. We speculate that the 0.1% SDS soluble Orb2 oligomers over time transition to the 2% SDS soluble Orb2 oligomers. As in the absence of Mrj in the knockout flies, both the 0.1% SDS soluble and 2% SDS soluble Orb2 oligomers are decreased, this suggests Mrj is promoting the formation of Orb2 oligomers. On the reviewer’s point, if Mrj can prevent the transition from 0.1% SDS soluble to 2% SDS soluble Orb2 oligomers, we think it is possible for Mrj to both promote oligomerization of Orb2 as well as prevent it from forming bigger non-functional oligomers, but the second point is not tested here. The relevant data is now presented in Figure 5H, I and J.
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I also find the sentence that "Mrj is probably regulating the oligomerization of endogenous Orb2 in the brain" somewhat an overstatement. I would rather prefer to say that the data show that Mrj1 affects the oligomeric behavior/status of Orb2.
Based on the reviewer’s suggestion we have now changed the sentence to Mrj is probably regulating the oligomeric status of Orb2
Figure 5:
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To my knowledge, the Elav driver regulates expression in all neurons, but not in glial cells that comprise a significant part of the fly heads/brain. The complete absence of Mrj in the fly-heads when using this driver is therefore somewhat surprising. Or do we need to conclude from this that glial cells normally already lack Mrj expression?
On driving Mrj RNAi with Elav Gal4, we did not detect any Mrj in the western. We attempted to address the glial contribution towards Mrj’s expression we used a Glia-specific driver Repo Gal4 line to drive the control and Mrj RNAi line and performed a western blot using fly head lysate with anti-Mrj antibody. In this experiment, we did not observe any difference in Mrj levels between the two sets. As the Mrj antibody raised by us works in western blots but not in immunostainings, we could not do a colocalization analysis with a glial marker. However, we used the Mrj knockout Gal4 line to drive NLS-GFP and performed immunostainings of these flies with a glial marker anti-Repo antibody. Here we see two kinds of cells in the brain, one which have GFP but no Repo and the other where both are present together. This suggest that while Glial cells have Mrj but probably majority of Mrj in the brain comes from the neurons. We also found a reference where it was shown that Elav protein as well as Elav Gal4 at earlier stages of development expresses in neuroblasts and in all Glia (Berger et al, 2007). So, another possibility is when we are driving Mrj RNAi using Elav Gal4, this knocks down Mrj in both the neurons as well as in the glia. This coupled with the catalytic nature of RNAi probably creates an effective knockdown of Mrj as seen in the western blot. This data is now added in Supplementary Figure 5G and H.
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Why not use these lines also for the memory test for confirmation? I understand the concerns of putative confounding effects of a full knockdown (which were however not reported), but now data rely only on the mushroom body-specific knockdown for the 201Y Gal4 line, for which the knockdown efficiency is not provided. But even more so, here a temperature shift (22oC-30oC) was required to activate the expression of the siRNA. For the effects of this shift alone no controls were provided. The functional memory data are nice and consistent with the hypothesis, but can it be excluded that the temperature shift (rather than the Mrj) knockdown has caused the memory defects? I think it is crucial to include the proper controls or use a different knockdown approach that does not require temperature shifts or even use the knockout flies.
We have now performed the memory experiments with Mrj knockout flies. Our experiments show at 16 and 24-hour time points Mrj knockout flies have significantly reduced memory in comparison to the control wildtype. This data is now added in Figure 6B.
Figure 6:
The finding of a co-IP between Rpl18 and Mrj (one-directional only) by no means suffices to conclude that Mrj may interact with nascent Orb2 chains here (which would be the relevant finding here). The fact that Mrj is a self-oligomerising protein (also in vitro, so irrespective of ribosomal associations!), and hence is found in all fractions in a sucrose gradient, also is not a very strong case for its specific interaction with polysomes. The finding that there is just more self-oligomerizing Orb2A co-sedimenting with polysomes in sucrose gradients neither is evidence for a direct effect of Mrj enhancing association of Orb2A with the translating ribosomes even though it would fit the hypothesis. So all in all, I think the data in this figure and non-conclusive and the related conclusions should be deleted.
We have now performed the reverse co-IP between Rpl18-Flag and Mrj-HA using anti-HA antibody and could detect an interaction between the two. This data is now added in Supplementary Figure 6A.
To address if Mrj is a self-oligomerizing protein that can migrate to heavier polysome fractions due to its size, we have loaded recombinant Mrj on an identical sucrose gradient as we use for polysome analysis. Post ultra-centrifugation we fractionated the gradients and checked if Mrj can be detected in the fraction numbers where polysomes are present. In this experiment, we could not detect recombinant Mrj in the heavier polysome fractions (data presented in Supplementary Figure 6B). Overall, our observations of Mrj-Rpl18 IPs, the presence of cellularly expressed Mrj in polysome fractions, and the absence of recombinant Mrj from these fractions, suggest a likelihood of Mrj’s association with the translating ribosomes.
On the reviewer’s point of us concluding Mrj may interact with nascent Orb2 chains, we have not mentioned this possibility in the manuscript as we don’t have any evidence to suggest this. We have also added a sentence: This indicates that in presence of Mrj, the association of Orb2A with the translating ribosomes is enhanced, however, if this is a consequence of increased Orb2A oligomers due to Mrj or caused by interaction between polysome-associated Orb2A and Mrj will need to be tested in future.
Based on these above-mentioned points, we hope we can keep the data and conclusions of this section.
Overall, provided that proper controls/additional data can be provided for the key experiments of memory consolidation, I find this an intriguing study that would point towards a role of a molecular chaperone in controlling memory functions via regulating the oligomeric status of a prion-like protein and that is worthwhile publishing in a good journal.
However, in terms of mechanistical interpretations, several points have to be reconsidered (see remarks on figure 1,4); this pertains especially to what is discussed on page 13. In addition, I'd like the authors to put their data into the perspective of the findings that in differentiated neurons DNAJB6 levels actually decline, not incline (Thiruvalluvan et al, 2020), which would be counterintuitive if these proteins are playing a role as suggested here in memory consolidation.
We have addressed the comments on Figures 1 and 4 earlier. We have also added new memory experiment’s data with the Mrj knockout in Figure 6.
We have attempted to put the observations with Drosophila Mrj in perspective to observations in Thiruvalluvan et al, on human DnaJB6 in the discussions as follows:
Can our observation in Drosophila also be relevant for higher mammals? We tested this with human DnaJB6 and CPEB2. In mice CPEB2 knockout exhibited impaired hippocampus-dependent memory (Lu et al, 2017), so like Drosophila Orb2, its mammalian homolog CPEB2 is also a regulator of long-term memory. In immunoprecipitation assay we could detect an interaction between human CPEB2 and human DnaJB6, suggesting the feasibility for DnaJB6 to play a similar role to Drosophila Mrj in mammals. However, as the human DnaJB6 level was observed to undergo a reduction in transitioning from ES cells to neurons, (Thiruvalluvan et al, 2020) how this can be reconciled with its possible role in the regulation of memory. We speculate, such a reduction if is happening in the brain will occur in a highly regulatable manner to allow precise control over CPEB2 oligomerization only in specific neurons where it is needed and the reduced levels of DnaJB6 is probably sufficient to aid CPEB oligomerization Alternatively, there may be additional chaperones that may function in a stage-specific manner and be able to compensate for the decline in levels of DNAJB6.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: The manuscript describes the role of the Hsp40 family protein Mrj in the prion-like oligomerization of Orb2. The authors demonstrate that Mrj promotes the oligomerization of Orb2, while a loss in Mrj diminishes the extent of Orb2 oligomerization. They observe that while Mrj is not an essential gene, a loss in Mrj causes deficiencies in the consolidation of long-term memory. Further, they demonstrate that Mrj associates with polysomes and increases the association of Orb2 with polysomes.
Major comments: None
Minor comments:
-
In the section describing the chaperone properties of Mrj in clearing Htt aggregates (Fig 2), the legend describes that "Mrj-HA constructs are more efficient in decreasing Htt aggregation compared to Mrj-RFP". It would be helpful to add Mrj-RFP to the quantification in Fig 2G to know exactly the difference in efficiency. Is there an explanation for why the 2 constructs behave differently?
We have added the quantitation of Htt aggregates in presence of Mrj-RFP in the revised version (Data presented in Figure 2G). While the efficiency of Mrj-RFP to decrease Htt aggregates is significantly less in comparison to Mrj-HA, it is still significantly better in comparison to the control CG7133-HA construct. It is possible, due to the tagging of Mrj with a larger tag (RFP), this reduces its ability to decrease the Htt aggregates in comparison to the construct where Mrj is tagged with a much smaller HA tag.
Figs A, B, C, G need to have quantification of the percentage of colocalization with details about the number of cells quantified for each experiment.
We have now added the intensity profile images and colocalization quantitation (pearson’s coefficient) in the Supplemental Figure 5A and B. This quantitation is done from multiple ROI’s taken from at 4-6 cells.
In Fig 6 B, C, F, G it would be helpful to label the 40S, 60S and 80S peaks in the A 254 trace.
We have now labeled the 80S, and polysome peaks in the Figure 7B, C, F and G. We could not separate the 40S and 60S peaks in the A254 trace.
It's interesting that Mrj has opposing functions with regard to aggregation when comparing huntingtin with Orb2. From the literature presented in the discussion, it appears as though chaperones including Mrj have an anti-aggregation role for prions. It would be helpful to have more discussion around why, in the case of Orb2, this is different. The discussion states that "The only Hsp40 chaperone which was found similar to Mrj in increasing Orb2's oligomerization is the yeast Jjj2 protein" - this point needs elaboration, as well as a reference.
In the discussions section we have now added the following speculations on this:
One question here is why Mrj behaves differently with Orb2 in comparison to other amyloids. Orb2 differs from other pathogenic amyloids in its extremely transient existence in the toxic intermediate form (Hervás et al, 2016). For the pathogenic amyloids, since they exist in the toxic intermediate form for longer, Mrj probably gets more time to act and prevent or delay them from forming larger aggregates. For Orb2, Mrj may help to quickly transition it from the toxic intermediate state, thereby helping this state to be transient instead of longer. An alternate possibility is post-transition from the toxic intermediate state, Mrj stabilizes these Orb2 oligomers and prevents them from forming larger aggregates. This can be through Mrj interacting with Orb2 oligomers and blocking its surface thereby preventing more Orb2 from assembling over it. Another difference between the Orb2 oligomeric amyloids and the pathogenic amyloids is in the nature of their amyloid core. For the pathogenic amyloids, this core is hydrophobic devoid of any water molecules, however for Orb2, the core is hydrophilic. This raises another possibility that if the Orb2 oligomers go beyond a certain critical size, Mrj can destabilize these larger Orb2 aggregates by targeting its hydrophilic core.
On the Jjj2 point raised by the reviewer, we have added the (Li et al, 2016a) reference now and elaborated as:
The only Hsp40 chaperone which was found similar to Mrj in increasing Orb2’s oligomerization is the yeast Jjj2 protein. In Jjj2 knockout yeast strain, Orb2A mainly exists in the non-prion state, whereas on Jjj2 overexpression the non-prion state could be converted to a prion-like state. In S2 cells coexpression of Jjj2 with Orb2A lead to an increase in Orb2 oligomerization (Li et al, 2016a). However, Jjj2 differs from Mrj, as when it is expressed in S2 cells, we do not detect it to be present in the polysome fractions.
The Jjj2 polysome data is now presented in Supplementary Figure 6C.
Reviewer #2 (Significance (Required)):
General assessment:
Overall, the work is clearly described and the manuscript is very well-written. The motivation behind the study and its importance are well-explained. I only have minor comments and suggestions to improve the clarity of the work. The study newly describes the interaction between the chaperone Mrj and the translation regulator Orb2. The experiments that the screen for proteins that interact with Orb2 and promote its oligomerization are very thorough. The experiments that delve into the role of Mrj in protein synthesis are a good start, and need to be explored further, but that is beyond the scope of this study.
Advance: The study describes a new interaction between the chaperone Mrj and the translation regulator Orb2. The study is helpful in expanding our knowledge of prion regulators as well factors that affect memory acquisition and consolidation.
Audience: This paper will be of most interest to basic researchers.
My expertise is in Drosophila genetics and neuronal injury.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The manuscript submitted by Desai et al. identifies a chaperone of the Hsp40 family (Mrj) that binds Orb2 and modulates its oligomerization, which is critical for Orb2 function in learning and memory in Drosophila. Orb2 are proteins with prion-like properties whose oligomerization is critical for their function in the storage of memories. The main contribution of the article is the screen of Hsp40 and Hsp70-family proteins that bind Orb2. The authors show IP results for all the candidates tested, including those that bind Fig. 1) and those that don't (Supp Fig 3). There is also a figure devoted to examining the interaction of Mrj with polyglutamine models (Htt). They also generate a KO mutant that is viable and shows no gross defects or protein aggregation. Lastly, they show that the silencing of Mrj in the mushroom body gamma neurons results in weaker memories in a courtship paradigm. Although the data is consistent and generally supportive of the hypothesis, key details are missing in several areas, including controls. Additionally, the interpretation of some results leaves room for debate. Overall, this is an ambitious article that needs additional work before publication.
Specific comments:
-
General concern over the interpretation of IP experiments and colocalization. These experiments don't necessarily reflect direct interactions. They are consistent with direct interaction but not the only explanation for a positive IP or colocalization.
This paper is centred on the interaction between Orb2A and Mrj, which we have detected using immunoprecipitation. The reviewer’s concern here is, this experiment is not able to distinguish if this can be a direct protein-protein interaction or if the two proteins are part of a complex.
To address this concern we have used purified recombinant protein-based pulldowns. Our experiments with purified protein pulldowns (GST tagged Mrj from E.coli with Orb2A from E.coli or Orb2A-GFP from Sf9 cells) suggest Orb2A and Mrj can directly interact amongst themselves. This data is now presented in Figure 1J and K.
The Huntingtin section has a few concerns. The IF doesn't show all controls and the quantification is not well done in terms of what is relevant. A major problem is the interpretation of Fig 2F. The idea is that Mrj prevents the aggregation of Htt, which is the opposite of what is observed with Orb2. The panel actually shows a large Htt aggregate instead of multiple small aggregates. This has been reported before in Drosophila and other systems with different polyQ models. Mrj and other Hsp40 and Hsp70 proteins modify Htt aggregation, but in an unexpected way. This affects the model shown in Fig. 6H. Lastly, Fig 2H and 2I show very different level of total Htt.
In Figure 2F of the previously submitted manuscript, we have shown representative images of HttQ103-GFP cells coexpressing with a control DnaJ protein CG7133-HA and Mrj-HA. In Figure 2G we quantitated the number of cells showing aggregates within the population of doubly transfected cells. On the reviewer’s point of figure 2F showing large Htt aggregates instead of multiple small aggregates, we do not see a large Htt aggregate in presence of Mrj in this figure, the pattern looks diffused here and very different from the control CG7133 where the aggregates are seen. We have performed the same experiment with a different Htt construct (588 amino acids long fragment) tagged with RFP, and here also we notice in presence of Mrj, the aggregates are decreased and the expression pattern looks diffused (Supplementary Figure 4E, 4F).
If the comment on large Htt aggregates in presence of Mrj is concerning figure 2E, here we show Mrj-RFP to colocalize with the Htt aggregates. Here, even though Mrj-RFP colocalizes with Htt aggregates, it rescues the Htt aggregation phenotype as in comparison to the control CG7133, the number of cells with Htt aggregates is still significantly less here. We have added this quantitation of rescue by Mrj-RFP in the revised manuscript now. The observation of colocalization of Mrj-RFP with Htt aggregates is similar to previous reports of chaperones rescuing Htt aggregation and yet showing colocalization with the aggregates. Both Hdj-2 and Hsc70 suppress Htt aggregation and yet were observed to colocalize with Htt aggregates in the cell line model as well as in nuclear inclusions in the brain (Jana et al, 2000). In a nematode model of Htt aggregation, DNJ-13 (DnaJB-1), HSP-1 (Hsc70), and HSP-11 (Apg-2) were shown to colocalize with Htt aggregates and yet decrease the Htt aggregation (Scior et al, 2018). Hsp70 was also found to colocalize with Htt aggregates in Hela cells (Kim et al, 2002).
Regarding Figures 2H and 2I, while figure 2H is of an SDS-PAGE to show no difference in the levels of monomeric HttQ103 (marked with *) in presence of Mrj and the control CG7133, figure 2I is for the same samples ran in an SDD-AGE where reduced amount of Htt oligomers as seen with the absence of a smear in presence of Mrj. The apparent difference in Htt levels between 2H and 2I is due to the detection of Htt aggregates/oligomers in the SDD-AGE which are unable to enter the SDS-PAGE and hence undetected. In Supplementary Figure 4E, similar experiments were done with the longer Htt588 fragment and here we notice in the SDD-AGE reduced intensity of the smear made up of Htt oligomers, again suggesting a reduction in Htt aggregates. Thus our results are not in contradiction to previous studies where Mrj was found to rescue Htt aggregate-associated toxicity.
Endogenous expression of Mrj using Gal4 line: where else is it expressed in the brain / head and in muscle. Fig 3G shows no muscle abnormalities but no evidence is shown for muscle expression. It is nice that Fig 3E and F show no abnormal aggregates in the Mrj mutant, but this would be maybe more interesting if flies were subjected to some form of stress.
We have now added images of the brain and muscles to show the expression pattern of Mrj. Using Mrj Gal4 line and UAS- CD8GFP, we noticed enriched expression in the optic lobes, mushroom body, and olfactory lobes. We also noticed GFP expression in the larval muscles and neuromuscular junction synaptic boutons. This data is now presented in Supplementary Figure 5C, D, E and F.
On the reviewer’s point of subjecting the Mrj KO flies to some form of stress, we have not performed this. We have added in the discussions a note of caution, that loss of Mrj may still result in a protein aggregation-related disease phenotype, probably under a sensitized condition of certain stresses which is not tested in this manuscript.
Fig. 5B shows no Mrj detectable from head homogenates in flies silencing Mrj in neurons with Elav-Gal4. It would be nice if they could show that ONLY neurons express Mrj in the head. Also noted, Elav-Gal4 is a weak driver, so it is surprising that it can generate such robust loss of Mrj protein
We have used an X chromosome Elav Gal4 driver to drive the UAS-Mrj RNAi line and here we could not detect Mrj in the western. To address the reviewer’s point on the glial contribution towards expression of Mrj, we used a Glial driver Repo Gal4 to drive Mrj RNAi. In this experiment, we did not detect any difference in Mrj levels between the control and the Mrj RNAi line (presented now in Supplementary Figure 5G). We also used the Mrj knockout Gal4 line to drive NLS-GFP and immunostained these using a glial marker anti-Repo antibody. Here, we were able to detect cells colabelled by GFP as well as Repo, suggesting Mrj is likely to be present in the glial cells (presented now in Supplementary Figure 5H). We also looked in the literature and found a reference where it was shown that Elav protein as well as Elav Gal4 at earlier stages of development expresses in neuroblasts and in all Glia (Berger et al, 2007). So, another possibility is when we are driving Mrj RNAi using Elav Gal4, this knocks down Mrj in both the neurons as well as in the glia.
Fig 4-Colocalization of Orb2 with Mrj lacks controls. The quantification could describe other phenomena because the colocalization is robust but the numbers shown describe something else.
We have now added the intensity profile and colocalization quantitation (pearson’s coefficient) in Supplemental Figure 5A and B. This quantitation is done from multiple ROI’s taken from 4-6 cells. Also, to suggest the interaction of Orb2 isoforms with Mrj, we are not depending on colocalization alone and have used immunoprecipitation experiments to support our observations.
Fly behavior. The results shown for Mrj RNAi alleles is fine but it would be more robust if this was validated with the KO line AND rescued with Mrj overexpression.
We have now performed memory assays with the Mrj knockout. Our experiments showed Mrj knockouts to show significantly decreased memory in comparison to wild-type flies at 16 and 24-hour time points (presented in Figure 6B). We have not been able to make an Mrj Knockout-UAS Mrj recombinant fly, most likely due to the closeness of the two with respect to their genomic location in second chromosome.
Minor comments:
Please, revise minor errors, there are several examples of words together without a space.
We have identified the words without space and have corrected them now.
Intro: describe the use of functional prions. Starting the paragraph with this sentence and then explaining what prion diseases are is a little confusing. Also "prion proteins" can be confusing because the term refers to PrP, the protein found in prions.
We have now altered the introduction and have described functional prions.
Results, second subtitle in page 5. This sentence is quite confusing using prion-like twice
We have now changed the heading to “Drosophila Mrj converts Orb2A from non-prion to a prion-like state.”
Page 6: "conversion from non-prion to prion-like form...". This can be presented differently. Prion-like properties are intrinsic, proteins don't change from non-prion to prion-like. They may be oligomeric or monomeric or highly aggregated but the prion-like property doesn't change
We agree with the reviewer's point of Prion-like properties are intrinsic, but the protein might or might not exist in the prion-like state or confirmation. When we are using the term conversion from non-prion to prion-like form we mean to suggest a conformational conversion leading to the eventual formation of the oligomeric species. We also noted the terminology of non-prion to prion-like state change is used in several papers (Satpute-Krishnan & Serio, 2005; Sw & Yo, 2012; Uptain et al, 2001).
Scale bars and text are too small in several figures
We have now mentioned in the figure legends the size of the scale bars. For several images we have made the scale bars also larger.
Not sure why Fig 4C is supplemental, seems like an important piece of data.
We have kept this data in the supplemental data as we performed this experiment with recombinant protein which is tagged with 6X His and we are not sure if this high degree of oligomerization/aggregation of recombinant Mrj and further precipitation over time, happens inside the cells/ brain.
Intro to Mrj KO in page 7 is too long. Most of it belongs in the discussion
We have now moved the portions on mammalian DNAJB6 which were earlier in the results section to the discussions section.
Change red panels in IF to other color to make it easier for colorblind readers.
We have now changed the red panels to magenta. We apologize for our figures not being colorblind friendly earlier.
The discussion is a little diffuse by trying to compare Orb2 with mammalian prions and amyloids and yeast prions.
We looked into the functional prion data and couldn’t find much on chaperone mediated regulation of these. Also, we felt comparing with the amyloids and yeast prions brings out the contrast with respect to the Mrj mediated regulatory differences between the two.
Reviewer #3 (Significance (Required)):
This is a paper with a broad scope and approaches. The paper describes the role of Mrj in the oligomerization of Orb2 by protein biochemistry techniques and determine the role of loss of Mrj in the mushroom bodies in fly behavior.
The audience for this content is basic research and specialized. The role of Mrj in Orb2 aggregation and function sheds new light on the mechanisms regulating the function of this protein involved in a novel mechanism of learning and memory.
References:
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Berger C, Renner S, Lüer K & Technau GM (2007) The commonly used marker ELAV is transiently expressed in neuroblasts and glial cells in the Drosophila embryonic CNS. Dev Dyn 236: 3562–3568
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Hervas R, Rau MJ, Park Y, Zhang W, Murzin AG, Fitzpatrick JAJ, Scheres SHW & Si K (2020) Cryo-EM structure of a neuronal functional amyloid implicated in memory persistence in Drosophila. Science 367: 1230–1234
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Jana NR, Tanaka M, Wang G h & Nukina N (2000) Polyglutamine length-dependent interaction of Hsp40 and Hsp70 family chaperones with truncated N-terminal huntingtin: their role in suppression of aggregation and cellular toxicity. Hum Mol Genet 9: 2009–2018
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Kim S, Nollen EAA, Kitagawa K, Bindokas VP & Morimoto RI (2002) Polyglutamine protein aggregates are dynamic. Nat Cell Biol 4: 826–831
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Li S, Zhang P, Freibaum BD, Kim NC, Kolaitis R-M, Molliex A, Kanagaraj AP, Yabe I, Tanino M, Tanaka S, et al (2016b) Genetic interaction of hnRNPA2B1 and DNAJB6 in a Drosophila model of multisystem proteinopathy. Hum Mol Genet 25: 936–950
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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 submitted by Desai et al. identifies a chaperone of the Hsp40 family (Mrj) that binds Orb2 and modulates its oligomerization, which is critical for Orb2 function in learning and memory in Drosophila. Orb2 are proteins with prion-like properties whose oligomerization is critical for their function in the storage of memories. The main contribution of the article is the screen of Hsp40 and Hsp70-family proteins that bind Orb2. The authors show IP results for all the candidates tested, including those that bind Fig. 1) and those that don't (Supp Fig 3). There is also a figure devoted to examining the interaction of Mrj with polyglutamine models (Htt). They also generate a KO mutant that is viable and shows no gross defects or protein aggregation. Lastly, they show that the silencing of Mrj in the mushroom body gamma neurons results in weaker memories in a courtship paradigm. Although the data is consistent and generally supportive of the hypothesis, key details are missing in several areas, including controls. Additionally, the interpretation of some results leaves room for debate. Overall, this is an ambitious article that needs additional work before publication.
Specific comments:
- General concern over the interpretation of IP experiments and colocalization. These experiments don't necessarily reflect direct interactions. They are consistent with direct interaction but not the only explanation for a positive IP or colocalization.
- The Huntingtin section has a few concerns. The IF doesn't show all controls and the quantification is not well done in terms of what is relevant. A major problem is the interpretation of Fig 2F. The idea is that Mrj prevents the aggregation of Htt, which is the opposite of what is observed with Orb2. The panel actually shows a large Htt aggregate instead of multiple small aggregates. This has been reported before in Drosophila and other systems with different polyQ models. Mrj and other Hsp40 and Hsp70 proteins modify Htt aggregation, but in an unexpected way. This affects the model shown in Fig. 6H. Lastly, Fig 2H and 2I show very different level of total Htt.
- Endogenous expression of Mrj using Gal4 line: where else is it expressed in the brain / head and in muscle. Fig 3G shows no muscle abnormalities but no evidence is shown for muscle expression. It is nice that Fig 3E and F show no abnormal aggregates in the Mrj mutant, but this would be maybe more interesting if flies were subjected to some form of stress.
- Fig. 5B shows no Mrj detectable from head homogenates in flies silencing Mrj in neurons with Elav-Gal4. It would be nice if they could show that ONLY neurons express Mrj in the head. Also noted, Elav-Gal4 is a weak driver, so it is surprising that it can generate such robust loss of Mrj protein
- Fig 4-Colocalization of Orb2 with Mrj lacks controls. The quantification could describe other phenomena because the colocalization is robust but the numbers shown describe something else.
- Fly behavior. The results shown for Mrj RNAi alleles is fine but it would be more robust if this was validated with the KO line AND rescued with Mrj overexpression.
Minor comments:
Please, revise minor errors, there are several examples of words together without a space.
Intro: describe the use of functional prions. Starting the paragraph with this sentence and then explaining what prion diseases are is a little confusing. Also "prion proteins" can be confusing because the term refers to PrP, the protein found in prions.
Results, second subtitle in page 5. This sentence is quite confusing using prion-like twice
Page 6: "conversion from non-prion to prion-like form...". This can be presented differently. Prion-like properties are intrinsic, proteins don't change from non-prion to prion-like. They may be oligomeric or monomeric or highly aggregated but the prion-like property doesn't change
Scale bars and text are too small in several figures
Not sure why Fig 4C is supplemental, seems like an important piece of data.
Intro to Mrj KO in page 7 is too long. Most of it belongs in the discussion
Change red panels in IF to other color to make it easier for colorblind readers.
The discussion is a little diffuse by trying to compare Orb2 with mammalian prions and amyloids and yeast prions.
Significance
This is a paper with a broad scope and approaches. The paper describes the role of Mrj in the oligomerization of Orb2 by protein biochemistry techniques and determine the role of loss of Mrj in the mushroom bodies in fly behavior.
The audience for this content is basic research and specialized. The role of Mrj in Orb2 aggregation and function sheds new light on the mechanisms regulating the function of this protein involved in a novel mechanism of learning and memory.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
Summary:
The manuscript describes the role of the Hsp40 family protein Mrj in the prion-like oligomerization of Orb2. The authors demonstrate that Mrj promotes the oligomerization of Orb2, while a loss in Mrj diminishes the extent of Orb2 oligomerization. They observe that while Mrj is not an essential gene, a loss in Mrj causes deficiencies in the consolidation of long-term memory. Further, they demonstrate that Mrj associates with polysomes and increases the association of Orb2 with polysomes.
Major comments: None
Minor comments:
- In the section describing the chaperone properties of Mrj in clearing Htt aggregates (Fig 2), the legend describes that "Mrj-HA constructs are more efficient in decreasing Htt aggregation compared to Mrj-RFP". It would be helpful to add Mrj-RFP to the quantification in Fig 2G to know exactly the difference in efficiency. Is there an explanation for why the 2 constructs behave differently?
- Figs A, B, C, G need to have quantification of the percentage of colocalization with details about the number of cells quantified for each experiment.
- In Fig 6 B, C, F, G it would be helpful to label the 40S, 60S and 80S peaks in the A 254 trace.
- It's interesting that Mrj has opposing functions with regard to aggregation when comparing huntingtin with Orb2. From the literature presented in the discussion, it appears as though chaperones including Mrj have an anti-aggregation role for prions. It would be helpful to have more discussion around why, in the case of Orb2, this is different. The discussion states that "The only Hsp40 chaperone which was found similar to Mrj in increasing Orb2's oligomerization is the yeast Jjj2 protein" - this point needs elaboration, as well as a reference.
Significance
General assessment:
Overall, the work is clearly described and the manuscript is very well-written. The motivation behind the study and its importance are well-explained. I only have minor comments and suggestions to improve the clarity of the work. The study newly describes the interaction between the chaperone Mrj and the translation regulator Orb2. The experiments that the screen for proteins that interact with Orb2 and promote its oligomerization are very thorough. The experiments that delve into the role of Mrj in protein synthesis are a good start, and need to be explored further, but that is beyond the scope of this study.
Advance:
The study describes a new interaction between the chaperone Mrj and the translation regulator Orb2. The study is helpful in expanding our knowledge of prion regulators as well factors that affect memory acquisition and consolidation.
Audience:
This paper will be of most interest to basic researchers. My expertise is in Drosophila genetics and neuronal injury.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
In this MS, Mrj - a member of the JDP family of Hsp70 co-chaperones was identified as a regulator of the conversion of Orb2A (the Dm ortholog of CPEB) to its prion-like form.
In drosophila, Mrj deletion does not cause any gross neurodevelopmental defect nor leads to detectable alterations in protein homeostasis. Loss of Mrj, however, does lead to altered Orb2 oligomerization. Consistent with a role of prion-like characteristics of Orb2 in memory consolidation, loss of Mrj results in a deficit in long-term memory.
Aside from the fact that there are some unclarities related to the physicochemical properties of Orb2 and how Mrj affects this precisely, the finding that a chaperone could be important for memory is an interesting observation, albeit not entirely novel.
In addition, there are several minor technical concerns and questions I have that I feel the authors should address, including a major one related to the actual approach used to demonstrate memory deficits upon loss of Mrj.
Significance
Figure 1 (plus related Supplemental figures):
- There seem to be two isoforms of Mrj (like what has been found for human DNAJB6). I find it striking to see that only (preferentially?) the shorter isoform interacts with Orb2. For DNAJB6, the long isoform is mainly related to an NLS and the presumed substrate binding is identical for both isoforms. If this is true for Dm-Mrj too, the authors could actually use this to demonstrate the specificity of their IPs where Orb2 is exclusively non-nuclear?
- I would be interested to know a bit more about the other 5 JDPs that are interactors with Orb2: are the human orthologs of those known? It is striking that these other 5 JDPs interact with Orb2 in Dm (in IPs) but have no impact on Sup35 prion behavior. Importantly, this does not imply they may not have impact on the prion-like behavior of other Dm substrates, including Dm-Orb2.
- The data in panels H,I indeed suggest that Mrj1 alters the (size of) the oligomers. It would be important to know what is the actual physicochemical change that is occurring here. The observed species are insoluble in 0.1 % TX100 but soluble in 0.1% SDS, which suggest they could be gels, but not real amyloids such as formed by the polyQ proteins that require much higher SDS concentrations (~2%) to be solubilized. This is relevant as Mrj1 reduces polyQ amyloidogenesis whereas is here is shown to enhance Orb2A oligomerization/gelidification. In the same context, it is striking to see that without Mrj the amount of Orb2A seems drastically reduced and I wonder whether this might be due to the fact that in the absence of Mrj a part of Orb2A is not recovered/solubilized due to its conversion for a gel to a solid/amyloid state? In other words: Mrj1 may not promote the prion state, but prevents that state to become an irreversible, non-functional amyloid?
Figure 2 (plus related Supplemental figures):
- It may be good for clarity to refer to the human Mrj as DNAJB6 according to the HUGO nomenclature. Also, the first evidence for its oligomerization was by Hageman et al 2010.
- It is striking to see that Mrj co-IPs with Hsp70AA, Hsp70-4 but not Hsp70Cb. The fact that interactions were detected without using crosslinking is also striking given the reported transient nature of J-domain-Hsp70 interactions Together, this may even suggest that Mrj-1 is recognized as a Hsp70 substrate (for Hsp70AA, Hsp70-4 but not Hsp70Cb) rather than as a co-chaperone. In fact, a variant of Mrj-1 with a mutation in the HPD motif should be used to exclude this option.
- The rest of these data reconfirm nicely that Mrj/DNAJB6 can suppress polyQ-Htt aggregation. Yet note that in this case the oligomers that enter the agarose gel are smaller, not bigger. This argues that Mrj is not an enhancer of oligomerization, but rather an inhibitor of the conversion of oligomers to a more amyloid like state.
Figure 3:
- The finding that knockout of DNAJB6 in mice is embryonic lethal is related to a problem with placental development and not embryonic development (Hunter et al, 1999; Watson et al, 2007, 2009, 2011) as well recognized by the authors. Therefore, the finding that deletion of Dm-Mrj has no developmental phenotype in Drosophila may not be that surprising.
- It is a bit more surprising that Mrj knockout flies showed no aggregation phenotype or muscle phenotype, especially knowing that DNAJB6 mutations are linked to human diseases associated with aggregation (again well recognized by the authors). However, most of these diseases are late-onset and the phenotype may require stress to be revealed. So, while important to this MS in terms of not being a confounder for the memory test, I would like to ask the authors to add a note of caution that their data do not exclude that loss of Mrj activity still may cause a protein aggregation-related disease phenotype. Yet, I also do think that for the main message of this MS, it is not required to further test this experimentally.
Figure 4:
- IPs were done with Orb2A as bite and clearly pulled down substantial amounts of GFP-tagged Mrj. For interactions with Orb2B, a V5-tagged Mrj was use and only a minor fraction was pulled down. Why were two different Mrj constructs used for Arb2A and Orb2b?
- In addition, I think it would be important what one would see when pulling on Mrj1, especially under non-denaturing conditions and what is the status of the Orb2 that is than found to be associated with Mrj (monomeric, oligomeric and what size).
- This also relates to my remark at figure 1 and the subsequent fractionation experiments they show here in which there is a slight (not very convincing) increase in the ratio of TX100-soluble and insoluble (0.1% SDS soluble) material. My question would be if there is a remaining fraction of 0.1% insoluble (2% soluble) Orb2 and how Mrj affects that? As stated before, this is (only) mechanistically relevant to understanding why there is less oligomers of Orb2 in terms of Mrj either promoting it or by preventing it to transfer from a gel to a solid state. The link to the memory data remains intriguing, irrespective of what is going on (but also on those data I do have several comments: see below).
- I also find the sentence that "Mrj is probably regulating the oligomerization of endogenous Orb2 in the brain" somewhat an overstatement. I would rather prefer to say that the data show that Mrj1 affects the oligomeric behavior/status of Orb2.
Figure 5:
- To my knowledge, the Elav driver regulates expression in all neurons, but not in glial cells that comprise a significant part of the fly heads/brain. The complete absence of Mrj in the fly-heads when using this driver is therefore somewhat surprising. Or do we need to conclude from this that glial cells normally already lack Mrj expression?
- Why not use these lines also for the memory test for confirmation? I understand the concerns of putative confounding effects of a full knockdown (which were however not reported), but now data rely only on the mushroom body-specific knockdown for the 201Y Gal4 line, for which the knockdown efficiency is not provided. But even more so, here a temperature shift (22oC-30oC) was required to activate the expression of the siRNA. For the effects of this shift alone no controls were provided. The functional memory data are nice and consistent with the hypothesis, but can it be excluded that the temperature shift (rather than the Mrj) knockdown has caused the memory defects? I think it is crucial to include the proper controls or use a different knockdown approach that does not require temperature shifts or even use the knockout flies.
Figure 6:
The finding of a co-IP between Rpl18 and Mrj (one-directional only) by no means suffices to conclude that Mrj may interact with nascent Orb2 chains here (which would be the relevant finding here). The fact that Mrj is a self-oligomerising protein (also in vitro, so irrespective of ribosomal associations!), and hence is found in all fractions in a sucrose gradient, also is not a very strong case for its specific interaction with polysomes. The finding that there is just more self-oligomerizing Orb2A co-sedimenting with polysomes in sucrose gradients neither is evidence for a direct effect of Mrj enhancing association of Orb2A with the translating ribosomes even though it would fit the hypothesis. So all in all, I think the data in this figure and non-conclusive and the related conclusions should be deleted.
Overall, provided that proper controls/additional data can be provided for the key experiments of memory consolidation, I find this an intriguing study that would point towards a role of a molecular chaperone in controlling memory functions via regulating the oligomeric status of a prion-like protein and that is worthwhile publishing in a good journal.
However, in terms of mechanistical interpretations, several points have to be reconsidered (see remarks on figure 1,4); this pertains especially to what is discussed on page 13. In addition, I'd like the authors to put their data into the perspective of the findings that in differentiated neurons DNAJB6 levels actually decline, not incline (Thiruvalluvan et al, 2020), which would be counterintuitive if these proteins are playing a role as suggested here in memory consolidation.
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Reply to the reviewers
We thank the reviewers for their time and for the helpful comments. We felt the reviews overall were fair and quite positive. All three reviewers felt the manuscript could be of broad, general interest, especially given the relevance of the protein (Pbp1/ataxin-2) to neurodegenerative conditions and stress granule biology. Reviewer 3 seems to have some doubt there could be specificity for the types of transcripts regulated by Pbp1, given prior studies of mammalian ataxin-2 which implicated 16,000+ mRNAs that could bind via PAR-CLIP experiments! However, our study shows the power of utilizing a simpler model organism and thinking about the metabolic state of cells for elucidating the function of this interesting protein. Although our demonstration of the specificity of Pbp1 for regulating Puf3-target mRNAs involved in mitochondrial biogenesis and mitochondrial function may be surprising to this reviewer, we have the utmost confidence in our data and feel the study represents a highly significant finding that will be of interest to many researchers.
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)): *
*In this manuscript, van de Poll et al. aim to further establish the function of poly(A) binding protein-binding protein 1 (Pbp1) and its relationship to the RNA-binding protein Puf3 in regulating the expression of mitochondrial proteins. This work builds upon a solid body of previous studies from this group regarding the function of Puf3 and the role of Pbp1 in regulating TORC1 signaling. Here, the authors show that Pbp1 has a physical and functional interaction with Puf3 and that ablation or disruption of Pbp1 eliminates this interaction and reduces the expression of some Puf3 target proteins. This work provides reliable data supporting a role for Pbp1 in the regulation of mitochondrial protein expression and that there is a clear functional interaction between Puf3 and Pbp1. Nonetheless, there are several issues that should be addressed before the manuscript is suitable for publication. *
*1.) The model put forward suggests that Pbp1 works to recruit Puf3 to the vicinity of mitochondria, where Puf3 can then promote the expression of its target mRNAs. In Figure 3A, however, deletion of Pbp1 has a stronger affect on the expression of COX2 than deletion of Puf3 alone, which would not be expected if the role of Pbp1 is to modulate Puf3 function. Similarly, the expression of COX2 is higher in the double deletion versus the Pbp1 single deletion. The authors should attempt to clarify this experimentally, or at least make mention of alternative mechanisms for Pbp1 which may be causing this. *
We have mentioned alternative mechanisms in the text. We suggest that Puf3-target mRNAs also can be translated through Tom20, in the absence of Puf3 (p. 8, ref 18). In single deletion strains lacking Pbp1 (but with Puf3 present), Puf3 may direct some of its target mRNAs to decay pathways, leading to lower Cox2 expression compared to double deletion strains that also lack Puf3. We performed qPCR analysis of several Puf3-target and other mRNAs in pbp1∆puf3∆ double deletion strains and some transcripts (e.g., COX17) would support this possibility (Fig S4).
* 2.) The authors mention that the increased pull-down of Puf3 with Pbp1 in respiratory conditions suggests that the Pbp1-Puf3 interaction is responsive to the cellular metabolic state (Figure 3B). However, the increase in Puf3 expression makes it difficult to compare the interactions between the two conditions. *
Yes this is correct, we stated this in the legend of Fig 4B as: “Increased amounts of Puf3 are associated with Pbp1 in respiratory conditions.” We clarified in the text that Puf3 expression increases in respiratory conditions and this likely explains the increased pull-down of Puf3 with Pbp1 (p. 10).
* 3.) The authors only look at a very small subset of Puf3 target mRNAs using qPCR when it would be much more informative and overall convincing to examine a larger amount using RNA-seq experiments. *
We conducted an RNA-seq experiment to compare transcriptomes of WT vs pbp1∆ cells in fermentative (YPD) vs respiratory (YPL) conditions and observed mRNAs with functions associated with mito-translation and mito-respiration (i.e., Puf3-targets) to be most differentially expressed – and majority of these are lower in abundance in pbp1∆ cells (new Fig 2).
* 4.) The authors consistently mention that Pbp1 function is helping to stabilize Puf3 target mRNAs. However, if the authors wish to prove this particular mode-of-action, more direct evidence should be provided, such as a pulse-chase experiment. Otherwise, other models allowing for increased mRNA abundance should be noted. *
Using thiolutin which is the standard for such expts, we measured mRNA half-lives of several Puf3-target and other mRNAs (COX17, COX10, POR1, ACT1) by qPCR in WT vs pbp1∆ cells. However, these data turned out to be difficult to interpret, as several “control” mRNAs exhibited different decay profiles in pbp1∆ vs WT cells, and their behavior was different in respiratory conditions compared to what was reported in common glucose media. Nonetheless, the data are included as Fig S2, and the important observation is that each of the Puf3-target mRNAs tested behaves similarly following thiolutin treatment, compared to non Puf3-target mRNAs. Given that Puf3-target mRNAs were more stable in pbp1∆ cells (compared to PGK1) following thiolutin treatment, we have deleted the term “stabilize” throughout the text. The exact fate of these mRNAs in normal vs pbp1∆ mutant cells will require more sophisticated investigation in future studies.
* 5.) Given the proposed model, one would expect Puf3 to have reduced mRNA binding upon deletion of Pbp1. It would be interesting to examine Puf3 mRNA binding, perhaps through cross-linking immunoprecipitation (CLIP), to see if this indeed is the case. This would provide further direct evidence that Pbp1 is functioning through Puf3 and facilitating its function. Similarly, the authors mention that Pbp1 contains putative RNA binding domains, however, they make no mention if these domains may contribute to its function in mitochondrial protein expression. *
We performed an RNA-IP experiment to test whether Puf3 has reduced binding to its target mRNAs in the absence of Pbp1. In new Fig 7, Puf3 is still able to bind its mRNA targets in the absence of Pbp1. However, the association of Pbp1 with these mRNAs is reduced in puf3∆ knockouts. Such results are perhaps expected as Puf3 has been shown to bind in a sequence-specific manner to a ~8 nt motif in the 3’UTR of its target mRNAs. However, it is unclear whether the Lsm / LsmAD domains of Pbp1 actually bind RNAs directly (hence our use of the term “putative”) - they may be involved in protein-protein interactions. Moreover, Fig 5 shows that deletion of both domains has no apparent effect on mitochondrial protein expression. We prefer to address the role of the Lsm and LsmAD domains of Pbp1 in a future study.
* Reviewer #1 (Significance (Required)):
Overall, this manuscript provides a modest advance, but one that could prove to have important implications for the field-especially if the Pbp1 findings prove relevant to its human ortholog, ataxin-2. The advance is limited by the robustness of the specific molecular model proposed and the extent to which the Pbp1-Puf3 relationship is examined on the gene-expression level.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this manuscript, the authors found that the pbp1∆ mutant grew poorly on nonfermentable carbon source medium (YP Lactate medium) and that the pbp1∆ mutant had decreased amount of Cox2 protein, a cytochrome c oxidase. The pbp1∆ mutant also had decreased amounts of COX17, COX10, and MRP51 mRNAs. Since these mRNAs are target mRNAs of the RNA-binding protein Puf3, the authors next investigated the relationship between Pbp1 and Puf3. The analysis of the GFP reporter gene containing Puf3-binding sites in the 3' UTR showed that the levels of GFP reporter mRNA and protein were decreased in the pbp1∆ mutant strain. This reduction was dependent on the Puf3-binding site in the 3' UTR. Next, the authors examined the genetic interaction between the pbp1∆ and puf3∆ mutants, and found that the levels of Cox2 protein were reduced in the two mutants. Finally, the authors showed the interaction between Pbp1 and Puf3 by co-immunoprecipitation and determined the regions of Pbp1 and Puf3 required for the interaction. They also showed that these regions in Pbp1 and Puf3 proteins are also important for the regulation of Cox2 protein levels. The story is very clear and the data is reliable. However, the data from Western blotting should be shown quantitatively to make the results more reliable. Also, although the story is based on the reduction of Cox2 protein level, it would be better to discuss whether other proteins or mRNAs should be considered as well.
Major comments:
Figure 2C. Protein levels of GFP should be quantified and the data should be shown. *
These data have been quantified (now Fig 3C).
* Figure 3. Not only the Cox2 protein level but also mRNA levels of COX2, COX17, COX10, MRP51, etc in pbp1∆ mutant, puf3∆ mutant and pbp1∆ puf3∆ double mutant should be shown. Then the point of action of Pbp1 and Puf3 would become clearer. *
The mRNA levels have been determined by qPCR and are now in Fig S4.
Figure 4. * For the domain analysis of Pbp1 protein, showing differences in cell proliferation as in Figure 1B would indicate the physiological importance of the domain. *
Growth curves of the various Pbp1 domain deletions have been performed and shown in Fig 5D. They do support the physiological importance of the domain(s).
* Figure 4B. Quantification of the amount of co-immunoprecipitated proteins would indicate the strength of binding. *
These data have been quantified (now Fig 5B).
* Figure 4C. Protein levels should be quantified and the data presented. *
These data have been quantified (now Fig 5C).
* Line 153-8 The description of Line 153-8 is not appropriate for this position because it breaks up the flow of the story before and after. *
These text have been moved as requested.
* Minor comments:
Line 153 Isn't the following the first reference cited for Pbp1 is a negative regulator of TORC1? Transient sequestration of TORC1 into stress granules during heat stress Terunao Takahara 1, Tatsuya Maeda Mol Cell. 2012 Jul 27;47(2):242-52. doi: 10.1016/j.molcel.2012.05.019. Epub 2012 Jun 21.
Ref19. Ref 19 also shows that the pbp1∆ mutant strains grow poorly on the medium containing glycerol and lactate as carbon sources.
Overall, the gene is not italicized. *
These requested edits to the references and text have been made in the revised version of the manuscript.
* Reviewer #2 (Significance (Required)):
This manuscript analyzes the relationship between Pbp1 and Puf3 in yeast. Since these proteins are evolutionarily conserved from yeast to humans and are also associated with disease in humans, this reviewer believes this manuscript will be of interest to a wide audience. *
Reviewer #3 (Evidence, reproducibility and clarity (Required)): *
In this study, van de Poll et al. describe the involvement of a cytosolic RNA-binding protein (Pbp1) in the transcriptional regulation of mitochondrial biogenesis during the shift from fermentative to respiratory growth in budding yeast. Using the advantage of yeast genetics and molecular biology, they show that a number of mitochondrial transcripts and proteins are downregulated in pbp1Δ cells both under normal growth conditions and during respiratory shift. Since Puf3, another RNA-binding protein, is known to regulate the fate of these transcripts, they further investigate the interaction between Pbp1 and Puf3. Through a series of biochemical assays, they characterize the interaction between Pbp1 and Puf3 taking place through their low-complexity domains, which is suggested by authors to stabilize and promote the translation of Puf3-target transcripts.
As stated in the manuscript, Pbp1 is an evolutionarily conserved protein, encoded by ATXN2 gene in humans. Due to its involvement in multiple neurological disorders, it has been widely studied in mouse models and patient samples. The transcriptome profiles of Atxn2-KO mouse liver and cerebellum have been published (albeit having used a relatively older microarray technology for today's standards), revealing a prominent dysregulation of global translational machinery, and the ER-protein secretion pathway (Fittschen et al., 2015). These findings were followed by numerous studies showing dysregulations of distinct transcript pools under examination. Moreover, a PAR-CLIP study showed ATXN2 to associate with ~16.000 transcripts, 8000 of which depended on its interaction with PABPC1 (Yokoshi et al., 2014). In that study, ATXN2 was shown to preferentially bind to target transcripts on 3'-UTR AU-rich sequences. In addition to PABPC1, some other RNA-binding proteins, like TDP-43, were also shown to modulate the indirect interaction of ATXN2 with transcripts, while it also maintained direct interactions through its Lsm and LsmAD domains. Altogether, the mammalian data on ATXN2 thus far depicts it as an avid interactor of numerous RNA-binding proteins and countless transcripts, including microRNAs. The authors however have not cited or compared their findings with this vast array of mammalian literature (with the exception of two properly discussed papers in Discussion).
Considering its stress-responsive nature and association with RNP granules, it is plausible to assume that ATXN2/Pbp1 could regulate certain groups of transcripts in terms of their stability (in stress granules and p-bodies) or active translation under given environmental conditions and cellular state. The work of van de Poll et al. in this regard is an important step in expanding our knowledge about the many downstream effects of ATXN2/Pbp1. Yet, the following issues should be solved:
1) The pre-eminence of the proposed group of affected transcripts (i.e. those associated with mitochondrial biogenesis) has to be empirically established. Among all its interactions with other RNA-binding proteins, how important or dominant is the interaction of Pbp1 with Puf3 for mitochondrial biogenesis during the shift towards respiratory growth? Line 74 in the Results says "Analysis of a panel of nuclear- and mitochondrial-encoded mRNAs..."; how broad was this panel? how were the genes selected? Considering the fact that ATXN2/Pbp1 is associated with an immense number of transcripts, hand-picking a number of Puf3 targets and selectively analyzing their expression will surely give some significant dysregulations. Therefore, an unbiased transcriptomic survey is necessary to see all Pbp1-dependent dysregulations during respiratory shift. Since it's a process that requires heavy mitogenesis, one can assume that many dysregulations will concern mitochondrial factors. Indeed, proteome surveys in Atxn2-KO mouse tissues and pbp1Δ yeast (under fermentative growth and stress) point out to a strong mitochondrial dysregulation, so it raises hopes to see an even stronger Pbp1 impact during the respiratory shift in yeast. Then, bioinformatic analyses can reveal what proportion of those are Puf3 targets. If the authors' premise is valid, then the Puf3-targets will stand out in the transcriptome data, and give them an unbiased, solid and much stronger base for the following interaction analyses. They can then compare this dataset to the readily available mouse transcriptome from Atxn2-KO or polyQ-disease models, and strengthen their hypothesis about ATXN2/Pbp1 regulating mitochondrial biogenesis in association with Puf3.
The Results text about Figure 1 in its current state is an overstatement of the available data. Line 81-84 suggests mitochondrially encoded Cox2 levels are reduced because some mitoribosome subunits are Puf3 targets, but pbp1Δ itself is known to have altered mitochondrial membrane potential which negatively impacts mitochondrial import. So, the reduction of Cox2 levels (and potentially other mitochondrial-encoded proteins, it was never checked) may have nothing to do with Puf3, but rather be a direct consequence of reduced mitoribosome import in pbp1Δ. In order to make this statement, the total mitochondrial translation rates of WT and pbp1Δ strains would have to be compared, and if they are found the same, a selective effect on Puf3-target proteins has to be shown among many tested candidates. Same applies to line 86 "the specific decrease in Puf3-target mRNAs in pbp1Δ cells" referring to Figure 3C. This statement cannot be made without analyzing a larger group of transcripts including the targets of other RNA-binding proteins. The current data does not support any specific dysregulation of Puf3-targets, it just shows some Puf3 targets to be dysregulated, however without the knowledge of how many significant among all Puf3-targets, or how significant are Puf3-targets compared to others. An unbiased, high-throughput transcriptome data, and detailed bioinformatic analyses should replace Figure 1C. The high variation among replicates at 1h-3h-5h time points is also alarming, and puts the reproducibility of these experiments under question. *
As mentioned in the response to Reviewer 1, we performed an unbiased RNA-seq experiment comparing transcriptomes of WT vs pbp1∆ cells. The data are quite striking and strongly support our hypothesis (new Fig 2). To address the reviewer’s concern that pbp1∆ phenotypes may be due to altered mito membrane potential and mito protein import, we have performed an experiment to examine import of Cox4, which is a protein substrate that is commonly used for this purpose (note COX4 is not a Puf3-target mRNA). Steady-state Cox4 protein amounts are similar in WT vs pbp1∆ cells. Moreover, following treatment of cells with the uncoupler CCCP, there is more of the “pre”-processed Cox4 form in WT cells compared to pbp1∆ cells. These data would argue against the reviewer’s hypothesis and are included in the revised manuscript as Fig S1. Since every mitochondrial ribosomal subunit gene transcript is a target of Puf3 (PMID: 16254148) and therefore subject to regulation by Pbp1, we would argue that a defect in mito biogenesis (due to compromised translation of these mRNAs) precedes and may explain any subsequent defect in mito membrane potential. *
2) Stabilization of mRNAs The basal reduction in the mRNA levels of the reporter construct in pbp1Δ is a strong but not necessarily direct evidence of stabilization by Pbp1. mRNA half-life analyses (i.e. degradation curves) should be performed with desired targets to measure stability in WT and pbp1Δ strains. *
As mentioned above in the response to Reviewer 1, we performed mRNA half-life analyses for several transcripts in WT vs pbp1∆ strains using thiolutin treatment. The results are not straightforward to interpret as loss of Pbp1 led to a stabilization of Puf3-target mRNAs (relative to PGK1), however all Puf3-target mRNAs that we examined exhibited similar decay profiles. Thus, we deleted the term “stabilize” and further determination of the fate of these mRNAs in the absence of new transcription will require more careful and sophisticated experiments.*
3) Cox2 levels Regarding Line 125: "Cox2 protein levels, which are dependent on the translation of Puf3-target mRNAs": This may be generally true, but the data here suggests otherwise. pbp1Δ cells have completely diminished Cox2 levels, whereas puf3Δ have approx. 50% reduction. This means that Pbp1 is more important to maintain normal Cox2 levels, and does so independent of Puf3. In contrast, puf3Δ "rescues" some of the defect in pbp1Δ cells and increases Cox2 abundance to ~50%. As stated above, Cox2 reduction in pbp1Δ could be a direct consequence of mitochondrial membrane depolarization unrelated to Puf3, and could be accompanied by many other non-Puf3-targets being downregulated. Therefore, the authors should refrain from "Cox2 levels are dependent on the translation of Puf3-target mRNAs" statements throughout the text without an experimental proof in the context of pbp1Δ strain. *
See response to Reviewer 1. We believe that in the absence of Pbp1, Puf3 may now preferentially promote decay of various mito biogenesis transcripts, leading to apparently lower Cox2 levels. Moreover, per the results of our Cox4 experiment (Fig S1), we would respectfully disagree with the reviewer’s hypothesis. Nonetheless, we included an additional statement that mitochondrial membrane depolarization, as a consequence of reduced expression of numerous Puf3-targets, could also contribute to lower Cox2 abundance (p. 6 and 15). *
4) Pbp1-Puf3 interaction The authors state that Pbp1-Puf3 interaction is required for Puf3-target mRNA stabilization and translation. This suggests that Pbp1 stabilizes this pool of mRNAs because of its interaction with Puf3 primarily, not the mRNAs themselves. One general question while studying the interaction between two RNA-binding proteins is whether they interact in an RNA-dependent manner in vivo. The co-IP analyses show the interaction between Pbp1 and Puf3 to increase under respiratory shift as expected. However, in co-IPs from cell lysates, many RNA-binding proteins may seemingly interact due to their association with translation machinery at that given time. But this does not mean "direct" protein-protein interaction, just a co-existence around actively translating ribosomes. In order to ensure the direct interaction of these two proteins, the same co-IPs should be performed with/out RNase treatment of the lysate (many protocols available online). Only if Pbp1-Puf3 interaction persists in RNase+ samples, they can conclude a direct interaction. In addition, RNA-immunoprecipitation analyses should be performed in Pbp1-Flag and Pbp1-Flag/ puf3Δ strains to check if the association of Pbp1 with Puf3-target mRNAs indeed depends on Puf3. *
This is a good suggestion. We performed an experiment to test whether RNase treatment alters interaction between Pbp1 and Puf3 and there was minimal effect, supporting the hypothesis that the interaction may be direct. We also performed RNA-IP of Pbp1 in the presence of absence of Puf3 (new Fig 7). As the reviewer predicted, the RNA-IP enrichment of Puf3-target mRNAs was reduced in puf3∆ strains, suggesting that the association of Pbp1 with such transcripts depends on Puf3. It is known from work by others that Puf3 contains a PUF domain that enables sequence-specific binding to a motif in the 3’UTR of its target mRNAs, so these results are quite sensible.
* Minor comments: • Second sentence of the Abstract ("How mutations in its mammalian ortholog ataxin-2 are linked to neurodegenerative conditions remains unclear") is semantically incorrect. The term "linked" suggests an observed but uncharacterized effect of a genetic variation on a certain syndrome. Diseases can be linked to a chromosome or a locus without knowing the exact causative mutation. How the CAG repeat expansion mutations in ATXN2 are causative of SCA2, ALS or Parkinson-plus syndromes are very well known. One should also be careful with using "mutations" as a general term in the context of ATXN2, because there are certain variations in and around ATXN2 locus leading to a decrease in its activity and metabolic problems, which is far from its neurodegeneration-causing mutations. If the authors meant to state that the pathological mechanism is unclear by this sentence, that would also be a negligence of the extensive literature around this topic. Multiple disease models in mouse, Drosophila and C. elegans collectively point out to an RNA metabolism deficit, caused by toxic ATXN2 aggregates that sequestrate other RNA-binding proteins and their target transcripts. The specific downstream effects involve synaptic strength, Calcium-related action potentials, ER stress and cholesterol/sphingolipid synthesis. Therefore, this sentence could be rephrased to "PolyQ expansion mutations in its mammalian ortholog ataxin-2 lead to spinocerebellar dysfunction due to toxic protein aggregation." and simply avoid going into mechanistic details as it is not necessary for this manuscript.
• Lines 241-243: "Human sequencing" is also an incorrect term. Can be rephrased to "PolyQ expansion mutations in ATXN2 are associated with SCA2 and ALS". The references 22-24 are the first association of polyQ mutations with SCA2, however a reference for ALS is missing. Elden et al. Nature 2010 should be cited here.
• The authors should discuss the relevance of these findings to the mammalian ortholog of Pum3, namely PUM1/2. Afterall, it is also a very important conserved protein and well-studied in mammalian literature. *
These changes to the text and references have been made.
* Following a better characterization of the transcript pools selectively affected by Pbp1 (meaning a transcriptome survey), a graphical abstract sort of scheme could be useful in putting the findings in perspective and conveying the message.*
We decided not to include a graphical abstract at this time, since it is difficult for us to “picture” what is going on inside an Pbp1-containing RNP granule at this time. * Reviewer #3 (Significance (Required)):
The intricate experiments characterizing the nature of interaction between Pbp1 and Puf3 (Figures 3B, 4, 5, 6) are quite convincing. However, some fundamental questions remain especially regarding the primary rationale of studying Pbp1-Puf3 relationship and the breadth of some conclusions. The data are of general interest to a broad audience. The statistical tests in Figure 1 are of concern. The reviewer(s) has experience both with yeast molecular biology and with mammalian Atxn2 function. *
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Referee #3
Evidence, reproducibility and clarity
In this study, van de Poll et al. describe the involvement of a cytosolic RNA-binding protein (Pbp1) in the transcriptional regulation of mitochondrial biogenesis during the shift from fermentative to respiratory growth in budding yeast. Using the advantage of yeast genetics and molecular biology, they show that a number of mitochondrial transcripts and proteins are downregulated in pbp1Δ cells both under normal growth conditions and during respiratory shift. Since Puf3, another RNA-binding protein, is known to regulate the fate of these transcripts, they further investigate the interaction between Pbp1 and Puf3. Through a series of biochemical assays, they characterize the interaction between Pbp1 and Puf3 taking place through their low-complexity domains, which is suggested by authors to stabilize and promote the translation of Puf3-target transcripts.
As stated in the manuscript, Pbp1 is an evolutionarily conserved protein, encoded by ATXN2 gene in humans. Due to its involvement in multiple neurological disorders, it has been widely studied in mouse models and patient samples. The transcriptome profiles of Atxn2-KO mouse liver and cerebellum have been published (albeit having used a relatively older microarray technology for today's standards), revealing a prominent dysregulation of global translational machinery, and the ER-protein secretion pathway (Fittschen et al., 2015). These findings were followed by numerous studies showing dysregulations of distinct transcript pools under examination. Moreover, a PAR-CLIP study showed ATXN2 to associate with ~16.000 transcripts, 8000 of which depended on its interaction with PABPC1 (Yokoshi et al., 2014). In that study, ATXN2 was shown to preferentially bind to target transcripts on 3'-UTR AU-rich sequences. In addition to PABPC1, some other RNA-binding proteins, like TDP-43, were also shown to modulate the indirect interaction of ATXN2 with transcripts, while it also maintained direct interactions through its Lsm and LsmAD domains. Altogether, the mammalian data on ATXN2 thus far depicts it as an avid interactor of numerous RNA-binding proteins and countless transcripts, including microRNAs. The authors however have not cited or compared their findings with this vast array of mammalian literature (with the exception of two properly discussed papers in Discussion).
Considering its stress-responsive nature and association with RNP granules, it is plausible to assume that ATXN2/Pbp1 could regulate certain groups of transcripts in terms of their stability (in stress granules and p-bodies) or active translation under given environmental conditions and cellular state. The work of van de Poll et al. in this regard is an important step in expanding our knowledge about the many downstream effects of ATXN2/Pbp1. Yet, the following issues should be solved:
- The pre-eminence of the proposed group of affected transcripts (i.e. those associated with mitochondrial biogenesis) has to be empirically established. Among all its interactions with other RNA-binding proteins, how important or dominant is the interaction of Pbp1 with Puf3 for mitochondrial biogenesis during the shift towards respiratory growth? Line 74 in the Results says "Analysis of a panel of nuclear- and mitochondrial-encoded mRNAs..."; how broad was this panel? how were the genes selected? Considering the fact that ATXN2/Pbp1 is associated with an immense number of transcripts, hand-picking a number of Puf3 targets and selectively analyzing their expression will surely give some significant dysregulations. Therefore, an unbiased transcriptomic survey is necessary to see all Pbp1-dependent dysregulations during respiratory shift. Since it's a process that requires heavy mitogenesis, one can assume that many dysregulations will concern mitochondrial factors. Indeed, proteome surveys in Atxn2-KO mouse tissues and pbp1Δ yeast (under fermentative growth and stress) point out to a strong mitochondrial dysregulation, so it raises hopes to see an even stronger Pbp1 impact during the respiratory shift in yeast. Then, bioinformatic analyses can reveal what proportion of those are Puf3 targets. If the authors' premise is valid, then the Puf3-targets will stand out in the transcriptome data, and give them an unbiased, solid and much stronger base for the following interaction analyses. They can then compare this dataset to the readily available mouse transcriptome from Atxn2-KO or polyQ-disease models, and strengthen their hypothesis about ATXN2/Pbp1 regulating mitochondrial biogenesis in association with Puf3.
The Results text about Figure 1 in its current state is an overstatement of the available data. Line 81-84 suggests mitochondrially encoded Cox2 levels are reduced because some mitoribosome subunits are Puf3 targets, but pbp1Δ itself is known to have altered mitochondrial membrane potential which negatively impacts mitochondrial import. So, the reduction of Cox2 levels (and potentially other mitochondrial-encoded proteins, it was never checked) may have nothing to do with Puf3, but rather be a direct consequence of reduced mitoribosome import in pbp1Δ. In order to make this statement, the total mitochondrial translation rates of WT and pbp1Δ strains would have to be compared, and if they are found the same, a selective effect on Puf3-target proteins has to be shown among many tested candidates. Same applies to line 86 "the specific decrease in Puf3-target mRNAs in pbp1Δ cells" referring to Figure 3C. This statement cannot be made without analyzing a larger group of transcripts including the targets of other RNA-binding proteins. The current data does not support any specific dysregulation of Puf3-targets, it just shows some Puf3 targets to be dysregulated, however without the knowledge of how many significant among all Puf3-targets, or how significant are Puf3-targets compared to others. An unbiased, high-throughput transcriptome data, and detailed bioinformatic analyses should replace Figure 1C. The high variation among replicates at 1h-3h-5h time points is also alarming, and puts the reproducibility of these experiments under question. 2. Stabilization of mRNAs The basal reduction in the mRNA levels of the reporter construct in pbp1Δ is a strong but not necessarily direct evidence of stabilization by Pbp1. mRNA half-life analyses (i.e. degradation curves) should be performed with desired targets to measure stability in WT and pbp1Δ strains. 3. Cox2 levels Regarding Line 125: "Cox2 protein levels, which are dependent on the translation of Puf3-target mRNAs": This may be generally true, but the data here suggests otherwise. pbp1Δ cells have completely diminished Cox2 levels, whereas puf3Δ have approx. 50% reduction. This means that Pbp1 is more important to maintain normal Cox2 levels, and does so independent of Puf3. In contrast, puf3Δ "rescues" some of the defect in pbp1Δ cells and increases Cox2 abundance to ~50%. As stated above, Cox2 reduction in pbp1Δ could be a direct consequence of mitochondrial membrane depolarization unrelated to Puf3, and could be accompanied by many other non-Puf3-targets being downregulated. Therefore, the authors should refrain from "Cox2 levels are dependent on the translation of Puf3-target mRNAs" statements throughout the text without an experimental proof in the context of pbp1Δ strain. 4. Pbp1-Puf3 interaction The authors state that Pbp1-Puf3 interaction is required for Puf3-target mRNA stabilization and translation. This suggests that Pbp1 stabilizes this pool of mRNAs because of its interaction with Puf3 primarily, not the mRNAs themselves. One general question while studying the interaction between two RNA-binding proteins is whether they interact in an RNA-dependent manner in vivo. The co-IP analyses show the interaction between Pbp1 and Puf3 to increase under respiratory shift as expected. However, in co-IPs from cell lysates, many RNA-binding proteins may seemingly interact due to their association with translation machinery at that given time. But this does not mean "direct" protein-protein interaction, just a co-existence around actively translating ribosomes. In order to ensure the direct interaction of these two proteins, the same co-IPs should be performed with/out RNase treatment of the lysate (many protocols available online). Only if Pbp1-Puf3 interaction persists in RNase+ samples, they can conclude a direct interaction. In addition, RNA-immunoprecipitation analyses should be performed in Pbp1-Flag and Pbp1-Flag/ puf3Δ strains to check if the association of Pbp1 with Puf3-target mRNAs indeed depends on Puf3.
Minor comments:
- Second sentence of the Abstract ("How mutations in its mammalian ortholog ataxin-2 are linked to neurodegenerative conditions remains unclear") is semantically incorrect. The term "linked" suggests an observed but uncharacterized effect of a genetic variation on a certain syndrome. Diseases can be linked to a chromosome or a locus without knowing the exact causative mutation. How the CAG repeat expansion mutations in ATXN2 are causative of SCA2, ALS or Parkinson-plus syndromes are very well known. One should also be careful with using "mutations" as a general term in the context of ATXN2, because there are certain variations in and around ATXN2 locus leading to a decrease in its activity and metabolic problems, which is far from its neurodegeneration-causing mutations. If the authors meant to state that the pathological mechanism is unclear by this sentence, that would also be a negligence of the extensive literature around this topic. Multiple disease models in mouse, Drosophila and C. elegans collectively point out to an RNA metabolism deficit, caused by toxic ATXN2 aggregates that sequestrate other RNA-binding proteins and their target transcripts. The specific downstream effects involve synaptic strength, Calcium-related action potentials, ER stress and cholesterol/sphingolipid synthesis. Therefore, this sentence could be rephrased to "PolyQ expansion mutations in its mammalian ortholog ataxin-2 lead to spinocerebellar dysfunction due to toxic protein aggregation." and simply avoid going into mechanistic details as it is not necessary for this manuscript.
- Lines 241-243: "Human sequencing" is also an incorrect term. Can be rephrased to "PolyQ expansion mutations in ATXN2 are associated with SCA2 and ALS". The references 22-24 are the first association of polyQ mutations with SCA2, however a reference for ALS is missing. Elden et al. Nature 2010 should be cited here.
- The authors should discuss the relevance of these findings to the mammalian ortholog of Pum3, namely PUM1/2. Afterall, it is also a very important conserved protein and well-studied in mammalian literature.
- Following a better characterization of the transcript pools selectively affected by Pbp1 (meaning a transcriptome survey), a graphical abstract sort of scheme could be useful in putting the findings in perspective and conveying the message.
Significance
The intricate experiments characterizing the nature of interaction between Pbp1 and Puf3 (Figures 3B, 4, 5, 6) are quite convincing. However, some fundamental questions remain especially regarding the primary rationale of studying Pbp1-Puf3 relationship and the breadth of some conclusions. The data are of general interest to a broad audience.<br /> The statistical tests in Figure 1 are of concern. The reviewer(s) has experience both with yeast molecular biology and with mammalian Atxn2 function.
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, the authors found that the pbp1∆ mutant grew poorly on nonfermentable carbon source medium (YP Lactate medium) and that the pbp1∆ mutant had decreased amount of Cox2 protein, a cytochrome c oxidase. The pbp1∆ mutant also had decreased amounts of COX17, COX10, and MRP51 mRNAs. Since these mRNAs are target mRNAs of the RNA-binding protein Puf3, the authors next investigated the relationship between Pbp1 and Puf3. The analysis of the GFP reporter gene containing Puf3-binding sites in the 3' UTR showed that the levels of GFP reporter mRNA and protein were decreased in the pbp1∆ mutant strain. This reduction was dependent on the Puf3-binding site in the 3' UTR. Next, the authors examined the genetic interaction between the pbp1∆ and puf3∆ mutants, and found that the levels of Cox2 protein were reduced in the two mutants. Finally, the authors showed the interaction between Pbp1 and Puf3 by co-immunoprecipitation and determined the regions of Pbp1 and Puf3 required for the interaction. They also showed that these regions in Pbp1 and Puf3 proteins are also important for the regulation of Cox2 protein levels.
The story is very clear and the data is reliable. However, the data from Western blotting should be shown quantitatively to make the results more reliable. Also, although the story is based on the reduction of Cox2 protein level, it would be better to discuss whether other proteins or mRNAs should be considered as well.
Major comments:
Figure 2C.
Protein levels of GFP should be quantified and the data should be shown.
Figure 3.
Not only the Cox2 protein level but also mRNA levels of COX2, COX17, COX10, MRP51, etc in pbp1∆ mutant, puf3∆ mutant and pbp1∆ puf3∆ double mutant should be shown. Then the point of action of Pbp1 and Puf3 would become clearer.
Figure 4.
For the domain analysis of Pbp1 protein, showing differences in cell proliferation as in Figure 1B would indicate the physiological importance of the domain.
Figure 4B.
Quantification of the amount of co-immunoprecipitated proteins would indicate the strength of binding.
Figure 4C.
Protein levels should be quantified and the data presented.
Line 153-8
The description of Line 153-8 is not appropriate for this position because it breaks up the flow of the story before and after.
Minor comments:
Line 153
Isn't the following the first reference cited for Pbp1 is a negative regulator of TORC1? Transient sequestration of TORC1 into stress granules during heat stress Terunao Takahara 1, Tatsuya Maeda Mol Cell. 2012 Jul 27;47(2):242-52. doi: 10.1016/j.molcel.2012.05.019. Epub 2012 Jun 21.
Ref19.
Ref 19 also shows that the pbp1∆ mutant strains grow poorly on the medium containing glycerol and lactate as carbon sources.
Overall, the gene is not italicized.
Significance
This manuscript analyzes the relationship between Pbp1 and Puf3 in yeast. Since these proteins are evolutionarily conserved from yeast to humans and are also associated with disease in humans, this reviewer believes this manuscript will be of interest to a wide audience.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, van de Poll et al. aim to further establish the function of poly(A) binding protein-binding protein 1 (Pbp1) and its relationship to the RNA-binding protein Puf3 in regulating the expression of mitochondrial proteins. This work builds upon a solid body of previous studies from this group regarding the function of Puf3 and the role of Pbp1 in regulating TORC1 signaling. Here, the authors show that Pbp1 has a physical and functional interaction with Puf3 and that ablation or disruption of Pbp1 eliminates this interaction and reduces the expression of some Puf3 target proteins. This work provides reliable data supporting a role for Pbp1 in the regulation of mitochondrial protein expression and that there is a clear functional interaction between Puf3 and Pbp1. Nonetheless, there are several issues that should be addressed before the manuscript is suitable for publication.
- The model put forward suggests that Pbp1 works to recruit Puf3 to the vicinity of mitochondria, where Puf3 can then promote the expression of its target mRNAs. In Figure 3A, however, deletion of Pbp1 has a stronger affect on the expression of COX2 than deletion of Puf3 alone, which would not be expected if the role of Pbp1 is to modulate Puf3 function. Similarly, the expression of COX2 is higher in the double deletion versus the Pbp1 single deletion. The authors should attempt to clarify this experimentally, or at least make mention of alternative mechanisms for Pbp1 which may be causing this.
- The authors mention that the increased pull-down of Puf3 with Pbp1 in respiratory conditions suggests that the Pbp1-Puf3 interaction is responsive to the cellular metabolic state (Figure 3B). However, the increase in Puf3 expression makes it difficult to compare the interactions between the two conditions.
- The authors only look at a very small subset of Puf3 target mRNAs using qPCR when it would be much more informative and overall convincing to examine a larger amount using RNA-seq experiments.
- The authors consistently mention that Pbp1 function is helping to stabilize Puf3 target mRNAs. However, if the authors wish to prove this particular mode-of-action, more direct evidence should be provided, such as a pulse-chase experiment. Otherwise, other models allowing for increased mRNA abundance should be noted.
- Given the proposed model, one would expect Puf3 to have reduced mRNA binding upon deletion of Pbp1. It would be interesting to examine Puf3 mRNA binding, perhaps through cross-linking immunoprecipitation (CLIP), to see if this indeed is the case. This would provide further direct evidence that Pbp1 is functioning through Puf3 and facilitating its function. Similarly, the authors mention that Pbp1 contains putative RNA binding domains, however, they make no mention if these domains may contribute to its function in mitochondrial protein expression.
Significance
Overall, this manuscript provides a modest advance, but one that could prove to have important implications for the field-especially if the Pbp1 findings prove relevant to its human ortholog, ataxin-2. The advance is limited by the robustness of the specific molecular model proposed and the extent to which the Pbp1-Puf3 relationship is examined on the gene-expression level.
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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 Naeli et al., presents study on effects of SARS-CoV-2 NSP2 protein on miRNA mediated translational repression. Authors show in multiple ways using reporter mRNAs with various miRNA sites that NSP2 protein stimulates miRNA mediated repression. The increase in miRNA repression is likely due to the interaction of NSP2 with either GIGYF2 or Argonaute protein directly thus making more stable repressive complex on mRNA. The manuscript is written clearly and methods provide enough details for reproducibility. Only major comment would be that authors could have tested multiple endogenous targets of miRNAs for extent of miRNA mediated expression in the presence of NSP2. This could be achieved using either western blots for known targets (looking at protein levels) or using targeted qRT-PCR or distribution of mRNAs in polysome fractions (mRNA translational repression. An alternative would be Ribo-Seq experiment.
Minor comment:
Line in introduction arguing: "The GIGYF2/4EHP complex is recruited by a variety of factors including miRNAs" should state miRISC instead of miRNAs.
Significance
General assessment: The study presents sold evidence that NSP2 protein interacts with miRISC complex and increases miRNA-mediated translational repression of reporter mRNAs. Multiple target sites for miR20, let7 and miR92 are tested as well as two different human cell lines (Hek293 and U87) which gives strength to study and reproducibility of the results. Focus on the endogenous miRNA targets in the presence or absence of the NSP2 protein would make study even stronger.
The advance of the study is more rigorous analyses of NSP2 protein effects on miRNA-mediated gene expression regulation with some novel mechanistic insights. The study will be of interest for specialized and basic research audience with potential impact on translational research.
My field of expertise covers mechanisms of gene expression regulation by miRNAs and RBPs as well as impact of mRNAs, nascent peptides and ribosomes on protein synthesis.
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Referee #2
Evidence, reproducibility and clarity
In this study, Naeli and collaborators propose a role for the SARS-CoV2 protein NSP2 in the miRNA-mediated translational repression. Their data show that NSP2 co-immunoprecipitate with the Argonaute AGO2 and the previously reported translation modulator GIGYF2. Using different reporters sensitive to miRNA repression, they show that overexpressing NSP2 enhances miRNA-mediated translational repression in different cell lines as well as one endogenous miRNA target CDK1 and thus without affecting the stability of targeted mRNAs. Interestingly, their data show that the effect of NSP2 depends on the number of miRNA binding sites suggesting that highly repressed mRNAs, due to the presence of several miRNA binding sites, are not affected by NSP2. Finally, using an AGO2 tethering reporter assay that does not rely on miRNA binding but needs two NSP2 interactors GIGYF2 and 4EHP, they demonstrate that overexpressing NSP2 still stimulates mRNA repression, suggesting that NSP2 can have a broader impact on miRISC-dependent silencing.
Overall, this is an interesting follow-up study from their previous paper (Xu et al., 2022) that have the potential to add another dimension to the modulation of mRNA translation by the SARS-CoV2 protein NSP2. But unfortunately, in its current form, the work falls short of supporting their claims appropriately and providing sufficient and relevant insights about the role of NSP2 in regulating the miRNA-mediate gene regulation. To overcome this, the authors should perform and add the following experiments to strengthen their study.
- Interaction of NSP2 with the miRISC: With the data presented here, we can only conclude that NPS2 forms a complex with AGO2. Is their interaction direct or indirect? Is miRNA- and TNRC6-bound AGO2 (and thus miRISC) associated with NSP2? To address those important questions, the authors should perform NSP2 immunoprecipitations in GIGYF2 (and 4EHP) KO cell lines and monitor the presence of AGO2 and miRNAs in the immunoprecipitated complex. Those experiments will define the type of interaction NSP2 has with the miRISC (GIGYF2 dependent or not).
- Along this line, is NSP2 action on miRNA-mediated gene regulation dependent or not of GIGYF2? Again, testing this by monitoring the repression of the different reporters upon NSP2 overexpression in the presence or not of GIGYF2 in cells will precise the contribution of NSP2 in miRNA-mediated gene silencing.
Besides these two sets of critical experiments that will define the relationship between NSP2 mRNA modulation and the microRNA pathway, it would be interesting for this study to readily test the effect of NSP2 on miRNA targets related to immune-regulatory processes and antiviral response. As the authors pointed out in their discussion, several mRNAs are involved in the control of genes found in those pathways. Demonstrating the contribution of NSP2 in the regulation of a few of them will strengthen their study's significance and interest by providing a possible mechanism at play during a SARS-CoV2 infection. Also, it would be interesting to test if the modulation of translation inhibition by NSP2 occurs in cells infected by the SARS-CoV2 virus. For instance, is NSP2 and miRISC interaction enhances during the viral infection? As the authors propose, NSP2 could also have improved antiviral microRNA repression, so it would be interesting to characterize this interplay in a relevant biological context.
Minor comment:
From the data presented in Figure S1A, it is impossible to conclude "that miR-20a represses the expression of the target mRNA in a GIGFY2-dependent manner" as its KO also affect the level/stability of 4EHP. Therefore, we cannot distinguish the contribution of GIGFY2 and 4EHP in this context as both protein levels decrease. The authors should tone down this statement on page 3.
Significance
With the addition of the proposed experiments, the revised study will better define the direct contribution of NSP2 with the miRISC. This work has the potential to provide another aspect of the mRNA translation modulation by the SARS-CoV2 protein NSP2 with the interesting angle of miRNA-mediated gene silencing.
As mentioned by the authors, another recent paper reports the potential impact of NSP2 on post-transcriptional silencing (Zou et al., iScience 2022). However, in contrast to the current study, this previous work did not directly test the interaction of NSP2 with the miRISC. Furthermore, it only used a single miRNA reporter (let-7) to support NSP2 contribution in miRNA-mediated gene silencing, which does not demonstrate the broader impact of NSP2 on this gene regulatory mechanism as tested in this current study. Upon revision, this study will provide more definitive proof of the involvement of NSP2 in miRNA-mediated gene regulation and thus will be of interest to experts in the miRNA field and scientists interested in understanding viruses/hosts interaction.
Although not essential, if the authors want to add data that addresses the function of NSP2 on this regulatory pathway in the context of viral infection (which seems feasible for this group), that will definitely increase the broader significance of their work.
I am an expert in molecular biology and molecular genetics, miRNA-mediated gene regulation, and small non-coding RNA biology.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript the authors examine whether SARS-CoV-2 protein, NSP2 mediate translation repression of cellular transcripts by increasing miRNA mediated suppression. The same authors previously demonstrated NSP2 interacts with GIGYF2 and this interaction suppresses the translation of the Ifnb mRNA. Here they extend this finding and using a series of reporters they illustrate that at least part of NSP2 translation suppression is mediated by increasing GIGYF2 mediated miRNA translation suppression. Overall the manuscript is clearly written and the experiments well executed.
Major comments:
Optional- The authors show that the ability of NSP2 to enhance miRNA-mediated repression is dependent on the extent of the initial repression and suggest this dependency on the initial repression levels may explain the discrepancy with published work showing NSP2 actually impairs (and not increase) microRNA-mediated silencing . Therefore, an important addition could be to examine what happen to translation in cells that express NSP2 and whether generally translation repression is significant in transcripts (native) that are enriched in miRNA binding site. This experiment will help to show NSP2 effect on native transcripts and potentially help to understand how much of these changes are likely explained by miRNAs.
Minor comments:
- Personally I found the term repression fold quite confusing and unintuitive. Why not to present the actual measurements so that the control (blue bars) have high value and the red bars (representing repression) have lower values?
- It seems inadequate to present on the same graph two values that are normalized to 1. For example, in figure 1D it will be important to show the mir20-Mut real values (at least mir20-Mut in NSP2 cells should not be normalized to 1). This will allow to show that the differences are indeed mediated by stronger translation repression of miR-20 WT luciferase in the presence of NSP2 and not by unexplained differences in mir20-mut luciferase expression. This is true for almost all the figures in the manuscript. Correspondingly, the statistical test should be two-factor ANOVA test examining if NSP2 expression significantly increase the difference between Luciferase miR20-WT and luciferase miR20-mut.
Significance
There is an urgent need for better molecular understanding of how SARS-CoV-2 proteins influence the machineries of the host cell.
This study investigates how NSP2 interaction with GIGYF2 mediate translation repression of cellular transcript. The authors also address the discrepancy with previously published work that showed NSP2 actually impairs (and not increase) microRNA-mediated silencing.
The paper would be of interest to RNA biologists and for molecular virologists that study SARS-CoV-2
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
I summarise the major findings of the work below. In my opinion the range and application of approaches has provided a broad evidence base that, in general, supports the authors conclusions. However, there are, in my opinion, particular failures to utilise and communicate this evidence. The manuscript may be much improved with attention in the following areas. In each case I will give general criticism with a few examples, but the principals of my comments could be applied throughout the work.
1) Insufficient quantification. The investigation combines various sources of qualitative data (EM, fluorescence microscopy, western blotting) to generate a reasonably strong evidence base. However, the work is over-reliant on representative images and should include more quantification from repeat experiments. When there are multiple fluorescence micrographs with intensity changes (not necessarily just representative images) (e.g. Figure 1 or 2) the authors should consider making measurements of these. Also the VLP production assays, which are assessed by western blotting would particularly benefit from a quantitative assessment (either by densitometry or, if samples remain, ELISA/similar approach).
We have performed quantification of immunofluoresence, western blotting and VLP experiments from existing data. These quantification are presented in our revised manuscript. An overview of new quantification is shown below:
Data shown
Quantification now shown in
Method
Analysis
Figure 1A
Supp F1C
IF
HAE (-/+ SARS-CoV-2)
- Tetherin total fluorescence intensity
Figure 1D
Supp F1E
IF
HeLa+ACE2 (-/+ SARS-CoV-2 )
- Tetherin total fluorescence intensity
Figure 2C
Supp F2B
IF
A549+ACE2 (-/+ SARS-CoV-2)
- Tetherin total fluorescence intensity
Figure 2G
Supp F2D
IF
T84 (-/+ SARS-CoV-2)
- Tetherin total fluorescence intensity
Supp F4A
Supp F4B
IF
HeLa + ss-HA-Spike transients (-/+ HA stained cells) - Tetherin total fluorescence intensity
Figure 4D
Supp F4E
IF
HeLa + TetOne ss-HA-Spike stables (-/+ Dox)
- Tetherin total fluorescence intensity
Figure 4F
Supp F4G
W blot
HeLa + TetOne ss-HA-Spike stables (-/+ Dox)
– Tetherin abundance
Figure 4G
Supp F4I
W blot – lysates
Spike VLP experiments
– tetherin abundance
Figure 4G
Supp F4J
W blot - VLPs
Spike VLP experiments
- N-FLAG abundance
Figure 6A
Supp F7A
W blot – lysates
ORF3a VLP experiments
– tetherin abundance
Figure 6A
Supp F7B
W blot - VLPs
ORF3a VLP experiments
- N-FLAG
For immunofluoresence anaysis, the mean, standard deviation, number of cells analysed and number of independent experiments are shown in the updated figure legends. Statistical analysis is also detailed in figure legends. Methods for the quantificaiton of fluoresence intensity is included in the Methods section.
Densitometry was performed on western blots and VLP experiments as suggested. The mean, standard devisation and number of independent expreiments analysed are expressed in figure legends. Methods for densityometry quantification is now included.
2) Insufficient explanation. I found some of the images and legends contained insufficient annotation and/or description for a non-expert reader to appreciate the result(s). Particularly if the authors want to draw attention to features in micrographs they should consider using more enlarged/inset images and annotations (e.g. arrows) to point out structures (e.g DMVs etc.). This short coming exacerbates the lack of quantification.
Additional detail has been provided to the figure legends, and we have updated several figures to draw attention to features in micrographs. Black arrowheads have been added to Figures 1E, 2D, 2H to highlight plasma membrane-associated virions, and asterisks to highlight DMVs in Figures 1E, 2D and Supplemental Figures 2C, 2E. Similarly, typical Golgi cisternae are highlighted by white arrowheads micrographs in Figure 2E. These figure legends have also been modified to highlight these additions.
3) Insufficient exploration of the data. I had a sense that some aspects of the data seem unconsidered or ignored, and the discussion lacks depth and reflection. For example the tetherin down-regulation apparent in Figures 1 and 2 is not really explained by the spike/ORF3a antagonism described later on, but this is not explicitly addressed.
We have made changes throughout the manuscript, but the discussion especially has been modified. We now discuss the ORF3a data in more depth, discuss possible mechanisms by which ORF3a alone enhances VLP release, and discuss our ORF7a data in context to previous reports.
The discussion has been updated to now include a better description of our data, and additional writing putting our work in to context with previously published work. See discussion section of revised manuscript.
Also, Figure 6 suggests that ORF3a results in high levels of incorporation of tetherin in to VLPs, but I don't think this is even described(?). The discussion should also include more comparison with previous studies on the relationship between SARS-2 and tetherin.
We have added a section to discuss how ORF3a may enhance VLP release,
‘We found that the expression of ORF3a enhanced VLP independently of its ability to relocalise tetherin (Figure 6A). This may be due to either the ability of ORF3a to induce Golgi fragmentation [38] which facilitates viral trafficking [39], or due to enhanced lysosomal exocytosis [37]. Tetherin was also found in VLPs upon co-expression with ORF3a (Figure 6A) which may also indicate to enhanced release via lysosomal exocytosis [37].
The secretion of lysosomal hydrolases has been reported upon expression of ORF3a [31] and whilst this may in-part be due to enhanced lysosome-plasma membrane fusion, our data highlights that ORF3a impairs the retrograde trafficking of CIMPR (Supplemental Figures 6B, 6F, 6G), which may similarly increase hydrolase secretion.’ – (Line 625-654).
The discussion has been developed to compare the relationship between SARS-CoV-2 and tetherin in previous studies,
‘SARS-CoV-1 ORF7a is reported to inhibit tetherin glycosylation and localise to the plasma membrane in the presence of tetherin [18]. We did not observe any difference in total tetherin levels, tetherin glycosylation, ability to form dimers, or surface tetherin upon expression of either SARS-CoV-1 or SARS-CoV-2 ORF7a (Figures 4A, 4B, 4C).
Others groups have demonstrated a role for ORF7a in sarbecovirus infection and both SARS-CoV-1 and SARS-CoV-2 virus lacking ORF7a show impaired virus replication in the presence of tetherin [18,41]. A direct interaction between SARS-CoV-1 ORF7a and SARS-CoV-2 ORF7a and tetherin have been described [18,41], although the precise mechanism(s) by which ORF7a antagonises tetherin remains enigmatic. We cannot exclude that ORF7a requires other viral proteins to antagonise tetherin, or that ORF7a antagonises tetherin via another mechanism. For example, ORF7a can potently antagonise IFN signalling [42] which would impair tetherin induction in many cell types.’ – (Line 667-704).
I have no minor comments on this draft of the manuscript.
Reviewer #1 (Significance (Required)):
Tetherin, encoded by the BST2 gene, is an antiviral restriction factor that inhibits the release of enveloped viruses by creating tethers between viral and host membranes. It also has a capacity for sensing and signalling viral infection. It is most widely understood in the context of HIV-1, however, there is evidence of restriction in a wide variety of enveloped viruses, many of which have evolved strategies for antagonising tetherin. This knowledge informs on viral interactions with the innate immune system, with implications for basic virology and translational research.
This study investigates tetherin in the context of SARS-CoV-2. The authors use a powerful collection of tools (live virus, gene knock out cells, recombinant viral and host expression systems) and a variety of approaches (microscopy, western blotting, infection assays), which is, itself, a strength. The study provides evidence to support a series of conclusions: I) BST2/tetherin restricts SARS-CoV-2 II) SARS-CoV-2 ablates tetherin expression III) spike protein can modestly down-regulate tetherin IV) ORF3A dysregulates tetherin localisation by altering retrograde trafficking. These conclusions are broadly supported by the data and this study make significant contributions to our understanding of SARS-CoV-2/tetherin interactions.
My enthusiasm is reduced by, in my opinion, a failure of the authors to fully quantify, explain and explore their data. I expect the manuscript could be significantly improved without further experimentation by strengthening these aspects.
This manuscript will be of interest to investigators in virology and/or cellular intrinsic immunity. Given the focus on SARS-CoV-2 it is possible/likely that it will find a slightly broader readership.
I have highly appropriate skills for evaluating this work being experienced in virology, SARS-CoV-2, cell biology and microscopy.
We wish to thank Reviewer #1 for their comments which have helped us to improve the quality of our revised manuscript.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
BST2/tetherin can restrict the release and transmission of many enveloped viruses, including coronaviruses. In many cases, restricted viruses have developed mechanisms to abrogate tetherin-restriction by expressing proteins that antagonize tetherin; HIV-1 Vpu-mediated antagonism of tetherin restriction is a particularly well studied example. In this paper, Stewart et al. report their studies of the mechanism(s) underlying SARS-CoV-2 antagonism of tetherin restriction. They conclude that Orf3a is the primary virally encoded protein involved and that Orf3a manipulates endo-lysosomal trafficking to decrease tetherin cycling and divert the protein away from putative assembly sites.
Major comments:- In my view some of the claims made by the authors are not fully supported by the data. For example, the bystander effect discussed in line 162 may suggest that infected cells can produce IFN but does not 'indicate' that they do
This text has now been edited,
‘The levels of tetherin in uninfected HAE cells is lower than observed in uninfected neighbours in infected wells demonstrating that infected HAE cells are able to generate IFN to act upon uninfected neighbouring cells, enhancing tetherin expression.’ - (Lines 163-172).
Most of the EM images show part of a cell profile, so statements such as (line 192) 'virus containing tubulovesicular organelles were often polarised towards sites of significant surface-associated virus' should be backed up with appropriate images, or indicated as 'not shown', or removed (the observation is not so important for this story). Line 196, DMVs can't be seen in these micrographs.
The statement 'virus containing tubulovesicular organelles were often polarised towards sites of significant surface-associated virus' has been removed. The micrographs in Figure 1E have been re-cropped, and image iii replaced with an image showing DMVs and budding virions. Plasma membrane-associated virions are highlighted by black arrowheads, DMVs by black asterisks, and intracellular virion by a white arrow.
Line 391, I can't see much change in CD63 distribution.
CD63 reproducibly appears clustered towards the nuclei in ORF3a expressing cells, whilst CD63 positive puncta are abundant in the periphery of mock cells. CD63 puncta are also larger, and the staining of CIMPR and VPS35 also appears to be associated with larger organelles. We have amended the text to now read,
‘Expression of ORF3a also disrupted the distribution of numerous endosome-related markers including CIMPR, VPS35, CD63, which all localised to larger and less peripheral puncta (Supplemental Figure 6B), and the mixing of early and late endosomal markers’ - (Line 469).
Quantification of the diameter of CD63 puncta indicate that they are larger in ORF3a expressing cells than in mock cells. Mock cells - 0.71μm (SD; 0.19), ORF3a - 1.15μm (SD;0.35). At least 75 organelles per sample, from 10 different cells. We have not included this data as we do not wish to labor this point but are happy to include this quantification if required to do so.
Line 321, the authors show that ORF7a does not affect tetherin localization, abundance, glycosylation or dimer formation, but they don't show that it doesn't restrict SARS-CoV-2. Can they be sure that epitope tagging this molecule does not abrogate function (or the functions of any of the other tagged proteins for that matter), or that ORF7a works in conjunction with one of the other viral proteins?
We are careful in the manuscript not to claim that ORF7a has no effect on tetherin. Our data indicate that ‘ORF7a does not directly influence tetherin localisation, abundance, glycosylation or dimer formation’ - (Line 361-362).
We were unable to reproduce an effect of ORF7a on tetherin glycosylation. Our data conflicts with that presented by Taylor et al, 2015, where ORF7a impaired tetherin glycosylation and ORF7a localised to the plasma membrane in tetherin expressing cells. The experiments performed by Taylor et al used HEK293 cells and ectopically expressed tagged tetherin. The differences in results may be attributed to the differences between cell lines or due to differences between endogenous or ectopic / tagged tetherin.
The study by Taylor et al uses SARS-CoV-1 ORF7a-HA from Kopecky-Bromberg et al., 2007 (DOI: 1128/JVI.01782-06), where the -HA tag is positioned at the C-terminus. Our ORF7a-FLAG constructs have a C-terminal epitope tag. While we cannot exclude the possibility that tagged proteins may act differently from untagged ones, the differences between our findings and previous work appear unlikely to be due to epitope tags.
Our manuscript states that although we cannot find any effect of ORF7a on tetherin localisation, abundance, glycosylation, or dimer formation, we cannot exclude that ORF7a impacts tetherin by another mechanism. For example, ORF7a has been found to antagonise interferon responses. Tetherin is abundantly expressed in HeLa cells and expression does not require induction through interferon. None of our experiments above would be impacted by interferon antagonism yet this could impact other cell types besides infection in vivo. These possibilities may explain the reported differential impact of ORF7a by different labs. An addition comment has been added to the discussion to reflect this,
’We cannot exclude that ORF7a requires other viral proteins to antagonise tetherin, or that ORF7a antagonises tetherin via another mechanism. For example, ORF7a potently antagonises IFN signalling [38], which would impair tetherin induction in many cell types. - (Line 701-704).
Note - Reference 38 has been added to the manuscript – Xia et al., Cell Reports DOI: 10.1016/j.celrep.2020.108234
In the ORF screen, a number of the constructs are expressed at low level, is it possible they [the authors] are missing something?
Some of the ORFs expressed in the miniscreen appear poorly expressed. We accept that in the use of epitope tagged constructs expression levels of individual viral proteins may impact upon a successful screen. However, this screen was performed to identify any potential changes in tetherin abundance or localisation, and the screen did successfully identify ORF3a, which we were able to follow-up and verify.
Line 376, the authors refer to ORF3a being a viroporin. A recent eLife paper (doi: 10.7554/eLife.84477; initially published in BioRxiv) refutes this claim and builds on other evidence that ORF3a interacts with the HOPS complex. The authors should at least mention this work, especially in the discussion, as it would seem to provide a molecular mechanism to support their conclusions.
This paper had not been peer reviewed at the time of our initial submission. We have now included the following text,
‘SARS-CoV-2 ORF3a is an accessory protein that localises to and perturbs endosomes and lysosomes [29]. It may do so by acting either as a viroporin [30] or by interacting with, and possibly interfering with the function of VPS 39, a component of the HOPS complex which facilitates tethering of late endosomes or autophagosomes with lysosomes [29,31]. Given ORF3a likely impairs lysosome function, the observed increased….’ - (Lines 444-449).
Fig 3, the growth curves illustrated in Fig3 C and D do not have errors bars; how many times were these experiments repeated?
These experiments require more repeats to include error bars. Infection and plaque assay (Figure 3C, 3D) are currently ongoing and we plan to complete them in the next 6-8 weeks and include them in the finalised manuscript.
In the new experiments, infections will additionally be performed at MOI 0.01, in addition to the previous MOIs (1 and 5).
Line 396, the authors show increased co-localization with LAMP1. As LAMP1 is found in late endosomes as well as lysosomes, they cannot claim the redistributed tetherin is specifically in lysosomes.
We have altered the text to now say:
‘The ORF3a-mediated increase in tetherin abundance within endolysosomes could be due to defective lysosomal degradation.’ - (Line 475).
There seems to be a marked difference in the anti-rb555 signal in the 'mock' cells in panels 5H and Suppl 6E. Is there a good reason for this, or does this indicate variability between experiments?
Antibody uptake experiments in Figure 5H and Supp Figure 6E were performed and acquired on different days. Relatively low levels of signal are available in these antibody uptake experiments, and the disperse labelling seen in the mocks does not aid this.
Fig 6a, why is there negligible VLP release from cells lacking BST2 and ORF3a-strep? How many times were these experiments performed? Is this a representative image? I think it confusing to refer to the same protein by two different names in the same figure (i.e. BST2 and tetherin). Do the authors know how the levels of ORF3a expressed in cells in these experiments compares to those seen in infected cells?
We have changed the blot in Figure 6A for one with clearer FLAG bands. Three independent experiments were performed for Figure 6A. Quantification of VLPs is now included in Supplemental Figure 7B.
We have changed ‘Bst2’ to ‘tetherin’ in all previous figures relating to protein; Figure 4G, Figure 6A, B, C.
We have no current information to compare ORF3a levels in these experiments versus in infected cells. We can investigate quantifying this if necessary.
My final point is, perhaps, the trickiest to answer, but nevertheless needs to be considered. As far as we know, SARS-CoV-2 and at least some other coronaviruses, bud into organelles of the early secretory pathway, often considered to be ERGIC. In the experiments shown here the authors provide evidence that ORF3a can influence tetherin recycling, but the main way of showing this is through its increased association with endocytic organelles. Do the authors have any evidence that Orf3a reduces tetherin levels in the ERGIC or whether the tetherin cycling pathway(s) involve the ERGIC?
This is an interesting point, and as the reviewer concedes, this is tricky to answer. Expression of ORF3a causes the redistribution or remodeling of various organelles (Figures 1E, 2D, 2F, Supp Figures 2C, 2E, 3E, 6B, 6C, 6D). We have been unable to test the direct involvement of ERGIC, despite attempts with a number of commercial antibodies. Given the huge rearrangements of organelles during SARS-CoV-2 infection, it is unclear exactly what will happen to the distribution of ERGIC.
Minor comments: Line 53, delete 'shell' its redundant and confusing when the authors have said coronaviruses have a membrane.
Deleted.
Line 61, delete 'the'
Deleted.
Line 72, delete 'enveloped'; coronaviruses already described as enveloped viruses (line 53)
Deleted.
Lines 93 - 100, lop-sided discussion of the viral life cycle; this paragraph is mostly about entry, which is not relevant to this paper, and does not really deal with the synthesis and assembly side of the cycle.
We have now added the following text,
‘….liberating the viral nucleocapsid to the cytosol of the cell. Upon uncoating, the RNA genome is released into the host cytosol and replication-transcription complexes assemble to drive the replication of the viral genome and the expression of viral proteins. Coronaviruses modify host organelles to generate viral replication factories - so-called DMVs (double-membrane vesicles) that act as hubs for viral RNA synthesis [10]. SARS-CoV-2 viral budding occurs at ER-to-Golgi intermediate compartments (ERGIC) and newly formed viral particles traffic through secretory vesicles to the plasma membrane where they are released to the extracellular space.’ - (Lines 95-104).
Line 103, why are the neighbouring cells 'naive'?
‘naïve’ removed.
Line 112 - 113, delete last phrase; tetherin is described as an IFN stimulated gene in line 111; to be accurate, the beginning of the sentence should be 'Tetherin is expressed from a type 1 Interferon stimulated gene ...'
Amended.
Line 118 - 119, should say 'For tetherin-restricted enveloped viruses' as not all enveloped viruses are restricted by tetherin.
Amended.
Line 131, coronaviruses are not the only family of tetherin-restricted viruses that assemble on intracellular membranes, e.g. bunyaviruses.
This has been modified and now reads,
‘In order for tetherin to tether coronaviruses, tetherin must be incorporated in the virus envelope during budding which occurs in intracellular organelles.’ - (Lines 133-135).
Line 192, there is no EM data in Supplemental Fig 1C.
This has now been removed.
Line 251, 'a synchronous infection event' should be 'synchronous infection' as there will be multiple infection events.
This has been changed.
Page 13 (and elsewhere), unlike Southern, 'Western' should not have a capital letter, except at the start of a sentence.
These have been updated throughout the manuscript (Lines 183, 341, 3549, 356, 392, 509, 763, 1330, 1399).
Lines 330 and 352, can the authors quantitate S protein-induced reduction in cell surface tetherin rather than using the somewhat subjective 'mild'?
These are now changed to,
‘Transient transfection of cells with ss-HA-Spike caused a 32% decrease in tetherin as observed by immunofluorescence (Supplemental Figure 4A, 4B), with…’ – (Line 370).
‘To explore whether the Spike-induced tetherin downregulation altered virus release, we performed experiments with virus like particles (VLPs) in HEK293T …’ – (Line 399).
Line 379, OFR, should be ORF.
Yes, changed.
Line 448, 'Tetherin retains the ability' - did it ever loose it?
This has been rephrased to,
‘Tetherin has the ability to restrict a number of different enveloped viruses that bud at distinct organelles.’ - (Line 547).
Line 451, 'luminal' is confusing in this context.
This has been modified to,
‘Tetherin forms homodimers between opposing membranes (e.g., plasma membrane and viral envelope) that are linked via disulphide bonds.’ - (Line 549).
Line 453, the process of virus envelopment is likely to be more than a 'single step'
This now reads,
‘…virus during viral budding, which occurs in modified ERGIC organelles.’ - (Line 552).
Line 457, in my view the notion that Vpu abrogation of tetherin restriction is just due to redistribution of tetherin to the TGN is somewhat simplistic and disregards a lot of other work.
We have removed mention of mechanisms of tetherin antagonism by other viruses. The key point we wish to make here is that tetherin is lost from the budding compartment. This now reads,
‘Many enveloped viruses antagonise tetherin by altering its localisation and removing it from the respective site of virus budding.’ – (Line 552-553).
Line 472, what is meant by 'resting states'?
This should have been ‘in the absence of stimulation’ and have now been re-written,
‘Tetherin is an IFN-stimulated gene (ISG) [13], and many cell types express low levels of tetherin in the absence of stimulation.’ - (Line 577).
Line 1204, how were 'mock infected cells .......... infected'?
This has now been re-written,
‘Differentiated nasal primary human airway epithelial (HAE) cells were embedded to OCT….’ - (Line 1385).
Reviewer #2 (Significance (Required)):
This study builds on published work supporting the notion that SARS-Cov-2 ORF3a is an antagonist for the restriction factor tetherin. Importantly, it provides insights to the the mechanism of ORF3a mediated tetherin antagonism, specifically to ORF3a inhibits tetherin cycling, diverting the protein to lysosomes and away from compartment(s) where virions assemble. Overall, the authors provide good supporting evidence for these conclusions, however there are issues that the authors need to address.
We wish to thank Reviewer #2 for their insightful comments and suggestions for improving this work.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Restriction factors are major barriers against viral infections. A prime example is Tetherin (aka BST2), which is able to physically tether budding virions to the plasma membrane preventing release of the infectious particles. Of note, tetherin has broad anti-viral activity and has been established as a crucial innate immune defense factor against HIV, IAV, SARS-CoV-2 and other important human pathogens. However, successful viruses like SARS-CoV-2 evolved strategies to counteract restriction factors and promote their replication. Important restriction factors, such as tetherin, may often be targeted by multiple viral strategies to ensure complete suppression of their anti-viral activities by the pathogen. Of note, it was previously published that the accessory protein ORF7a of SARS-CoV-2 binds to (Petrosino et al, Chemistry Europe, 2021) and antagonizes it (Martin-Sancho et al, Molecular Cell, 2021). Previous data on SARS-CoV also revealed that ORF7a promotes cleavage of tetherin (Taylor et al, 2015, J Virol). In this manuscript, the authors show that tetherin restricts SARS-CoV-2 by tethering virions to the plasma membrane and propose that tetherin is targeted by two proteins of SARS-CoV-2. Whereas the Spike protein promotes degradation of tetherin, the accessory protein ORF3a redirects tetherin away from newly forming SARS-CoV-2 virions. While the overall findings that both S and ORF3a are additionally targeting tetherin is both novel and intriguing, additional evidence is needed to support this. In addition, the authors show that in their experimental setups ORF7a does not induce cleavage of tetherin. This is in direct contrast to previously published data both on SARS-CoV(-1) and -2 (Taylor et al, 2015, J Virol; Petrosino et al, Chemistry Europe, 2021; Martin-Sancho et al, Molecular Cell, 2021). From my point of view that needs further experimental confirmation. While the authors state that the impact of Spike on tethrin is mild, the experiments should still allow the conclusion whether there is a (mild) effect or not. The mechanism of ORF3a is fortunately more robustly assessed and provides some novel insights. Unfortunately, the whole manuscript suffers from a striking lack of quantifications. In addition, it is not clear whether and how many times experiments were repeated to the same results. Overall, the data in this manuscript seem very speculative and preliminary and thus do not support the authors conclusions.
Major:
Much of the data seems like it was only done once. As I am sure that this is a writing issue, please clearly state how many times the individual assays were repeated, provide the quantification graphs and appropriate statistics. Some experiments may need additional quantification and confirmation by other methods to be convincing.
Quantification is provided throughout the revised manuscript. Figure legends have also been updated to provide information on quantification and statistical analysis.
For example, Figure 1A, C and D: Please quantify the levels of tetherin and use an alternative readout, e.g. Western blotting of infected cells.
Quantification has been performed and included in our revised manuscript in Supplemental Figures 1C, 1E. Tetherin is not shown in Figure 1C.
A table is provided (above) to highlight the additional quantification.
Figure 2A: Please quantify.
We are not sure we understand this point. The western blot shown in Figure 2A demonstrates the ectopic expression of ACE2 in our A549 cell line. A549 cells have been used by many labs to study SARS-CoV-2 infection, but express negligible ACE2.
Fig 3A: Please show and confirm successful tetherin KO in the cell lines that are used not only in microscopy.
A new blot is now shown in Figure 3A, including a blot demonstrating tetherin loss in both KO lines.
Figure 4C: Please quantify
Currently flow cytometry experiments have been performed twice each and this is now detailed in the figure legends. The data shown in each panel is representative and the data has been explored using analogous approaches. For example, Figure 4C is complemented by Figures 4A and 4B, Figures 4E is complemented by 4D and 4F. We do not feel that repeating these flow cytometry analysis will significantly improve the manuscript.
Figure 4D: Please quantify the effects are not obvious from the images provided.
Quantification is now provided in Supplemental Figure 4E.
Figure 4E, F Please provide a quantification of multiple independent repeats, the claimed differences are neither striking nor obvious.
Quantification of 4F is now provided in Supplemental Figure 4G. Tetherin levels were quantified to be reduced by 25% (SD: 8%) by addition of Doxycycline and induction of ss-HA-Spike. Information for quantification is provided in figure legends.
Figure 5A: Please quantify
These experiments have currently been performed twice and this is now described in the figure legends. Data shown is representative. We can perform one more repeat of these experiments to quantify if neccessary, but do not feel it will significantly alter the manuscript.
Figure 3C and D: At timepoint 0 the infection input levels are different. The initial infection levels have to be the same to draw the conclusion that tetherin KO affects virion release and not the initial infection efficiency. Can the authors either normalize or ensure that the initial infection is the same in all conditions and that variations in the initial infection efficiency do not correlated with the impact of tetherin on replication/release ? How often were those experiments repeated? Are the marginal differences in infectious titre significant? Overall the impact of tetherin on SARS-CoV-2 is very underwhelming but that may be due to efficient viral tetherin-counteraction strategies. Why is the phenotype inverted at 72 h?
Equal amounts of virus, as measured by plaque-forming units (PFU), were used for both HeLa cell lines and thus at 0 hpi the variation seen is within the parameters of the assay used. It remains possible that tetherin affects virus entry but this is unlikely and this assay was not designed to investigate that effect.
Growth curve assays are currently being repeated using an MOI of 0.01, 1 and 5. We are removing the 72 hpi sample from future experiments. At this time point, we find that the extensive cell death caused by viral replication (especially at higher MOIs) makes it difficult to accurately separate the released from intracellular fractions and conclusions cannot be accurately drawn from the data.
Additional repeats of these experiments are in progress and will be included in the finalised manuscript.
Figure 4B and C: Can the authors provide an explanation why SARS-CoV ORF7a is not inducing cleavage/removes glycosylation of tetherin. To show that the assays work, an independent positive control needs to be included. The FACS data in C is unfortunately not quantified.
See above comments (Reviewer #2) regarding discussion on ORF7a. Additional text has been included to discuss ORF7a data,
‘SARS-CoV-1 ORF7a is reported to inhibit tetherin glycosylation and localise to the plasma membrane in the presence of tetherin [18]. We did not observe any difference in total tetherin levels, tetherin glycosylation, ability to form dimers, or surface tetherin upon expression of either SARS-CoV-1 or SARS-CoV-2 ORF7a (Figures 4A, 4B, 4C).
Others groups have demonstrated a role for ORF7a in sarbecovirus infection and both SARS-CoV-1 and SARS-CoV-2 virus lacking ORF7a show impaired virus replication in the presence of tetherin [18,41]. A direct interaction between SARS-CoV-1 ORF7a and SARS-CoV-2 ORF7a and tetherin have been described [18,41], although the precise mechanism(s) by which ORF7a antagonises tetherin remains enigmatic. We cannot exclude that ORF7a requires other viral proteins to antagonise tetherin, or that ORF7a antagonises tetherin via another mechanism. For example, ORF7a can potently antagonise IFN signalling [42] which would impair tetherin induction in many cell types.’ – (Line 667-704).
Fig 4G: The rationale and result of this experiment are not clear.
The rationale for Spike VLP experiments is explained at Line 403. Given that Spike caused a reproducible decrease in cellular tetherin, we examined whether this downregulation was sufficient to antagonise tetherin and increase VLP yield.
Fig 6: What is the benefit of doing the VLP assays as opposed to genuine virus experiments? To me it rather seems to be making the data unnecessarily complex. Again, no quantifications or repeats are provided.
VLPs are used to separate the budding and release process from the replication process of RNA viruses. VLPs have been used in a number of SARS-CoV (DOI: 1002/jmv.25518) and HIV-1 (DOI: https://doi.org/10.1186/1742-4690-7-51) studies to analyse the impact of tetherin (and tetherin mutants) on release.
VLP experiment quantification are now included throughout.
Minor: Fig 1D: How do the authors explain the mainly intracellular Spike staining?
We do not understand this point. Spike staining is intracellular, whether expressed alone or in the context of infected cells.
Please add statistical analyses on the data e.g. Fig. 3 C and D
Additional repeats of these experiments are in progress and will be included in the finalised manuscript.
Fig. 4B and F: Why do the annotated sizes of tetherin differ between the blots?
Figures 4B and 4F are run in non-reduced and reduced conditions respectively. In order to best show the dimer deficient C3A-Tetherin, blots are typically run in non-reduced conditions to exemplify dimer formation and to highlight any defects in dimer formation. The rest of the blots in the manuscript are run in denaturing conditions to aid blotting of other proteins. (Lines 957-958) and now (Lines 1356-1357).
Fig. 5A: What is ORF6a? Do the authors mean ORF6?
Yes, this has been changed.
An MOI of 1 is NOT considered a low or relevant MOI. Can the authors either rephrase or repeat experiments with an actual low or relevant MOI i.e. 0.01 ?
We are currently repeating these experiments and are including MOIs of 0.01, 1 and 5.
Why were the cell models switched between Figure 1 and 2 and essentially the same experiments repeated?
HeLa cells express high levels of tetherin at steady state, whilst A549 cells require IFN stimulation. HeLa cells demonstrate that tetherin downregulation occurs via an IFN-independent manner. A549 and T84 cells are more physiologically relevant cell types for SARS-CoV-2 infection. These points are stated in Lines 230 and 261.
The manuscript may benefit a lot from streamlining and removing unessential deviations from the main message (e.g. discussions why multistep/single step growth curves are used/not relevant; why are they shown if the authors conclude that a single step is not relevant?). The discussion is extremely lengthy and does not provide sufficient discussion of the presented data.
The multistep/single step growth curve text will be adapted, but it will be re-written after additional infection experiments.
We have removed from the Discussion a small section discussing ORF7a mutants, given that the emphasis of our manuscript is not on ORF7a.
We have also removed a small section describing the rearrangements of intracellular organelles by SARS-CoV-2 as it does not directly relate to the central message of our manuscript.
According to my opinion, the current manuscript does not provide significant advancement for the field. While the intention was to update and expand our existing knowledge about tetherin restriction by SARS-CoV-2, the experiments do not support this yet. However, the general premise and approach/concept of the manuscript would be appealing to a broader audience. I especially like the notion that multiple proteins of SARS-CoV-2 could synergistically counteract an important innate immune defense factor, tetherin. My expertise is on SARS-CoV-2 and the interplay between the virus and host cell restriction factors.
Reviewer #3 (Significance (Required)):
According to my opinion, the current manuscript does not provide significant advancement for the field. While the intention was to update and expand our existing knowledge about tetherin restriction by SARS-CoV-2, the experiments do not support this yet. However, the general premise and approach/concept of the manuscript would be appealing to a broader audience. I especially like the notion that multiple proteins of SARS-CoV-2 could synergistically counteract an important innate immune defense factor, tetherin. My expertise is on SARS-CoV-2 and the interplay between the virus and host cell restriction factors.
We thank Reviewer#3 for their comments and suggestions for improving this work.
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Referee #3
Evidence, reproducibility and clarity
Restriction factors are major barriers against viral infections. A prime example is Tetherin (aka BST2), which is able to physically tether budding virions to the plasma membrane preventing release of the infectious particles. Of note, tetherin has broad anti-viral activity and has been established as a crucial innate immune defense factor against HIV, IAV, SARS-CoV-2 and other important human pathogens. However, successful viruses like SARS-CoV-2 evolved strategies to counteract restriction factors and promote their replication. Important restriction factors, such as tetherin, may often be targeted by multiple viral strategies to ensure complete suppression of their anti-viral activities by the pathogen. Of note, it was previously published that the accessory protein ORF7a of SARS-CoV-2 binds to (Petrosino et al, Chemistry Europe, 2021) and antagonizes it (Martin-Sancho et al, Molecular Cell, 2021). Previous data on SARS-CoV also revealed that ORF7a promotes cleavage of tetherin (Taylor et al, 2015, J Virol).
In this manuscript, the authors show that tetherin restricts SARS-CoV-2 by tethering virions to the plasma membrane and propose that tetherin is targeted by two proteins of SARS-CoV-2. Whereas the Spike protein promotes degradation of tetherin, the accessory protein ORF3a redirects tetherin away from newly forming SARS-CoV-2 virions.
While the overall findings that both S and ORF3a are additionally targeting tetherin is both novel and intriguing, additional evidence is needed to support this. In addition, the authors show that in their experimental setups ORF7a does not induce cleavage of tetherin. This is in direct contrast to previously published data both on SARS-CoV(-1) and -2 (Taylor et al, 2015, J Virol; Petrosino et al, Chemistry Europe, 2021; Martin-Sancho et al, Molecular Cell, 2021). From my point of view that needs further experimental confirmation. While the authors state that the impact of Spike on tethrin is mild, the experiments should still allow the conclusion whether there is a (mild) effect or not. The mechanism of ORF3a is fortunately more robustly assessed and provides some novel insights. Unfortunately, the whole manuscript suffers from a striking lack of quantifications. In addition, it is not clear whether and how many times experiments were repeated to the same results. Overall, the data in this manuscript seem very speculative and preliminary and thus do not support the authors conclusions.
Major
Much of the data seems like it was only done once. As I am sure that this is a writing issue, please clearly state how many times the individual assays were repeated, provide the quantification graphs and appropriate statistics. Some experiments may need additional quantification and confirmation by other methods to be convincing. For example, Figure 1A, C and D: Please quantify the levels of tetherin and use an alternative readout, e.g. Western blotting of infected cells. Figure 2A: Please quantify. Fig 3A: Please show and confirm successful tetherin KO in the cell lines that are used not only in microscopy. Figure 4C: Please quantify. Figure 4D: Please quantify the effects are not obvious from the images provided. Figure 4E,F Please provide a quantification of multiple independent repeats, the claimed differences are neither striking nor obvious. Figure 5A: Please quantify.
Figure 3C and D: At timepoint 0 the infection input levels are different. The initial infection levels have to be the same to draw the conclusion that tetherin KO affects virion release and not the initial infection efficiency. Can the authors either normalize or ensure that the initial infection is the same in all conditions and that variations in the initial infection efficiency do not correlated with the impact of tetherin on replication/release ? How often were those experiments repeated? Are the marginal differences in infectious titre significant? Overall the impact of tetherin on SARS-CoV-2 is very underwhelming but that may be due to efficient viral tetherin-counteraction strategies. Why is the phenotype inverted at 72 h? Figure 4B and C: Can the authors provide an explanation why SARS-CoV ORF7a is not inducing cleavage/removes glycosylation of tetherin. To show that the assays work, an independent positive control needs to be included. The FACS data in C is unfortunately not quantified.
Fig 4G: The rationale and result of this experiment are not clear.
Fig 6: What is the benefit of doing the VLP assays as opposed to genuine virus experiments? To me it rather seems to be making the data unnecessarily complex. Again, no quantifications or repeats are provided.
Minor
Fig 1D: How do the authors explain the mainly intracellular Spike staining?
Please add statistical analyses on the data e.g. Fig. 3 C and D
Fig. 4B and F: Why do the annotated sizes of tetherin differ between the blots?
Fig. 5A: What is ORF6a? Do the authors mean ORF6?
An MOI of 1 is NOT considered a low or relevant MOI. Can the authors either rephrase or repeat experiments with an actual low or relevant MOI i.e. 0.01 ?
Why were the cell models switched between Figure 1 and 2 and essentially the same experiments repeated? The manuscript may benefit a lot from streamlining and removing unessential deviations from the main message (e.g. discussions why multistep/single step growth curves are used/not relevant; why are they shown if the authors conclude that a single step is not relevant?). The discussion is extremely lengthy and does not provide sufficient discussion of the presented data.
According to my opinion, the current manuscript does not provide significant advancement for the field. While the intention was to update and expand our existing knowledge about tetherin restriction by SARS-CoV-2, the experiments do not support this yet. However, the general premise and approach/concept of the manuscript would be appealing to a broader audience. I especially like the notion that multiple proteins of SARS-CoV-2 could synergistically counteract an important innate immune defense factor, tetherin. My expertise is on SARS-CoV-2 and the interplay between the virus and host cell restriction factors.
Significance
According to my opinion, the current manuscript does not provide significant advancement for the field. While the intention was to update and expand our existing knowledge about tetherin restriction by SARS-CoV-2, the experiments do not support this yet. However, the general premise and approach/concept of the manuscript would be appealing to a broader audience. I especially like the notion that multiple proteins of SARS-CoV-2 could synergistically counteract an important innate immune defense factor, tetherin.
My expertise is on SARS-CoV-2 and the interplay between the virus and host cell restriction factors.
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Referee #2
Evidence, reproducibility and clarity
BST2/tetherin can restrict the release and transmission of many enveloped viruses, including coronaviruses. In many cases, restricted viruses have developed mechanisms to abrogate tetherin-restriction by expressing proteins that antagonize tetherin; HIV-1 Vpu-mediated antagonism of tetherin restriction is a particularly well studied example. In this paper, Stewart et al. report their studies of the mechanism(s) underlying SARS-CoV-2 antagonism of tetherin restriction. They conclude that Orf3a is the primary virally encoded protein involved and that Orf3a manipulates endo-lysosomal trafficking to decrease tetherin cycling and divert the protein away from putative assembly sites.
Major comments:
In my view some of the claims made by the authors are not fully supported by the data. For example, the bystander effect discussed in line 162 may suggest that infected cells can produce IFN but does not 'indicate' that they do. Most of the EM images show part of a cell profile, so statements such as (line 192) 'virus containing tubulovesicular organelles were often polarised towards sites of significant surface-associated virus' should be backed up with appropriate images, or indicated as 'not shown', or removed (the observation is not so important for this story). Line 196, DMVs can't be seen in these micrographs. Line 391, I can't see much change in CD63 distribution.
Line 321, the authors show that ORF7a does not affect tetherin localization, abundance, glycosylation or dimer formation, but they don't show that it doesn't restrict SARS-CoV-2. Can they be sure that epitope tagging this molecule does not abrogate function (or the functions of any of the other tagged proteins for that matter), or that ORF7a works in conjunction with one of the other viral proteins? In the ORF screen, a number of the constructs are expressed at low level, is it possible they are missing something?
Line 376, the authors refer to ORF3a being a viroporin. A recent eLife paper (doi: 10.7554/eLife.84477; initially published in BioRxiv) refutes this claim and builds on other evidence that ORF3a interacts with the HOPS complex. The authors should at least mention this work, especially in the discussion, as it would seem to provide a molecular mechanism to support their conclusions.
Fig 3, the growth curves illustrated in Fig3 C and D do not have errors bars; how many times were these experiments repeated?
Line 396, the authors show increased co-localization with LAMP1. As LAMP1 is found in late endosomes as well as lysosomes, they cannot claim the redistributed tetherin is specifically in lysosomes.
There seems to be a marked difference in the anti-rb555 signal in the 'mock' cells in panels 5H and Suppl 6E. Is there a good reason for this, or does this indicate variability between experiments?
Fig 6a, why is there negligible VLP release from cells lacking BST2 and ORF3a-strep? How many times were these experiments performed? Is this a representative image? I think it confusing to refer to the same protein by two different names in the same figure (i.e. BST2 and tetherin). Do the authors know how the levels of ORF3a expressed in cells in these experiments compares to those seen in infected cells?
My final point is, perhaps, the trickiest to answer, but nevertheless needs to be considered. As far as we know, SARS-CoV-2 and at least some other coronaviruses, bud into organelles of the early secretory pathway, often considered to be ERGIC. In the experiments shown here the authors provide evidence that ORF3a can influence tetherin recycling, but the main way of showing this is through its increased association with endocytic organelles. Do the authors have any evidence that Orf3a reduces tetherin levels in the ERGIC or whether the tetherin cycling pathway(s) involve the ERGIC?
Minor comments:
Overall, the manuscript should be carefully edited to ensure the text reads clearly. A few examples of thing that need to be fixed are:-
Line 53, delete 'shell' its redundant and confusing when the authors have said coronaviruses have a membrane.
Line 61, delete 'the'
Line 72, delete 'enveloped'; coronaviruses already described as enveloped viruses (line 53)
Lines 93 - 100, lop-sided discussion of the viral life cycle; this paragraph is mostly about entry, which is not relevant to this paper, and does not really deal with the synthesis and assembly side of the cycle.
Line 103, why are the neighbouring cells 'naive'?
Line 112 - 113, delete last phrase; tetherin is described as an IFN stimulated gene in line 111; to be accurate, the beginning of the sentence should be 'Tetherin is expressed from a type 1 Interferon stimulated gene ...'
Line 118 - 119, should say 'For tetherin-restricted enveloped viruses' as not all enveloped viruses are restricted by tetherin.
Line 131, coronaviruses are not the only family of tetherin-restricted viruses that assemble on intracellular membranes, e.g. bunyaviruses.
Line 192, there is no EM data in Supplemental Fig 1C.
Line 251, 'a synchronous infection event' should be 'synchronous infection' as there will be multiple infection events
Page 13 (and elsewhere), unlike Southern, 'Western' should not have a capital letter, except at the start of a sentence.
Lines 330 and 352, can the authors quantitate S protein-induced reduction in cell surface tetherin rather than using the somewhat subjective 'mild'?
Line 379, OFR, should be ORF.
Line 448, 'Tetherin retains the ability' - did it ever loose it?
Line 451, 'luminal' is confusing in this context.
Line 453, the process of virus envelopment is likely to be more than a 'single step'
Line 457, in my view the notion that Vpu abrogation of tetherin restriction is just due to redistribution of tetherin to the TGN is somewhat simplistic and disregards a lot of other work.
Line 472, what is meant by 'resting states'?
Line 1204, how were 'mock infected cells .......... infected'?
Significance
This study builds on published work supporting the notion that SARS-Cov-2 ORF3a is an antagonist for the restriction factor tetherin. Importantly, it provides insights to the the mechanism of ORF3a mediated tetherin antagonism, specifically to ORF3a inhibits tetherin cycling, diverting the protein to lysosomes and away from compartment(s) where virions assemble. Overall, the authors provide good supporting evidence for these conclusions, however there are issues that the authors need to address.
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Referee #1
Evidence, reproducibility and clarity
I summarise the major findings of the work below. In my opinion the range and application of approaches has provided a broad evidence base that, in general, supports the authors conclusions. However, there are, in my opinion, particular failures to utilise and communicate this evidence. The manuscript may be much improved with attention in the following areas. In each case I will give general criticism with a few examples, but the principals of my comments could be applied throughout the work.
- Insufficient quantification. The investigation combines various sources of qualitative data (EM, fluorescence microscopy, western blotting) to generate a reasonably strong evidence base. However, the work is over-reliant on representative images and should include more quantification from repeat experiments. When there are multiple fluorescence micrographs with intensity changes (not necessarily just representative images) (e.g. Figure 1 or 2) the authors should consider making measurements of these. Also the VLP production assays, which are assessed by western blotting would particularly benefit from a quantitative assessment (either by densitometry or, if samples remain, ELISA/similar approach).
- Insufficient explanation. I found some of the images and legends contained insufficient annotation and/or description for a non-expert reader to appreciate the result(s). Particularly if the authors want to draw attention to features in micrographs they should consider using more enlarged/inset images and annotations (e.g. arrows) to point out structures (e.g DMVs etc.). This short coming exacerbates the lack of quantification.
- Insufficient exploration of the data. I had a sense that some aspects of the data seem unconsidered or ignored, and the discussion lacks depth and reflection. For example the tetherin down-regulation apparent in Figures 1 and 2 is not really explained by the spike/ORF3a antagonism described later on, but this is not explicitly addressed. Also, Figure 6 suggests that ORF3a results in high levels of incorporation of tetherin in to VLPs, but I don't think this is even described(?). The discussion should also include more comparison with previous studies on the relationship between SARS-2 and tetherin.
I have no minor comments on this draft of the manuscript.
Significance
Tetherin, encoded by the BST2 gene, is an antiviral restriction factor that inhibits the release of enveloped viruses by creating tethers between viral and host membranes. It also has a capacity for sensing and signalling viral infection. It is most widely understood in the context of HIV-1, however, there is evidence of restriction in a wide variety of enveloped viruses, many of which have evolved strategies for antagonising tetherin. This knowledge informs on viral interactions with the innate immune system, with implications for basic virology and translational research.
This study investigates tetherin in the context of SARS-CoV-2. The authors use a powerful collection of tools (live virus, gene knock out cells, recombinant viral and host expression systems) and a variety of approaches (microscopy, western blotting, infection assays), which is, itself, a strength. The study provides evidence to support a series of conclusions: I) BST2/tetherin restricts SARS-CoV-2 II) SARS-CoV-2 ablates tetherin expression III) spike protein can modestly down-regulate tetherin IV) ORF3A dysregulates tetherin localisation by altering retrograde trafficking. These conclusions are broadly supported by the data and this study make significant contributions to our understanding of SARS-CoV-2/tetherin interactions.
My enthusiasm is reduced by, in my opinion, a failure of the authors to fully quantify, explain and explore their data. I expect the manuscript could be significantly improved without further experimentation by strengthening these aspects.
This manuscript will be of interest to investigators in virology and/or cellular intrinsic immunity. Given the focus on SARS-CoV-2 it is possible/likely that it will find a slightly broader readership.
I have highly appropriate skills for evaluating this work being experienced in virology, SARS-CoV-2, cell biology and microscopy.
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Reply to the reviewers
We thank the reviewers for their enthusiasm for our work and constructive feedback.
Below please find our point-by-point response to the comments:
Reviewer #1 -Key conclusions that were less convincing: -RhoA and NMII are in the title as mechanistic downstream regulators of CaM, but the results in Fig 8 call into question the role of RhoA. Why does RhoA activation not influence cell size and circularity? Can you overexpress MRLC-GFP and inhibit Rho and restore the wt phenotype? The role of NMII is also not clear - why does overexpressing MLCK-CA not have a phenotype but overexpressing MLCK downstream target MRLC show the phenotype? Are there any alternative pathways to regulate MRLC? It's not being discussed or described in 6D's schematic.
Response: Rho activation usually leads to the formation of more stress fibers and therefore does not lead to decreased cell size and increased circularity observed in MFN2 KO. The phenotype is restored by either ROCK or MLCK knockdown. We have discussed in the main text that the formation of PAB requires both RhoA and NMII activation under restricted spatiotemporal control.
MRLC has three major regulators (Ikebe & Hartshorne, 1985; Isotani et al., 2004). As we discussed, MLCK and ROCK phosphorylate MRLC at either Ser19 or Ser19 and Thr18. MRLC is dephosphorylated and inactivated by its phosphatase MLCP. We tried to knock down MLCP in wt MEF cells but failed to see any cell morphology changes (data not shown).
We were also surprised to see MRLC-GFP overexpression with Rho Activator can phenocopy PAB, but “MLCK-CA + Rho Activator” failed to. We believe it is because MLCK-CA constitutively over-activates a broad range of downstream effectors while overexpressing MRLC mimics endogenous activation or NMII alone. Also, only a proportion of cells acquired PAB structure under Rho Activator and MRLC overexpression, which indicates PAB formation also requires specific spatiotemporal controls.
*Rewrite for clarity -The role of ER/mito contacts in the system was unclear (since ER/mito contacts were not observed nor evaluated directly). *
__Response: __We have included additional data to measure ER/mito contacts in MEFs. Our result is consistent with numerous previous reports that MFN2 regulates ER/mito contacts. The data is now included in Fig. S3.
* -What role does focal adhesions have on PAB formation or any part of the model - There were results showing larger focal adhesions in the MFN2-/- cells, but not sure how this fits in with the bigger picture of contractility and PABs, and focal adhesions were not in the model in Figure 5.*
__Response: __Focal adhesion and actomyosin are tightly coupled, and our work focuses on the actin network. Our model did not include FAs since FA is not a significant focus in this study.
* -Whether regulating calcium impacts PAB formation*
__Response: __Calcium likely regulates PAB formation. We have shown PAB cell percentage decreases in mfn2-/- with ER-mito tethering contrast in Fig. S3.
-The role of PABs in migration is also unclear - can you affect PAB formation or get rid of PABs and quantify cell migration?
__Response: __Our data suggest that PAB formation and cell migration are inversely correlated. Since PAB results from a contractile actin band on the cell periphery, its role in defective cell spreading and migration is expected. We demonstrated that MLCK and ROCK knockdown reduced PABs and rescued cell spreading.
-It was hard to understand the correlation between the membrane tension of MFN2-/- cells and their ability to spread on softer substrates. How does this result fit in with the overarching model?
__Response: __Reduced membrane tension is presumably associated with decreased cell spreading. Softer substrates attenuate the mechanical force on focal adhesion proteins and the actin cytoskeleton (Burridge & Chrzanowska-Wodnicka, 2003; Pelham & Wang, 1997; Wong et al., 2015), which is required for focal adhesion maturation. As a result, softer substrates can reduce the over-contraction in the MFN2 KO cells. The results support the model that MFN2 KO cells have enhanced cell contraction on the substrates dependent on substrate interaction and force transduction on focal adhesions. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
__Response: __We have removed the MFN2-related disease from the introduction to focus the paper more on cell biology in vitro.
*-There were a number of findings that did not seem to fit in with the paper, or they were included, but were not robustly described nor quantified. As an example, Paxillin-positive focal adhesions were evaluated in MFN2-/- and with various pharmacological approaches, but there is no quantification with respect to size, number, or distribution of focal adhesions, despite language in the main text that there are differences between conditions. *
__Response: __We have quantified the focal adhesions in the KO cells, and the data is now included in Fig. 5. We used the actin distribution to quantify the “PAB”; therefore, FAs are not a significant focus of this study.
*Also, the model was presented in figure 5, and then there were several pieces of data presented afterward, some that are included in the model (myosin regulation), and some that are not in the model (membrane tension, TFM, substrate stiffness, etc). * __Response: __Membrane tension and substrate stiffness dependence are physical properties of the cell. The model focuses on the molecular mechanism that leads to PAB formation.
The stiffness/tension figure was not clear to me, and it was difficult to make sense of the data since one would predict that an increase in actomyosin contractility at the cortex would lead to higher membrane tension, not lower, and then how membrane tension relates to spreading on soft matrices is also unclear.
__Response: __The result was surprising to us initially. However, the MFN2 KO cells have increased actomyosin contractility only at the cell-substrate interface but not throughout the entire cell cortex. A less spread cell would have a more relaxed membrane and display a lower membrane tension, consistent with our observation. Softer matrices reduce cell contractility at the cell-substrate interface, which allows MFN2 KO cells to relax and spread better. We have emphasized in the discussion of our manuscript that MFN2 KO cells have an increase in actomyosin contractility only at the cell-substrate interface.
The manuscript seems like an amalgamation of different pieces of data that do not necessarily fit together into a cohesive story, so the authors are encouraged to either remove these data, or shore them up and weave them into the narrative.
__Response: __We respectfully disagree with the reviewer since the cell morphology, actin structure, substrate interaction, and cell mechanics are tightly correlative and provide a complete picture of the role of MFN2 in regulating cell behavior.
* Request additional experiments 1. -The imaging used for a lot of the quantification (migration, circularity) is difficult to resolve. The cells often look like they are not imaged in the correct imaging plane. It would be helpful to have better representative images such that it is clear how the cells were tracked and how cell periphery regions of interest were manually drawn. Focal adhesions should also be shown without thresholding.*
__Response: __We used a TIRF microscope and imaged a Z stack. Imaris was used to combine the Z-stack images. The images in the manuscripts are now of the lowest stack with background subtraction.
2. -For most of the quantification, it appears that the experiment was only performed once and that a handful of cells were quantified. The figure legend indicates the number of cells (often reported as >12 cells or >25 cells), but the methods indicate that high content imaging was performed, and so the interpretation is that these experiments were only performed once. Biological replicates are required. If the data do represent at least 3 biological replicates, then more cell quantification is required (12 or 25 cells in total would mean quantifying a small number of cells per replicate).
Response: __We quantified more cells and indicated the number of cells quantified in the figure legends. The experiments are with three biological replicates.__
* 3. -Mitochondrial morphology and quantification should be performed in the MFN2 knockdown and rescue lines.*
__Response: __Mitochondrial morphology is well characterized in the Mfn2 KO and rescue MEF cells (Chen et al., 2003; Naon et al., 2016; Samanas et al., 2020). We observed a similar phenotype using mito-RFP to label mitochondrial structure (Fig. S1).
4.-Many of the comparisons throughout the figures is between MFN2 knockdown and MFN2 knockdown plus rescue or genetic/pharmacological approaches, but a comparison that is rarely made is between wildtype and experimental. These comparisons could be useful in comparing partial rescues and potential redundancies with the other mitofusin.
Response: We have included the WT in our assays (Fig. 2-6). We also confirmed that MFN1 could not rescue the MFN2 defects (Fig. 2). We observed partial and complete rescue in different assays. It would be difficult to conclude whether the phenotype is due to the redundancies with the other mitofusin because not all cells are rescued at the endogenous level.
* 5. -For the mito/ER tethering experiments, it is important to show that ER/mito contacts are formed and not formed in the various conditions with imaging approaches.*
__Response: __We adopted a previously established method to quantify ER-mitochondria contacts with the probe SPLICSL (Cieri et al., 2017; Vallese et al., 2020). Our results align with previous reports that Mfn2-null MEFs displayed significantly decreased ER-mitochondria contacts. MFN2 re-expression or ER-mitochondria tethering structure restored the contacts. (Fig. S3).
* 6. -For some of the pharmacological perturbations, it would be helpful to show that the perturbation actually led to the expected phenotype - as an example, in cells treated with different concentrations of A23187, what are the intracellular calcium levels and how do these treatments influence PAB formation? This aspect should be generally applied across the study - when a modification is made, that particular phenotype should first be evaluated, before dissecting how the perturbation affects downstream phenotypes.*
__Response: __We selected a collection of well-characterized inhibitors broadly used in the literature for pharmacological perturbations. For example, numerous studies used A23187 treatment to raise intracellular calcium to examine related actin cytoskeleton changes (Carson et al., 1994; Goldfine et al., 1981; Shao et al., 2015). We titrated the drugs in WT in preliminary experiments and observed similar phenotypes. (data not shown). We then use the same concentration to treat the MFN2 KO cells. Overall, we use pharmacological perturbations as supporting evidence. We use genetics (knockdown or overexpression) to validate our results.
7. -In Figures 4 and 5, the thresholding approaches in the images make the focal adhesions difficult to resolve, and therefore it is difficult to determine the size. As described above, these metrics should be defined and quantified.
__Response: __We used a TIRF microscope and imaged a Z stack. Imaris was used to combine the Z-stack images. The images in the manuscripts are now of the lowest stack with background subtraction.
8. -What is a PAB? How is it defined? What metrics make a structure a PAB versus regular cortical actin - are there quantifiable metrics? In figure 8, there are some structures that are labelled as a PAB, but some aren't (as an example, the left panel in 8b is a PAB, but the right panel in 8A is not, but they look the same), so a PAB should be defined with quantifiable measures, and then applied to the entire study.
__Response: __We developed an algorism to quantify PAB cells. We first used the ImageJ plugin FiloQuant (Jacquemet et al., 2019) to identify the cell border and cytoskeleton, then used our custom algorism to quantify the percentage of actin in the cell border area. The cellular circularity is also calculated at the same time. If the cell contains more than 50% actin in the cell border area, and the circularity is higher than 0.6, we then count it as a “PAB” cell (Fig. S2).
-As described above, why does RhoA activation not influence cell size and circularity? Can you overexpress MRLC-GFP and inhibit Rho and restore the wildtype phenotype?
__Response: __Rho activation usually leads to the formation of more stress fibers and therefore does not lead to decreased cell size and increased circularity observed in MFN2 KO.
We are sorry that we don’t understand the rationale of this experiment proposed by the reviewer. ROCK inhibition restored the wildtype phenotype in MFN2 KO cells (Fig.7). Figure 8 is to create the MFN2 KO phenotype in WT cells, which requires both Rho and MRLC overactivation.
* 10 Are the data and the methods presented in such a way that they can be reproduced? -We appreciate that the authors quantified many parameters, although some quantifications were missing. There are some missing methods - how was directionality quantified, was migration quantified by selecting the approximate center of cells using MTrackJ or were centroids quantified by outlining cells, for instance. Also, given that some of the phenotypes were somewhat arbitrarily assigned (ie. what constitutes a PAB?), it may be difficult to reproduce these approaches and interpret data appropriately.*
__Response: __We have clarified directionality quantification methods and other details. We used MTrackJ to track cell migration. And as we mentioned above, we came up with a customized algorithm to quantify PAB cells, which shows the critical effectors in a more quantifiable way.
* 11. Are the experiments adequately replicated and statistical analysis adequate? -Unfortunately, while the approximate number of cells was reported, the number of biological replicates were not reported, and therefore, the experimental information and statistical analyses are not adequate.*
__Response: __We have quantified more cells and indicated the number of repeats and cells quantified in the figure legend. Minor comments: Specific experimental issues that are easily addressable.
* 12. - for some of the graphs - mostly about calcium levels - fold change is shown, but raw values should also be included to determine whether the basal levels of calcium are different across the conditions.*
__Response: __Delta F/F0 is the standard method to normalize dye loading in cells for calcium concentration measurements (Kijlstra et al., 2015; Zhou et al., 2021).
13. - scale bars in every panel should also help make the points clearer.
__Response: __We have added scale bars in all panels.
* Reviewer #2 (Evidence, reproducibility and clarity (Required)): 1. Fig. 1A: The Mfn1 Western Blot is not of publication quality. Moreover, quantitation is necessary.*
__Response: __We performed additional western blots, changed the representative images, and quantified the level of knockdown and overexpression (Fig.2 and 7). We did not quantify the WB in Fig.1A since it was to confirm that the Mfn1-/- or Mfn2-/- were knock-out cell lines.
2. Fig. 1B (as well as Fig. 2G and others): the date do not reflect cellular size but instead spread cellular area.
__Response: __We thank the reviewer for this suggestion. We have changed all similar descriptions to “Spread Area” in the main text and figures.
3. Fig. 1C, D: Mfn1-null MEFs appear to be more spindle-shaped than wt cells, yet their circularity tends to be elevated. Do the authors have an explanation?
__Response: __The circularity of Mfn1-/- MEFs has a slight increase but is not significant compared to the wt cells. As we observed, Mfn1-/- MEFs have fewer protrusions than wt, which may contribute to the slight increase in its circularity (Fig. 5C). However, this is not the focus of this study.
* 4. Fig. 2A: The Mfn1 levels in Mfn2-/- + Mfn2 are lower than Mfn2-/-? Does this imply a crosstalk between Mfn1 and Mfn2 expression.*
__Response: __We agree with the reviewer that a compensatory change in MFN1 expression might happen in Mfn2-/- + MFN2 MEFs. Previous research also indicated crosstalk between MFN1 and MFN2 expression (Sidarala et al., 2022).
* 5. Fig. 2H: The authors should provide co-staining of mitochondria and Mfn2 as well.*
__Response: __Co-staining of mitochondria and MFN2 in Mfn2-/- MEFs or rescue lines has been done in numerous previous studies (Chen et al., 2003; Naon et al., 2016; Samanas et al., 2020). In this work, we transfected our cells with mito-RFP and showed mitochondria changes in Mfn2-/- and rescue MEF cells (Fig. S1G).
6. Fig. 4D-E: Western blots are not of publication quality. Looking at the blots provided in Fig. 4D, the reviewer is not convinced with the quantitative data shown in Fig. 4E. For instance, the intensity of pCaMKII band for "vec" does not look 3x higher than that of "+MFN2", whereas that of "+MFN2" looks much higher than that of WT.
__Response: __We have performed additional western blots and changed the representative images.
* 7. Fig. 5C: The authors should stain for vinculin, which are present in mature FAs only, rather than paxillin which are present in all FAs. This would strengthen the authors' conclusions. Also, FA size should be quantified.*
__Response: __We have quantified FA size in Figure 5. The maturity of FAs is not a major focus of this study. It is likely that most FAs here are mature since they are connected with stress fibers.
* 8. Fig. 6C - Why does the background have a grid and appear grey in color? Also, the cell interior appears in different colors in the different images. The authors should take a z-stack of images and provide the raw image files.*
__Response: __We used a TIRF microscope and imaged a Z stack. Imaris was used to combine the Z-stack images. The images in the manuscripts are now of the lowest stack with background subtraction.
9. Fig 7C: The MLCII Western blot is not of publication quality, and may affect the quantification provided in Fig. 7D.
__Response: __We have performed additional western blots and changed the representative images.
* 10. Fig 8: Do cell treatments with Rho Activator and MLCK-CA also impair migration velocity similar to Mfn2-null cells?*
__Response: __Our data indicated that Rho Activator and MRLC induced the “PAB” structure seen in MFN2 KO cells. It is likely that cell migration is impaired here. Spatiotemporal regulation of Rho Activation is important to cell migration, it is known that Rho overactivation can significantly inhibit cell migration (Nobes & Hall, 1999). Showing Rho Activator and MLCK-CA will reduce cell migration will not add new knowledge to the cell migration field. However not all cell migration defects are associated with the PAB. We, therefore, focused on PAB quantification in this figure.
11. Fig. 9A: The authors claim that wt cells have actin bundles that protrude against the membrane while Mfn2-null cells do not. This does not look convincing as the Mfn2-null actin bundle seem to be pushing against the membrane at the bottom of the image. No quantification is provided. It is unclear what conclusion can be drawn from the super-resolution images.
__Response: __We used super-resolution imaging to demonstrate the details of the peripheral actin band (PAB) structure. We have used two boxes to enlarge the regions where membrane parallel actin structures are predominant. The quantification of PAB is provided in other figures.
12. Suppl. Fig. 5C: The authors should take images using a confocal microscope for cells with Flipper-TR construct, eliminate the background and the cell center to only consider the cell periphery. Nikon TE2000 does not seem to be a confocal microscope.
Response: __The amount of Flipper-TR that MEF cells can take in was limited. With the current signal-to-noise ratio, complete background elimination is not feasible. A confocal microscope is not necessary for Flipper-TR FLIM imaging (García-Calvo et al., 2022). __* Reviewer #3 (Evidence, reproducibility and clarity (Required)):
General Comments (Major) 1. Data Presentation and analysis: The data analysis would benefit from using a method such as Super-Plots to show the data from separate biological repeats and to use N numbers that represent the number of biological repeats rather than the number of cells analysed. Please see the following reference for a suggestion on how to analyse the data: Lord SJ, Velle KB, Mullins RD, Fritz-Laylin LK. SuperPlots: Communicating reproducibility and variability in cell biology. J Cell Biol. 2020 Jun 1;219(6):e202001064. doi: 10.1083/jcb.202001064. PMID: 32346721; PMCID: PMC7265319.*
__Response: __We have changed the dot colors to show data from separate biological repeats.
- Another general comment is that many of the experiments show analysis of very few numbers of cells or maybe only one field of view in a microscopy quantification experiment. This seems unusually low - for example, in Figure 1E only 6 cells have been analysed. It seems like more could have been done and if statistical analysis like we suggest in 1 above is used, this might reveal that some of the differences are less significant than the authors think/report. This is important, as cells are noisy and it is unusual to have such high significance for experiments like cell migration and other parameters unless a lot of measurements are made. In Figure 1G, it appears that only one field of view has been used to quantify the data. We routinely use 3-5 fields of view to get a representative sample of what the cells are doing.*
__Response: __We have quantified more cells and indicated the number of repeats and cells quantified in the figure legend.
- Some of the micrographs appear to be missing scale bars- e.g. Fig. 2H, Fig. 8*
__Response: __We have included scale bars in the lower right corner of all panels.
* 4. In the cell tracking experiments, only some of the cells in the images appear to have been tracked. How were the tracked cells chosen? Normally, we would track every cell to avoid bias in selection.*
__Response: __We tracked all the cells in the view at the beginning of the experiments.
5. The western blot images do not show the molecular size of the bands. Show ladder position
__Response: __We have added bands to show molecular weights.
6. Mostly the graphs show individual data points, which is good, but in some cases only a bar is shown- it would be nice to have individual points overlaid on the bars- e.g. Figure 1I, 4E, 5B, 5E, 7B, 7D
__Response: __We have updated the graph to show individual points.
7. Many of the confocal images look very processed- they have no background and have a hazy black halo around the cell. I am not familiar with the type of processing that was done and I worry that the images are only showing a masked and processed version of the actual data. The authors need to explain what processing they have done and probably also to provide the unprocessed images in a supplementary figure or dataset for readers to see. The methods description is inadequate as it only says Image J was used to process the data.
__Response: __We used a TIRF microscope and imaged a Z stack. Imaris was used to combine the Z-stack images. The images in the manuscripts are now of the lowest stack with background subtraction.
* Individual comments on Figures: Figure 1: See general comments above- consider to use Superplots, more cells and more fields of view in quantifications. Show experimental points in bar graph.*
__Response: __We have quantified more cells and used super plots to display the data. The number of repeats and cells quantified are indicated in the figure legend.
Figure 2: In 2E, the colours are very similar for two of the experiments so it is difficult to distinguish them- e.g. the MFN1 vs MFN2 rescue data both appear dark blue. Response: We have changed the color for MFN1 rescue to distinguish the two samples better.
In 2H are the magnifications really the same for the WT as the +DOX and -DOX? The cell in the WT looks huge. Is this representative? Also, the phalloidin stain looks very spotty on the WT. This seems unusual.
__Response: __The images are of the same scale. The Mfn2-/- MEFs are smaller, and DOX-induced MFN2 expression can only partially rescue the cell size.
* Figure 3: Not many cells were analysed in 3B, especially the zero time point.*
__Response: __We have quantified more cells.
* Please define +T, we assume it is the tether construct, but it is not defined*
__Response: __We defined T as a tether in the main text and the figure legend. In 3F, how were the tracked cells chosen?
__Response: __We tracked all the cells in the view at the beginning of the experiments.
* Figure 4:* 4B: Why have they not tested FK506 and STO609 on the WT cells?
__Response: __We focused on understanding the MFN2 KO phenotype. Since neither FK506 nor STO609 altered the MFN2 KO phenotype, we did not include them in the WT group.
4C: How were the tracked cells chosen?
__Response: __We tracked all the cells in the view at the start of the experiments.
4D-E: The blot doesn't look representative of the quantification- were the numbers normalised to vinculin? The difference between WT and vector looks too large to be real if the amounts were normalised to the vinculin, as vinculin is increased in vector. Likewise, the pCAMKII looks to be substantially decreased from the +MFN2, but this is not what the quantification shows.
__Response: __We have performed additional western blots and changed the representative images.
Figure 5: 5B- please clarify which ratio is shown here. I assume it is the ratio of RhoA-GTP vs RhoA between the zero and 4 minute time points.
__Response: __Yes, we have clarified this point in the figure legend.
5C- These images appear to have a mask around the cell. It is hard to tell where the edge of the cell really is- what sort of processing was used? Especially for the paxillin staining, why is there no cytoplasm shown? Is this because the image is in TIRF?
__Response: __We used a TIRF microscope and imaged a Z stack. Imaris was used to combine the Z-stack images. The images in the manuscripts are now of the lowest stack with background subtraction.
Figure 6: Figure 6C- the blebbistatin treated cell looks very large- is this representative?
__Response: __Yes, Blebbistatin-treated cells are larger (Fig. 6A).
Figure 7: Fig 7C- The lanes for MLCII are all run together- is this from a different gel? Is this quantification accurate?
__Response: __We have performed additional western blots and changed the representative images.
Fig. 7F- What is the % level of knockdown achieved?
__Response: __The level of knockdown is labeled on the figure.
Figure 8: Fig 8A,B- does the scale bar represent all of the images in these two panels?
__Response: __Yes, the figure legend is updated to clarify this point.
Fig 8C,D- Superplots would be helpful here.
__Response: __We have used super plots to display the data.
Supplementary Data: The OCR data do not add much and are not discussed much in the manuscript. Perhaps they could be omitted.
__Response: __Our OCR data ruled out the possibility of metabolic regulation. Since MFN2 is a mitochondria protein with its typical functions in metabolic pathways, we cannot omit its influence on metabolism here. As we observed, shMLCK enhanced OCR, shROCK reduced OCR, and both knock-down rescued cell morphology and motility. We believe that PAB formation is independent of MFN2’s function in metabolic regulation.
Figure S3- The figure label doesn't match the manuscript test- was fibrinogen or collagen used?
__Response: __We tried cover glass alone, collagen, and fibronectin-coated glass. The PAB formation is independent of these extracellular substrates. We did not try fibrinogen because MEF cell is reported to prefer fibronectin (Lehtimäki et al., 2021).
Reference
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Cieri, D., Vicario, M., Giacomello, M., Vallese, F., Filadi, R., Wagner, T., Pozzan, T., Pizzo, P., Scorrano, L., Brini, M., & Calì, T. (2017). SPLICS: a split green fluorescent protein-based contact site sensor for narrow and wide heterotypic organelle juxtaposition. Cell Death & Differentiation 2018 25:6, 25(6), 1131–1145. https://doi.org/10.1038/s41418-017-0033-z
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Kijlstra, J. D., Hu, D., Mittal, N., Kausel, E., van der Meer, P., Garakani, A., & Domian, I. J. (2015). Integrated Analysis of Contractile Kinetics, Force Generation, and Electrical Activity in Single Human Stem Cell-Derived Cardiomyocytes. Stem Cell Reports, 5(6), 1226. https://doi.org/10.1016/J.STEMCR.2015.10.017
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Referee #3
Evidence, reproducibility and clarity
This study explores the importance of MFN2, a known endoplasmic reticulum-mitochondria linker protein, in cell motility and actin-myosin organization. It is known that the mitofusin proteins MFN1 and MFN2 can tether the mitochondria to the ER and are connected with calcium regulation in muscle and non-muscle cell types. Calcium flux mediated by mitofusins has previously been implicated in apoptosis and ER stress. In this study, the authors show that loss or depletion of MFN2 (but not MFN1) can lead to aberrant calcium increase in the cytoplasm and trigger actin-myosin reorganisation. They show that the actin and myosin changes are linked with activation of RhoA and also that they can be suppressed by inhibiting myosin light chain phosphorylation/ activation. They also show that cells with reduced MFN2 are softer (using atomic force microscopy), which agrees with activation of RhoA and contractility. If cells are plated on softer substrata, it partially compensates for the over-activation of RhoA.
In many places, the data support the claims made, but in several places the experiments could be made more convincing or be more clearly presented. Some of the experiments appear to have been repeated only 1-2 times and very few cells or fields of view have been analysed.
General Comments (Major)
- Data Presentation and analysis: The data analysis would benefit from using a method such as Super-Plots to show the data from separate biological repeats and to use N numbers that represent the number of biological repeats rather than the number of cells analysed. Please see the following reference for a suggestion on how to analyse the data: Lord SJ, Velle KB, Mullins RD, Fritz-Laylin LK. SuperPlots: Communicating reproducibility and variability in cell biology. J Cell Biol. 2020 Jun 1;219(6):e202001064. doi: 10.1083/jcb.202001064. PMID: 32346721; PMCID: PMC7265319.
- Another general comment is that many of the experiments show analysis of very few numbers of cells or maybe only one field of view in a microscopy quantification experiment. This seems unusually low - for example, in Figure 1E only 6 cells have been analysed. It seems like more could have been done and if statistical analysis like we suggest in 1 above is used, this might reveal that some of the differences are less significant than the authors think/report. This is important, as cells are noisy and it is unusual to have such high significance for experiments like cell migration and other parameters unless a lot of measurements are made. In Figure 1G, it appears that only one field of view has been used to quantify the data. We routinely use 3-5 fields of view to get a representative sample of what the cells are doing.
- Some of the micrographs appear to be missing scale bars- e.g. Fig. 2H, Fig. 8
- In the cell tracking experiments, only some of the cells in the images appear to have been tracked. How were the tracked cells chosen? Normally, we would track every cell to avoid bias in selection.
- The western blot images do not show the molecular size of the bands.
- Mostly the graphs show individual data points, which is good, but in some cases only a bar is shown- it would be nice to have individual points overlaid on the bars- e.g. Figure 1I, 4E, 5B, 5E, 7B, 7D
- Many of the confocal images look very processed- they have no background and have a hazy black halo around the cell. I am not familiar with the type of processing that was done and I worry that the images are only showing a masked and processed version of the actual data. The authors need to explain what processing they have done and probably also to provide the unprocessed images in a supplementary figure or dataset for readers to see. The methods description is inadequate as it only says Image J was used to process the data.
Individual comments on Figures:
Figure 1: See general comments above- consider to use Superplots, more cells and more fields of view in quantifications. Show experimental points in bar graph.
Figure 2: In 2E, the colours are very similar for two of the experiments so it is difficult to distinguish them- e.g. the MFN1 vs MFN2 rescue data both appear dark blue. In 2H are the magnifications really the same for the WT as the +DOX and -DOX? The cell in the WT looks huge. Is this representative? Also, the phalloidin stain looks very spotty on the WT. This seems unusual.
Figure 3: Not many cells were analysed in 3B, especially the zero time point. Please define +T, we assume it is the tether construct, but it is not defined In 3F, how were the tracked cells chosen?
Figure 4: 4B: Why have they not tested FK506 and STO609 on the WT cells? 4C: How were the tracked cells chosen? 4D-E: The blot doesn't look representative of the quantification- were the numbers normalised to vinculin? The difference between WT and vector looks too large to be real if the amounts were normalised to the vinculin, as vinculin is increased in vector. Likewise, the pCAMKII looks to be substantially decreased from the +MFN2, but this is not what the quantification shows.
Figure 5: 5B- please clarify which ratio is shown here. I assume it is the ratio of RhoA-GTP vs RhoA between the zero and 4 minute time points. 5C- These images appear to have a mask around the cell. It is hard to tell where the edge of the cell really is- what sort of processing was used? Especially for the paxillin staining, why is there no cytoplasm shown? Is this because the image is in TIRF?
Figure 6: Figure 6C- the blebbistatin treated cell looks very large- is this representative?
Figure 7: Fig 7C- The lanes for MLCII are all run together- is this from a different gel? Is this quantification accurate? Fig. 7F- What is the % level of knockdown achieved?
Figure 8: Fig 8A,B- does the scale bar represent all of the images in these two panels? Fig 8C,D- Superplots would be helpful here.
Supplementary Data:
The OCR data do not add much and are not discussed much in the manuscript. Perhaps they could be omitted. Figure S3- The figure label doesn't match the manuscript test- was fibrinogen or collagen used?
Significance
The main novelty here appears to be the connection between excess cytoplasmic calcium, MFN2 loss and RhoA/myosin activation. This is interesting and a useful addition to the literature. It is unclear what the significance is perhaps, as increased cytoplasmic calcium is likely to cause multiple effects in addition to these. So, this effect may be a side-effect of uncoupling the ER and the mitochondria. Nonetheless, it is important to know about this and it will likely inform future studies on the mitofusins.
This will be of interest to basic researchers studying mitochondria function and the connections between signaling and mitochondria function.
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, Wang et al. investigate the role of Mitofusin 2 (Mfn2) in MEF morphology and migration. MEFs lacking Mfn2 exhibit a rather circular shape and reduced migratory potential due to increased cytosolic Ca2+, which activates Ca2+/calmodulin-dependent protein kinase II, RhoA and myosin light-chain kinase (MLCK), triggering non-muscle myosin II overactivation and formation of an F-actin ring at the cell periphery. Overall, this is an interesting study. However, additional work is needed for this manuscript to reach publication quality.
Major Concerns:
- Several of the Western blots are not of publication quality. This may affect their quantification, and the authors' conclusions.
- The authors should examine how treatment of wt MEFs with Rho Activator and MLCK-CA affect cell motility (point #10).
- The reviewer is not convinced that the membrane tension measurements were performed correctly (see point #12 below). The reviewer would expect that the presence of an F-actin ring at the cell periphery would increase the membrane tension, which is opposite to the authors' findings.
Specific Comments:
- Fig. 1A: The Mfn1 Western Blot is not of publication quality. Moreover, quantitation is necessary.
- Fig. 1B (as well as Fig. 2G and others): the date do not reflect cellular size but instead spread cellular area.
- Fig. 1C, D: Mfn1-null MEFs appear to be more spindle-shaped than wt cells, yet their circularity tends to be elevated. Do the authors have an explanation?
- Fig. 2A: The Mfn1 levels in Mfn2-/- + Mfn2 are lower than Mfn2-/-? Does this imply a crosstalk between Mfn1 and Mfn2 expression.
- Fig. 2H: The authors should provide co-staining of mitochondria and Mfn2 as well.
- Fig. 4D-E: Western blots are not of publication quality. Looking at the blots provided in Fig. 4D, the reviewer is not convinced with the quantitative data shown in Fig. 4E. For instance, the intensity of pCaMKII band for "vec" does not look 3x higher than that of "+MFN2", whereas that of "+MFN2" looks much higher than that of WT.
- Fig. 5C: The authors should stain for vinculin, which are present in mature FAs only, rather than paxillin which are present in all FAs. This would strengthen the authors' conclusions. Also, FA size should be quantified.
- Fig. 6C - Why does the background have a grid and appear grey in color? Also, the cell interior appears in different colors in the different images. The authors should take a z-stack of images and provide the raw image files.
- Fig 7C: The MLCII Western blot is not of publication quality, and may affect the quantification provided in Fig. 7D.
- Fig 8: Do cell treatments with Rho Activator and MLCK-CA also impair migration velocity similar to Mfn2-null cells?
- Fig. 9A: The authors claim that wt cells have actin bundles that protrude against the membrane while Mfn2-null cells do not. This does not look convincing as the Mfn2-null actin bundle seem to be pushing against the membrane at the bottom of the image. No quantification is provided. It is unclear what conclusion can be drawn from the super-resolution images.
- Suppl. Fig. 5C: The authors should take images using a confocal microscope for cells with Flipper-TR construct, eliminate the background and the cell center to only consider the cell periphery. Nikon TE2000 does not seem to be a confocal microscope.
Significance
Delineating the role of Mfn2 in cell migration will represent a good, fundamental contribution to the field of cell migration. The reviewer finds this manuscript to be conceptually interesting. Unfortunately, there are technical issues, which need to be fixed so that the readers feel confident about the conclusion of this study.
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Referee #1
Evidence, reproducibility and clarity
Summary:
Wang et al use a combination of cell biological and biochemical approaches to show that Mitofusin2 (MFN2) - a protein typically known to regulate mitochondrial morphology - regulates cell morphology by regulating calcium levels and downstream cell contractility players. They show that cells deficient in MFN2 exhibit increased intracellular calcium levels, and overactivation of myosin II, leading to increased cell contractility. Furthermore, MFN2-deficient cells exhibit an F-actin ring around the cell periphery (which they call PABs). The study takes advantage of both pharmacological and genetic perturbations, as well a variety of assays to support many of their findings; however, it is unclear how these findings are related to each other. Furthermore, MFN2-related disease was raised a few times in the abstract and throughout the manuscript, but it's unclear how the findings in the paper relate to disease states, both in terms of the cell biology, as well as the model that was used (MEFs). This reviewer applauds the authors for exploring MFN2 function outside of its conventional role in mitochondria; but it was difficult to parse through the findings to resolve a mechanistic explanation for how MFN2 affect cell behavior, and what role, if any, PABs have on biological function. While it is important to dissect mitochondrial-independent functions for MFN2, given the whole scale changes in cells in MFN2-deficient cells, and the fact that there is a metabolic phenotype, it is difficult to know how many of the observed phenotypes are downstream of perturbed mitochondrial function versus on cytoskeletal dynamics directly.
Major comments:
Are the key conclusions convincing?
- Key conclusions that were convincing:
- MFN2-/- cells exhibit decreased cell velocity, decreased cell size, increased cell circularity, and increased intracellular calcium
- modifying the levels of calcium has an effect on cell circulariy.
- MFN2-/- cells exhibit increased activation of contractility players
- Key conclusions that were less convincing:
- RhoA and NMII are in the title as mechanistic downstream regulators of CaM, but the results in Fig 8 call into question the role of RhoA. Why does RhoA activation not influence cell size and circularity? Can you overexpress MRLC-GFP and inhibit Rho and restore the wt phenotype? The role of NMII is also not clear - why does overexpressing MLCK-CA not have a phenotype but overexpressing MLCK downstream target MRLC show the phenotype? Are there any alternative pathways to regulate MRLC? It's not being discussed or described in 6D's schematic.
- The role of ER/mito contacts in the system was unclear (since ER/mito contacts were not observed nor evaluated directly).
- What role does focal adhesions have on PAB formation or any part of the model - There were results showing larger focal adhesions in the MFN2-/- cells, but not sure how this fits in with the bigger picture of contractility and PABs, and focal adhesions were not in the model in Figure 5.
- Whether regulating calcium impacts PAB formation
- The role of PABs in migration is also unclear - can you affect PAB formation or get rid of PABs and quantify cell migration?
- It was hard to understand the correlation between the membrane tension of MFN2-/- cells and its ability to spread on softer substrates. How does this result fit in with the overarching model?
Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
- There were a number of findings that did not seem to fit in with the paper, or they were included, but were not robustly described nor quantified. As an example, Paxillin-positive focal adhesions were evaluated in MFN2-/- and with various pharmacological approaches, but there is no quantification with respect to size, number, or distribution of focal adhesions, despite language in the main text that there are differences between conditions. Also, the model was presented in figure 5, and then there were several pieces of data presented afterward, some that are included in the model (myosin regulation), and some that are not in the model (membrane tension, TFM, substrate stiffness, etc). The stiffness/tension figure was not clear to me, and it was difficult to make sense of the data since one would predict that an increase in actomyosin contractility at the cortex would lead to higher membrane tension, not lower, and then how membrane tension relates to spreading on soft matrices is also unclear. The manuscript seems like an amalgamation of different pieces of data that do not necessarily fit together into a cohesive story, so the authors are encouraged to either remove these data, or shore them up and weave them into the narrative.
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.
- The imaging used for a lot of the quantification (migration, circularity) is difficult to resolve. The cells often look like they are not imaged in the correct imaging plane. It would be helpful to have better representative images such that it is clear how the cells were tracked and how cell periphery regions of interest were manually drawn. Focal adhesions should also be shown without thresholding.
- For most of the quantification, it appears that the experiment was only performed once and that a handful of cells were quantified. The figure legend indicates the number of cells (often reported as >12 cells or >25 cells), but the methods indicate that high content imaging was performed, and so the interpretation is that these experiments were only performed once. Biological replicates are required. If the data do represent at least 3 biological replicates, then more cell quantification is required (12 or 25 cells in total would mean quantifying a small number of cells per replicate).
- Mitochondrial morphology and quantification should be performed in the MFN2 knockdown and rescue lines.
- Many of the comparisons throughout the figures is between MFN2 knockdown and MFN2 knockdown plus rescue or genetic/pharmacological approaches, but a comparison that is rarely made is between wildtype and experimental. These comparisons could be useful in comparing partial rescues and potential redundancies with the other mitofusin.
- For the mito/ER tethering experiments, it is important to show that ER/mito contacts are formed and not formed in the various conditions with imaging approaches
- For some of the pharmacological perturbations, it would be helpful to show that the perturbation actually led to the expected phenotype - as an example, in cells treated with different concentrations of A23187, what are the intracellular calcium levels and how do these treatments influence PAB formation? This aspect should be generally applied across the study - when a modification is made, that particular phenotype should first be evaluated, before dissecting how the perturbation affects downstream phenotypes.
- In Figures 4 and 5, the thresholding approaches in the images make the focal adhesions difficult to resolve, and therefore it is difficult to determine the size. As described above, these metrics should be defined and quantified.
- What is a PAB? How is it defined? What metrics make a structure a PAB versus regular cortical actin - are there quantifiable metrics? In figure 8, there are some structures that are labelled as a PAB, but some aren't (as an example, the left panel in 8b is a PAB, but the right panel in 8A is not, but they look the same), so a PAB should be defined with quantifiable measures, and then applied to the entire study.
- As described above, why does RhoA activation not influence cell size and circularity? Can you overexpress MRLC-GFP and inhibit Rho and restore the wildtype phenotype?
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.
- These suggested experiments described above will take a substantial amount of time and money, as it appears that some experiments were only performed once, and therefore many of these experiments might need to be performed 2-3 more times. Also, experiments showing that addition of drugs lead to expected outcomes prior to analyzing downstream phenotypes will also require a significant amount of time. It is hard to predict how long it will take, but we would guess, 6-8 months?
Are the data and the methods presented in such a way that they can be reproduced?
- We appreciate that the authors quantified many parameters, although some quantifications were missing. There are some missing methods - how was directionality quantified, was migration quantified by selecting the approximate center of cells using MTrackJ or were centroids quantified by outlining cells, for instance. Also, given that some of the phenotypes were somewhat arbitrarily assigned (ie. what constitutes a PAB?), it may be difficult to reproduce these approaches and interpret data appropriately.
Are the experiments adequately replicated and statistical analysis adequate?
- Unfortunately, while the approximate number of cells was reported, the number of biological replicates were not reported, and therefore, the experimental information and statistical analyses are not adequate.
Minor comments:
Specific experimental issues that are easily addressable. - for some of the graphs - mostly about calcium levels - fold change is shown, but raw values should also be included to determine whether the basal levels of calcium are different across the conditions. - scale bars in every panel should also help make the points clearer.
Are prior studies referenced appropriately?
- Yes
Are the text and figures clear and accurate?
- Some of the data in the figures were unclear - see above for more info.
Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
- See above for more info.
Significance
Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
- There is a growing field of mitochondrial biology and how it relates to cell migration. This paper examines the function of a key mitochondrial morphology regulator, MFN2, and dissects a role for MFN2 in migration at the level of cytoskeletal regulation. We think that this is interesting, and that it's clear that MFN2 has multiple functions in the cell, but the phenotypes are so pleiotropic that it's difficult to parse out mechanistic understanding. The authors also describe a new actin architecture - a structure that they refer to as PABs - but there is no indication that PABs form in other cell types or tissues, or in other contexts, so it is unclear whether PABs are an important structure or an artifact of the system. Furthermore, part of the motivation of the work seems to be to understand MFN-related pathologies, but using a MEF system does not necessarily allow for that. One way to strengthen this part of the manuscript is to potentially use disease-relevant MFN2 mutations and determine downstream effects on cell morphology and migration.
State what audience might be interested in and influenced by the reported findings.
- This work would appeal to card-carrying cell biologists.
Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.
- cell migration; actin; mitochondria
- Key conclusions that were convincing:
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Reply to the reviewers
We would like to thank all the reviewers for their positive evaluations of our work and constructive comments, in particular for highlighting that our work “provides new insight into cancer metabolism knowledge”, is “conceptually interesting and experimentally well performed” and “the findings presented here will be very interesting to a broad range of researchers, including the cancer, metabolism and wider cell biology communities”.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): Nazemi et al. show that the extracellular matrix (ECM) has a crucial role in sustaining the growth of invasive breast and pancreatic cells during nutrient deprivation. In particular, under amino acid starvation, cancer cells internalize ECM by macropinocytosis and activate phenylalanine and tyrosine catabolism, which in turn support cell growth in nutrient stress conditions. The paper is well written and the results shown are very interesting. The experimental plan is well designed to assess the hypothesis and the description of the methods is sufficiently detailed to reproduce the analyses, which are also characterized by appropriate internal controls. Finally, the data provided sustain the conclusions proposed by the authors.
* Major comment:*
Since the authors performed their experiments on invasive breast and pancreatic cancers and it has been noted that stress conditions could promote the escape of cancer cells from the site of origin (e.g., Jimenez and Goding, Cell Metabolism 2018; Manzano et al, EMBO Reports 2020), it would be interesting to evaluate how ECM internalization could have a role in sustaining the invasive abilities of cancer cells under amino acid starvation. Which is the impact of the inhibition of macropinocytosis and tyrosine catabolism on cell invasion? The authors could evaluate this aspect by in vitro 2D and 3D analysis.
This is a very important point, and we are planning to investigate this by using:
- 2D single cell migration assays on cell-derived matrices (we have extensively used this system to characterise invasive cell migration; Rainero et al., 2015; Rainero et al., 2012)
- 3D spheroids assays, to assess collective/3D cell invasion through collagen I and matrigel mixtures. Both experiments will be performed under amino acid starvation, in the presence of pharmacological inhibitors and siRNAs targeting macropinocytosis (FRAX597, PAK1) and tyrosine catabolism (Nitisinone, HPDL). Preliminary data suggest that both FRAX597 and Nitisinone reduce cell invasiveness.
In addition, to strengthen the paper and give a stronger significance in terms of clinical translatability, it could be useful to implement the analysis of breast and pancreatic patients by publicly dataset evaluating for example free survival, disease free survival, overall survival and metastasis free survival.
We have now included in the manuscript new data in figure 6 O-R showing that high HPDL expression correlates with reduces overall survival, distant metastasis-free survival, relapse-free survival and palliative performance scale in breast cancer patients. In response to other reviewers’ comments, we have removed the pancreatic cancer data from our manuscript.
Minor Comment:
The text and the figures are clear and accurate. The references cited support the hypothesis, rightly introduce the results and are appropriate for the discussion. However, the paragraph relative to figure 4 is a little confusing. Changing the order of the description of the results could be useful.
We apologise for the lack of clarity in this section. We have now re-organised the data both in the figure and in the result section, to describe the findings in a more logical way.
Reviewer #1 (Significance (Required)): Based on my metabolic background in tumour aetiology and progression, I think that this study provides new insights into cancer metabolism knowledge, in particular on how the stroma may drive metabolic reprogramming of cancer cells sustaining cell growth in nutrient stress conditions. Together with other similar studies on the stromal non-cellular components, the data here shown can contribute to expand the knowledge on the factors that promote cancer metabolic plasticity, which is exploited from cancer cells to obtain advantages in terms of growth, survival and progression. In conclusion, I think that the results shown are new and the manuscript is well presented. Following the short revision process suggested, it will be eligible for a final publication in a medium-high impact factor journal.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
- Please find enclosed my reviewing comments on the manuscript entitled "The extracellular matrix supports cancer cell growth under amino acid starvation by promoting tyrosine catabolism" by Nazemi et al.*
In this manuscript the group of Elena Romero and colleagues provides evidence that breast cancer cells, and pancreatic cancer cell, use matrix proteins degradation to feed their proliferative metabolic needs under amino acid starvation. Under this drastic condition, cancer cells use micropinocytosis to uptake matrix proteins, a process that requires mTORC1 activation and PAK1. Furthermore, a metabolomic study demonstrates that ECM-dependent cancer cell growth relies on tyrosine catabolism. Altogether, I found this study conceptually interesting and experimentally well performed. Experiments are well controlled and state-of-the-art technologies used in this manuscript make it a good candidate for publication. However, some aspects of the work need to be strengthen to reinforce the overall good quality of the manuscript, therefore, please find below some experimental propositions. 1. Despite the reviewer proposition, I believe that the additional experiments using the PDAC cancer cell does not improve the quality of the manuscript. Instead, it brings confusion to me, since the relative addition is minor compare to what is demonstrated using breast cancer cells.
We have decided to remove the pancreatic cancer cell data from the manuscript.
To importantly improve the potential impact of this manuscript, I suggest to add in vivo data using either syngenic mice model of breast cancer or xenografted human breast cancer cells in nude mice. What would be the impact of micropinocytosis and tyrosine catabolism inhibition on cancer growth, in vivo, should be demonstrated? If possible, it may be interesting to demonstrate that this micropinocytosis may interfere with cancer evolution toward a metastatic phenotype using, for example, the PyMT-MMTV mice model of breast cancer development?
We will perform orthotopic mammary fat pad injections in immunocompetent mice, to monitor primary tumour growth and localised invasion in the presence of Nitisinone or vehicle control. PyMT-driven breast cancer cells have been generated in the Blyth lab, from FVB-pure MMTV-PyMT mice and we have preliminary data indicating that these cells are able to internalise ECM and grow under starvation in an ECM-dependent manner. Prior to performing any in vivo work, we will perform further in vitro experiment to confirm the role of tyrosine catabolism in these cells. Nitisinone is an FDA-approved drug that has already been used in mouse models. Blood tyrosine levels can be measured to assess tyrosine catabolism inhibition by Nitisinone. These experiments will be conducted in collaboration with the Blyth lab at the CRUK Beatson Institute in Glasgow.
Data obtained using cancer cells with different metastatic property suggest that the ability to use ECM to compensate for soluble nutrient starvation is acquired during cancer progression. To further demonstrate that it is the case, would it be possible that non metastatic breast cancer cells are not able to perform micropinocytosis? Is PAK1 overexpressed with increase cancer cells metastatic ability, without affecting invasive capacity in 3D spheroids?
To address these points, we have started to measure PAK1 expression across the MCF10 series of cell lines, where MCF10A are non-transformed mammary epithelial cells, MCF10A-DCIS are ductal carcinoma in situ cells and MCF10CA1 are metastatic breast cancer cells. Our preliminary data show that there is no upregulation of PAK1 expression in the metastatic cells compared to non-transformed or non-invasive cancer cells. This suggest that the over-expression of PAK1 might not be a valuable strategy to address this point.
In addition, we found that collagen I uptake was upregulated in MCF10CA1 compared to MCF10A and MCF10A-DCIS. We will corroborate our preliminary data by quantifying collagen I and cell-derived matrices internalisation across the 3 cell lines.
What would be the efficacy to promote the ECM-dependent growth under starvation following a mTORC1 in non-invasive cancer cells?
We will measure the growth of MCF10A and MCF10A-DCIS on ECM under starvation in the presence of the mTOR activator MHY1485. Western blot analysis of downstream targets of mTORC1 (p-S6 and p-4EBP1) will confirm the extent of mTOR activation.
The discrepancy of cancer cells proliferation under starvation condition between plastic and ECM-based supports could be explained by the massive difference of support rigidity. This is also probably the case between CDM made by normal fibroblast and CAF. It brings the question of studying the role of matrix stiffness in regard to micropinocytosis-dependent cancer cells growth. It would also explain why this process is link to aggressive cancer cell behaviour, as ECM goes stiffer with time in cancer development. It may not be the case, but the demonstration that mechanical cues from the ECM could regulate the micropinocytosis-dependent cancer cells growth under amino acid starvation could bring additional value to the manuscript.
We will use 2 experimental approaches to address the effect of different stiffness in ECM-dependent cell growth:
- Polyacrylamide hydrogels coated with different ECM components.
- Collagen I gels in which the stiffness is modified by Ribose treatment (this approach has been published by the Parson’s lab). Our preliminary data confirmed that ribose cross-linking increased YAP nuclear localisation and collagen I can still be internalised under these conditions. We will assess ECM endocytosis and cell growth under starvation conditions (using EdU incorporation in conjunction with A and high throughput imaging with B)
Along with this, it has been demonstrated that matrix rigidity regulates glutaminolysis in breast cancer, resulting in aspartate production and cancer cells proliferation. Is asparate production increase by micropinocytosis? Could you rescue cancer cells growth by aspartate supplementation?
Our metabolomics experiments were performed under amino acid starvation; therefore glutamine was not present in the media. Nor glutaminolysis intermediates nor aspartate were upregulated on ECM compared to plastic in our datasets, suggesting that aspartate might not be involved in this system. We added this point in the discussion. However, glutamine, glutamate and aspartate were found to be upregulated on collagen I compared to plastic in complete media, where the most enriched pathway was alanine, aspartate and glutamate metabolism. Future work will address the role of the ECM in supporting cancer cell metabolism in the absence of nutrient starvation.
Data presented in Fig 1 and SF1 show that breast cancer cell lines growth in a comparable manner either they are cultured on plastic or on 3D ECM substrates in complete media. Again, on thick 3D substrates, in which the stiffness is lower compared to plastic, I would have thought that cancer cells would have grown slower. Could you please discuss this finding in regard to the literature?
Our experiments in full media were performed in the presence of dialysed serum, to represent a better control for the starvation conditions, which were in the presence of dialysed serum. This is consistent with a vast body of literature assessing nutrient starvation conditions in the presence of dialysed serum. This could explain the discrepancy between ours and published results. We have addressed this point in the discussion.
If you have the capacity to do so in your lab or in collaboration, would it be possible to measure the exact stiffness of the different matrix you use in this manuscript? Or using hydrogel, would it be possible to study the role of matrix stiffness in the ECM-dependent cancer cells growth under AA starvation? I would understand that this may be out of the scope of the present manuscript, but I again believe that such finding would reinforce the manuscript.
We don’t have the capacity to measure the stiffness in our lab, however NF-CDM and CAF-CDM, generated by the same cells and using the same protocol, have been previously measured at ~0.4kPa and ~0.8 kPa, respectively (Hernandez-Fernaud et al., 2017). We have now included this in the paper. As mentioned in response to point 4, we will use hydrogels to directly test the effect of matrix stiffness on ECM-dependent cell growth under nutrient starvation.
In SF 3A-C, it is shown that ECM does not affect caspase-dependent cell death under AA starvation. Did you considered a non-caspase dependent cell death that may be triggered by AA starvation?
We will complement the caspase 3/7 data by performing PI staining, to detect all forms of cell death. Preliminary data indicate that, consistent with our cas3/7 data, amino acid starvation promotes cell death, but the presence of the ECM doesn’t affect the percentage of PI positive cells, corroborating our conclusions that the ECM modulates cell proliferation and not cell death. We will complete these experiments in both MDA-MB-231 and MCF10CA1 cells and will include them in figure S3.In fig 5, it is shown that inhibition of Focal Adhesion Kinase (FAK) does not impair the ECM-dependent rescue of cancer cell growth under starvation. To further decipher the concept of adhesion dependent signalling, maybe the authors could also inhibit the Src kinase or ITG-beta1 activation?
Integrin b1 is also required for ECM internalisation (our unpublished data), therefore interfering with integrin function would make the interpretation of the data quite complex. As suggested by the reviewer, we will use the Src inhibitor PP2, which has been extensively used in the literature in MDA-MB-231 cells. Preliminary data indicate that, despite significantly reducing cell proliferation in complete media, Src inhibition does not affect cell growth on collagen I under amino acid starvation, consistent with our FAK inhibitor data. We will complete these experiments on both collagen I and cell-derived matrices and will include them in figure 5.
Minor comment, in F1B, it is written "AA free starvation" while in every others legend, it is written "AA starvation". I believe the "free" should be removed.
We apologise for this mistake; we have now removed “free” from the legend.
Reviewer #2 (Significance (Required)): Altogether, I found this study conceptually interesting and experimentally well performed. Experiments are well controlled and state-of-the-art technologies used in this manuscript make it a good candidate for publication. However, some aspects of the work need to be strengthen to reinforce the overall good quality of the manuscript.
Reviewer #3 (Evidence, reproducibility and clarity (Required)): In this manuscript the authors explore the mechanisms that metastatic cancer cells use to adapt their metabolism. The authors show that the growth of cancer cell lines is supported by uptake of ECM components in nutrient-starved conditions. The authors propose a very interesting mechanism in which the cells adapt their metabolism to ECM uptake as nutrient source via a PAK1-dependent macropinocytosis pathway which in turn increases tyrosine catabolism. Several key aspects of the authors complex hypothesis require further controls to fully support the authors ideas. As a disclaimer we do not feel qualified enough to comment on the metabolite experiments. Please find our detailed comments below.
* Major -The ECM mediated increase of cell growth under amino acid (AA) starvation is nicely shown In Fig.1 but the authors should include the full medium data from figure S1 in the graphs of Fig. 1 to enable the reader to evaluate the magnitude of rescue effect of the ECM components. The values should also be included in the results text*.
We have now moved all the complete media data into the main figure and highlighted the extent of the rescue in the result section.
Also the authors only glutamine starve in Fig1&2 and then don't mention it again can the authors please include a sentence to explain why this experiment was dropped.
As now highlighted in the result section, we focused on the amino acid starvation as it resulted in the strongest difference between normal and cancer. On the one hand, also non-invasive breast cancer cells can use ECM (namely matrigel) to grow under glutamine starvation, while this is not the case under amino acid starvation. On the other hand, only CAF-CDM, but not normal-CDM, could rescue cell growth under amino acid starvation. We reasoned that this condition was more likely to identify cancer-specific phenotypes.
- The evaluation of uptake pathways is very interesting. The focus on macropinocytosis is not entirely justified in our opinion looking at FigS4A. Caveolin1/2 and DNM1/3 seem to have strongest effect on uptake of Matrigel and not PAK1? Statements like "Since our data indicate that macropinocytosis is the main pathway controlling ECM endocytosis..." are not justified nor are they really needed in our opinion. Several pathways can be implicated in passive uptake.
We have now removed the statement, as suggested by the reviewer. In addition, we will assess CDM uptake upon caveolin 1/2 and DNM 2/3 knock-down, to test whether the effects are matrigel specific.
- The authors use FAK inhibition to evaluate the effect of focal adhesion signalling on their phenotypes and conclude that there is no connection between the observed increase of cell proliferation in presence of ECM and adhesion signalling. To make this assessment the authors need at the very least to show that their FAK inhibitor treatment at the used concentration results in changes in focal adhesions and the associated force transduction.
In the result section, we are including a western blot analysis showing that the concentration of FAK inhibitor used in sufficient so significantly reduced FAK auto-phosphorylation. Based on published evidence (Horton et al., 2016), FAK inhibition does not affect focal adhesion formation, but only the phosphorylation events. Therefore, we don’t think that we will be able to detected changes in focal adhesions regardless of the concentration of the inhibitor we use. To strengthen the observation that ECM-dependent cell growth in independent from adhesion signalling, as suggested by reviewer #2, we will use the Src inhibitor PP2, which has been extensively used in the literature in MDA-MB-231 cells. Preliminary data indicate that, despite significantly reducing cell proliferation in complete media, Src inhibition does not affect cell growth on collagen I under amino acid starvation, consistent with our FAK inhibitor data. We will complete these experiments on both collagen I and cell-derived matrices and will include them in figure 5.
-The pancreatic cancer data currently feels a bit like an afterthought. We suggest to remove this data from the manuscript. If this data is included we suggest the authors should expand this section and repeat key experiments of earlier figures.
We have now removed these data from the manuscript, as this was also the suggestion of reviewer #2.
-Was the fetal bovine serum (FBS) and Horse Serum (HS) the authors use in their experiments tested for ECM components? The authors mention that the FBS for MDA231 cells was dialysed but not the HS.
HS was used at a much lower concentration that FBS in our cell proliferation experiments (2.5% compared to 10%). We will characterise both sera components by mass spectrometry analysis, in collaboration with Dr Collins, biOMICS Facility, University of Sheffield.
Minor comments:
-Please can the authors provide experimental data directly comparing NF-CAM versus CAF-CDM on the same graph (Figure 1D-E).
In the experiments included in the manuscript, the two matrices were generated independently, and we don’t feel it is appropriate to combine the results in the same graph. We are now repeating these experiments by generating both matrices in the same plates, so that we can present the data in the same graph. -Please can the authors give more insight to the use of 25% Plasmax to mimic starved tumor microenvironment. Is there previous research that suggests the nutrient values are representative of TME?
Apologies for not clarifying this in the initial submission, the rationale behind this choice is based on the observation that, in pancreatic cancers, nutrients were shown to be depleted between 50-75% (Kamphorst et al., 2015). We have now stated this in the result section.
-Fig3E Can the authors please include example images of the pS6 staining in the supplementary figures and explain "mTOR endosomal index" in figure legend.
We have now included the representative images (new figure 3E) and we have described how the mTOR endosomal index was calculated both in the figure legend and in the method section. -Can the authors include a negative control for the mTORC1 localisation in Fig.3 (such as use of rapamycin/Torin)?
Amino acid starvation is the gold-standard control for mTORC1 lysosomal targeting, as described in a variety of publications, including Manifava et al., 2016; Meng et al., 2021; Averous et al., 2014. In addition, Torin 1 treatment has been shown to result in a significant accumulation of mTOR on lysosomes compared with untreated cells (Settembre et al., 2012). Consistent with this, we looked at mTOR localisation in the presence of Rapamycin and we did not detect any reduction in lysosomal targeting.
- The PAK1 expression level blots in the knockdown experiments should be quantified from N=3.
We have not included the quantification of the western blots in the new supplementary figure 5.
-What is the FA index in Fig.5, explain how it is calculated. Why not use FA size alone?
We have now defined this is the method section. We haven’t used FA size alone, as this measure can be affected by cell size. If a cell is bigger, the overall FA size will be bigger, but this doesn’t necessarily reflect a change in adhesions.
-Can the authors please use paragraphs on page 9 to improve readability. We apologise for overlooking this, we have now used paragraph in this section.
Reviewer #3 (Significance (Required)): The findings presented here will be very interesting to a broad range of researchers including the cancer, metabolism and wider cell biology communities. The Rainero lab has progressed the idea that ECM uptake supports cancer progression and the data presented here has the potential to significantly advance our understanding of the underlying cellular mechanisms.
-
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Referee #3
Evidence, reproducibility and clarity
In this manuscript the authors explore the mechanisms that metastatic cancer cells use to adapt their metabolism. The authors show that the growth of cancer cell lines is supported by uptake of ECM components in nutrient-starved conditions. The authors propose a very interesting mechanism in which the cells adapt their metabolism to ECM uptake as nutrient source via a PAK1-dependent macropinocytosis pathway which in turn increases tyrosine catabolism. Several key aspects of the authors complex hypothesis require further controls to fully support the authors ideas. As a disclaimer we do not feel qualified enough to comment on the metabolite experiments. Please find our detailed comments below.
Major
- The ECM mediated increase of cell growth under amino acid (AA) starvation is nicely shown In Fig.1 but the authors should include the full medium data from figure S1 in the graphs of Fig. 1 to enable the reader to evaluate the magnitude of rescue effect of the ECM components. The values should also be included in the results text. Also the authors only glutamine starve in Fig1&2 and then don't mention it again can the authors please include a sentence to explain why this experiment was dropped.
- The evaluation of uptake pathways is very interesting. The focus on macropinocytosis is not entirely justified in our opinion looking at FigS4A. Caveolin1/2 and DNM1/3 seem to have strongest effect on uptake of Matrigel and not PAK1? Statements like "Since our data indicate that macropinocytosis is the main pathway controlling ECM endocytosis..." are not justified nor are they really needed in our opinion. Several pathways can be implicated in passive uptake.
- The authors use FAK inhibition to evaluate the effect of focal adhesion signalling on their phenotypes and conclude that there is no connection between the observed increase of cell proliferation in presence of ECM and adhesion signalling. To make this assessment the authors need at the very least to show that their FAK inhibitor treatment at the used concentration results in changes in focal adhesions and the associated force transduction.
- The pancreatic cancer data currently feels a bit like an afterthought. We suggest to remove this data from the manuscript. If this data is included we suggest the authors should expand this section and repeat key experiments of earlier figures.
- Was the fetal bovine serum (FBS) and Horse Serum (HS) the authors use in their experiments tested for ECM components? The authors mention that the FBS for MDA231 cells was dialysed but not the HS.
Minor comments:
- Please can the authors provide experimental data directly comparing NF-CAM versus CAF-CDM on the same graph (Figure 1D-E)
- Please can the authors give more insight to the use of 25% Plasmax to mimic starved tumor microenvironment. Is there previous research that suggests the nutrient values are representative of TME?
- Fig3E Can the authors please include example images of the pS6 staining in the supplementary figures and explain "mTOR endosomal index" in figure legend.
- Can the authors include a negative control for the mTORC1 localisation in Fig.3 (such as use of rapamycin/Torin)?
- The PAK1 expression level blots in the knockdown experiments should be quantified from N=3
- What is the FA index in Fig.5, explain how it is calculated. Why not use FA size alone?
- Can the authors please use paragraphs on page 9 to improve readability.
Significance
The findings presented here will be very interesting to a broad range of researchers including the cancer, metabolism and wider cell biology communities. The Rainero lab has progressed the idea that ECM uptake supports cancer progression and the data presented here has the potential to significantly advance our understanding of the underlying cellular mechanisms.
-
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Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
Please find enclosed my reviewing comments on the manuscript entitled "The extracellular matrix supports cancer cell growth under amino acid starvation by promoting tyrosine catabolism" by Nazemi et al.
In this manuscript the group of Elena Romero and colleagues provides evidence that breast cancer cells, and pancreatic cancer cell, use matrix proteins degradation to feed their proliferative metabolic needs under amino acid starvation. Under this drastic condition, cancer cells use micropinocytosis to uptake matrix proteins, a process that requires mTORC1 activation and PAK1. Furthermore, a metabolomic study demonstrates that ECM-dependent cancer cell growth relies on tyrosine catabolism.
Altogether, I found this study conceptually interesting and experimentally well performed. Experiments are well controlled and state-of-the-art technologies used in this manuscript make it a good candidate for publication. However, some aspects of the work need to be strengthen to reinforce the overall good quality of the manuscript, therefore, please find below some experimental propositions.
- Despite the reviewer proposition, I believe that the additional experiments using the PDAC cancer cell does not improve the quality of the manuscript. Instead, it brings confusion to me, since the relative addition is minor compare to what is demonstrated using breast cancer cells.
- To importantly improve the potential impact of this manuscript, I suggest to add in vivo data using either syngenic mice model of breast cancer or xenografted human breast cancer cells in nude mice. What would be the impact of micropinocytosis and tyrosine catabolism inhibition on cancer growth, in vivo, should be demonstrated? If possible, it may be interesting to demonstrate that this micropinocytosis may interfere with cancer evolution toward a metastatic phenotype using, for example, the PyMT-MMTV mice model of breast cancer development?
- Data obtained using cancer cells with different metastatic property suggest that the ability to use ECM to compensate for soluble nutrient starvation is acquired during cancer progression. To further demonstrate that it is the case, would it be possible that non metastatic breast cancer cells are not able to perform micropinocytosis? Is PAK1 overexpressed with increase cancer cells metastatic ability, without affecting invasive capacity in 3D spheroids? What would be the efficacy to promote the ECM-dependent growth under starvation following a mTORC1 activation or PAK1 activation in non-invasive cancer cells?
- The discrepancy of cancer cells proliferation under starvation condition between plastic and ECM-based supports could be explained by the massive difference of support rigidity. This is also probably the case between CDM made by normal fibroblast and CAF. It brings the question of studying the role of matrix stiffness in regard to micropinocytosis-dependent cancer cells growth. It would also explain why this process is link to aggressive cancer cell behaviour, as ECM goes stiffer with time in cancer development. It may not be the case, but the demonstration that mechanical cues from the ECM could regulate the micropinocytosis-dependent cancer cells growth under amino acid starvation could bring additional value to the manuscript.
- Along with this, it has been demonstrated that matrix rigidity regulates glutaminolysis in breast cancer, resulting in aspartate production and cancer cells proliferation. Is asparate production increase by micropinocytosis? Could you rescue cancer cells growth by aspartate supplementation?
- Data presented in Fig 1 and SF1 show that breast cancer cell lines growth in a comparable manner either they are cultured on plastic or on 3D ECM substrates in complete media. Again, on thick 3D substrates, in which the stiffness is lower compared to plastic, I would have thought that cancer cells would have grown slower. Could you please discuss this finding in regard to the literature? If you have the capacity to do so in your lab or in collaboration, would it be possible to measure the exact stiffness of the different matrix you use in this manuscript? Or using hydrogel, would it be possible to study the role of matrix stiffness in the ECM-dependent cancer cells growth under AA starvation? I would understand that this may be out of the scope of the present manuscript, but I again believe that such finding would reinforce the manuscript.
- In SF 3A-C, it is shown that ECM does not affect caspase-dependent cell death under AA starvation. Did you considered a non-caspase dependent cell death that may be triggered by AA starvation?
- In fig 5, it is shown that inhibition of Focal Adhesion Kinase (FAK) does not impair the ECM-dependent rescue of cancer cell growth under starvation. To further decipher the concept of adhesion dependent signalling, maybe the authors could also inhibit the Src kinase or ITG-beta1 activation?
- Minor comment, in F1B, it is written "AA free starvation" while in every others legend, it is written "AA starvation". I believe the "free" should be removed.
Significance
Altogether, I found this study conceptually interesting and experimentally well performed. Experiments are well controlled and state-of-the-art technologies used in this manuscript make it a good candidate for publication. However, some aspects of the work need to be strengthen to reinforce the overall good quality of the manuscript.
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Referee #1
Evidence, reproducibility and clarity
Nazemi et al. show that the extracellular matrix (ECM) has a crucial role in sustaining the growth of invasive breast and pancreatic cells during nutrient deprivation. In particular, under amino acid starvation, cancer cells internalize ECM by macropinocytosis and activate phenylalanine and tyrosine catabolism, which in turn support cell growth in nutrient stress conditions.
The paper is well written and the results shown are very interesting. The experimental plan is well designed to assess the hypothesis and the description of the methods is sufficiently detailed to reproduce the analyses, which are also characterized by appropriate internal controls. Finally, the data provided sustain the conclusions proposed by the authors.
Major comment:
Since the authors performed their experiments on invasive breast and pancreatic cancers and it has been noted that stress conditions could promote the escape of cancer cells from the site of origin (e.g., Jimenez and Goding, Cell Metabolism 2018; Manzano et al, EMBO Reports 2020), it would be interesting to evaluate how ECM internalization could have a role in sustaining the invasive abilities of cancer cells under amino acid starvation. Which is the impact of the inhibition of macropinocytosis and tyrosine catabolism on cell invasion? The authors could evaluate this aspect by in vitro 2D and 3D analysis. In addition, to strengthen the paper and give a stronger significance in terms of clinical translatability, it could be useful to implement the analysis of breast and pancreatic patients by publicly dataset evaluating for example free survival, disease free survival, overall survival and metastasis free survival.
Minor Comment:
The text and the figures are clear and accurate. The references cited support the hypothesis, rightly introduce the results and are appropriate for the discussion. However, the paragraph relative to figure 4 is a little confusing. Changing the order of the description of the results could be useful.
Significance
Based on my metabolic background in tumour aetiology and progression, I think that this study provides new insights into cancer metabolism knowledge, in particular on how the stroma may drive metabolic reprogramming of cancer cells sustaining cell growth in nutrient stress conditions. Together with other similar studies on the stromal non-cellular components, the data here shown can contribute to expand the knowledge on the factors that promote cancer metabolic plasticity, which is exploited from cancer cells to obtain advantages in terms of growth, survival and progression.
In conclusion, I think that the results shown are new and the manuscript is well presented. Following the short revision process suggested, it will be eligible for a final publication in a medium-high impact factor journal.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
This study by Viedor et al. examines the role of TIS7 (IFRD1) and its ortholog SKMc15 (IFRD2) in the regulation of adipogenesis via their ability to modulate the levels of DLK1 (Pref-1), a well-known inhibitor of adipogenesis. They generate SKMc15 KO mice and cross them to previously published TIS7 KO mice. All 3 mutant strains show decreased fat mass, with the effect being most pronounced in double KO mice (dKO). Using mouse embryonic fibroblasts (MEFs) from mutant mice, they authors ascribe a defect in adipogenic differentiation of mutant cells to an upregulation of DLK-1. In the case of TIS7, they propose that this is due to its known inhibition of Wnt signaling, which regulates DLK-1 expression. In the case of SKMc15, they suggest a new mechanism linked to its ability to suppress translation. Overall, the work is of interest, with the finding, that SKMc15 regulates adipocyte differentiation being its novelty, and generally well done, though multiple aspects need to be improved to bolster the conclusions put forth.
**Major concerns:**
1)The main mechanism put forth by the authors to explain the inability of dKO cells to differentiate into adipocytes is the upregulation of DLK-1 levels. However, this notion is never directly tested. Authors should test if knockdown of DLK-1 in dKO cells is sufficient to correct the defect in differentiation, or if additional factors are involved.
Response: In response to the reviewer’s concerns, we have generated two stable cell lines expressing short hairpin RNAs directed against DLK1 in the TIS7 SKMc15 dKO MEFs. With these two and the parental dKO MEF cell line, we have performed adipogenesis differentiation experiments as explained in the manuscript before. Figure EV2C (left and right panels) shows that knockdown of DLK1 with two different DLK1 shRNA constructs (targeting DLK1 with or without the extracellular cleavage site) significantly (P2)There are multiple instances were the authors refer to "data not shown", such as when discussing the body length of dKO mice. Please show the data in all cases (Supplementary Info is fine) or remove any discussion of data that is not shown and cannot be evaluated.
Response: Following three results were in the initial version of our manuscript mentioned as “data not shown”:
- line 137: “body length, including the tail did not significantly differ between WT and dKO mice”
- line 307: “higher concentrations of free fatty acids in the feces of dKO mice”
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line 331: “effects of ectopic expression of TIS7, SKMc15 and their co-expression on DLK-1 levels” In the current version of the manuscript, we provide these results as:
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Figure EV1A shows no significant difference in body length.
- The significantly elevated levels of free fatty acids and energy determined by bomb calorimetry in the feces of dKO animals fed HFD are shown in Figures 6A and B, respectively.
- The significant inhibitory effect of ectopic expression of TIS7 and SKMc15 on DLK1 levels was identified by both qPCR and WB analyses, which are shown in Figure 3B. 3)Indirect calorimetry data shown in Fig. S1 should include an entire 24 hr cycle and plots of VO2, activity and other measured parameters shown (only RER and food intake are shown), not just alluded to in the legend.
Response: Based on the reviewer’s suggestion, we present here a table containing all parameters measured in the indirect calorimetry experiment.
Metabolic phenotyping presented in Figure EV1B containing 21 hours measurement was performed exactly according to the standardized protocol previously published by Rozman J. et al. [1]. All phenotyping tests were performed following the International Mouse Phenotyping Resource of Standardized Screens (IMPReSS) pipeline routines.
4)It is surprising that the dKO mice weight so much less than WT even though their food consumption and activity levels are similar, and their RER does not indicate a switch in fuel preference. An explanation could be altered lipid absorption. The authors indicate that feces were collected. An analysis of fat content in feces (NEFAs, TG) needs to be performed to examine this possibility. The discussion alludes to it, but no data is shown.
__Response: __We thank the reviewer for bringing up this important point that prompted us to present data clarifying this aspect of the metabolic phenotype of dKO mice. As shown in Figures 6A,B, while fed with HFD, dKO mice had higher concentrations of free fatty acids in the feces (109 ± 10.4 µmol/g) when compared to the WT animals (78 ± 6.5 µmol/g) and a consequent increase in feces energy content (WT: 14.442 ± 0.433 kJ/g dry mass compared to dKO: 15.497 ± 0.482 kJ/g dry mass). Thus, lack of TIS7 and SKMc15 reduced efficient free fatty acid uptake in the intestines of mice.
5)It would be important to know if increased MEK/ERK signaling and SOX9 expression are seen in fat pads of mutant mice, not just on the MEF system. Similarly, what are the expression levels of PPARg and C/EBPa in WAT depots of mutant mice?
Response: To address this point, we have now performed the MEK/ERK activity measurement for the revised version of the manuscript in gonadal WAT tissue (GWAT). As noted in samples from several mice, there was an increase in p42 and p44 MAPK phosphorylation in G WAT isolated from dKO mice compared with the G WAT from WT control mice (Figure 4G).).
The mRNA expression levels of PPARg and C/EBPa were significantly downregulated in GWAT samples isolated from dKO mice compared with levels from WT control animals (Figure 4H). However, we did not find any significant difference in SOX9 expression in fat pads. Total amounts of Sox9 mRNA in terminally differentiated adipocytes were very low and not within the reliable detection range, and the variation between animals within the same group was too great. Therefore, we provide these data only for the reviewer’s information here and do not present them in the manuscript.
6)Analysis of Wnt signaling in Fig. 3c should also include a FOPflash control reporter vector, to demonstrate specificity. Also, data from transfection studies should be shown as mean plus/minus STD and not SEM. This also applies to all other cell-based studies (e.g., Fig. 6b,c).
Response: To address the reviewer’s concerns, we performed FOPflash control reporter measurements in MEFs of all four genotypes. As expected, in every tested cell line the luciferase activity of the FOPflash reporter was substantially lower than that of TOPflash, confirming the specificity of this reporter system.
We also thank the reviewer for this important reference to our statistical analyses. We have revised the original data and found that the abbreviation SEM was inadvertently used in the legends instead of STD. STD was always used in the original analyses and therefore we have corrected all legends accordingly in the new version of the manuscript.
7)It is unclear why the authors used the MEF model rather than adipocyte precursors derived from the stromal vascular fraction (SVF) of fat pads from mutant mice. If they did generate data from SVF progenitors, they should include it.
__Response: __We agree with this comment, although performing the experiments was challenging enough for us. Therefore, we isolated inguinal fat pads and obtained SVF cells from mice of all four genotypes (WT, TIS7, SKMc15 single and double KOs) and have repeated crucial experiments, i.e. adipocyte differentiation, DLK1, PPARg and C/EBPa mRNA and protein analyses in these cells. Novel data gained in this cell system fully confirmed our previous observations in MEFs. Therefore, in the current version of the manuscript we have replaced figures describing the effects of lacking TIS7 and SKMc15 in MEFs by adipose tissues samples (Figures 2D,E, 4G,H,I and 6C) or SVF cells from inguinal WAT (Figures 2A,B,F,G,H, 3C,D,E and F). In addition to the results obtained from SVF cells of inguinal WAT, we also obtained comparable data from SVF cells isolated from fat pads of gonadal WAT. We provide the results from gonadal WAT hereafter for the reviewers' information only.
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The only experiments where we have still used data obtained in MEFs are those where the ectopic expression or effects of shRNA were necessary (e.g. Figures 2C, 3B,H,I, 5F,G EV2B,C and EV3 A-F).
8)Given that the authors' proposed mechanism involves both, transcriptional and post-transcriptional regulation of DLK-1 by TIS7 and SKMc15, Fig. 4d should be a Western blot capturing both of these events, and not just quantitation of mRNA levels.
Response: As requested by the reviewer, we have added in Figure 3B the Western blot analysis of DLK1 expression. Secondly, this experiment was entirely redone and we now show the effects of ectopic expression of SKMc15, TIS7 alone and their combination side by side with the control GFP. We present here the effects of stable expression of ectopic TIS7 and SKMc15 in dKO MEFs following the viral delivery of expression constructs, antibiotic selection and 8 days of adipocyte differentiation.
9)There is no mention of the impact on brown adipose tissue (BAT) differentiation of KO of TIS7, SKMc15, or the combination. Given the role of BAT in systemic metabolism beyond energy expenditure, the authors need to comment on this issue.
Response: We thank the reviewer for bringing up this important point that prompted us to better describe the phenotype of TIS7, SKMc15 and double knockout mice. We measured DLK1 protein levels in BAT isolated from WT, TIS7, and SKMc15 mice with single and double knockout and detected a significant increase in DLK1 protein levels in all three knockout genotypes. Five mice per genotype were analyzed, and the statistical analysis in Figure 4I represents the mean ± STD. The p-values are based on the results of the Student's t-test and one-way Anova analysis (p-value = 0.0241).
**Minor comments:**
10)The y axis in Fig. 2c is labeled as gain of body weight (g). Is it really the case that WT mice gained 30 g of body weight after just 3 weeks of HFD? This rate of increase seems extraordinary, and somewhat unlikely. Please re-check the accuracy of this panel.
Response: We thank the reviewer for drawing our attention to the apparent mislabeling of the y-axis. The correct labeling is: "Increase in body weight in %" and Figure 1F has been corrected accordingly.
11)The Methods indicates all statistical analysis was performed using t tests, but this is at odds with some figure legends that indicate additional tests (e.g., ANCOVA).
Response: This inaccurate information in the manuscript was corrected.
12)Please specify in all cases the WAT depot used for the analysis shown (e.g., Fig. 3d is just labeled as WAT, as are Fig. 4a,e, etc.).
Response: This information was added at all appropriate places of the manuscript.
13)Fig. 5d is missing error bars, giving the impression that this experiment was performed only once (Fig. 5c). The legend has no details. Please amend.
__Response: __We thank the reviewer for this important point regarding the statistical analyses. In the new version of the manuscript, we have included a graph (now Figure 4D) depicting results of three independent experiments including the results of the statistical analysis performed. Statistical analysis was performed using One-Way ANOVA (P=0.0016).
Reviewer #1 (Significance (Required)):
The role of TIS7 in adipocyte differentiation is well established. The only truly novel finding in this work is the observation that SKMc15 also plays a role in adipogenesis. The molecular mechanisms proposed (modulation of DLK-1 levels) are not novel, but make sense. However, they need to be bolstered by additional data.
**Referees cross-commenting**
I think we are all in agreement that the findings in this work are of interest, but that significant additional work is required to discern the mechanisms involved. In my view, a direct and specific link between SKMc15 and translation of DLK-1 needs to be established and its significance for adipogenesis in cells derived from the SVF of fat pads determined. Reviewer 2 has suggested some concrete ways to provide evidence of a direct link.
__Response: __We agree with the reviewer's comment and have also noted that this point will be crucial in assessing the novelty value of our manuscript, as was also expressed in the referees cross-commenting. Therefore, we have now additionally performed a polysomal RNA analysis, which has of course been included in the current version of the manuscript.
We analyzed the differences in DLK-1 translation between wild-type control cells and SKMc15 knockout cells in the gradient-purified ribosomal fractions by DLK-1 qPCR. Our analysis identified significantly (pSimilarly, as proposed by the reviewer, we have established stromal vascular fraction cell cultures from inguinal fat pads. In SVF cells of TIS7 and SKMc15 single and double knockout mice, we found increased DLK1 mRNA and protein levels (Figures 2F,G and H) as well as decreased PPARg and C/EBPa levels (Figures 3C,D,E and F). Specifically, we found that the ability of knockout SVF cells to differentiate into adipocytes was significantly downregulated (Figures 2A and B), fully confirming our original findings in TIS7 and SKMc15 knockout MEFs.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
**Summary:**
In the current study, Vietor et al. aimed to explore the regulation of Delta-like homolog 1 (DLK-1), an inhibitor of adipogenesis, and demonstrated a role for TIS7 and its orthologue SKMc15 in the regulation of adipogenesis by controlling the level of DLK-1. Using mouse models with whole body deficiency of TIS7 (TIS7 KO) or SKMc15 (SKMc15KO) and double KO (TIS7 and SKMc15 dKO) mice, the authors used a combination of in-vivo experiments and cell culture experiments with mouse embryonic fibroblasts derived from the KO animals, to show that the concurrent depletion of TIS7 and SKMc15 dramatically reduced the amount of adipose tissues and protected against diet-induced obesity in mice, which was associated with defective adipogenesis in vitro.
**Major Comments:**
Overall, this study presents convincing evidence that TIOS7 and SKMc15 are necessary for optimal adipogenesis, and proposes a novel mechanism for the control of DLK1 abundance via coordinated regulation of DLK-1 transcription and translation. However, a number of questions remain largely unanswered. In particular, the direct ability of SKMc15 to regulate the translation of DLK-1 is lacking, and this claim remains speculative. SKMc15 being a general inhibitor of translation, SKMc15 may have an effect on adipogenesis independently of its regulation of DLK-1. Thus, addressing the following comments would further improve the quality of the manuscript:
Response:
We have been very attentive to these comments to improve the novelty and quality of our manuscript and have tried to address them experimentally. Therefore, this thorough revision of our manuscript took a longer time. First, we identified polysomal enrichment of DLK-1 RNA in SKMc15 KO MEFs, demonstrating that SKMc15 translationally affects DLK-1 levels (Figure 3I). Second, treatment with a recombinant DLK-1 protein as well as its ectopic expression quite clearly blocked adipocyte differentiation of WT MEFs (Figures EV3B,C). In addition, two different shRNA constructs targeting DLK-1 significantly induced adipocyte differentiation of TIS7 SKMc15 dKO MEFs (Figure EV2C, left and right panels). We believe that these results, taken together, sufficiently support our proposed mechanism, namely that TIS7 and SKMc15 control adipocyte differentiation through DLK-1 regulation.
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The experimental evidence supporting that SKMc15 controls DLK-1 protein levels comes primarily from the observations that DLK-1 abundance is further increased in SKMc15 KO and dKO WAT than in TIS7KO WAT (Fig 3d), and that translation is generally increased in SKMc15 KO and dKO cells (Fig 5a). However, since the rescue experiment is performed in dKO cells, by restoring both TIS7 and SKMc15 together, it is impossible to disentangle the effects on DLK-1 transcription, DLK-1 translation and on adipogenesis. A more detailed description of the TIS7 and SKM15c single KO cells, with or without re-expression of TIS7 and SKMc15 individually, at the level of DLK-1 mRNA expression and DLK-1 protein abundance would be necessary. In addition, polyribosome fractioning followed by qPCR for DLK-1 in each fraction, and by comparison with DLK-1 global expression in control and SKMc15 KO cells, would reveal the efficiency of translation for DLK-1 specifically, and directly prove a translational control of DLK-1 by SKMc15. Alternatively, showing that DLK-1 is among the proteins newly translated in SKMc15 KO cells (Fig. 5a) would be helpful. Response: As suggested by the reviewer we used single TIS7 and SKMc15 knockout cells and demonstrated that both, TIS7 and SKMc15, affect Dlk-1 mRNA levels. We identified a highly significant effect on total DLK-1 mRNA levels in SKMc15 knockout MEFs as presented in Figure 3H. We also show that DLK-1 mRNA is specifically enriched in polysomal fractions obtained from proliferating SKMc15 knockout MEFs when compared to WT MEFs. However, the strong accumulation of DLK-1 mRNA in polysomes cannot be explained by transcriptional upregulation of DLK-1 alone, suggesting that regulation also occurs at the translational level. We took up this suggestion and ectopically expressed TIS7 and SKMc15 separately or together. For this purpose, we used not only MEF cell lines with double knockout but also with single knockout. Our recent data showed that stable ectopic expression of SKMc15 significantly increased adipocyte differentiation in both, single and double TIS7 and SKMc15 knockout MEF cell lines (Figures EV1C,D and EV2A). Ectopic expression of TIS7 significantly induced the adipocyte differentiation in TIS7 single knockout MEFs (Figure EV1C). In addition, both genes down regulated DLK-1 mRNA expression in dKO MEFs (Figure EV2A, bar chart on the right). We fully agree with the opinion of both reviewers and as already explained above we identified by qPCR in the polysomes that SKMc15 directly regulates DLK-1 translation (Figure 3I).
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While the scope of the study focuses on the molecular control of adipogenesis by TIS7 and SKMc15 via the regulation of DLK-1, basic elements of the metabolic characterization of the KO animals providing the basis for this study would be useful. Since the difference in body weight between WT and dKO animals is already apparent 1 week after birth (Fig 1a), it would be interesting to determine whether the fat mass is decreased at an earlier age than 6 months (Fig 1b). The dKO mice are leaner despite identical food intake, activity and RER (Sup Fig 1). It remains unclear whether defective fat mass expansion is a result or consequence of this phenotype. Is the excess energy stored ectopically? The authors mention defective lipid absorption, however, these data are not presented in the manuscript. It would be interesting to investigate the relative contribution of calorie intake and adipose lipid storage capacity in the resistance to diet-induced obesity. In addition, data reported in Fig 1c seem to indicate a preferential defect in visceral fat development, as compared to subcutaneous fat. It would be relevant if the authors could quantify it and comment on it. Are TIS7 and SKMc15 differentially expressed in various adipose depots? The authors used embryonic fibroblasts as a paradigm to study adipogenesis. It would be important to investigate, especially in light of the former comment, whether pre-adipocytes from subcutaneous and visceral stroma-vascular fractions present similar defects in adipogenesis. Response: We addressed the issue of lipid storage capacity raised by the reviewer using two experimental methods. First, we have analyzed feces of mice fed with high fat diet. The free fatty acids content in dKO mice feces was significantly (PConcerning the question of younger animals, we have repeated microCT fat measurements on a group of 1-2 months old WT and dKO male mice (n=4 per group). The total amount of abdominal fat was in WT mice significantly higher than in dKO mice (P=0.019; Student’s T-test). We provide these data only for the reviewer’s information here and do not present them in the manuscript.
We have also followed the reviewer’s advice and revisited our microCT measurements of abdominal fat and anylyzed the possible differences between subcutaneous and visceral fat. In all three types of abdominal fat mass measurement (total, subcutaneous and visceral) there was always significantly (ANOVA P=0.034 subcutaneous, P=0.002 total and P=0.002 visceral fat) less fat in the dKO group (n=8) of mice when compared to WT (n=12) mice. However, the difference was more prominent in visceral (P=0.001; Student’s T-test) than in subcutaneous fat (P=0.027; Student’s T-test). We provide these data only for the reviewer’s information here and do not present them in the manuscript.
In addition, we have analyzed the expression of TIS7 and SKMc15 mRNA expression in both, inguinal and gonadal WAT. Our qPCR result showed that both genes are expressed in different types of WAT. The qPCR analysis was performed on RNA isolated from undifferentiated SVF cells isolated from several animals. The expression of TIS7 and SKMc15 was normalized on GAPDH. Data represent mean and standard deviation of technical replicates from several mice as labeled in the graph. We provide these data only for the reviewer’s information here and do not present them in the manuscript.
Topics of a) stromal vascular fraction as a source of pre-adipocytes and b) comparison of TIS7 and SKMc15 roles in gonadal vs. inguinal fat pads we answered in response to the Reviewer #1, point 7. The results are presented in Figures 2, 3 and 4 and in this document.
Both data and methods are explained clearly. The experiments are, for the most part, adequately replicated. However, whenever multiple groups are compared, ANOVA should be employed instead of t-test for statistical analysis.
Response: Thank you for pointing this out. Wherever it was applicable, we used ANOVA for the statistical analysis of data.
**Minor comments:**
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Figure 4 d. The appropriate control would be WT with empty vector Response: this experiment was entirely replaced by the new Figure 3B where stably transfected MEF cells expressing TIS7 or SKMc15 were used.
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Figure 7c/d. The appropriate control would be WT with empty vector Response: We have now generated new, confirmatory data in MEF cells stably expressing TIS7 or SKMc15 following lentiviral expression.
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Figure 5C. An additional control would be WT with WT medium __Response: __We agree with your suggestion and therefore we have incorporated this control in all experimental repeats presented in the new Figure 4C.
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Figure 2: In the legends, the "x" is missing for the dKO regression formula __Response: __Thank you, we have corrected this mistake. In the current version of the manuscript it is Figure 1D.
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Since the role of SKMc15 in adipogenesis has never been described, the authors could consider describing the single SKMc15 KO in addition to the dKO, or explain the rationale for focusing the study on dKO. __Response: __The original reason for focusing on dKO mice and cells was the obvious and dominant phenotype in this animal model. However, we have sought to address the reviewer's concerns and have now also examined DLK-1 mRNA levels in proliferating SKMc15 knockout MEFs (Figure 3H). In addition to this experiment, we measured DLK-1 mRNA levels also during the process of adipocyte differentiation of single knockout cells. In WT MEFs we observed a transient increase of DLK-1 mRNA only on day 1. In contrast, significantly elevated DLK-1 mRNA levels were found in TIS7 single-knockout MEFs throughout the differentiation process, with the highest level reached at day 8. Interestingly, in SKMc15 single knockout MEFs we found an upregulation of DLK-1 mRNA level in proliferating cells but not a further increase during the differentiation. This supported our idea that SKMc15 acts mainly via translational regulation of DLK-1. We provide these data only for the reviewer’s information here and do not present them in the manuscript.
To emphasize this point, we revised the entire manuscript accordingly and added data on SKMc15 knockout mice. In particular, experiments presenting data characterizing SKMc15 single knockout mice are presented in: Figures 1C,D,E and F, Figures 2A,B,C and D, Figures 3E,F,H and I, Figures 4A and I and in Figure EV1D.
Reviewer #2 (Significance (Required)):
While the effects of DLK-1 on adipogenesis have been widely documented, the factors controlling DLK-1 expression and function remain poorly understood. Here the authors propose a novel mechanism for the regulation of DLK-1, and how it affects adipocyte differentiation. This study should therefore be of interest for researchers interested in the molecular control of adipogenesis and cell differentiation in general. Furthermore, the characterization of the function of SKMc15 in the control of translation may be of interest to a broader readership.
**Referees cross-commenting**
I agree with all the comments raised by the other reviewers. Addressing the often overlapping but also complementary questions would help to clarify the molecular mechanisms by which TIS7 and SKMc15 control adipogenesis, and support the conclusions raised by the authors.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In the article, "The negative regulator DLK1 is transcriptionally regulated by TIS7 (IFRD1) and translationally by its orthologue SKMc15 (IFRD2)", the authors performed a double knockout (dKO) of TIS7 and its orthologue SKMc15 in mice and could show that those dKO mice had less adipose tissue compared to wild-type (WT) mice and were resistant to a high fat-diet induced obesity. The study takes advantage of number of different methods and approaches and combines both in vivo and in vitro work. However, some more detailed analysis and clarifications would be needed to fully justify some of the statements. Including the role of TIS7 as a transcriptional regulator of DLK1, SKMc15 as translational regulator of DLK1 and overall contribution of DLK1 in the observed differentiation defects. The observed results could still be explained by many indirect effects caused by the knock-outs and more direct functional connections between the studied molecules would be needed. Moreover, some assays appear to be missing biological replicates and statistical analysis. Please see below for more detailed comments:
**Major comments:**
-Are the key conclusions convincing? Yes.
-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? No.
-Would additional experiments be essential to support the claims of the paper? Yes. Please see my comments.
-Are the suggested experiments realistic in terms of time and resources? Recombinant DLK1 10 μg - Tetu-bio - 112€ ; 8 days of adipocyte differentiation in 3 biological replicate ~ 1 month.
__Response: __We followed the advice of the individual reviewers as expressed in “Referees cross-commenting” and tested this idea experimentally. Since the manufacturer couldn’t suppy information on biological activities of recombinant DLK-1 proteins, we analyzed in vivo the effects of two different ones, namely RPL437Mu01 and RPL437Mu02. The 8-day adipocyte differentiation protocol showed that the RPL437Mu02 protein was cytotoxic to WT MEF cells and therefore could not be used for analysis. On the other hand, treatment with the Mu01 recombinant DLK-1 protein did not result in a substantial cell death. According to oil red O staining, incubation with 3.3 mg/ml (final concentration) RPL437Mu01 led to 75% inhibition of adipocyte differentiation when compared to not treated WT MEFs (Figure EV3B and C).
-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?
Adequately reproduced yes. Please see my comments concerning the statistical analysis.
1)Fig1a: In the method section it is written that an unpaired 2-tailed Student's t test was used for all statistical comparisons. However, here something like Multivariate analysis of variance (MANOVA) should rather be used to assess statistical significance between the mice. Moreover, the details of this should be clearly stated in the corresponding Figure legend.
__Response: __Based on this suggestion, we have revised all of our statistical analyses. In several cases, (Figures 1F, 2B and C) we have replaced the statistical analysis using Student’s T test with Anova. However, based on the definition “the difference between ANOVA and MANOVA is merely the number of dependent variables fit. If there is one dependent variable then the procedure ANOVA is used”, in case of Figure 1A we used ANOVA.
2)Fig2a: please use an appropriate title for Fig2a instead of "Abdominal fat vs. body mass".
Response: Title of the Figure 1D (formerly Figure 2a) we changed to “Effect of TIS7 and SKMc15 on the abdominal fat mass”.
3)Fig2c: in the method section it is written that an unpaired 2-tailed Student's t test was used for all statistical comparisons. However, in Fig2c 4 groups are compared (WT, TIS7 KO, SKMc15 KO and dKO) and thus something like Multivariate analysis of variance (MANOVA) should rather be used to assess statistical significance.
Response: For Figure 1F (formerly Figure 2c), in the revised version of the manuscript, we applied the ordinary one-way ANOVA with Holm-Šidák's multiple comparison test. This analysis gave us statistically even more significant results concerning the difference between WT and dKO mice than previously found by Student's T test. The results in detail were as follows:
Holm-Šidák's multiple comparisons test Summary Adjusted P Value
WT vs. TIS7 KO ** 0,0096
WT vs. SKMc15 KO * 0,0308
WT vs. dKO **** 4)Fig2 conclusion: Additive or just showing stronger effect?
Response: We have re-phrased the concluding summary for Figure 1F (formerly Figure 2c). We agree that the precise description of differences found between the weight of single and double knockout animals should be described as “stronger” and not additive effect of knockout of both genes.
5)Fig3a: the microscope picture for SKMc15 KO shows that cells might have died. Please state the percentage of cell death.
Response: We would like to comment on these concerns of the reviewer as follows: In the image in Figure 3 of the original manuscript, the density of SKMc15 KO MEF cells after the adipocyte differentiation protocol was lower than in the WT control. Regarding the possible cell death, the cells stained with Oil Red O were adherent and alive. The adipocyte differentiation protocol consists of 3 days proliferation and further 5 days of differentiation including three changes of media during which dead cells are washed away and their vitality cannot be checked. However, in the meantime, we have repeated this protocol and the density of SKMc15 knockout MEFs was now not substantially lower than those of controls. Despite the comparable cell density, we have seen a substantial negative effect of the SKMc15 knockout on the adipogenic differentiation ability of these cells. Several examples are shown here:
TIS7 +/+ SKMc15 +/+ MEFs
TIS7 +/+ SKMc15 -/- MEFs
oil red O staining; 8d differentiated cells
Importantly, in the current version of our manuscript we replaced MEFs (shown in the former Figure 3a) by SVF cells (Figure 2A in the current manuscript). In these cells we did not see any significant difference in their density after 8 days of the adipocyte differentiation protocol.
6)Fig3b: It would be informative to additionally observe some of marker genes for adipogenesis and whether all of them are affected.
Response: In our newly established SVF cell lines, derived from inguinal WAT we have confirmed data previously identified in MEFs. As shown in the new Figure 3, PPARg and C/EBPa mRNA levels were downregulated in all knockout SVF cell lines, both undifferentiated (Figures 3C and D) and adipocyte differentiated (Figures 3E and F). On the other hand, DLK-1 mRNA and protein levels, both in undifferentiated (Figures 2F and G) and adipocyte differentiated (Figure 2H) SVF cells were significantly upregulated in dKO cells when compared to WT cells.
7)Fig3b: instead of using an unpaired 2-tailed Student's t test with proportion, an one-way ANOVA would be more appropriate.
__Response: __On the recommendation of the reviewer, we applied a simple ANOVA to our new data from SVF cells using the Holm-Šidák test for multiple comparisons. The Anova summary using GraphPad Prism Ver. 9.2 identified statistically highly significant (P value 8)Fig3c: Same comment as for Fig3b.
__Response: __Also, in this experiment (now Figure 2C) we used ordinary one-way ANOVA with Holm-Šidák's multiple comparisons test. The ANOVA summary identified statistically highly significant (P value 9)Fig3d: A representative Western blot for 3 independent experiments is shown. Please add the other two as supplementary materials.
__Response: __Here we provide examples of the requested two additional, independent experiments. These refer now to the Figure 2D in the revised version of the manuscript:
31 07 2020
= manuscript
b____-catenin
22 07 2020
WT
TIS7 KO
dKO
SKMc15 KO
WT
TIS7 KO
dKO
SKMc15 KO
actin
b____-catenin
30 07 2020
actin
b____-catenin
WT
TIS7 KO
dKO
SKMc15 KO
WT
TIS7 KO
dKO
SKMc15 KO
actin
10)Fig3d:Is this distinguishing between the active and inactive catenin?
__Response: __No, the b-catenin antibody, that we used is not discriminating between active and inactive b-catenin forms.
11)Fig4a: Please perform qPCR for measuring DLK-1 mRNA levels in TIS7 KO and SKMc15 KO samples to check whether there is a correlation between mRNA and protein level as the statement of the authors is that "DLK1 is transcriptionally regulated by TIS7 (IFRD1) and translationally by its orthologue SKMc15".
Response: Similar questions were raised by Reviewer 2 on p. 11 “Since the role of SKMc15 in adipogenesis has never been described, the authors could consider describing the single SKMc15 KO in addition to the dKO, or explain the rationale for focusing the study on dKO.” Please see our reply to his comment.
12)Fig4c: please add the other two western blots as supplementary materials.
__Response: __Here we provide data from two additional, independent experiments.
13)Fig4d: The effects in MEFs appear quite modest. What about a rescue with TIS7 or SKMc15 alone?
__Response: __As mentioned already in response to the question 2 of Reviewer #1, in our newly performed experiments we found significant inhibitory effects of ectopic TIS7 and SKMc15 expression on DLK1 levels, identified both by qPCR and WB analyses (Figure 3B).
14)Page 12, row 207: I would not call histones transcription factors.
__Response: __We re-phrased this sentence accordingly.
15)Fig4e: Would be good to see a schematic overview of the locations of the ChIP primers in relation to the known binding sites and the gene (TSS, gene body). Moreover, the results include an enrichment for only one region while in the text two different regions are discussed. Importantly, to confirm the specificity of the observed enrichment, a primer pair targeting an unspecific control region not bound by the proteins should be included.
__Response: __The selection of oligonucleotide sequences used for ChIP analyses of the binding of b-catenin, TIS7 and SKMc15 to the Dlk-1 promoter was, based on the following reference, as mentioned in Methods section of our original manuscript on p.21, line 494: Paul C, Sardet C, Fabbrizio E. “The Wnt-target gene Dlk-1 is regulated by the Prmt5-associated factor Copr5 during adipogenic conversion”. Biol Open. 2015 Feb 13;4(3):312-6. doi: 10.1242/bio.201411247.
We used two regions of the Dlk-1 promoter: a proximal one, encompassing the TCF binding site 2 (TCFbs2) and a more distal one, annotated as “A”:
Oligonucleotide sequences used for ChIP PCR:
Dlk-1 TCFbs2 5'f CATTTGACGGTGAACATATTGG
5'r GCCCAGACCCCAAATCTGTC
Dlk-1 region A (-2263/-2143) 5'f TTGTCTAACCACCCTACCTCAAA
5’r CTCTGAGAAAAGATGTTGGGATTT
We observed specific binding at the proximal site.
16)Fig5a: Has this experiment been replicated? That is no mention about the reproducibility or quantification of this result. This is the main experiment regarding the role of SKMc15 as a translational regulator of DLK1, also mentioned in the title of the manuscript.
__Response: __This relates to the Figure 4A in the revised manuscript. Yes, we repeated this experiment several times. Here we provide images and quantifications of three independent experiments.
17)Fig5b: Showing another unaffected secreted protein would be an appropriate control here.
Response: As recommended by the reviewer, we have performed an additional WB with a recombinant anti-Collagen I antibody [Abcam, [EPR22209-75] ab255809]. Medium from 8 days adipocyte differentiated WT and dKO MEFs was concentrated using Centriprep 30K and resolved on 10% SDS-PAGE gel. Western blot presented in the new Fig 4 B shows even slightly higher amounts of Collagen-1 protein in medium from WT than in dKO MEFs. Mw of the detected band was approximately 35 kDa, which corresponded to the manufacturer’s information.
18)Fig5c: I would recommend to perform additional experiments to prove that DLK-1 secreted in the medium can contribute and is responsible for the inhibition of the differentiation. Indeed, a time course of adipocyte differentiation followed by the addition of soluble DLK-1 would confirm that DLK-1 can inhibit adipocyte differentiation in this experimental setup. Moreover, silencing (for example RNAi) of DLK1 in the dKO cells before harvesting the conditioned media would allow to estimate the contribution of DLK1 to the observed inhibition of differentiation by the media. This is important because many other molecules could also be mediating this inhibition.
__Response: __We agree with this reviewer’s concern, which are shared by other reviewers. Similarly, as in response to Reviewer #2 and as already mentioned above, in response to “major comments” of Reviewer #3, in our novel experiments we found that treatment with recombinant DLK-1 protein as well as ectopic expression of DLK-1 blocked adipocyte differentiation of WT MEFs (Figures EV3B,C,D and E) as well as medium from dKO shDLK-1 391 cells (Figure EV3F).
19)Fig5c: The details and the timeline of the experiment with conditioned media are not provided in the figure or in the methods. At what time point was conditioned media changed? How long were the cells kept in conditioned media? How does this compare to the regular media change intervals? Could the lower differentiation capacity relate to turnover of the differentiation inducing compounds in the media due to longer period between media change? Moreover, is the result statistically significant after replication?
__Response: __Based on the reviewer`s comment we have added technical information concerning the experimental protocol of the treatment with conditioned media. In general, the treatment for adipocyte differentiation was identical with the previous experiments. The only difference was that after three days in proliferation medium, we used either fresh differentiation medium or 2-day-old differentiation medium from dKO control or dKO-shDLK-1 391 cell cultures then for wild-type cells, as shown in the figure (Figure EV3F). Cells were incubated additional five days with the differentiation medium with two changes of media, every second day. The adipocyte differentiation of medium “donor” cells and the DLK-1 protein levels in these cells were monitored by oil red O staining and Western blot analysis, respectively.
Additionally, we show now in Figure 4C representative images from three independent biological repeats and in Figure 4D the statistical analysis confirming a significant decrease in adipocyte differentiation ability of WT MEFs following their incubation with a conditioned differentiation medium from dKO MEFs.
20)Fig5d: please add a statistical analysis of the oil-red-o quantification.
__Response: __As requested, we included statistical analysis of at least three independent experiments. In Figure 4D we present the statistical analysis confirming a significant decrease in adipocyte differentiation of WT MEFs following their incubation with the differentiation medium from dKO cells. Additionally, Figure 4C shows representative images of oil red O staining from several independent experiments.
21)Fig7c-d: Does overexpression also rescue the PPARg and CEBPa induction during differentiation. The importance of their induction in undifferentiated MEFs is a little difficult to judge.
__Response: __We have focused our attention primarily on the ability of TIS7 and SKMc15 to “rescue” the adipocyte differentiation phenotype of dKO MEFs. dKO MEFs stably expressing SKMc15, TIS7 or both genes were differentiated into adipocytes for 8 days and afterwards stained with oil red O. There was a statistically significant increase in oil red O staining following the individual ectopic expression of SKMc15 (p=5.7E-03), a negative effect of TIS7 ectopic expression and a significant (p=9.3E-03), positive effect of co-expression of both genes (Figure EV2A). We found a significant decrease in Dlk-1 mRNA expression following the ectopic expression of TIS7 and/or SKMc15 (Figure EV2A, very right panel). However, C/EBPa mRNA levels were only partially rescued in 8 days differentiated MEFs by TIS7 and/or SKMc15 ectopic expression, and PPARg mRNA levels were not significantly altered.
22)Fig8: it is not surprising that PPARg targets are not induced in the absence of PPARg. What is the upstream event explaining this defect? Is DLK1 alone enough to explain the results? Could there be additional mediators of the differences? How big are transcriptome-wide differences between WT MEFs and dKO MEFs?
__Response: __We agree with the reviewer that the lean phenotype of dKO mice most likely cannot be explained by simple transcriptional regulation of PPARg. Although we showed that in undifferentiated MEFs, the levels of PPARg and C/EBPa are controlled (or upregulated) by both TIS7 and SKMc15, we also expected differences in the expression of genes regulating fat uptake. To determine changes in expression of lipid processing and transporting molecules, we performed transcriptome analyses of total RNA samples isolated from the small intestines of HFD-fed WT type and dKO animals. Cluster analyses of lipid transport-related gene transcripts revealed differences between WT type and dKO animals in the expression of adipogenesis regulators. Those included among other genes the following, mentioned as examples:
- peroxisome proliferator-activated receptors γ (PPARγ) and d [2], fatty acid binding proteins 1 and 2 (FABP1, 2) [3],
- cytoplasmic fatty acid chaperones expressed in adipocytes,
- acyl-coenzyme A synthetases 1 and 4 (ACSL1,4) found to be associated with histone acetylation in adipocytes, lipid loading and insulin sensitivity [4],
- SLC27a1, a2 fatty acid transport proteins, critical mediators of fatty acid metabolism [5],
- angiotensin-converting enzyme (ACE) playing a regulatory role in adipogenesis and insulin resistance [6],
- CROT, a carnitine acyltransferase important for the oxidation of fatty acids, a critical step in their metabolism [7],
- phospholipase PLA2G5 robustly induced in adipocytes of obese mice [8]; [9]. Parts of the following text are embedded in the manuscript.
We decided to study in more detail the regulation of CD36 that encodes a very long chain fatty acids (VLCFA) transporter because CD36 is an important fatty acid transporter that facilitates fatty acids (FA) uptake by heart, skeletal muscle, and also adipose tissues [10]. PPARγ induces CD36 expression in adipose tissue, where it functions as a fatty acid transporter, and therefore, its regulation by PPARγ contributes to the control of blood lipids. Diacylglycerol acyltransferase 1 (DGAT1), a protein associated with the enterocytic triglyceride absorption and intracellular lipid processing is besides CD36 another target gene of adipogenesis master regulator PPARγ [11]. DGAT1 mRNA levels are strongly up regulated during adipocyte differentiation [12], its promoter region contains a PPARγ binding site and DGAT1 is also negatively regulated by the MEK/ERK pathway. DGAT1 expression was shown to be increased in TIS7 transgenic mice [13] and its expression was decreased in the gut of high fat diet-fed TIS7 KO mice [14]. Importantly, DGAT1 expression in adipocytes and WAT is up regulated by PPARγ activation [11].
Heatmap of hierarchical cluster analysis of intestinal gene expression involved in lipid transport altered in TIS7 SKMc15 dKO mice fed a high-fat diet for 3 weeks.
What is the upstream event explaining this defect?
Wnt pathway causes epigenetic repression of the master adipogenic gene PPARγ. There are three epigenetic signatures implicated in repression of PPARγ: increased recruitment of MeCP2 (methyl CpG binding protein 2) and HP-1α co-repressor to PPARγ promoter and enhanced H3K27 dimethylation at the exon 5 locus in a manner dependent on suppressed canonical Wnt. These epigenetic effects are reproduced by antagonism of canonical Wnt signaling with Dikkopf-1.
Zhu et al. showed that Dlk1 knockdown causes suppression of Wnt and thereby epigenetic de-repression of PPARγ [15]. Dlk1 levels positively correlate with Wnt signaling activity and negatively with epigenetic repression of PPARγ [16]. Activation of the Wnt pathway caused by DLK1 reprograms lipid metabolism via MeCP2-mediated epigenetic repression of PPARγ [17]. Blocking the Wnt signaling pathway abrogates epigenetic repressions and restores the PPARγ gene expression and differentiation [18].
**Minor comments:**
1)Please use the same font in the main text for the references.
Response: We thank the reviewer for the remark. This issue was corrected.
Reviewer #3 (Significance (Required)):
The study provides interesting insights into the role of these factors in adipocyte differentiation that would be relevant especially to researchers working on adipogenesis and cellular differentiation in general. The authors find the studied factors to have additive contribution to the differentiation efficiency. However, the exact nature of the roles and whether they are strictly speaking additive or synergistic is not clear. More detailed analysis of their contribution and molecular interplay would add to the broader interest of the study on molecular networks controlling cellular differentiation.
**Referees cross-commenting**
I very much agree on the different points raised by the other reviewers, some of which are also matching my own already raised concerns. And therefore it makes sense to request these modifications from the authors.
References
- Rozman, J., M. Klingenspor, and M. Hrabe de Angelis, A review of standardized metabolic phenotyping of animal models. Mamm Genome, 2014. 25(9-10): p. 497-507.
- Lefterova, M.I., et al., PPARgamma and the global map of adipogenesis and beyond. Trends Endocrinol Metab, 2014. 25(6): p. 293-302.
- Garin-Shkolnik, T., et al., FABP4 attenuates PPARgamma and adipogenesis and is inversely correlated with PPARgamma in adipose tissues. Diabetes, 2014. 63(3): p. 900-11.
- Joseph, R., et al., ACSL1 Is Associated With Fetal Programming of Insulin Sensitivity and Cellular Lipid Content. Mol Endocrinol, 2015. 29(6): p. 909-20.
- Anderson, C.M. and A. Stahl, SLC27 fatty acid transport proteins. Mol Aspects Med, 2013. 34(2-3): p. 516-28.
- Riedel, J., et al., Characterization of key genes of the renin-angiotensin system in mature feline adipocytes and during in vitro adipogenesis. J Anim Physiol Anim Nutr (Berl), 2016. 100(6): p. 1139-1148.
- Zhou, S., et al., Increased missense mutation burden of Fatty Acid metabolism related genes in nunavik inuit population. PLoS One, 2015. 10(5): p. e0128255.
- Wootton, P.T., et al., Tagging SNP haplotype analysis of the secretory PLA2-V gene, PLA2G5, shows strong association with LDL and oxLDL levels, suggesting functional distinction from sPLA2-IIA: results from the UDACS study. Hum Mol Genet, 2007. 16(12): p. 1437-44.
- Sergouniotis, P.I., et al., Biallelic mutations in PLA2G5, encoding group V phospholipase A2, cause benign fleck retina. Am J Hum Genet, 2011. 89(6): p. 782-91.
- Coburn, C.T., et al., Defective uptake and utilization of long chain fatty acids in muscle and adipose tissues of CD36 knockout mice. J Biol Chem, 2000. 275(42): p. 32523-9.
- Koliwad, S.K., et al., DGAT1-dependent triacylglycerol storage by macrophages protects mice from diet-induced insulin resistance and inflammation. J Clin Invest, 2010. 120(3): p. 756-67.
- Cases, S., et al., Identification of a gene encoding an acyl CoA:diacylglycerol acyltransferase, a key enzyme in triacylglycerol synthesis. Proc Natl Acad Sci U S A, 1998. 95(22): p. 13018-23.
- Wang, Y., et al., Targeted intestinal overexpression of the immediate early gene tis7 in transgenic mice increases triglyceride absorption and adiposity. J Biol Chem, 2005. 280(41): p. 34764-75.
- Yu, C., et al., Deletion of Tis7 protects mice from high-fat diet-induced weight gain and blunts the intestinal adaptive response postresection. J Nutr, 2010. 140(11): p. 1907-14.
- Zhu, N.L., et al., Hepatic stellate cell-derived delta-like homolog 1 (DLK1) protein in liver regeneration. J Biol Chem, 2012. 287(13): p. 10355-10367.
- Zhu, N.L., J. Wang, and H. Tsukamoto, The Necdin-Wnt pathway causes epigenetic peroxisome proliferator-activated receptor gamma repression in hepatic stellate cells. J Biol Chem, 2010. 285(40): p. 30463-71.
- Tsukamoto, H., Metabolic reprogramming and cell fate regulation in alcoholic liver disease. Pancreatology, 2015. 15(4 Suppl): p. S61-5.
- Miao, C.G., et al., Wnt signaling in liver fibrosis: progress, challenges and potential directions. Biochimie, 2013. 95(12): p. 2326-35.
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Referee #3
Evidence, reproducibility and clarity
In the article, "The negative regulator DLK1 is transcriptionally regulated by TIS7 (IFRD1) and translationally by its orthologue SKMc15 (IFRD2)", the authors performed a double knockout (dKO) of TIS7 and its orthologue SKMc15 in mice and could show that those dKO mice had less adipose tissue compared to wild-type (WT) mice and were resistant to a high fat-diet induced obesity. The study takes advantage of number of different methods and approaches and combines both in vivo and in vitro work. However, some more detailed analysis and clarifications would be needed to fully justify some of the statements. Including the role of TIS7 as a transcriptional regulator of DLK1, SKMc15 as translational regulator of DLK1 and overall contribution of DLK1 in the observed differentiation defects. The observed results could still be explained by many indirect effects caused by the knock-outs and more direct functional connections between the studied molecules would be needed. Moreover, some assays appear to be missing biological replicates and statistical analysis. Please see below for more detailed comments:
Major comments:
-Are the key conclusions convincing? Yes.
-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? No.
-Would additional experiments be essential to support the claims of the paper? Yes. Please see my comments.
-Are the suggested experiments realistic in terms of time and resources? Recombinant DLK1 10 μg - Tetu-bio - 112€ ; 8 days of adipocyte differentiation in 3 biological replicate ~ 1 month.
-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? Adequately reproduced yes. Please see my comments concerning the statistical analysis.
1)Fig1a: In the method section it is written that an unpaired 2-tailed Student's t test was used for all statistical comparisons. However, here something like Multivariate analysis of variance (MANOVA) should rather be used to assess statistical significance between the mice. Moreover, the details of this should be clearly stated in the corresponding Figure legend.
2)Fig2a: please use an appropriate title for Fig2a instead of "Abdominal fat vs. body mass".
3)Fig2c: in the method section it is written that an unpaired 2-tailed Student's t test was used for all statistical comparisons. However, in Fig2c 4 groups are compared (WT, TIS7 KO, SKMc15 KO and dKO) and thus something like Multivariate analysis of variance (MANOVA) should rather be used to assess statistical significance.
4)Fig2 conclusion: Additive or just showing stronger effect?
5)Fig3a: the microscope picture for SKMc15 KO shows that cells might have died. Please state the percentage of cell death.
6)Fig3b: It would be informative to additionally observe some of marker genes for adipogenesis and whether all of them are affected.
7)Fig3b: instead of using an unpaired 2-tailed Student's t test with proportion, an one-way ANOVA would be more appropriate.
8)Fig3c: Same comment as for Fig3b.
9)Fig3d: A representative Western blot for 3 independent experiments is shown. Please add the other two as supplementary materials.
10)Fig3d:Is this distinguishing between the active and inactive catenin?
11)Fig4a: Please perform qPCR for measuring DLK-1 mRNA levels in TIS7 KO and SKMc15 KO samples to check whether there is a correlation between mRNA and protein level as the statement of the authors is that "DLK1 is transcriptionally regulated by TIS7 (IFRD1) and translationally by its orthologue SKMc15".
12)Fig4c: please add the other two western blots as supplementary materials.
13)Fig4d: The effects in MEFs appear quite modest. What about a rescue with TIS7 or SKMc15 alone?
14)Page 12, row 207: I would not call histones transcription factors.
15)Fig4e: Would be good to see a schematic overview of the locations of the ChIP primers in relation to the known binding sites and the gene (TSS, gene body). Moreover, the results include an enrichment for only one region while in the text two different regions are discussed. Importantly, to confirm the specificity of the observed enrichment, a primer pair targeting an unspecific control region not bound by the proteins should be included.
16)Fig5a: Has this experiment been replicated? That is no mention about the reproducibility or quantification of this result. This is the main experiment regarding the role of SKMc15 as a translational regulator of DLK1, also mentioned in the title of the manuscript.
17)Fig5b: Showing another unaffected secreted protein would be an appropriate control here.
18)Fig5c: I would recommend to perform additional experiments to prove that DLK-1 secreted in the medium can contribute and is responsible for the inhibition of the differentiation. Indeed, a time course of adipocyte differentiation followed by the addition of soluble DLK-1 would confirm that DLK-1 can inhibit adipocyte differentiation in this experimental setup. Moreover, silencing (for example RNAi) of DLK1 in the dKO cells before harvesting the conditioned media would allow to estimate the contribution of DLK1 to the observed inhibition of differentiation by the media. This is important because many other molecules could also be mediating this inhibition.
19)Fig5c: The details and the timeline of the experiment with conditioned media are not provided in the figure or in the methods. At what time point was conditioned media changed? How long were the cells kept in conditioned media? How does this compare to the regular media change intervals? Could the lower differentiation capacity relate to turnover of the differentiation inducing compounds in the media due to longer period between media change? Moreover, is the result statistically significant after replication?
20)Fig5d: please add a statistical analysis of the oil-re3d-o quantification.
21)Fig7c-d: Does overexpression also rescue the PPARg and CEBPa induction during differentiation. The importance of their induction in undifferentiated MEFs is a little difficult to judge.
22)Fig8: it is not surprising that PPARg targets are not induced in the absence of PPARg. What is the upstream event explaining this defect? Is DLK1 alone enough to explain the results? Could there be additional mediators of the differences? How big are transcriptome-wide differences between WT MEFs and dKO MEFs?
Minor comments:
1)Please use the same font in the main text for the references.
Significance
The study provides interesting insights into the role of these factors in adipocyte differentiation that would be relevant especially to researchers working on adipogenesis and cellular differentiation in general. The authors find the studied factors to have additive contribution to the differentiation efficiency. However, the exact nature of the roles and whether they are strictly speaking additive or synergistic is not clear. More detailed analysis of their contribution and molecular interplay would add to the broader interest of the study on molecular networks controlling cellular differentiation.
Referees cross-commenting
I very much agree on the different points raised by the other reviewers, some of which are also matching my own already raised concerns. And therefore it makes sense to request these modifications from the authors.
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Referee #2
Evidence, reproducibility and clarity
Summary:
In the current study, Vietor et al. aimed to explore the regulation of Delta-like homolog 1 (DLK-1), an inhibitor of adipogenesis, and demonstrated a role for TIS7 and its orthologue SKMc15 in the regulation of adipogenesis by controlling the level of DLK-1. Using mouse models with whole body deficiency of TIS7 (TIS7 KO) or SKMc15 (SKMc15KO) and double KO (TIS7 and SKMc15 dKO) mice, the authors used a combination of in-vivo experiments and cell culture experiments with mouse embryonic fibroblasts derived from the KO animals, to show that the concurrent depletion of TIS7 and SKMc15 dramatically reduced the amount of adipose tissues and protected against diet-induced obesity in mice, which was associated with defective adipogenesis in vitro.
Major Comments:
Overall, this study presents convincing evidence that TIOS7 and SKMc15 are necessary for optimal adipogenesis, and proposes a novel mechanism for the control of DLK1 abundance via coordinated regulation of DLK-1 transcription and translation. However, a number of questions remain largely unanswered. In particular, the direct ability of SKMc15 to regulate the translation of DLK-1 is lacking, and this claim remains speculative. SKMc15 being a general inhibitor of translation, SKMc15 may have an effect on adipogenesis independently of its regulation of DLK-1. Thus, addressing the following comments would further improve the quality of the manuscript:
•The experimental evidence supporting that SKMc15 controls DLK-1 protein levels comes primarily from the observations that DLK-1 abundance is further increased in SKMc15 KO and dKO WAT than in TIS7KO WAT (Fig 3d), and that translation is generally increased in SKMc15 KO and dKO cells (Fig 5a). However, since the rescue experiment is performed in dKO cells, by restoring both TIS7 and SKMc15 together, it is impossible to disentangle the effects on DLK-1 transcription, DLK-1 translation and on adipogenesis. A more detailed description of the TIS7 and SKM15c single KO cells, with or without re-expression of TIS7 and SKMc15 individually, at the level of DLK-1 mRNA expression and DLK-1 protein abundance would be necessary. In addition, polyribosome fractioning followed by qPCR for DLK-1 in each fraction, and by comparison with DLK-1 global expression in control and SKMc15 KO cells, would reveal the efficiency of translation for DLK-1 specifically, and directly prove a translational control of DLK-1 by SKMc15. Alternatively, showing that DLK-1 is among the proteins newly translated in SKMc15 KO cells (Fig. 5a) would be helpful.
•While the scope of the study focuses on the molecular control of adipogenesis by TIS7 and SKMc15 via the regulation of DLK-1, basic elements of the metabolic characterization of the KO animals providing the basis for this study would be useful. Since the difference in body weight between WT and dKO animals is already apparent 1 week after birth (Fig 1a), it would be interesting to determine whether the fat mass is decreased at an earlier age than 6 months (Fig 1b). The dKO mice are leaner despite identical food intake, activity and RER (Sup Fig 1). It remains unclear whether defective fat mass expansion is a result or consequence of this phenotype. Is the excess energy stored ectopically? The authors mention defective lipid absorption, however, these data are not presented in the manuscript. It would be interesting to investigate the relative contribution of calorie intake and adipose lipid storage capacity in the resistance to diet-induced obesity. In addition, data reported in Fig 1c seem to indicate a preferential defect in visceral fat development, as compared to subcutaneous fat. It would be relevant if the authors could quantify it and comment on it. Are TIS7 and SKMc15 differentially expressed in various adipose depots? The authors used embryonic fibroblasts as a paradigm to study adipogenesis. It would be important to investigate, especially in light of the former comment, whether pre-adipocytes from subcutaneous and visceral stroma-vascular fractions present similar defects in adipogenesis.
We estimate the suggested experiments above realistic in terms of time and resources and important to support the major conclusions of the study. Both data and methods are explained clearly. The experiments are, for the most part, adequately replicated. However, whenever multiple groups are compared, ANOVA should be employed instead of t-test for statistical analysis.
Minor comments:
•Figure 4 d. The appropriate control would be WT with empty vector
•Figure 7c/d. The appropriate control would be WT with empty vector
•Figure 5C. An additional control would be WT with WT medium
•Figure 2: In the legends, the "x" is missing for the dKO regression formula
•Since the role of SKMc15 in adipogenesis has never been described, the authors could consider describing the single SKMc15 KO in addition to the dKO, or explain the rationale for focusing the study on dKO.
Significance
While the effects of DLK-1 on adipogenesis have been widely documented, the factors controlling DLK-1 expression and function remain poorly understood. Here the authors propose a novel mechanism for the regulation of DLK-1, and how it affects adipocyte differentiation. This study should therefore be of interest for researchers interested in the molecular control of adipogenesis and cell differentiation in general. Furthermore, the characterization of the function of SKMc15 in the control of translation may be of interest to a broader readership.
Referees cross-commenting
I agree with all the comments raised by the other reviewers. Addressing the often overlapping but also complementary questions would help to clarify the molecular mechanisms by which TIS7 and SKMc15 control adipogenesis, and support the conclusions raised by the authors.
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Referee #1
Evidence, reproducibility and clarity
This study by Viedor et al. examines the role of TIS7 (IFRD1) and its ortholog SKMc15 (IFRD2) in the regulation of adipogenesis via their ability to modulate the levels of DLK1 (Pref-1), a well-known inhibitor of adipogenesis. They generate SKMc15 KO mice and cross them to previously published TIS7 KO mice. All 3 mutant strains show decreased fat mass, with the effect being most pronounced in double KO mice (dKO). Using mouse embryonic fibroblasts (MEFs) from mutant mice, they authors ascribe a defect in adipogenic differentiation of mutant cells to an upregulation of DLK-1. In the case of TIS7, they propose that this is due to its known inhibition of Wnt signaling, which regulates DLK-1 expression. In the case of SKMc15, they suggest a new mechanism linked to its ability to suppress translation. Overall, the work is of interest, with the finding that SKMc15 regulates adipocyte differentiation being its novelty, and generally well done, though multiple aspects need to be improved to bolster the conclusions put forth.
Major concerns:
1)The main mechanism put forth by the authors to explain the inability of dKO cells to differentiate into adipocytes is the upregulation of DLK-1 levels. However, this notion is never directly tested. Authors should test if knockdown of DLK-1 in dKO cells is sufficient to correct the defect in differentiation, or if additional factors are involved.
2)There are multiple instances were the authors refer to "data not shown", such as when discussing the body length of dKO mice. Please show the data in all cases (Supplementary Info is fine) or remove any discussion of data that is not shown and cannot be evaluated.
3)Indirect calorimetry data shown in Fig. S1 should include an entire 24 hr cycle and plots of VO2, activity and other measured parameters shown (only RER and food intake are shown), not just alluded to in the legend.
4)It is surprising that the dKO mice weight so much less than WT even though their food consumption and activity levels are similar, and their RER does not indicate a switch in fuel preference. An explanation could be altered lipid absorption. The authors indicate that feces were collected. An analysis of fat content in feces (NEFAs, TG) needs to be performed to examine this possibility. The discussion alludes to it, but no data is shown.
5)It would be important to know if increased MEK/ERK signaling and SOX9 expression are seen in fat pads of mutant mice, not just on the MEF system. Similarly, what are the expression levels of PPARg and C/EBPa in WAT depots of mutant mice?
6)Analysis of Wnt signaling in Fig. 3c should also include a FOPflash control reporter vector, to demonstrate specificity. Also, data from transfection studies should be shown as mean plus/minus STD and not SEM. This also applies to all other cell-based studies (e.g., Fig. 6b,c).
7)It is unclear why the authors used the MEF model rather than adipocyte precursors derived from the stromal vascular fraction (SVF) of fat pads from mutant mice. If they did generate data from SVF progenitors, they should include it.
8)Given that the authors' proposed mechanism involves both, transcriptional and post-transcriptional regulation of DLK-1 by TIS7 and SKMc15, Fig. 4d should be a Western blot capturing both of these events, and not just quantitation of mRNA levels.
9)There is no mention of the impact on brown adipose tissue (BAT) differentiation of KO of TIS7, SKMc15, or the combination. Given the role of BAT in systemic metabolism beyond energy expenditure, the authors need to comment on this issue.
Minor comments:
10)The y axis in Fig. 2c is labeled as gain of body weight (g). Is it really the case that WT mice gained 30 g of body weight after just 3 weeks of HFD? This rate of increase seems extraordinary, and somewhat unlikely. Please re-check the accuracy of this panel.
11)The Methods indicates all statistical analysis was performed using t tests, but this is at odds with some figure legends that indicate additional tests (e.g., ANCOVA).
12)Please specify in all cases the WAT depot used for the analysis shown (e.g., Fig. 3d is just labeled as WAT, as are Fig. 4a,e, etc.).
13)Fig. 5d is missing error bars, giving the impression that this experiment was performed only once (Fig. 5c). The legend has no details. Please amend.
Significance
The role of TIS7 in adipocyte differentiation is well established. The only truly novel finding in this work is the observation that SKMc15 also plays a role in adipogenesis. The molecular mechanisms proposed (modulation of DLK-1 levels) are not novel, but make sense. However, they need to be bolstered by additional data.
Referees cross-commenting
I think we are all in agreement that the findings in this work are of interest, but that significant additional work is required to discern the mechanisms involved. In my view, a direct and specific link between SKMc15 and translation of DLK-1 needs to be established and its significance for adipogenesis in cells derived from the SVF of fat pads determined. Reviewer 2 has suggested some concrete ways to provide evidence of a direct link.
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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: The manuscript analyzes how the constriction of a tissue by an enveloping basement membrane alters the migration of cells migrating through that tissue. The tissue analyzed is the Drosophila egg chamber, an important model for basement membrane studies in vivo, and the cells migrating through it are the border cells. The border cells migrate through the center of the egg chamber, moving as a cluster between the nurse cells, which are in turn surrounded by follicle cells, which secrete the basement membrane on the outside of the egg chamber. The authors decrease and increase the basement membrane stiffness with various genetic perturbations, and they find that the border cells move more rapidly when the stiffness is reduced. They then investigate how basement membrane stiffness is communicated to the border cells several cell layers inside, by measuring cortical tension with laser-recoil. They found that external basement membrane stiffness alters the cortical tension of the nurse cells and the follicle cells, such that reduced matrix stiffness causes reduced cortical tension; further, reducing cortical tension directly within the cells also results in increased border cell migration rates. They conclude that basement membrane stiffness can alter cell migration in a new way, by altering constriction and cortical tension, with an inverse relationship between stiffness and migration rate. This is a strong manuscript and I would request very few changes.
The authors are commended on the rigor and completeness of their study. Several independent methods are used to alter basement membrane stiffness (loss of laminin, knock-down of laminin, knock-down of collagen IV, over-production of collagen IV - all of which end up changing collagen IV levels) and all show the same result. Further, they are extremely rigorous about testing and excluding an attractive alternative hypothesis, that the basement membrane of the border cell cluster itself controls its migration rate. The use of mirror-Gal4 is very elegant and convincing, as it expressed only in the central part of the egg chamber, and they found border cells responded differently only in that region. Moreover, the authors were exceptionally thorough in reproducing the basement membrane mechanical data in their own hands using the bursting assay. Overall, the experimental data support the claims of the paper. There is only one more control I would like to see, for the knockdown of laminin in the border cell cluster with a triple-Gal4 combination. Presumably using all three Gal4 lines was necessary to get complete knockdown, and it would be nice to see anti-laminin for the border cell cluster under these knockdown conditions.
Despite the rigor, because all of the manipulations to the basement membrane alter the levels of collagen IV, the authors cannot formally exclude the possibility that collagen IV in the basement membrane has another function besides stiffness, perhaps sequestering a signaling ligand, and that this other function somehow alters the cortical tension of the egg chamber. In the paper by Crest et al, externally applied collagenase served as a control for this possibility, but collagenase will not work for the authors because this study is in vivo. I suggest the authors bring up this caveat in the discussion. If they wanted to extend the study (optional), they could knock down the crosslinking enzyme peroxidasin in the egg chamber, which ought to reduce basement membrane stiffness without changing the collagen content. The problem here is that it hasn't already been shown to work that way in the egg chamber, and so both stiffness and collagen levels would need to be measured. Testing the stiffness directly would be difficult, since the bursting assay is not actually a measurement of stiffness (more on that below). Rather than go this route, I suggest just acknowledging the formal possibility, which seems to me unlikely anyway.
In terms of clarity, the manuscript absolutely needs a schematic at the beginning to introduce the egg chamber and border cell migration, labeling the cell types, showing the route and direction of border cell migration, and labeling the A/P axis. Without this the non-expert reader cannot readily understand the study.
Finally, in terms of clarity, the authors repeatedly use statements such as "stiffness influences migration rate". Influences how? These results are not intuitive to me, and it would help enormously if the authors would make statements like, decreasing stiffness increases migration (as I tried to in my summary). Here are two examples of statements to refine: • Line 189 - "We found that reducing laminin levels affected the migration speed of both phases (Fig.1F, G)." Please say increased, not affected. • Line 245 -"Altogether, these results demonstrate that the stiffness of the follicle BM influences dynamics and mode of BC migration." Again, be specific about how. There are many such statements, from the abstract to the results to the discussion, where it would help the clarity to be more precise about what kind of influence.
Minor comments: • The movies are beautiful! • All the quantitative data are shown in bar charts with means and errors. It is much better to show the individual data points, superimposing the means and distributions on top of the individual points. • The bursting assay does not actually measure basement membrane stiffness; rather, it measures failure after elastic expansion. These are related, as was found by Crest et al and the authors say that at one point, but stiffness and failure are not the same thing. Please change the language discussing this assay to "mechanical properties" rather than stiffness. • The laser-recoil assays are done well and are convincing. Throughout the results section, the authors describe these as measuring "cortical tension", which is correct. However, in the figure legends the language changes to "membrane tension" which is only one component of cortical tension. Change them all to cortical tension. • In the Discussion, it would be nice to include something on the two different modes of migration (tumbling and not tumbling). • I suggest changing the title to remove the word "forces", because forces are never directly measured from basement membrane. • Although Dai et al (Science 2020) is discussed near the end, I suggest bringing this reference up to the introduction, so the reader can have the background on the mechanical aspects of border cell migration at the start of this study. • Two typos (there may be more): At the bottom of Fig. 2, text turns strangely white that should probably be black; and in line 260, you mean Fig. S5 not S4 (laser ablation).
Significance
Mechanobiology, and mechanobiology of the basement membrane, is a vibrant area of study now, arising from the intersection of biophysics/engineering and genetics. There is general interest in how the basement membrane alters forces within the tissue, and this study is the first to my knowledge to relate basement membrane mechanics to migration via constriction and cortical tension. The authors do a great job of discussing the broader significance of their work in the Discussion. To greatly broaden the scope of this work in the future, the authors could collaborate with a mouse team to look for similar responses in a mammalian tissue, as they discuss. It is worth noting that there is a lot of work on matrix stiffness and migration showing that stiffness promotes migration speed; in these cases, matrix is a substrate, not a compression mechanism. But the opposite nature of the result in interesting and makes this work non-intutive and perhaps hard for some readers to grasp.<br /> As the paper is written now, I think the audience for this work would mostly be oogenesis, border cell migration, and/or basement membrane researchers in the Drosophila community, of which there are many (I am in this camp). With some rewriting to make it more accessible to other audiences, I think it would be interesting to a larger developmental biology audience. The content is not like any other paper I know, but it may be similar in scope and subject matter to the papers detailing how follicle cells and basement membrane interact during follicle rotation.
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Referee #2
Evidence, reproducibility and clarity
Ester and her colleagues described a force model that controls border cell migration by varying the stiffness of the basement membrane. It's based on the modification of laminin and Coll IV which are components of the basement membrane. To reduce BMs stiffness, they introduced LanB1RNAi or the LanB1 mutant to inhibit laminin production or vkgRNAi to reduce Coll IV. They also applied EHBP1mCh to enhance BM stiffness. Furthermore, they applied laser ablition to confirm that the BM stiffness affects the tension of nurse cells and follicle cells, thus regulating border cell behavour by changing environmental properties. It is a nice work revealing how the environment controls border cell migration; however, there are several points that concern me: 1. It's reported that actin polymerization at the front of the cell generates protrusions, as well as that myosin contractility helps to suppress lateral random protrusions, thus leading to a directed and efficient cell migration. So why do more lateral protrusions (tj>LanB1RNAi) produce a faster migration speed? 2. We know some labs also did experiments with those Kel/Dic mutant flies. And the Kel mutant is very sick, which sometimes leads to NC degeneration. As a result, we have serious doubts that this mutant's border cell migration will remain normal. 3. From figure4, we noticed that with mirrGal4, the vertex distance increase is much lower than tjGal4 (control of D, H and K), and even with expressing the EHPB1mCh, the distance is still lower than the tjGal4 control. These indicate the NC cortical tension is lower with mirrGal4 expression, which is patially against the paper's main point. (Similar issue in figure5 D and E). 4. Sfigure1 A and B seem not to have the right contrast (the blue and the red should have the same brightness), so the comparison of the intensities might be inaccurate and needs to be requantified after adjustment of the images. 5. Sfigure2 A-E showed that the vkgRNAi has the highest bursting frequency, whereas F and G do not. And the majority of the data from F does not fit with A-E, and it is unclear what timepoint sF.G. is at. 6. SFigure 6 only displayed a representative image of the control condition; the lack of representative images for the other conditions resulted in unconvincing results. 7. Some figures and movies have prominent variation of migrating stages, such as not-detached border cells compared with detached border cells. This might strongly cause the results inconsistent with each other. 8. There are numerous typos in both the manuscript and the figures. Based on all these concerns, I recommend authors to do some improvement before this manuscript is accepted by some reputed journals.
Significance
Strengths: the manuscript is well written and organised; limitation: figures and results are not supportive enough, and thus conclusion is not completely convincing, statistical quantification is not clear and somehow confusing.
Advice: If the conclusion is solid, this story will fill the unclear importance of surrounding environment on cell-rich tissue for collective cell migration. Concept is very novel while needing more supporting data. It is a fundamental study for development biology.
Audience: The story will fit well for developmental and cell biology, as well as people with biomechanical background.
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Referee #1
Evidence, reproducibility and clarity
The manuscript by Lopez et al have employed the ex vivo model of Border cell migration in Drosophila ovaries to examine the constriction forces imposed by basement membrane on migrating border cells. The authors have extensively employed live cell imaging coupled with genetics to demonstrate that basement membrane encasing fly eggs modulates the dynamics of migrating border cells. Through laser ablation experiments they show that basement influences the tension of the underlying follicle cell and nurse cells which in turn affects the migration efficiency of collectively moving border cells. Over all the experiments are well quantified with good degree of statistics that drive the claim of the authors.
Major comments: Over in all the images, it is very hard to appreciate the overall contour of the egg chamber. This is important to get an insight regarding the stage of the egg chamber being evaluated.
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By depleting the constituents of basement membrane, the authors show that the speed of the migrating border cells increases. However in Supplementary Figure 1A and B where that authors have depleted LanB1, the migrating border cell cluster seems to lag while the control has reached the oocyte boundary. Is this a single off phenomena?
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This is regarding the osmotic swelling experiments. The frequency and speed of bursting of egg chambers in deionized water was used to evaluate the stiffness of basement membrane in different genetic background. As egg chambers of different stages have variable sizes, it would be fair to evaluate egg chambers of only a particular stage for this analysis as the tonocity of the egg chambers may depend on their size.
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Line 211, "Live time lapse imaging, showed that the overexpression of EHBP1mCh in all FCs delayed BC migration (tslGFP; tj> EHBP1mCh, Figure S4A-B', Movie S4, n=6)." Though the border cell cluster hasn't moved significantly in Fig S4B', the egg chamber development seems to be stalled as the movement of main body follicle cells is affected. My concern if over expression of EHBP1mCh in the follicle cells is stalling the oogenesis itself could that indirectly affect the border cell movement. Secondly though EHBP1 has been shown to affect secretion of the basement membrane constituents, it could also modulate asymmetric secretion of other components. Can the authors evaluate if over expression of EHBP1mCh rescues the delay in migrating border cells in Lanb1 heterozygous background to render stronger support to their claim.
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In Supplementary Fig 7 B and B' the nurse cell morphology seems to be affected. Could the distorted nurse cell morphology in the abi-depleted germline cell affecting the migration efficiency of border cells.
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Line 313-314 The authors state that "The radius of curvature of a spherical interface is inversely proportional to the difference in pressure between the two sides of the interface." This may be applicable to a smooth surface but may be not directly applicable to the cell membrane as there are local regional variations and thus any inference on the cytoplasmic pressure of nurse cells may be misleading.
Minor comment:
- In supplementary figure 6D, the square boxes are obscuring the border cell membrane and it will be better if the authors can modify the figure to render more clarity.
- There are couple of places where sentence structure needs to be corrected.
Referees cross-commenting
I agree with all the comments of other reviewers. Overall I also feel that results do not strongly support the main conclusions. The authors draw major conclusions based on experiments that are merely suggestive rather than being conclusive. Some of the concerns are listed. Like Reviewer 3 raising the concern that Collagen IV may have other functions in the basement membrane other than providing stiffness. A similar concern I too have raised regarding over-expression of EHBP1. I agree with Reviewer 3 that there are several other factors that can affect the outcome of bursting assay besides the stiffness of the basement membrane itself. So the authors need to be careful in linking the bursting frequency of the egg chamber with the stiffness of the basement membrane itself.
I agree with other reviewers that the quality of the images need to be better. In addition, the image presented should be representative of the population and should fit with the over claim made by the authors (Point No 3 of Reviewer 2 and Point No 1 of Reviewer1). I also agree that authors need to explain Reviewer 2's concern (Point No-1) as to why the lateral protrusion in tj>LanB1RNAi doesn't inhibit the movement of border cell clusters but rather produce faster migration speeds?
Lastly it is important for the authors to verify that like Kel/Dic mutants are indeed effective or any genetic perturbation like overexpression of EHBP1mCh is not the stalling the oogenesis progression perse, thus giving a false impression of altered migratory speed of border cell clusters.
Significance
The role basement membrane is well documented in affecting the shape of neighbouring cells Here the authors claim that the stiffness of basement membrane is regulating the migration efficiency of the border cells. I believe that basement membrane encasing the follicle and underlying germline cells provides a very narrow passage for the border cells to migrate. Any mechanical perturbation that releases or increases the pressure or make the nurse cells membranes less or more taut will affect the dynamics of migrating border cells. Though the authors have demonstrated this with very elegant experiments, I am afraid that their findings are standard outcomes in any physically constrained system and somehow doesn't significantly advance the field.
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Reply to the reviewers
Manuscript number: RC-2022-01776
Corresponding author(s): David Bryant
1. General Statements [optional]
We describe an ARF6 GTPase module that controls integrin recycling to drive invasion in PTEN-null Ovarian Cancer (OC). We used high-throughput, time-lapse imaging and machine learning to characterise spheroid behaviours from a series of cell lines modelling common genetic lesions in OC patients. We identified that PTEN loss was associated with increased invasion, the formation of invasive protrusions enriched for the PTEN substrate PI(3,4,5)P3, and enhanced recycling of integrins in an ARF6-dependent matter. We utilised Mass Spectrometry proteomics and unbiased labelling to investigate the interactome of ARF6, identifying a single ARF GAP (AGAP1) and a single ARF GEF (CYTH2). Importantly, this ARF6-AGAP1-CYTH2 modality was associated with poor clinical outcome in patients.
We thank all Reviewers for their highly complementary assessment of our manuscript, describing our paper as a "very impressive study, very well done and controlled with rigorous statistical analyses that uses sophisticated methods", a study that is "stunning in its thoroughness and depth and breadth of its molecular analysis", with "experiments are properly designed, and the data are well presented. The conclusions are appropriate and supported by the data". Finally, we would like to thank the reviewers for appreciating that our results are "of significance for both scientific discovery and clinical application, which will interest the broad audience in both basic and clinical research".
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 comments in bold. Our response in non-bold.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
This paper by Konstantinou et al aims at deciphering the mechanisms by which PTEN loss could be driving poorer prognosis in patients. The authors use their great high-throughput 3D screening method coupled to an unbiased proteomic method and a CRISPR screen to uncover a new pro-invasive axis driving collective invasion of high-grade serous ovarian carcinoma (HGSOC) cells. Overall, this is a very impressive study, very well done and controlled with rigorous statistical analyses that uses sophisticated methods to convincingly show that the CYTH2-ARF6-AGAP1-ITGA6/ITGB1 module is required for the pro-invasive effect of PTEN depletion and discriminates patients with poorest prognosis.
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MAJOR COMMENTS __
Below are listed all the claims that, in my opinion, are not adequately supported by the data.
1) Choice of the cell line: More justification on the use of the ID8 cell line and on the p53 deletion is needed. The authors need to clearly state that most p53 mutations in ovarian cancer are missense mutations that lead to a strong accumulation of a p53 protein devoid of transcriptional activity. Nevertheless, it seems that p53 mutations are not associated to differences in patient survival. Hence the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained. Moreover, the in vivo experiments already performed in the literature mentioned in the discussion should be mentioned in the introduction to provide more context and physiological relevance to this study (especially regarding the special focus on the p53 null/ dKO cells throughout the study).
We will update the manuscript with a detailed explanation of the cell line of choice. Briefly, while indeed Tp53 is found mutated in HGSOC, approximately 30-35 % of these are classified as null mutations (PMID: 21552211), making models with null Trp53 representative of the clinical situation. Further, there is no difference in patient outcome in HGSOC by Tp53 mutation type (PMID: 20229506), while gene expression data from TCGA suggest that HGSC is marked by loss of wild-type P53 signalling regardless of Tp53 mutation type (PMID 25109877). Thus, we believe our choice of model can faithfully mirror the clinical situation.
2) "Therefore, PTEN loss in ovarian cancer, particularly at the protein level, occurs in the tumour epithelium and is associated with upregulated AKT signalling and poor overall survival". This claim is an over-interpretation and over-generalisation of the data presented. I appreciate the honesty of the authors in showing all the ovarian datasets that are available and highlight the discrepancies in expression of the proteins they study in stroma and epithelium. I think the way to present these data in the text without over-interpreting and generalizing would be to show that there is a clear epithelial-specific downregulation of PTEN at the mRNA level. Most likely due to the contribution to other cell types in the stroma, only 3 out of 5 bulk tumour mRNA datasets show a tumour specific downregulation of PTEN and no association with survival based on a median split of PTEN mRNA expression. Nevertheless, although there is no direct correlation between PTEN mRNA and protein levels, patients with low PTEN protein levels have poorer survival that is associated to an upregulation of Akt signalling. This allows to have a clearer conclusion, based solely on the protein data presented and no over-generalisation using the mRNA data. This, to me, makes a stronger case for studying PTEN loss in ovarian cancer and is fully supported by the data presented.
We will incorporate this reviewer suggestion into the modified manuscript.
3) PTEN loss induces modest effects in 2D culture. The authors make claims regarding the fact that some of the phenotypes they look at happen after PTEN depletion alone or in combination with p53 loss and are more prominent in 3D vs 2D. Many of these are insufficiently backed up by data. A few key experiments are also only performed in 2D and should be done in 3D. Finally, some clarifications if the role of PTEN is most prominent on either collective, ECM-induced or 3D-dependent invasion.
some clarifications if the role of PTEN is most prominent on either collective, ECM-induced or 3D-dependent invasion
We believe that the reviewer may be confused. Both of our models, either spheroids or invading monolayers, are events occurring inside gels of ECM. Therefore, these are all are 3D, ECM-induced, collective invasion. We have not performed 2D migration assays. We apologise that the this was not clearer in the first submission. We will correct this in the updated manuscript.
First, the authors claim that PTEN loss alone (i.e. without p53 deletion) leads to changes in Akt signalling. Supp fig 1H clearly shows that there is no significant increase in Akt activation, although there seems to be one in the Western Blot (WB) presented in supp fig 1G. There is a clear, significant increase in the Akt activation in all the PTEN KO clones when in association with p53 loss though. This claim is hence not backed up by data and the conclusion seems to be that the effect on Akt signalling requires both deletion of p53 and PTEN.
The reviewer is correct: that the increase to pAKT levels upon PTEN KO is more robust with co-KO of TP53, thereby indicating synergy with p53. We will update the manuscript to note this, accordingly.
It will be interesting to see a quantification of the pS473-Akt staining (supp fig S1J), as it seems from these images that pAkt is preferentially found on rounded cells. It should also be performed in 3D conditions to see if there is an enrichment at invasive tips and back-up the invasion data.
This observation made us realise that the images we had included were giving the wrong impression (that pAkt levels would be highest in round cells). Based on the quantitation in Fig. S1M, PTEN KO cells (which have elevated pAkt levels), show a marked depletion of rounded cells. Therefore, pAkt elevated is not associated with being enriched in rounded cells. We will replace this image with cells mirroring the phenotypes quantified in Fig S1M.
We used 2D for quantitation of pAKT staining, as we perform a like for like comparison. We cannot compare pAkt in 3D protrusions accurately between genotypes because of the frequency of protrusions: in p53 KO protrusion are rare. In 3D, therefore, it is not a situation where protrusions are present in both genotypes and we compare enrichment or depletion in a stable structure. Rather, what we can provide is whether when protrusions form, there is clear pAkt labelling in a protrusion. We will include for the revision a representative image of each phenotype in 3D, including a 3D Trp53-/-;Pten-/- spheroid stained for pAKT S473.
Arf6 is recruited to the invasive tips of cells invading a 2D wound (fig4D). How do the authors reconcile the fact that all the machinery required for 3D invasion is present but that PTEN loss has a modest effect on cells in 2D? If the wound assay was done on glass, it should be done again on ECM coated glass to see if it recapitulates the effects seen in 3D. This experiment will help deconvolute if the effect of PTEN loss is more linked to collective behaviour than 3D organization or presence of ECM.
We again apologise for not being clearer in our description. Both the wound assays and the IF of invading monolayer were performed with cell monolayers invading into Matrigel. Monolayers are grown on top of Matrigel, wounded, and then overlayed with Matrigel. Therefore, this is orthogonal to our spheroid assay, and completely 3D. We will address this comment by changing the text in the results section to highlight the 3D nature of the method.
The recycling assays are all done in 2D, condition under which the authors claim that the PTEN phenotype is weakest. Although I understand that it is not possible to do this assay in 3D, its contribution to elucidating the mechanism by which integrins participate in the PTEN loss invasive phenotype is not clear. The requirement of integrins relies on the data showing that ITGB1 KO results in no collagen4-positive basement membrane of the cysts and greatly impaired invasion. Experiments looking at the integrin localisation would be helpful: can an enrichment at the invasive tips can be seen? Are ITGA6 and/or ITGB1 repartitions homogeneous between the cysts membranes and the invasive tips? In my opinion the Src/FAK data is not enough to draw the conclusions of fig7I schematic.
We will endeavour to include images of 3D spheroids of Trp53-/-;Pten-/- cells and stained for β1 integrin (total and active) and α5 integrin to interrogate localisation at the tips.
4) Expression of AGAP1 isoforms do not alter ARF6 levels. Data in fig 6C, D show a significant downregulation of Arf6 and Akt signalling after expression of AGAP1S. Can the authors clarify what they mean?
We thank the reviewer for picking up that discrepancy between the results and the text. We will change the relevant text to highlight that expression of AGAP1S is associated with a statistically significant reduction of roughly 30% in ARF6 levels and 10% in p:t AKT. We do not know why AGAP1s may enact such an effect.
5) Arf6 is not modulated in the different cell lines: data in fig4B (far right graph) and supp fig 4B, J seem to indicate otherwise. Can the authors clarify what they mean?
It is not clear exactly what the reviewer is referring to here. If the reviewer is referring to Supplementary Figure 4B, this is an experiment examining the levels of ARF5 or ARF6 upon knockdown, so levels would be expected to vary. Fig S4B does not correspond to the experiment performed in S4J. Our interpretation is that loss of p53 alone or in combination with Pten does not seem to be consistently be accompanied with an increase in either the levels of total or bulk GTP-bound ARF6 that could explain the dependency of Trp53-/-;Pten-/- on the GTPase for the invasive phenotype. We will make our interpretation clearer in the text
6) Immunofluorescence panels without quantifications: Quantifications for the different stainings shown in fig3A; 4D, E; 5H; 7B and supp fig S1L, J; S3 need to be included to fully back the conclusions of the authors. Indeed, these images are used to draw conclusions and not only as illustrations.
It is not possible to do a direct comparison between protrusion vs no protrusion (see our response above). We will include a line scan to show clear enrichment at the end of the tip for image shown. Quantitation for Figure S1L is already included (S1K and M), quantitation for Figure S1J is presented in Fig S1I and for Fig 5H quantitation of the phenotype is present in Fig 5I.
7) Quantifications of invasion show that WT cysts become hyper-protrusive at around the half experiment mark (around 30-40hrs). Nevertheless, all movies or galleries show spherical cysts, which does not seem representative. Can the authors change this or explain why these images/movies were chosen?
We present the fold change at each time point because that is intuitively easier to understand rather than the raw number. The quantitation does not show that the cysts necessarily become hyper-protrusive at the specific timepoint, but rather that the proportion of hyper-protrusive cysts observed in this genotype peaks at the specific timepoint. This phenotype may still be in the minority of behaviours. As an example, something that occurs 5% of the time in the control, with a two-fold increase in behaviours, might still only be 10% of the population. Therefore, adding in a picture that may be representative of a small proportion of the population may not be a realistic depiction of what is happening across the entire population. We will provide the reviewer with the exact percentage of spheroids that are classified as hyper-protrusive at the specific cell line across timepoints, to make this clearer.
8) Since it seems that the main effect of PTEN is to drive the localisation and intensity of recycling of Arf6 cargoes, it will be helpful to confirm that all the proteins involved in the Arf6 module be shown to be accumulated/present at the pro-invasive tips. Immunofluorescence stainings showing the presence of AGAP1 (could be done with the AGAP1S isoform that is mNeon-tagged), pS473-Akt, ITGB1 (active integrin if possible, otherwise total integrin), ITGA5, PI3K should be included if possible. A quantification comparing signal in the cysts and in the invasive tips should also be included to see if there is an accumulation to PIP3-enriched areas.
We will endeavour to include the requested images.
9) Data in fig5I convincingly show that PTEN loss induces a fragmented collagen4-positive basement membrane. The authors use this data to claim that this is one of the ways that PTEN could be driving invasion but no correlation between these structures and the hyper-protrusive phenotype is made. This experiment needs to be done to support this claim.
This comment made us realise that in an attempt to make images simpler (displayed nuclei and COL4 only), we omitted a staining for where protrusions were moving through gaps in the ECM. We will update these times to demonstrate such events.
__
MINOR COMMENTS __
1) Data visualization: I think that the heatmap representation is overkill when only 2 or 3 conditions are presented. A graph showing the evolution of area or spherical/Hyper-protrusive phenotype proportions across time would be easier to read and more impactful: each genotype could be presented with a colour and the spherical/hyper-protrusive phenotypes as either plain or dashed lanes across time. I understand that this representation allows for the stats to be done at each time points but they are generally pretty clear (especially for the PTEN KO or dKO phenotypes) and do not need to be done for each time point in my opinion. These heatmaps could be put in supplementary figures if the authors feel strongly about putting stats for each time points.
We thank their reviewer for their suggestion. We believe that our approach, while complex, is the best visualisation to reflect both the changes across time but also between conditions while allowing appreciation of the statistical significance. This visualisation has been optimised by our lab over years of working with this type of data and we would prefer that they remain consistent with the accepted standard of our other publications. We are, however, happy to expand the explanation in the text on how to interpret the bubble heatmaps.
Fig supp S1M, fig 5I should be presented as a stacked histogram to improve readability and merged with fig supp S1K.
We will merge Figures S1M and S1K. We believe that Figure 5I is easier to read as is.
Displaying fold change as antilog rather than log values would be easier for the reader to realise the magnitude of the differences.
We disagree with the reviewer.
A bar graph would be easier to read than the matrix representation for fig 6B.
We disagree with the reviewer as we feel it makes it easier to directly compare each lipid between the two cell lines.
The way Area data is presented throughout to me makes it very difficult to understand what is going on. Could the authors at least give some explanations in figure legends. A curve graph displaying the evolution of the area across time would be easier to read and see the differences between conditions.
Please see our response to Minor point 1
2) It is confusing that, in fig supp S1M, there is a significant decrease of the rounded phenotype after PTEN loss that is not associated to a significant change in another of the categories. Could the authors explain how?
This can be simply explained from our data: while the rounded phenotype was reduced in a consistent way across replicate experiments (therefore resulting in significance), the effect on the other two phenotypes was not consistent (not set in magnitude and directionality). This therefore does not lead to a significant (i.e. consistent) effect on the latter two phenotypes. PTEN loss therefore seems to allow cells to undergo – at the expense of being round - a range of shape changes, rather than a set phenotype.
3) One of the big differences of the PTEN KO cells seems their ability to invade through the matrigel bed and migration on the glass below (supp movie S2). From what I gather, these cysts would be considered out of focus and excluded from the analysis. Would it be possible that this would minimize some of the results? Would it be possible to include a quantification of this particular phenotype to confirm it is specific to PTEN KO cells?
In the same spirit, could the authors provide the percentage of non-classified cysts, to make sure that the same proportion of cysts is quantified across all different genotypes.
Indeed, we cannot exclude that we under-estimate the magnitude of the effect on the PTEN null. We will include this point in the discussion. We can include a reviewer-only figure showing the proportion of cysts and levels of the ‘OutOfFocus’ objects across cell lines.
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4) Can the authors clarify how a 0 fold change (in log value) in fig 2D can be highly significant? __
We believe that the reviewer is equating statistical significance with something being biologically meaningful. Statistical analysis does not indicate a priori whether something is biologically meaningful. Rather, it assesses the likelihood that an observed result is occurring by chance (or not). For instance, if a small change (e.g 0.04 in a log2 fold change) occurred repeatedly across experimental replicates this is unlikely to be a result of chance, and therefore could be statistically significant. Yet, such a small magnitude of effect is probably biologically minor. This is why our heatmaps provide both statistical significance, fold change, and consistency in magnitude of effect.
5) Delta isoform of PI3K seems to have an effect on area in the middle of the experiment, but has no effect at all on invasion. Could the authors comment? Are these smaller cysts still as invasive? There might be an interesting uncoupling between proliferation and invasion there.
The cysts are actually slightly larger with PI3Kδ inhibition and there is no change in invasion. We will expand our comments in text as well to account for this observation.
6) ITGB1 depletion seems to induce a downregulation of Akt protein. Is that right? Does it change Akt localisation? Is there a dose effect whereby there is not enough Akt protein to mediate invasion?
The p:t AKT ratio does not change consistently across all gRNAs (Figure 5C) but we can look at Akt (total) protein levels and include this information if needed.
__
7) Stats should be added directly on the graphs for the recycling assays, doing a pairwise comparison of the different genotypes for each time points. Can the authors clarify what the t-32min quantification graphs adds (fig7E, supp fig S8G-I)? I would advise to remove them, as this data is already presented in the recycling assay graphs. __
We don't include these because although they are technical replicates, they are demonstrative of a single experiment. What we include instead is the quantitation across independent biological experiments (which each have their own internal multiple technical replicates), where it is appropriate to include statistical analysis.
8) There is a substantial amount of typos and erroneous references to figures. I listed below the ones that I spotted and I encourage the authors to carefully check.
- there are some mistakes in referencing the number of cysts in supp table 1. There is for example no cysts experiments in Figure 1 but yet there are some references to figure 1 in supp table 1. Please correct it. I think it will be easier for the reader if the number of cysts quantified for each conditions was also indicated in the figure legends. Supp table 1 can still be included for readers that want additional details.
- comma missing page 3
- page 3 and 4: PI(3,4)2 means PI(3,4)P2? Can be shorten to PIP2 for ease of read and specify if it is another PIP2 specie otherwise
- define CYTH abbreviation: I suppose this is for cytohesin?
- fig1F-I: don't understand why TCGA.OV is specified on some but not all the graphs. It seems to me that all the data are from TCGA.OV? Makes it seems it is nit the case
- legend of fig1H, I: y axis is -Log10 values in 1I, not Log10 values
- page 6: dKO abbreviation is already specified above and should be used to avoid repetition and for ease of read
- supp fig S1D: missing legend for the second bar (after Wild Type)
- supp fig S1N: legend of the X-axis should be below the axis
- supp fig S1O: the numerotation of the X-axis needs to be below the line of the axis for ease of read, not above it
- legend of S2A: clones 1.12 and 1.15 are p53-/-;PTEN-/- and not PTEN-/-
- supp figS2C can the authors specify the different stages of matrigel (liquid or gel) that are used for the invasion assay, to make it easier for the non-specialist to understand what is going on. Please confirm that the 50% GFR matrigel makes a gel on top of the cells and fill in the wound to produce the 3D invasion assay setup.
- page 7: no parental cells are used in S3A, B only p53 null and p53 null and dKO. Please also specify what cells are being compared in the text
- description of arrow heads and colours need to be moved to figure legends and not in main text (page 7)
- fig 2D: the signification of the dot in the circles needs to be in the legends (since it is its first apparition in the manuscript). It only appears later on, in supp2A legend. Additional description of the matrices is necessary, as they contain a lot of information to digest to understand fully what is going on
- legend of fig3: error in figure reference: area data is D and not E, protrusive phenotypes are E and not F
- arrow missing in fig3B
- fig 3D,E, G, H: please indicate the cell line studied
- fig 3I: the different genotypes need to be stated on the galleries for clarity
- page 8: define Arf6-mNG in the text
- __ page 9: "We thank the reviewer for their careful examination of the manuscript. We will go through all above points and make the corresponding careful adjustments to the manuscript.
OPTIONAL SUGGESTIONS
1) Choice of cell line: There is a high number of patients (around 9% according to (Cole et al. 2016)) that present the R248Q gain-of-function mutation. A recent study has shown that this mutant p53 protein is associated to an activation of Akt signalling and an increase of the intercellular trafficking of EGFR (Lai et al. 2021). Given that EGFR was also a hit in this screen, that is seems to have a central role in Arf6 cargoes (fig 4G), I think it would be a great addition to this study. It could hence cooperate with PTEN loss to drive strong, robust invasion.
This is an excellent observation and one we will likely follow-up in an independent study.
2) Are MAPK involved in the PTEN KO pro-invasive phenotype? In particular Erk1/2, since EGFR is one of the PTEN loss induced Arf6 cargoes.
This is an excellent observation and one we will likely follow-up in an independent study.
__
REFERENCE Cole, Alexander J., Trisha Dwight, Anthony J. Gill, Kristie-Ann Dickson, Ying Zhu, Adele Clarkson, Gregory B. Gard, et al. 2016. « Assessing Mutant P53 in Primary High-Grade Serous Ovarian Cancer Using Immunohistochemistry and Massively Parallel Sequencing ». Scientific Reports 6 (1): 26191. _https://doi.org/10.1038/srep26191_.
Lai, Zih-Yin, Kai-Yun Tsai, Shing-Jyh Chang, et Yung-Jen Chuang. 2021. « Gain-of-Function Mutant TP53 R248Q Overexpressed in Epithelial Ovarian Carcinoma Alters AKT-Dependent Regulation of Intercellular Trafficking in Responses to EGFR/MDM2 Inhibitor ». International Journal of Molecular Sciences 22 (16): 8784. _https://doi.org/10.3390/ijms22168784_. __
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The authors have conducted a study of the molecular requirements for cancer invasion that is stunning in its thoroughness and depth and breadth of its molecular analysis. The writing is exceptionally precise though also very dense (see below). The molecular model proposed is that PTEN loss (in a p53 null background) leads to reliance upon ARF6 for invasion, with regulation through interactions with AGAP1 and beta1-integrin and it is convincingly demonstrated. They focus on interpreting the consequences of genetic and pharmacologic manipulations in a cell line, using a series of 2D and 3D assays. The phenotypes are more prominent in 3D assays.
Concerns and Suggestions:
- There is a disconnect between the essentially complete loss of protrusions and invasion in 3D (e.g. 4A) and the reduction in magnitude of protrusive invasion but the continued presence of elongated cells with protrusions in 2D (e.g. S4C). This discrepancy is present in a couple of comparisons and is glossed over in quick callouts to many figure panels.
We thank the reviewer for mentioning this as this comment was very helpful in determining that we needed to clarify our description of the role of ARF6 to protrusion formation vs maturation. In the Trp53-/- genotype, protrusions can form, but they rapidly retract, failing to mature into structures that drive invasion through ECM (e.g. Figure S2E). This protrusion maturation occurs upon PTEN KO. When ARF6 depleted, PTEN-null cells can form protrusions, but now again lack the ability to mature into invasion-inducing structures.
This concept of needing ARF6 for protrusion maturation and maintenance is underpinned by our model of ARF6 regulating recycling of active integrin back to the protrusion front. Indeed, we have observed ARF6 being required not for protrusion initiation, but rather ensuring protrusions are not retracted in other contexts (i.e. upon loss of the ARF6 GEF protein IQSEC1 in invading 3D culture of PC3 cells; PMID: 33712589).
We also note that, as responded to Reviewer 1, the assay is a 3D invasion rather than 2D migration assay, with cells sandwiched between Matrigel.
We will update the relevant sections of the results and discussion with the point above.
Once a journal has been identified, it would be wise for the editor to allow some flexibility in word limit to enable some very dense sections to be expanded slightly to guide the reader through the experiments and results more clearly. For example, in the section "ARF6 regulates active integrin pools...", there are callouts like (Fig. 7C,E; S8A-C; G-I) and then (Fig. 7D,E; Fig. S8E-F, H-I). It takes a lot of time to unpack these different experimental claims based on a single sentence.
We greatly appreciate the refreshing comments of this reviewer to advocate for actions to improve clarity in our reporting. We would take glad advantage of such a possibility.
The patient data on CYTH2 and its relationship to survival is modestly convincing.
In Ovarian Cancer, effects on survival are often minor. This is not a disease where one often sees large shifts in survival, which is why we are so excited about the large shifts that we do see with the ARF GTPase module we identified. However, we concede that the effects on CYTH2, although significant, are not vast changes. We will point this out and tone down our language.
Very minor- search on %- there are a few inconsistencies in terms of spaces and commas vs. periods. The Methods also have some inconsistencies in terms of spaces between numbers and units or numbers and degrees Celsius. References are also in a different font. Overall it was extremely carefully written though (just dense).
We thank the reviewer for their careful inspection of our manuscript. We will carefully go over the sections flagged before resubmission
Reviewer #2 (Significance (Required)):
One limitation of the experimental design is that the depth of molecular analysis in vitro comes at the expense of any in vivo validation, which the authors acknowledge in the Discussion. They attempt to make similar points using analysis of patient survival data from public databases but these analyses generally yielded small magnitude differences. The main audience for this study is likely to be cell biologists interested in cell migration, cell-ECM adhesion, cancer invasion, and GTPases. I don't see any need for new experiments- what can be done has been done and then some. I do think that it would benefit readers if the text could be made less dense.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary: Using a murine HGSOC 3D cell model, in combination with analysis of human ovarian cancer datasets, the authors uncover a CYTH2-ARF6-AGAP1 signaling module regulated by PTEN and identify a biomarker for tumor invasion and targeted therapy.
Major comments:
__The findings of this study are significant as they reveal a critical signaling module that controls tumor invasion by mediating tumor cell interaction with the extracellular matrix. The experiments are properly designed, and the data are well presented. The conclusions are appropriate and supported by the data. The limitation of the study has also been discussed properly.
One suggestion regarding the survival analysis in Fig. 6 and 7. __
The authors noted that the CYTH2-ARF6-AGAP1 module is not specifically or only induced in Pten-null contexts, but rather that Pten-null cells become more dependent on the module for enacting the invasive phenotype. Based on this, it would be interesting to evaluate how the PTEN status impacts the survival difference by integrating the PTEN genomic status (WT versus mutation) or its expression level (protein or mRNA) into the survival analysis of patient cohorts in Fig. 6 and Fig. 7.
We thank the reviewer for this excellent point. We will include such analysis, where possible. One consideration will be that extensive division of patients based on these molecular characteristics may results in patient numbers too low to draw conclusions of significance.
**Referees cross-commenting**
Gene deletion and mutation may elicit different functional outcomes. I therefore agree with Reviewer #1 that "the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained".
We will make our reasons for this choice clear in the text before submission. Please refer to response to Reviewer 1, Major comment 1.
Reviewer #3 (Significance (Required)):
The model used and data presented in this study are of significance for both scientific discovery and clinical application, which will interest the broad audience in both basic and clinical research.
3. Description of the revisions that have already been incorporated in the transferred manuscript
4. Description of analyses that authors prefer not to carry out
-
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Referee #3
Evidence, reproducibility and clarity
Summary:
Using a murine HGSOC 3D cell model, in combination with analysis of human ovarian cancer datasets, the authors uncover a CYTH2-ARF6-AGAP1 signaling module regulated by PTEN and identify a biomarker for tumor invasion and targeted therapy.
Major comments:
The findings of this study are significant as they reveal a critical signaling module that controls tumor invasion by mediating tumor cell interaction with the extracellular matrix. The experiments are properly designed, and the data are well presented. The conclusions are appropriate and supported by the data. The limitation of the study has also been discussed properly.
One suggestion regarding the survival analysis in Fig. 6 and 7. The authors noted that the CYTH2-ARF6-AGAP1 module is not specifically or only induced in Pten-null contexts, but rather that Pten-null cells become more dependent on the module for enacting the invasive phenotype. Based on this, it would be interesting to evaluate how the PTEN status impacts the survival difference by integrating the PTEN genomic status (WT versus mutation) or its expression level (protein or mRNA) into the survival analysis of patient cohorts in Fig. 6 and Fig. 7.
Referees cross-commenting
Gene deletion and mutation may elicit different functional outcomes. I therefore agree with Reviewer #1 that "the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained".
Significance
The model used and data presented in this study are of significance for both scientific discovery and clinical application, which will interest the broad audience in both basic and clinical research.
-
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Referee #2
Evidence, reproducibility and clarity
The authors have conducted a study of the molecular requirements for cancer invasion that is stunning in its thoroughness and depth and breadth of its molecular analysis. The writing is exceptionally precise though also very dense (see below). The molecular model proposed is that PTEN loss (in a p53 null background) leads to reliance upon ARF6 for invasion, with regulation through interactions with AGAP1 and beta1-integrin and it is convincingly demonstrated. They focus on interpreting the consequences of genetic and pharmacologic manipulations in a cell line, using a series of 2D and 3D assays. The phenotypes are more prominent in 3D assays.
Concerns and Suggestions:
- There is a disconnect between the essentially complete loss of protrusions and invasion in 3D (e.g. 4A) and the reduction in magnitude of protrusive invasion but the continued presence of elongated cells with protrusions in 2D (e.g. S4C). This discrepancy is present in a couple of comparisons and is glossed over in quick callouts to many figure panels.
- Once a journal has been identified, it would be wise for the editor to allow some flexibility in word limit to enable some very dense sections to be expanded slightly to guide the reader through the experiments and results more clearly. For example, in the section "ARF6 regulates active integrin pools...", there are callouts like (Fig. 7C,E; S8A-C; G-I) and then (Fig. 7D,E; Fig. S8E-F, H-I). It takes a lot of time to unpack these different experimental claims based on a single sentence.
- The patient data on CYTH2 and its relationship to survival is modestly convincing.
- Very minor- search on %- there are a few inconsistencies in terms of spaces and commas vs. periods. The Methods also have some inconsistencies in terms of spaces between numbers and units or numbers and degrees Celsius. References are also in a different font. Overall it was extremely carefully written though (just dense).
Significance
One limitation of the experimental design is that the depth of molecular analysis in vitro comes at the expense of any in vivo validation, which the authors acknowledge in the Discussion. They attempt to make similar points using analysis of patient survival data from public databases but these analyses generally yielded small magnitude differences. The main audience for this study is likely to be cell biologists interested in cell migration, cell-ECM adhesion, cancer invasion, and GTPases. I don't see any need for new experiments- what can be done has been done and then some. I do think that it would benefit readers if the text could be made less dense.
-
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Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
This paper by Konstantinou et al aims at deciphering the mechanisms by which PTEN loss could be driving poorer prognosis in patients. The authors use their great high-throughput 3D screening method coupled to an unbiased proteomic method and a CRISPR screen to uncover a new pro-invasive axis driving collective invasion of high-grade serous ovarian carcinoma (HGSOC) cells. Overall, this is a very impressive study, very well done and controlled with rigorous statistical analyses that uses sophisticated methods to convincingly show that the CYTH2-ARF6-AGAP1-ITGA6/ITGB1 module is required for the pro-invasive effect of PTEN depletion and discriminates patients with poorest prognosis.
Major comments
Below are listed all the claims that, in my opinion, are not adequately supported by the data.
- Choice of the cell line: More justification on the use of the ID8 cell line and on the p53 deletion is needed. The authors need to clearly state that most p53 mutations in ovarian cancer are missense mutations that lead to a strong accumulation of a p53 protein devoid of transcriptional activity. Nevertheless, it seems that p53 mutations are not associated to differences in patient survival. Hence the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained. Moreover, the in vivo experiments already performed in the literature mentioned in the discussion should be mentioned in the introduction to provide more context and physiological relevance to this study (especially regarding the special focus on the p53 null/ dKO cells throughout the study).
- "Therefore, PTEN loss in ovarian cancer, particularly at the protein level, occurs in the tumour epithelium and is associated with upregulated AKT signalling and poor overall survival". This claim is an over-interpretation and over-generalisation of the data presented. I appreciate the honesty of the authors in showing all the ovarian datasets that are available and highlight the discrepancies in expression of the proteins they study in stroma and epithelium. I think the way to present these data in the text without over-interpreting and generalizing would be to show that there is a clear epithelial-specific downregulation of PTEN at the mRNA level. Most likely due to the contribution to other cell types in the stroma, only 3 out of 5 bulk tumour mRNA datasets show a tumour specific downregulation of PTEN and no association with survival based on a median split of PTEN mRNA expression. Nevertheless, although there is no direct correlation between PTEN mRNA and protein levels, patients with low PTEN protein levels have poorer survival that is associated to an upregulation of Akt signalling. This allows to have a clearer conclusion, based solely on the protein data presented and no over-generalisation using the mRNA data. This, to me, makes a stronger case for studying PTEN loss in ovarian cancer and is fully supported by the data presented.
- PTEN loss induces modest effects in 2D culture. The authors make claims regarding the fact that some of the phenotypes they look at happen after PTEN depletion alone or in combination with p53 loss and are more prominent in 3D vs 2D. Many of these are insufficiently backed up by data. A few key experiments are also only performed in 2D and should be done in 3D. Finally, some clarifications if the role of PTEN is most prominent on either collective, ECM-induced or 3D-dependent invasion.
First, the authors claim that PTEN loss alone (i.e. without p53 deletion) leads to changes in Akt signalling. Supp fig 1H clearly shows that there is no significant increase in Akt activation, although there seems to be one in the Western Blot (WB) presented in supp fig 1G. There is a clear, significant increase in the Akt activation in all the PTEN KO clones when in association with p53 loss though. This claim is hence not backed up by data and the conclusion seems to be that the effect on Akt signalling requires both deletion of p53 and PTEN.
It will be interesting to see a quantification of the pS473-Akt staining (supp fig S1J), as it seems from these images that pAkt is preferentially found on rounded cells. It should also be performed in 3D conditions to see if there is an enrichment at invasive tips and back-up the invasion data.
Arf6 is recruited to the invasive tips of cells invading a 2D wound (fig4D). How do the authors reconcile the fact that all the machinery required for 3D invasion is present but that PTEN loss has a modest effect on cells in 2D? If the wound assay was done on glass, it should be done again on ECM coated glass to see if it recapitulates the effects seen in 3D. This experiment will help deconvolute if the effect of PTEN loss is more linked to collective behaviour than 3D organization or presence of ECM.
The recycling assays are all done in 2D, condition under which the authors claim that the PTEN phenotype is weakest. Although I understand that it is not possible to do this assay in 3D, its contribution to elucidating the mechanism by which integrins participate in the PTEN loss invasive phenotype is not clear. The requirement of integrins relies on the data showing that ITGB1 KO results in no collagen4-positive basement membrane of the cysts and greatly impaired invasion. Experiments looking at the integrin localisation would be helpful: can an enrichment at the invasive tips can be seen? Are ITGA6 and/or ITGB1 repartitions homogeneous between the cysts membranes and the invasive tips? In my opinion the Src/FAK data is not enough to draw the conclusions of fig7I schematic. 4. Expression of AGAP1 isoforms do not alter ARF6 levels. Data in fig 6C, D show a significant downregulation of Arf6 and Akt signalling after expression of AGAP1S. Can the authors clarify what they mean? 5. Arf6 is not modulated in the different cell lines: data in fig4B (far right graph) and supp fig 4B, J seem to indicate otherwise. Can the authors clarify what they mean? 6. Immunofluorescence panels without quantifications: Quantifications for the different stainings shown in fig3A; 4D, E; 5H; 7B and supp fig S1L, J; S3 need to be included to fully back the conclusions of the authors. Indeed, these images are used to draw conclusions and not only as illustrations. 7. Quantifications of invasion show that WT cysts become hyper-protrusive at around the half experiment mark (around 30-40hrs). Nevertheless, all movies or galleries show spherical cysts, which does not seem representative. Can the authors change this or explain why these images/movies were chosen? 8. Since it seems that the main effect of PTEN is to drive the localisation and intensity of recycling of Arf6 cargoes, it will be helpful to confirm that all the proteins involved in the Arf6 module be shown to be accumulated/present at the pro-invasive tips. Immunofluorescence stainings showing the presence of AGAP1 (could be done with the AGAP1S isoform that is mNeon-tagged), pS473-Akt, ITGB1 (active integrin if possible, otherwise total integrin), ITGA5, PI3K should be included if possible. A quantification comparing signal in the cysts and in the invasive tips should also be included to see if there is an accumulation to PIP3-enriched areas. 9. Data in fig5I convincingly show that PTEN loss induces a fragmented collagen4-positive basement membrane. The authors use this data to claim that this is one of the ways that PTEN could be driving invasion but no correlation between these structures and the hyper-protrusive phenotype is made. This experiment needs to be done to support this claim.
Minor comments
- Data visualization: I think that the heatmap representation is overkill when only 2 or 3 conditions are presented. A graph showing the evolution of area or spherical/Hyper-protrusive phenotype proportions across time would be easier to read and more impactful: each genotype could be presented with a colour and the spherical/hyper-protrusive phenotypes as either plain or dashed lanes across time. I understand that this representation allows for the stats to be done at each time points but they are generally pretty clear (especially for the PTEN KO or dKO phenotypes) and do not need to be done for each time point in my opinion. These heatmaps could be put in supplementary figures if the authors feel strongly about putting stats for each time points.
Fig supp S1M, fig 5I should be presented as a stacked histogram to improve readability and merged with fig supp S1K.
Displaying fold change as antilog rather than log values would be easier for the reader to realise the magnitude of the differences.
A bar graph would be easier to read than the matrix representation for fig 6B.
The way Area data is presented throughout to me makes it very difficult to understand what is going on. Could the authors at least give some explanations in figure legends. A curve graph displaying the evolution of the area across time would be easier to read and see the differences between conditions. 2. It is confusing that, in fig supp S1M, there is a significant decrease of the rounded phenotype after PTEN loss that is not associated to a significant change in another of the categories. Could the authors explain how? 3. One of the big differences of the PTEN KO cells seems their ability to invade through the matrigel bed and migration on the glass below (supp movie S2). From what I gather, these cysts would be considered out of focus and excluded from the analysis. Would it be possible that this would minimize some of the results? Would it be possible to include a quantification of this particular phenotype to confirm it is specific to PTEN KO cells?
In the same spirit, could the authors provide the percentage of non-classified cysts, to make sure that the same proportion of cysts is quantified across all different genotypes. 4. Can the authors clarify how a 0 fold change (in log value) in fig 2D can be highly significant? 5. Delta isoform of PI3K seems to have an effect on area in the middle of the experiment, but has no effect at all on invasion. Could the authors comment? Are these smaller cysts still as invasive? There might be an interesting uncoupling between proliferation and invasion there. 6. ITGB1 depletion seems to induce a downregulation of Akt protein. Is that right? Does it change Akt localisation? Is there a dose effect whereby there is not enough Akt protein to mediate invasion? 7. Stats should be added directly on the graphs for the recycling assays, doing a pairwise comparison of the different genotypes for each time points. Can the authors clarify what the t-32min quantification graphs adds (fig7E, supp fig S8G-I)? I would advise to remove them, as this data is already presented in the recycling assay graphs. 8. There is a substantial amount of typos and erroneous references to figures. I listed below the ones that I spotted and I encourage the authors to carefully check.
- a. there are some mistakes in referencing the number of cysts in supp table 1. There is for example no cysts experiments in Figure 1 but yet there are some references to figure 1 in supp table 1. Please correct it. I think it will be easier for the reader if the number of cysts quantified for each conditions was also indicated in the figure legends. Supp table 1 can still be included for readers that want additional details.
- b. comma missing page 3
- c. page 3 and 4: PI(3,4)2 means PI(3,4)P2? Can be shorten to PIP2 for ease of read and specify if it is another PIP2 specie otherwise
- d. define CYTH abbreviation: I suppose this is for cytohesin?
- e. fig1F-I: don't understand why TCGA.OV is specified on some but not all the graphs. It seems to me that all the data are from TCGA.OV? Makes it seems it is nit the case
- f. legend of fig1H, I: y axis is -Log10 values in 1I, not Log10 values
- g. page 6: dKO abbreviation is already specified above and should be used to avoid repetition and for ease of read
- h. supp fig S1D: missing legend for the second bar (after Wild Type)
- i. supp fig S1N: legend of the X-axis should be below the axis
- j. supp fig S1O: the numerotation of the X-axis needs to be below the line of the axis for ease of read, not above it
- k. legend of S2A: clones 1.12 and 1.15 are p53-/-;PTEN-/- and not PTEN-/-
- l. supp figS2C can the authors specify the different stages of matrigel (liquid or gel) that are used for the invasion assay, to make it easier for the non-specialist to understand what is going on. Please confirm that the 50% GFR matrigel makes a gel on top of the cells and fill in the wound to produce the 3D invasion assay setup.
- m. page 7: no parental cells are used in S3A, B only p53 null and p53 null and dKO. Please also specify what cells are being compared in the text
- n. description of arrow heads and colours need to be moved to figure legends and not in main text (page 7)
- o. fig 2D: the signification of the dot in the circles needs to be in the legends (since it is its first apparition in the manuscript). It only appears later on, in supp2A legend. Additional description of the matrices is necessary, as they contain a lot of information to digest to understand fully what is going on
- p. legend of fig3: error in figure reference: area data is D and not E, protrusive phenotypes are E and not F
- q. arrow missing in fig3B
- r. fig 3D,E, G, H: please indicate the cell line studied
- s. fig 3I: the different genotypes need to be stated on the galleries for clarity
- t. page 8: define Arf6-mNG in the text
- u. page 9: "<" symbol should be an alpha symbol
- v. fig 4A: indicate the cell line used on the figure
- w. supp fig S4E: why is it specified mouse-specific for the shArf6?
- x. 4H, I, J: indicate on the figure if these interactors are mostly unchanged, strong interactors or weak interactors for clarity
- y. legend of fig4H: "coloured spots underneath denote the protein complex that each interactor belongs (in J)" should indicate panel G and not J
- z. fig4I, J: are you sure of the legend for the fold change coloring? Log2 of 1 is a 0 fold change, i don't see how these could show any significant difference (i.e. some of the pale red circles are significant)
- aa. page 11: description of the assay (starting with "Machine learning classification of...") is very confusing, please clarify
- bb. page16: figure 4H should be 4I (PTEN-null specific association of Arf6 with ITGA5)
- cc. supp fig S5H-P: choose Tumour or cancer to homogeneise naming across the graphs
- dd. fig 5H: box are difficultly visible in green, change color to yellow or something more visible
- ee. page 13: Fig6E, F should also refer to 6G
- ff. LCM abbreviation on page 10 and 12 refers to LCMD? Otherwise please define it.
Optional suggestions
- Choice of cell line: There is a high number of patients (around 9% according to (Cole et al. 2016)) that present the R248Q gain-of-function mutation. A recent study has shown that this mutant p53 protein is associated to an activation of Akt signalling and an increase of the intercellular trafficking of EGFR (Lai et al. 2021). Given that EGFR was also a hit in this screen, that is seems to have a central role in Arf6 cargoes (fig 4G), I think it would be a great addition to this study. It could hence cooperate with PTEN loss to drive strong, robust invasion.
- Are MAPK involved in the PTEN KO pro-invasive phenotype? In particular Erk1/2, since EGFR is one of the PTEN loss induced Arf6 cargoes.
Reference
Cole, Alexander J., Trisha Dwight, Anthony J. Gill, Kristie-Ann Dickson, Ying Zhu, Adele Clarkson, Gregory B. Gard, et al. 2016. « Assessing Mutant P53 in Primary High-Grade Serous Ovarian Cancer Using Immunohistochemistry and Massively Parallel Sequencing ». Scientific Reports 6 (1): 26191. https://doi.org/10.1038/srep26191.
Lai, Zih-Yin, Kai-Yun Tsai, Shing-Jyh Chang, et Yung-Jen Chuang. 2021. « Gain-of-Function Mutant TP53 R248Q Overexpressed in Epithelial Ovarian Carcinoma Alters AKT-Dependent Regulation of Intercellular Trafficking in Responses to EGFR/MDM2 Inhibitor ». International Journal of Molecular Sciences 22 (16): 8784. https://doi.org/10.3390/ijms22168784.
Significance
It has only been recently appreciated that PTEN loss is a driver in ovarian cancer (Martins et al. 2020) but no studies to data have aimed at understanding the mechanisms. This study is hence the first to propose one and as such provides a very valuable advance for researchers interested in ovarian cancer. The authors also propose that the CYTH2-ARF6-AGAP1 high mRNA be used as a signature of worsen prognosis. This hence paves the way to better understanding and stratify patients with ovarian cancers.
One of the main difference after PTEN loss is the accumulation of PIP3 in pro-invasive tips that correlates with the recruitment of Arf6 to these tips. The authors have developed a very powerful automated quantification pipeline to follow the behaviour of cysts grown in 3D that they have coupled to an unbiased proteomic method to identify interactors and a CRISPR screen to test their functional relevance. This is clearly the strongest aspect of the paper that allows them to gather very robust data and identify the machinery driving invasion in PTEN KO cells. The authors' model claims that this in turns recruit the Arf6 machinery, composed of CYTH2 2G (the only CYTH2 isoform correlated to a poorer prognosis, preferentially binding PIP3) and AGAP1 that leads to a local increase in active integrin recycling that mediates the more invasive phenotype of PTEN depleted cells. It is rightfully mentioned in the discussion that PTEN depletion only leads to a modest change in Arf6 interactors, and that most likely PTEN loss acts by locally directing the Arf6 machinery to the invasive tips. Indeed, the authors convincingly show that Arf6, AGAP1 and ITGB1 are required for the formation of these invasive protrusions.
The limitation of this study is the combination of 2D and 3D experiments to drive general conclusions on the mechanism. These are listed in the previous section. Another big limitation, in my opinion, is the choice of the cell model: indeed, nearly all patients present a vast increase in the amount of the p53 protein present due to a very large number of mutations that in most cases prevent its binding to DNA. Throughout this paper the authors have used a p53 null cell line that expresses no p53 protein. This is not compatible with the clinical situation. Moreover, since p53 also present frequent gain-of-function mutations that have been shown to be associated to an increase of Akt signalling and intercellular trafficking of EGFR. Studying the implication of the Arf6 module identified here in a context of p53 WT or mutant protein overexpression would be of great interest.
Reference
Martins, Filipe Correia, Dominique-Laurent Couturier, Anna Paterson, Anthony N. Karnezis, Christine Chow, Tayyebeh M. Nazeran, Adekunle Odunsi, et al. 2020. « Clinical and Pathological Associations of PTEN Expression in Ovarian Cancer: A Multicentre Study from the Ovarian Tumour Tissue Analysis Consortium ». British Journal of Cancer 123 (5): 793‑802. https://doi.org/10.1038/s41416-020-0900-0.
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Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.
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Reply to the reviewers
1. General Statements [optional]
We are grateful to the reviewers for highlighting the value and power of our 3D chimeric dataset to explore cancer/stellate interactions in pancreatic cancer invasion. We also appreciate their support of our findings identifying divergent roles for the two related enzymes ADAMTS2 and ADAMTS14. We thank the reviewers for their detailed comments, which have allowed us to prepare a significantly stronger and clearer manuscript.
Following the reviewers comments we have made three major changes to the manuscript, which we will outline here in addition to the point-by-point rebuttal.
- i) Revised manuscript structure. We have modified the structure of the manuscript, which we hope improves the clarity and accessibility of the work.
Figure 1 remains the description of our 3D invasion model and our approach to identify stellate cell and cancer cell transcriptomic information from this context.
Figure 2 describes our focus on proteases and now includes concordance of our data with clinical data sets. This is also now where we describe the strikingly opposing roles for ADAMTS2 and ADAMTS14 in regulating invasion.
Figure 3 is now the figure demonstrating that ADAMTS2 and ADAMTS14 have an equal contribution to collagen processing from stellate cells. This is an important experiment given that the main physiological roles for these enzymes are in the processing of collagen, and the importance of collagen for cancer progression. It was therefore reasonable to hypothesise that the effect of these enzymes on invasion could be due to differences in their collagen processing in this context. The finding that both have an equal effect on collagen processing points towards a wider, and more diverse, role for these enzymes in regulating biology.
Figure 4 describes the divergent roles of these two enzymes on myofibroblast differentiation, and by extension TGFβ bioavailability. In this figure we now include experiments with TGFβ reporter constructs, which demonstrate an increase in active TGFβ following loss of ADAMTS14 and a reduction in TGFβ activity following loss of ADAMTS2.
Figure 5 is our matrisomic experiment to identify enriched enzyme-specific substrates following knockdown of either ADAMTS2 or ADAMTS14.
Figure 6 details our investigation into the substrate responsible for the reduction in invasion following loss of ADAMTS2. As the previous matrisomic experiment identified only two enriched ADAMTS2 substrates, we investigated both in our 3D assays, identifying SERPINE2 as the responsible substrate. Further analysis identified a reduction in plasmin activity in ADAMTS2 deficient cells. This was rescued with co-knockdown of SERPINE2, implicating this pathway as being crucial for mediating the effect of ADAMTS2. Additionally, we now include experiments demonstrating that concomitant knockdown of SERPINE2 alongside ADAMTS2 rescues the reduction in TGFβ activity observed with ADAMTS2 loss alone.
Figure 7 describes our analysis of ADAMTS14 substrates. As the matrisomics identified a large change in proteins following ADAMTS14 knockdown, we performed an siRNA screen of candidates to identify those responsible for ADAMTS14 phenotype. This, followed by further validation in our 3D invasive assay, revealed Fibulin2 as the responsible substrate. Fibulin2 has a well-established role in regulating TGFβ release from the matrix. In accordance with this we present new data using TGFβ reporter constructs, which demonstrate that the increase in active TGFβ following ADAMTS14 knockdown can be reversed with co-knockdown of Fibulin2.
- ii) Improvement of the clinical significance of our chimeric data set and ADAMTS proteins. Ideally, we would like to present IHC images of ADAMTS2 and ADAMTS14 expression in PDAC tissue samples to corroborate our in vitro findings. However as these enzymes are secreted, this precludes antibody based imaging, as it would not provide cell type specific information. RNA scope presents an alternative, however we have experienced technical issues with this technique due to RNA degradation in PDAC tissue and unavailability of ADAMTS2/14 specific probes. In place of this we have used a range of publically available resources.
We have compared our chimeric data set with human clinical data using the resource published by Maurer and colleagues (PMID: 30658994). This paper presents transcriptomic data from PDAC tumour and stromal compartments using laser microdissection of clinical tissue. In accordance with our data set, the majority of metzincins, including ADAMTS2 and ADAMTS14, are expressed in the stromal compartment. These data are presented in updated figure 2.
We have also examined ADAMTS2 and ADAMTS14 expression in PDAC and CAF subtypes using publically available data sets. Using the TCGA dataset, we identified that ADAMTS2 and ADAMTS14 are highly expressed in PDAC tumours compared to normal counterparts. As the majority of PDAC is comprised of stroma, the bulk transcriptomic data from TCGA, combined with the results from the Maurer publication, lead us to conclude that this expression reflects the stromal origin of these proteases. In addition, using publically available single cell RNA sequencing data published by Luo and colleagues (PMID: 36333338), we identified ADAMTS2 and ADAMTS14 expression in the prominent PDAC CAF subtypes, inflammatory and myofibroblastic CAFs. Together these data demonstrate that these enzymes are enriched in clinical disease, which when combined with our mechanistic 3D studies implies a greater role for these enzymes in disease progression than previously appreciated.
iii) Improved mechanistic link between ADAMTS2 and ADAMTS14 with TGFβ bioavailability
To strengthen the association between ADAMTS2 and ADAMTS14 function, their substrates SERPINE2 and Fibulin2, and TGFβ bioavailability, we have performed the following experiments using TGFβ reporter constructs:
We have taken conditioned media from stellate cells lacking either ADAMTS2 or ADAMTS14, along with co-knockdown of their substrate, and stimulated a recipient cell line expressing a SMAD Luciferase reporter. These cells express luciferase in response to TGFβ stimulation. In accordance with a role for ADAMTS14 and Fibulin2 in regulating TGFβ, we demonstrate that following ADAMTS14 knockdown there is a strong increase in active TGFβ in the media (Figure 4I), which is abrogated with co-knockdown of Fibulin2 (Figure 7F).
We have also obtained a fluorescent reporter, CAGA-eGFP, which expresses GFP in response to TGFβ stimulation in order to examine TGFβ activity in 3D cultures. Stellate cells expressing this construct were embedded in collagen: Matrigel hydrogels following knockdown of either ADAMTS2 or ADAMTS14 and CAGA fluorescence recorded after 72 hours of culture. In accordance with our data, stellate cells deficient in ADAMTS14 showed increased fluorescence in 3D, indicative of increased TGFβ activity, which was abrogated with co-knockdown of Fibulin2 (Figure 4J, K and 7G, H). Equally, loss of ADAMTS2 reduced TGFβ activity in 3D culture, which was rescued with co-knockdown of SERPINE2 (Figure 4J, K and 6 D, E).
These experiments confirm a link between the ADAMTS enzyme, its relevant substrate, and TGFβ bioavailability. Together with extensive published work linking SERPINE2 and Fibulin2 with TGFβ release we are confident in our proposed mechanism for the dichotomic relationship of ADAMTS2 and ADAMTS14 in regulating TGFβ and thus myofibroblast action.
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. *
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Reviewer #1 (Evidence, reproducibility and clarity (Required)):
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This study aims to explain the opposing contributions of stromal stellate cells/CAFs to PDAC. By first identifying stroma-specific proteases, followed by a process of candidate selection and elimination, the authors find that two specific metalloproteases that share enzymatic activity against collagen in fact have differential activity on TGFb availability. This could be interpreted as a way of shaping the CAF population and tumor-promotin or -restricting properties of the stroma.
There are several flaws that the authors could address to improve the manuscript:
- In the flow of experiments and analyses, there is a strange mix of fully unbiased discovery phases followed by functional experiments that do not consider all possible candidates to test, and vice versa. For instance, from the mixed-species transcript analysis, ADAMTS2 and -14 are chosen based on their shared collagenase activity based on literature. However, the authors then perform again a proteomics analysis to identify things from the entire matrisome that are cleaved by these enzymes? Then, for ADAMTS2 a co-silencing approach is done on one selected candidate (Serpine2), but for ADAMTS14 an siRNA screen is performed? The problem of this approach is that the rationale for some studied enzymes is very strong, where as for others it is not.
We thank the reviewer for their comment and trust the revised manuscript provides more clarity for the rationale of our approach. We performed the chimera sequencing as a discovery experiment to reveal the communication between cancer and stellate cells in a 3D, invasive context. We present the chimera experiment and data here as a resource for the community, with our analysis of ADAMTS2 and ADAMTS14 function serving as a first example of the biological insight this data set can reveal. Other insights revealed from this dataset are active avenues of research in our group.
Our finding that ADAMTS2 and ADAMTS14 have dramatically opposing roles in regulating invasion was especially striking given their equal contribution to collagen processing in this context. This led us to conclude that the divergent nature of these enzymes must be due to enzyme-specific substrates. A substrate repertoire for these enzymes has been previously published (PMID: 26740262) and we reasoned that the responsible substrate would be enriched following knockdown of the relevant enzyme. Thus we preformed matrisomics on cells lacking either of these enzymes, which did indeed reveal enrichment of known, enzyme-specific substrates that we could use for further analysis.
The matrisome following ADAMTS2 knockdown was minimally changed and only presented enrichment of two ADAMTS2 substrates. As there was only a minimal cellular phenotype in 2D following loss of ADAMTS2, we decided to concentrate our studies on the two identified substrates in our 3D assay. Conversely as the matrisome following ADAMTS14 knockdown was dramatically different from control cells, and ADAMTS14 knockdown presented a clear phenotype in αSMA expression, we decided to perform a screen of all matrisome hits. This highlighted the role of IL-1β in mediating myofibroblast differentiation, which has been reported elsewhere and validated our approach. Further, this refined the number of enriched ADAMTS14 substrates to two, MMP1 and Fibulin2, with Fibulin2 being identified as the responsible candidate in our 3D assays.
The ECM is more than just collagen. Choosing these two metalloproteases based on their shared collagen substrate is an approach that perhaps oversimplifies the ECM a bit, and again, does not provide the strongest rationale that these metalloproteases are most likely to explain counteracting stromal activities on tumor growth and progression.
We fully agree with the reviewers comment and feel our work acutely demonstrates this point. Loss of either ADAMTS2 or ADAMTS14 had similar effects on collagen processing; implicating their divergent roles on invasion was independent of their effects on collagen regulation. This work therefore showcases the incredible complexity of ECM regulation in tumour progression. As discussed in the manuscript, collagen along with other elements of the ECM can regulate tumour progression and we believe our work adds an additional facet to this.
Related to the above: How were the stellate cells used for the matrisome analysis grown? In the suspension setup or adherent? This will have a large impact on the outcome. Is there for instance hyaluronic acid in this matrix?
The matrisome analysis was conducted on cells cultured in 2D. Vitamin C was added to the media to promote matrix production. We agree that this is not truly reflective of the in vivo situation but as a discovery tool this led us to identify the ADAMTS2 and ADAMTS14 substrates responsible for the function observed in 3D.
- Performing the species-specific transcript analysis both ways is a neat approach, but why did the authors ignore the opportunity to formally overlay/compare the two stromal gene sets to define likely candidates based on statistics?
We primarily used this approach as a discovery tool to identify key differences between cancer and stellate cell compartments. Comparing the two species data sets is problematic as the murine cancer cells express many elements found in the stellate cells, while the human data set presents a cleaner comparison. This is evident from comparing metzincin expression in the two data sets. The human data set (Figure 2A) shows clear separation between cancer and stellate compartments, which is less evident in the murine data set (Supp figure 2A). As noted in supplementary figure 1A, unlike the human cancer cells used in this study, the murine cancer cells are capable of invading without stellate support (although when cultured with stellate cells invasive projections are always stellate led). Nevertheless the murine data set matches the human, although with less clarity.
Minor comments: The bioinformatics Methods need more details on how reads were mapped to the different genomes. How many mismatches were allowed and was the mapping done separately or using for instance Xenofilter?
We have improved the methodology section to include more detail for this separation. Using STAR aligner, reads were mapped to host species using a combined human and mouse genome. Ambiguous reads were subsequently discarded from the analysis. While there are bioinformatic packages that seek to match ambiguous reads to parent species we did not use these for our analysis.
The authors use the knowledge on the activities of both ADAMTS2 and -14 on collagen as a rationale to choose these two. Is there really a need for the paragraph (and associated figures) from line 102 on?
Given the prominent role collagen has been shown to have in regulating PDAC progression and the primary role for ADAMTS2 and ADAMTS14 being collagen processing, we initially hypothesised that the divergent role for these enzymes on invasion could be due to differences in collagen processing in this context. The fact that both equally contribute to collagen processing is surprising and adds to the novelty of our findings that these enzymes have a more complex role in regulating stromal biology.
We have altered the structure of the manuscript to emphasise this point. The divergent roles of ADAMTS2 and ADAMTS14 on invasion are now presented in Figure 2, with their equal role in collagen processing now presented after in Figure 3. Figure 4 onwards now details the opposing roles of these enzymes in myofibroblast differentiation and our investigation into the enzyme-specific substrates responsible for this.
Abstract, line 21; some words are missing?
We thank the reviewer for bringing this to our attention and have now amended the abstract.
Were the siRNA screen hits validated?
Yes, hits relevant for our further investigations, MMP1 and Fibulin2, are presented in the manuscript.
What is the genotype of the mouse cancer cells? KPC-derived?
DT6066 are KPC derived while R254 are derived from KPF mice. This has been added to the methods with relevant reference.
Reviewer #1 (Significance (Required)):
The trick of dissecting tumor from stromal signals in spheroid cocultures by RNA-Seq is a cool trick, but not new and the authors should probably cite some prior work.
We have included reference to other work where researchers have used species deconvolution to explore heterocellular interactions (Lines 68-72). However, we believe our work is one of the first to use this approach to explore cellular interactions in an in vitro, 3D, invasive context.
What this all means for patients (or in vivo tumors even) remains unclear. There is some debate on whether highly activated CAFs (ACTA2/aSMA+ cells, some call them myCAFs) are indeed tumor-restrictive or whether they promote invasion. The authors appear to argue the latter (which I can agree with) but without any translational work to show what the net outcome of this mechanism is, the study remains descriptive and perhaps of limited interest.
We contend that our 3D invasion model is a powerful tool to understand the role of stellate cells in leading invasion. We have shown the utility of this model in several studies to dissect the biology of this cell type, revealing the importance of the nuclear translocation of FGFR1 in stellate invasion (PMID: 36357571), the role of the kinase PKN2 in regulating stellate heterogeneity (PMID: 35081338) and the influence of cancer cell-derived exosomes on stellate invasion (PMID: 33592190).
CAFs within PDAC stroma are highly plastic and can adopt multiple functions depending on distinct environmental cues. Thus, identifying how they are regulated is of paramount importance if they are to be therapeutically targeted. We contend that our mechanistic studies using heterocellular 3D models can aid in the dissection of the biology of these cells with more granularity than offered by clinical or in vivo studies, particularly in the context of secreted proteases. To add clinical relevance for our findings we have compared our chimera data set with previously published laser microdissected tumour and stroma PDAC tissue (Figure 2B), and identified ADAMTS2 and ADAMTS14 expression in prominent CAF subtypes (inflammatory and myofibroblastic) from published single cell RNA seq data taken from tumours (Supp figure 2C). As these enzymes are produced in multiple CAF subtypes, genetically targeting them in vivo appears prohibitive. The generation of ADAMTS2 and ADAMTS14 specific inhibitors would be required to assess their roles in vivo.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The manuscript by Carter and colleagues examines that role of cancer-associated fibroblasts (CAFs) in regulation of invasion in a 3D co-culture assay with epithelial cells. The authors propose that invasive chains of cancer cells are led by fibroblasts. The authors utilise a system of co-culture to create chimeric human-mouse fibroblast-cancer cell spheroids (both directions utilised, to eliminate species bias) to allow for in situ sequencing of the co-operating transcriptional programmes of each cell type during 3D invasion. From this powerful approach, this allowed the authors to identify two key two collagen-processing enzymes, ADAMTS2 and ADAMTS14, as contributing to CAF function in their system. The authors identify that these two enzymes have opposing roles in invasion, and map some of their key substrates in invasion, which extend beyond collagen-processing. The authors propose that one key function is to control the processing of TGFbeta, the latter of which is a regulator of the myofibroblast subpopulation of CAF. Overall, the findings of the manuscript are interesting, but need some further proof-of-principal demonstrations to extend their findings to support the claims within.
- The authors demonstrate a clear role of ADAMTS2 and ADAMTS14 in stellate function during differentiation and invasion. Is there any evidence of such changes in patient materials? Could the authors query publicly available databases of micro-dissected stroma vs epithelium to validate the translational relevance of their findings?
We thank the reviewer for their suggestion; we have now explored clinical relevance of ADAMTS2 and ADAMTS14 expression in two ways. We have used previously published work by Maurer and colleagues (PMID: 30658994), which descibes transcriptomic analysis of laser microdissected tumour and stroma from pancreatic cancer tissue. In accordance with our chimeric data set the majority of metzincins, including ADAMTS2 and ADAMTS14, are expressed in the sromal compartment (Figure 2B). We have also used publically available scRNA seq data to examine ADAMTS2 and ADAMTS14 expression in distinct CAF subtypes (Supp Figure 2C). Both ADAMTS2 and ADAMTS14 are expressed in inflammatory and myofibroblastic CAFs, with ADAMTS14 expression lower than that of ADAMTS2. Given the complexity of CAF heterogeneity it is possible that ADAMTS2/14 secretion by one population regulates the resulting phenotype of surrounding CAFs, however this hypothesis if beyond the scope of our current work.
Major comments: - Page no. 4, Line 71, The authors conclude that the invasion in the chimeric spheroids is "led by" stellate cells. This is a key concept in the manuscript. How do the authors define the "led by" phenomena? What is the frequency that this occurs?
In our experience all invasive projections are stellate led, defined as a stellate-labelled nucleus present at the tip of invasive projections. Indeed the human cancer cells used in this study are incapable of invading in the absence of stellate cells (Supp figure 1 A). We have previously reported this model where we demonstrated FGFR1 activity in the stellate cells is crucial for invasion (PMID: 36357571). Others have demonstrated the general importance for fibroblasts in leading invasion (PMID: 18037882, 28218910). Interestingly in our study, mouse cancer cells were capable of invading in the absence of stellate cells. However, when cultured with stellate cells, projections were predominantly stellate led.
- For Figure 2A and S2A, the text suggests that the heatmap represents the stellate vs cancer cell expression (as shown in Figure 1B and S1B) in the respective species but the labelling below the heatmap suggests they are all cancer cells (Mia, Pan, R2 and DT). Is this a typo? Could the authors clarify this?
We use Mia, Pan, R2 and DT to define the sphere combination from which the data originated. We have improved the clarity of the heatmaps by colour coding the different cell types within each sphere, and matching it with the cell type data presented in the heat map. We hope this improved labelling makes the heatmaps more accessible.
- The text and the figures are lacking information about the cell line names used in the experiment, e.g, Figure 2C, 2D, 2SB, 2SC and 2SD does not indicate what cell line was used in the study. This is the same with other figures as well. Please indicate in all instances exactly which samples are queried.
We have now included reference to the cell type and stellate cell species used in each experiment in relevant figure legends. Key 3D invasive experiments were conducted with both human and mouse stellate cells.
- It's mentioned in the text that the authors have used the cancer and stellate cells in a 1:2 ratio but the numbers of stellate cells look different between different spheroids confocal images. e.g. The numbers look very different between the Miapaca2:PS1 vs Miapaca2:mPSC spheroids. Is this simply the representative images, or are their bona fide differences. This, in turn, would impact on claims of cells being 'led' by stellate cells. Can the authors clarify?
This is a consequence of the method by which the stellate cells were immortalised. Human PS1 stellate cells were immortalised with hTERT, while mouse stellate cells were immortalised with SV40. A consequence of this is that the mouse stellate cells proliferate faster in 3D than the human stellate cells, with both proliferating slower than the cancer cell compartment. So while spheroids start at 1000 cells (666 stellate, 333 cancer) with stellate cells as the prominent component they are quickly overtaken by the cancer cells. Despite this difference in proliferation we find no difference in the invasive capacity of the stellate cells, with invasive projections always stellate led irrespective of whether they are human or mouse.
- While for most of the experiments the authors generated the chimeric spheroids first and then performed the respective experiments, it appears that for the invasion assay simply co-culture of Cancer cells and stellate cells was done. Is this correct? Have the authors tried performing the assay with the chimeric spheroids to see if the stellate cells still invade?
The Boyden chamber migration assay was conducted by seeding a co-culture of stellate and cancer cells in the apical compartment then imaging their migration to the basolateral side. This provided a second method to predominantly showcase the enhanced migration of cells lacking ADAMTS14 in a manner that could be quantified over time. We have not tried placing spheroids in the apical compartment and imaging invasion through the pores.
- The authors claim that ADAMTS2 and ADAMTS14 regulate the bioavailability of TGFB, and this is a key reason that these regulate CAF differentiation. However, there is no direct demonstration of this concept, which is conspicuous by absence. Could the authors either directly demonstrate this, or remove such notions from the results, and explicitly state that this is an untested speculation in discussion? Examples of this are:
o Line 173, authors state "ADAMTS2 facilitates TGFβ release through degradation of the plasmin inhibitor, SERPINE2 (Figure 5D)"
o Line 196 authors conclude "Together these data implicate 197 ADAMTS14 as a key regulator of TGFβ bioavailability (Figure 6F)."
o Line 240 states "This reduces the activation of Plasmin, preventing the release of TGFβ (Figure 5C)." Since this is just a model without detailed experiments, It will be better to propose rather than conclude.
We appreciate the reviewer’s concern and have now added additional experiments to strengthen the association of ADAMTS enzymes and TGFβ bioavailability.
Using a TGFβ-responsive luciferase reporter we demonstrate that the media from stellate cells lacking ADAMTS14 has greatly increased amounts of active TGFβ (Figure 4), which is abrogated when Fibulin2 is knocked down alongside (Figure 7). This links ADAMTS14 and Fibulin2 to TGFβ activity. Given the extensive literature detailing a role for Fibulin2 in regulating matrix TGFβ release through interactions with fibrillin (e.g, PMID: 19349279, 12598898, 12429738) we believe this is how ADAMTS14 is regulating myofibroblast differentiation. As we do not directly examine the association of Fibulin2 with fibrillin in this manuscript we have amended the associated statements to reflect this.
We have also used a TGFβ-responsive fluorescent reporter to examine TGFβ activity of stellate cells in 3D. Consistent with our results, loss of ADAMTS2 reduces, while loss of ADAMTS14 enhances, TGFβ activity (Figure 4), which can be reversed with concomitant knockdown of their respective substrates SERPINE2 (Figure 6) and Fibulin2 (Figure 7).
- Figure S5C shows a less invasive phenotype in the NTCsi + ADAMTS14si spheroids compared to the NTCsi + NTCsi control. However, there appears no appreciable difference between NTCsi + ADAMTS14si and NTCsi + NTCsi spheroids' brightfield images in Figure 5SD.
Could the authors comment on this?
We thank the reviewer for bringing this to our attention and apologise for our mistake. The images were positioned erroneously. This has now been corrected and the images reflect the quantification that demonstrates a clear increase in invasion following loss of ADAMTS14, which is abrogated with co-knockdown of Fibulin2.
Minor Comments: - Page no. 2, Line 20 has an incomplete sentence "Crosstalk between cancer and stellate cells is pivotal in pancreatic cancer, resulting in differentiation 21 of stellate cells into myofibroblasts that drive."
Apologies for the error. This has been rectified.
- Figure 2C; Figure S2C and Figure S5E lack quantification for the western blots.
We have now included densitometry for all western blots, presenting values relative to the respective loading control and normalised to the experimental control. Values are averages taken from all biological repeats with significance indicated where relevant.
- Why did the authors choose to investigate the Metzincin family? Could the authors provide their reasoning to investigate these proteins, to the exclusion of other candidates?
We focused on the metzincin family, as they are best known for their involvement in cancer invasion. A goal for this manuscript is to present our chimera data set as a discovery tool for the community. While this initial manuscript focuses on protease activity, we have further projects on-going that have used this data set to identify important elements of cancer/stellate communication.
- Info about the number of fields imaged per sample for the microscopy data is missing in the figure legends (e.g. Figure 2F and 2I, Figure 5SF).
We have now included a statement in each relevant figure legend to indicate that quantification was performed on at least five fields of view per biological repeat.
- Any particular reason why the ADAMTS2 expression was not checked through Western blotting like ADAMTS14 in Figure S2B.
We attempted to examine ADAMTS2 by western blotting but were unable to find an antibody that produced consistent results with our samples, and corroborated consistent knockdown by PCR.
- The legends for Figure 3SC and 5SF mention that "Images are representative of at least two biological replicates". How many technical replicates were used? It would be useful if the relative intensity of the images is measured and plotted in a graph.
We have now moved these images to the main figure alongside quantification of αSMA intensity. Images are collected from two biological repeats with quantification obtained from at least five fields of view per image. Together these data strongly demonstrate that loss of ADAMTS14 increases αSMA fibre intensity, which is blocked by either an inhibitor of TGFβ signalling (Figure 4), or co-knockdown of Fibulin2 (Figure 7).
Reviewer #2 (Significance (Required)):
This work provides an examination of the cross talk between fibroblasts and cancer cells in a 3-Dimensional culture model of pancreatic tumour cell invasion. By using chimeric human-mouse spheroids, the authors are able to identify cell-type specific transcripts by bulk RNA sequencing in situ. This advance is not to be underestimated as a number of existing approaches for cell type-specific profiling (eg. single-cell sequencing) relies upon dissociation of cell communities prior to sequencing. It is very likely that transcriptional programmes change during this isolation process. This approach allows the authors to identify transcriptional co-operating programmes in situ. This data provides a resource to understand this key co-operation of these two cell types during tumourigenesis, and will be of interest to the pancreatic cancer field. In addition, the mapping of the key substrate of these enzymes provides further insights that may be useful in understanding the expanded target repertoire of these enzymes beyond collagen processing.
We thank the reviewer for their strong support of our chimeric spheroid approach and resulting investigation into the dichotomic roles of ADAMTS2 and ADAMTS14.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
AMADTS2 and ADAMTS14 belong to the disintegrin and metalloproteinase with thrombospondin motif protein family, mainly produced by pancreatic stellate cells (PSC) and are related to cancer cell invasion. This study reveals that ADAMTS2 and ADAMTS14 have opposite roles in myofibroblast differentiation based on experiments testing HSC driven cancer cell invasion, variant expression of HSC activation makers and the related downstream targets analysed upon RNA sequencing analyses. The authors (TA) established PSC/cancer cell chimeric spheroids for investigating the crosstalk between these cell types in 3D in vitro. Based on their findings, they claim that ADAMTS2 and ADAMTS14 have different functions regarding PSC and TGF-β activation. However, their conclusions mainly rely on quantitatve data of invasion and mechanistic details are completely lacking.
Comments: Typos, even in the abstract, e.g. first sentence incomplete
We apologise for the error in the abstract and have rectified this in the revised manuscript.
Introduction is rather sparce with one third of the text repeating the results of the study
Our manuscript details a discovery experiment using chimeric spheroids to identify cancer cell and stellate cell transcriptomes in a 3D invasive context. We then showcase the power of this data set by using it to identify and then describe divergent roles for ADAMTS2 and ADAMTS14 in shaping stellate cell biology. Given this two-tiered approach we incorporated text that would normally be placed in the introduction into the results section (e.g. our description of the importance of collagen processing in PDAC, presented as a prelude to the results from figure 3). We feel this improves the flow of the manuscript, rather than having information that isn’t necessarily relevant to the reader at the outset.
Some citations do not at all fit with the position where they are placed; needs approval
We have examined this in detail and are confident in our use of appropriate references throughout.
In this study, it is said that TS2 (AMADTS2) and TS14 (ADAMTS14) have opposite functions on myofibroblast differentiation, with individual depletion leading to distinct matrisomal phenotypes in PSC. However, both similarly contribute to collagen processing. As we know, collagen is increased in response to TGFβ signaling, since TS2 depletion (knock down, kd) inhibits and TS14 kd is suggested to promote TGFβ activation, it is expected that this has impact on the available collagen levels. How do the authors explain that nevertheless the kd effect on collagen is very similar?
The primary effects of these enzymes are on the processing of pro-collagen to its mature form, rather than on the production of collagen. This is evidenced in figure 3B where collagen expression in the whole cell lysate is the same following ADAMTS2 knockdown, and slightly reduced with loss of ADAMTS14, but the mature form is lost in the cell culture supernatant.
While myofibroblast differentiation is associated with increased collagen production, it is possible that this is perturbed in a situation where the cell is surrounded by collagen that is incompletely processed (e.g. through biomechanical feedback). Given that our results clearly indicated that the effect of ADAMTS2 and ADAMTS14 on invasion is independent of their roles in collagen processing, this avenue is beyond the scope of the current manuscript.
The authors claim that TS2 facilitates TGFβ release and TS14 is a key regulator of TGFβ bioavailability. However, throughout the whole data, there is no experimental evidence for this conclusion. TGFβ activation, LAP concentration and downstream effects should be provided.
Most of the conclusions in the manuscript are based on effects to invasion and the estimated quantification histograms. "Black boxes in between the treatment, e.g. knockdown and readout, that relate to the signals and mechanisms remain black boxes throughout. For example, the impact of the treatments on stellate cell activation markers, the cancer cells invasion signaling, the SERPINE2- and Fibulin2-dependent myofibroblast differentiation pathways should be mechanistically investigated.
We disagree with this comment. Our invasive model shows a clear role for ADAMTS2 and ADAMTS14 in regulating invasion, which is mitigated by disrupting their substrates SERPINE2 and Fibulin2.
ADAMTS2 loss is associated with a reduction in plasmin activity, which again is mitigated with concurrent loss of SERPINE2. Equally, inhibition of plasmin activity with Aprotinin matches the loss of invasion observed with loss of ADAMTS2. Plasmin has a well-established role in mediating TGFβ release from the matrix. We have now included additional experiments using a TGFβ fluorescent reporter in 3D culture. This demonstrates that loss of ADAMTS2 reduces TGFβ activity, which can be rescued with co-knockdown of SERPINE2 (Figure 6). Our data therefore support a mechanism where ADAMTS2 blocks TGFβ release from the matrix, and therefore myofibroblast differentiation, through its regulation of SERPINE2 activity.
We have strengthened our proposed mechanism for ADAMTS14 regulation of TGFβ through Fibulin2 with the use of both luciferase and fluorescent TGFβ reporter constructs. Using these reporters, we demonstrate that stellate cells lacking ADAMTS14 exhibit increased TGFβ activity (Figure 4), which is mitigated with co-knockdown of Fibulin2 (Figure 7). Combined with the effects on αSMA expression and 3D invasion, our data fit with a model where ADAMTS14 regulates TGFβ bioavailability through Fibulin2.
The authors investigate one cell line each for their conclusions; we know that different cell lines behave differently; can they confirm that the finding they present is of general validity or a finding that is specific for the tested cancer/PSC cell lines. Can the principle findings also be proven in primary cells. More importantly, the authors should proof their findings in PaCa tissue of patients as follows: Expression of the proteases in the tissue, related variation of matrisome signatures, e.g. by snRNASeq, to confirm relevance of the finding.
All our key 3D invasive experiments are repeated with both human and mouse stellate cells, adding strength to our proposed association with ADAMTS2 and SERPINE2, and ADAMTS14 and Fibulin2, on the invasive capacity of stellate cells. As detailed above we have explored the clinical relevance of our findings by examining laser dissected tumour and stromal data from PDAC tissue, and scRNA fibroblast data. These data confirm that ADAMTS2 and ADAMTS14 are predominantly expressed in the stromal compartment of the tumour and are associated with key CAF subtypes present in the PDAC environment, inflammatory and myofibroblastic CAFs.
Details related to the figures: Figure 1: Are the numbers of PSC and PaCa cells integrated in the spheres related to the numbers found in patients?
The 2:1 ratio of stellate to cancer cells used to produce spheres is a technical requirement and reflects the numbers in patients (PMID: 23359139). Cancer cells will proliferate substantially faster than the stellate cells so at the end of the experiment (day 3) the spheres are predominantly cancer cells. Nevertheless the stellate cells are able to drive invasion of the cancer cells, which can be quantitatively assessed in this model.
B, it seems that the PSC in the spheroid are not equally distributed but instead are all located in close vicinity to eachother in a cloud; is that the representative situation for the spheres and is this similar in the PaCa cancer tissue? Does this have influence on the results?
We have replaced this image with a more representative image that shows mouse stellate cells dispersed throughout the sphere.
Figure 2: It is interesting to hear that BMP1, which is actually a ligand for BMP signaling is a protease for Collagen. How does this work?
While the BMP family generally belong to the TGFβ superfamily, BMP1 is the exception in that it is a C-terminal collagenase. Please refer to reference 21 in the manuscript (PMID: 33879793), which details the role of BMP1 on collagen processing and the resulting effect on PDAC progression.
C, Quantification of all blots should be presented.
We have now included densitometry for all western blots, presenting values relative to the loading control and normalised to the experimental control. Values are averages taken from all biological repeats with significance indicated by stars.
Figure S2: TS2 kd and TS14 kd should be confirmed and provided by both qrt PCR and WB data.
We were unable to assess ADAMTS2 knockdown by western blot due to the quality of available antibodies. We are confident that either western or PCR confirmation of knockdown is sufficient, especially given the strong phenotype observed with the resulting knockdown.
Figure 3: F; this result is arguing against the conclusion that TGFb bioavailability is a function of the ADAMs, since the kd impacts on the treatment result with exogenous TGFb. This suggests an effect downstream of ligand activation by proteasomal cleavage, e.g. receptor activation or signal transduction; this needs clarification. H, I: TGFβR inhibitor reduces TS14kd enhanced αSMA expression. How is unclear and needs clarification, since from F we know that already activated TGFβ needs TS2 to fully induce αSMA expression.
SupplFig.3: B, C, as above!
αSMA expression in stellate cells requires continuous exposure to TGFβ over 48 hours. Active TGFβ has an incredibly short half-life (minutes) and so requires positive feedback to maintain signalling. We propose that following ADAMTS2 knockdown the cells are incapable of releasing further TGFβ to maintain the phenotype. Equally following ADAMTS14 knockdown the cells are able to release more TGFβ, which is incapable of initiating signalling when the receptor is blocked.
Figure 4: TIMP1 is a canonical TGFb signaling target gene in fibrosis. How the authors explain that TIMP1 is upregulated in both knockdowns, when they claim that TS2 and 14 have opposing functions on TGFb activation. This result as well puts their conclusions as regards TGFb and also the myofibroblast phenotype into question. Especially, since TIMP1 signifies stellate cell activation not only in the pancreas, but also in the liver and kidney. C, D, E should be explained in more detail and all details of the results should be presented.
TIMP1 is a substrate for both ADAMTS2 and ADAMTS14, so its enrichment following knockdown of either is unsurprising, reflective of reduced cleavage of TIMP1. Both our 3D invasive assessment in Figure 6 and αSMA imaging in supplementary figure 5 demonstrate that TIMP1 is not responsible for the effect observed as a consequence from loss of either ADAMTS2 or ADAMTS14.
This holds also for the different myofibroblast phenotypes. All data should be included. From recent scRNASeq investigations, several myofibroblast populations were described and compared, e.g my-stellate cells vs i-stellate cells. To which of these phenotypes the identified populations belong?
As mentioned above, we have interrogated publically available data sets and identified ADAMTS2 and ADAMTS14 expression in multiple CAF subtypes. As these proteases are secreted it is probable that one CAF subtype can control the phenotype of surrounding CAFs through ADAMTS2 and ADAMTS14 production. While intriguing, this hypotheses is beyond the scope of the current work.
Figure 5: C, Only brightfield images are provided, confocal images are suggested for comparison of +/- Aprotinin treatment.
We do not think the addition of confocal images will add to the comparison. Aprotinin clearly reduces invasion, which coupled with the action of stellate-derived SERPINE2 on invasion, and reduced plasmin activity following ADAMTS2 knockdown, suggests that plasmin is important for regulating the effects of ADAMTS2 on invasion.
The efficiency of TS2 and Serpine2 kd should be provided by qrt PCR and WB.
TS2 kd promoted SERPINE2 expression should also be presented by qrt PCR and WB.
We are confident that either western or PCR confirmation of knockdown is sufficient. Of note is that following ADAMTS2 knockdown, SERPINE2 expression is unchanged (sup figure 4C). This would indicate that the enrichment of SERPINE2 observed in the matrisome following loss of ADAMTS2 is reflective of reduced cleavage, rather than a change in expression.
Figure 6: A, why ta use aSMA and not invasive activity as a readout here?
Increased αSMA expression following ADAMTS14 knockdown provides a strong, clear, 2D phenotype to act as a readout for an siRNA screen with high-content imaging. Performing such a screen with our 3D invasive model is currently impractical.
There are many parameters leading to decreased aSMA expression upon kd; (1) why only MMP1 and Fibulin were selected as candidates?
From our αSMA screen, MMP1 and Fibulin2 knockdown were the only candidates that were able to both prevent an increase in αSMA seen with ADAMTS14 loss alone, and are known ADAMTS14 substrates. Further validation in our 3D invasive model demonstrated that Fibulin2 and not MMP1 was responsible for the effect of ADAMTS14 loss on invasion.
(2) the single kd control of the screen candidates is missing!
We feel this control is not needed, as the goal of the experiment was to establish which candidate was responsible for mediating the effects brought about by ADAMTS14 knockdown. Increased αSMA expression with IL-1β loss validates our approach, as this is a known negative regulator of TGFβ signalling.
(3) Can it be expected that all these matrisomal proteins are involved in aSMA expression regulation? I have doubts.
We agree with the reviewers comment, from the siRNA screen (sup figure 5B) it is clear that the majority of the identified matrisome proteins have a minimal effect on αSMA expression following loss of ADAMTS14.
C, D, E, why MMP1 was not also tested in these assays?
Our spheroid assay clearly demonstrated that invasion was enhanced following ADAMTS14 knockdown even with co-knockdown of MMP1. Given the strong rescue observed with co-knockdown of Fibulin2 we proceeded to further analyse this candidate over MMP1.
F, Fibrillin is shown in the figure but not described in the text. It would be quite interesting to see whether Fibrillin kd has the same effect as TS14 kd on LTGF-β activation (which of course need to be shown experimentally).
The association of fibrillin with TGFβ release is well established as it underpins the biology behind Marfan syndrome. Loss of fibrillin, or mutations to its TGFβ binding sites results in a phenotype consistent with super active TGFβ signalling.
E, what is the meaning of αSMA intensity quantification? By IF staining of αSMA? PSC αSMA expression should be quantified by qrt PCR and WB.
We have now incorporated the confocal images analysing αSMA expression into the main figure and labelled the quantification accordingly. We feel this improves the clarity of the figures. Every western blot is now presented with quantification.
Also here, kd efficiency of TS14 and Fibulin2 should be provided by qrt PCR and WB.
Figure S5E should be part of figure 6, qrt PCR of Fibulin2 should be added.
We have moved this western blot to the main figure (Fig 7C). We feel additional PCR validation of Fibulin 2 knockdown is not necessary.
Figure 5/6 and throughout: It is claimed that ADAMTS2 and ADAMTS14 regulate TGFβ bioavailability through SREPINE2-Plasmin and Fibulin2. As mentioned above, TGFβ activation is only mentioned in the schemes, but no experimental evidence is given. In addition, according to previous studies, ADAMTSs can activate latent TGFβ directly by interaction with the LAP of latent TGFβ. .
We have now included extra experimental evidence to support an association of ADAMTS proteins with TGFβ bioavailability. Using a TGFβ luciferase reporter construct, we demonstrate that active TGFβ is increased following loss of ADAMTS14, which is abrogated with concomitant loss of Fibulin2. This provides further evidence that ADAMTS14 is mediating its effects on myofibroblast differentiation / invasion through TGFβ release.
Figure 3B, C, and 6D: We are confused from the migration/invasion assays. Invasion should be based on migration of tumor cells, whereas in the migration assays only stellate cells seem to be active? Can you explain this to us? According to Figure 3B, stellate and cancer cells are cocultured in the chamber. Is this the same condition as for the experiment presented as figure 6D?
In our migration assay, stellate and cancer cells are co-cultured in the apical chamber and cell migration imaged over time. We pooled data of both cancer and stellate cell migration following stellate specific knockdown of either ADAMTS2 or ADAMTS14, which showed an increase in cell migration following loss of ADAMTS14. In figure 7, we again use this assay to demonstrate that Fibulin2 expression accounts for the phenotype observed from loss of ADAMTS14.
In summary, this study for the first time found that ADAMTS2 and ADAMTS14 have opposite roles on myofibroblast differentiation, which is shown by using chimeric spheroids of stellate and pancreatic cancer cells. The authors claim a therapeutic potential for pancreatic cancer by regulating ADAMTS2/14-mediated stellate cell activation, which should avoid cancer cell invasion. The approach is interesting and there is preliminary evidence, however the study has many gaps and requires substantive workload.
We thank the reviewer for their support of our findings. We hope the additional data, combined with the known role for these substrates in the regulation of TGFβ, strengthens the clarity of our manuscript.
-
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
AMADTS2 and ADAMTS14 belong to the disintegrin and metalloproteinase with thrombospondin motif protein family, mainly produced by pancreatic stellate cells (PSC) and are related to cancer cell invasion. This study reveals that ADAMTS2 and ADAMTS14 have opposite roles in myofibroblast differentiation based on experiments testing HSC driven cancer cell invasion, variant expression of HSC activation makers and the related downstream targets analysed upon RNA sequencing analyses. The authors (TA) established PSC/cancer cell chimeric spheroids for investigating the crosstalk between these cell types in 3D in vitro. Based on their findings, they claim that ADAMTS2 and ADAMTS14 have different functions regarding PSC and TGF-β activation. However, their conclusions mainly rely on quantitatve data of invasion and mechanistic details are completely lacking.
Comments:
Typos, even in the abstract, e.g. first sentence incomplete Introduction is rather sparce with one third of the text repeating the results of the study Some citations do not at all fit with the position where they are placed; needs approval
In this study, it is said that TS2 (AMADTS2) and TS14 (ADAMTS14) have opposite functions on myofibroblast differentiation, with individual depletion leading to distinct matrisomal phenotypes in PSC. However, both similarly contribute to collagen processing. As we know, collagen is increased in response to TGFβ signaling, since TS2 depletion (knock down, kd) inhibits and TS14 kd is suggested to promote TGFβ activation, it is expected that this has impact on the available collagen levels. How do the authors explain that nevertheless the kd effect on collagen is very similar?
The authors claim that TS2 facilitates TGFβ release and TS14 is a key regulator of TGFβ bioavailability. However, throughout the whole data, there is no experimental evidence for this conclusion. TGFβ activation, LAP concentration and downstream effects should be provided.
Most of the conclusions in the manuscript are based on effects to invasion and the estimated quantification histograms. "Black boxes in between the treatment, e.g. knockdown and readout, that relate to the signals and mechanisms remain black boxes throughout. For example, the impact of the treatments on stellate cell activation markers, the cancer cells invasion signaling, the SERPINE2- and Fibulin2-dependent myofibroblast differentiation pathways should be mechanistically investigated.
The authors investigate one cell line each for their conclusions; we know that different cell lines behave differently; can they confirm that the finding they present is of general validity or a finding that is specific for the tested cancer/PSC cell lines. Can the principle findings also be proven in primary cells. More importantly, the authors should proof their findings in PaCa tissue of patients as follows: Expression of the proteases in the tissue, related variation of matrisome signatures, e.g. by snRNASeq, to confirm relevance of the finding.
Details related to the figures:
Figure 1: Are the numbers of PSC and PaCa cells integrated in the spheres related to the numbers found in patients? B, it seems that the PSC in the spheroid are not equally distributed but instead are all located in close vicinity to eachother in a cloud; is that the representative situation for the spheres and is this similar in the PaCa cancer tissue? Does this have influence on the results?
Figure 2: It is interesting to hear that BMP1, which is actually a ligand for BMP signaling is a protease for Collagen. How does this work? C, Quantification of all blots should be presented.
Figure S2: TS2 kd and TS14 kd should be confirmed and provided by both qrt PCR and WB data.
Figure 3: F; this result is arguing against the conclusion that TGFb bioavailability is a function of the ADAMs, since the kd impacts on the treatment result with exogenous TGFb. This suggests an effect downstream of ligand activation by proteasomal cleavage, e.g. receptor activation or signal transduction; this needs clarification. H, I: TGFβR inhibitor reduces TS14kd enhanced αSMA expression. How is unclear and needs clarification, since from F we know that already activated TGFβ needs TS2 to fully induce αSMA expression.
SupplFig.3: B, C, as above!
Figure 4: TIMP1 is a canonical TGFb signaling target gene in fibrosis. How the authors explain that TIMP1 is upregulated in both knockdowns, when they claim that TS2 and 14 have opposing functions on TGFb activation. This result as well puts their conclusions as regards TGFb and also the myofibroblast phenotype into question. Especially, since TIMP1 signifies stellate cell activation not only in the pancreas, but also in the liver and kidney. C, D, E should be explained in more detail and all details of the results should be presented. This holds also for the different myofibroblast phenotypes. All data should be included. From recent scRNASeq investigations, several myofibroblast populations were described and compared, e.g my-stellate cells vs i-stellate cells. To which of these phenotypes the identified populations belong?
Figure 5: C, Only brightfield images are provided, confocal images are suggested for comparison of +/- Aprotinin treatment. The efficiency of TS2 and Serpine2 kd should be provided by qrt PCR and WB. TS2 kd promoted SERPINE2 expression should also be presented by qrt PCR and WB.
Figure 6: A, why ta use aSMA and not invasive activity as a readout here? There are many parameters leading to decreased aSMA expression upon kd; (1) why only MMP1 and Fibulin were selected as candidates? (2) the single kd control of the screen candidates is missing! (3) Can it be expected that all these matrisomal proteins are involved in aSMA expression regulation? I have doubts. C, D, E, why MMP1 was not also tested in these assays? F, Fibrillin is shown in the figure but not described in the text. It would be quite interesting to see whether Fibrillin kd has the same effect as TS14 kd on LTGF-β activation (which of course need to be shown experimentally). E, what is the meaning of αSMA intensity quantification? By IF staining of αSMA? PSC αSMA expression should be quantified by qrt PCR and WB. Also here, kd efficiency of TS14 and Fibulin2 should be provided by qrt PCR and WB.
Figure S5E should be part of figure 6, qrt PCR of Fibulin2 should be added.
Figure 5/6 and throughout: It is claimed that ADAMTS2 and ADAMTS14 regulate TGFβ bioavailability through SREPINE2-Plasmin and Fibulin2. As mentioned above, TGFβ activation is only mentioned in the schemes, but no experimental evidence is given. In addition, according to previous studies, ADAMTSs can activate latent TGFβ directly by interaction with the LAP of latent TGFβ. . Figure 3B, C, and 6D: We are confused from the migration/invasion assays. Invasion should be based on migration of tumor cells, whereas in the migration assays only stellate cells seem to be active? Can you explain this to us? According to Figure 3B, stellate and cancer cells are cocultured in the chamber. Is this the same condition as for the experiment presented as figure 6D?
In summary, this study for the first time found that ADAMTS2 and ADAMTS14 have opposite roles on myofibroblast differentiation, which is shown by using chimeric spheroids of stellate and pancreatic cancer cells. The authors claim a therapeutic potential for pancreatic cancer by regulating ADAMTS2/14-mediated stellate cell activation, which should avoid cancer cell invasion. The approach is interesting and there is preliminary evidence, however the study has many gaps and requires substantive workload.
Significance
AMADTS2 and ADAMTS14 belong to the disintegrin and metalloproteinase with thrombospondin motif protein family, mainly produced by pancreatic stellate cells (PSC) and are related to cancer cell invasion. This study reveals that ADAMTS2 and ADAMTS14 have opposite roles in myofibroblast differentiation based on experiments testing HSC driven cancer cell invasion, variant expression of HSC activation makers and the related downstream targets analysed upon RNA sequencing analyses.
The authors (TA) established PSC/cancer cell chimeric spheroids for investigating the crosstalk between these cell types in 3D in vitro. Based on their findings, they claim that ADAMTS2 and ADAMTS14 have different functions regarding PSC and TGF-β activation. However, their conclusions mainly rely on quantitatve data of invasion and mechanistic details are completely lacking.
Comments:
Typos, even in the abstract, e.g. first sentence incomplete Introduction is rather sparce with one third of the text repeating the results of the study Some citations do not at all fit with the position where they are placed; needs approval
In this study, it is said that TS2 (AMADTS2) and TS14 (ADAMTS14) have opposite functions on myofibroblast differentiation, with individual depletion leading to distinct matrisomal phenotypes in PSC. However, both similarly contribute to collagen processing. As we know, collagen is increased in response to TGFβ signaling, since TS2 depletion (knock down, kd) inhibits and TS14 kd is suggested to promote TGFβ activation, it is expected that this has impact on the available collagen levels. How do the authors explain that nevertheless the kd effect on collagen is very similar?
The authors claim that TS2 facilitates TGFβ release and TS14 is a key regulator of TGFβ bioavailability. However, throughout the whole data, there is no experimental evidence for this conclusion. TGFβ activation, LAP concentration and downstream effects should be provided.
Most of the conclusions in the manuscript are based on effects to invasion and the estimated quantification histograms. "Black boxes in between the treatment, e.g. knockdown and readout, that relate to the signals and mechanisms remain black boxes throughout. For example, the impact of the treatments on stellate cell activation markers, the cancer cells invasion signaling, the SERPINE2- and Fibulin2-dependent myofibroblast differentiation pathways should be mechanistically investigated.
The authors investigate one cell line each for their conclusions; we know that different cell lines behave differently; can they confirm that the finding they present is of general validity or a finding that is specific for the tested cancer/PSC cell lines. Can the principle findings also be proven in primary cells. More importantly, the authors should proof their findings in PaCa tissue of patients as follows: Expression of the proteases in the tissue, related variation of matrisome signatures, e.g. by snRNASeq, to confirm relevance of the finding.
Details related to the figures:
Figure 1: Are the numbers of PSC and PaCa cells integrated in the spheres related to the numbers found in patients? B, it seems that the PSC in the spheroid are not equally distributed but instead are all located in close vicinity to eachother in a cloud; is that the representative situation for the spheres and is this similar in the PaCa cancer tissue? Does this have influence on the results?
Figure 2: It is interesting to hear that BMP1, which is actually a ligand for BMP signaling is a protease for Collagen. How does this work? C, Quantification of all blots should be presented.
Figure S2: TS2 kd and TS14 kd should be confirmed and provided by both qrt PCR and WB data.
Figure 3: F; this result is arguing against the conclusion that TGFb bioavailability is a function of the ADAMs, since the kd impacts on the treatment result with exogenous TGFb. This suggests an effect downstream of ligand activation by proteasomal cleavage, e.g. receptor activation or signal transduction; this needs clarification. H, I: TGFβR inhibitor reduces TS14kd enhanced αSMA expression. How is unclear and needs clarification, since from F we know that already activated TGFβ needs TS2 to fully induce αSMA expression.
SupplFig.3: B, C, as above!
Figure 4: TIMP1 is a canonical TGFb signaling target gene in fibrosis. How the authors explain that TIMP1 is upregulated in both knockdowns, when they claim that TS2 and 14 have opposing functions on TGFb activation. This result as well puts their conclusions as regards TGFb and also the myofibroblast phenotype into question. Especially, since TIMP1 signifies stellate cell activation not only in the pancreas, but also in the liver and kidney. C, D, E should be explained in more detail and all details of the results should be presented. This holds also for the different myofibroblast phenotypes. All data should be included. From recent scRNASeq investigations, several myofibroblast populations were described and compared, e.g my-stellate cells vs i-stellate cells. To which of these phenotypes the identified populations belong?
Figure 5: C, Only brightfield images are provided, confocal images are suggested for comparison of +/- Aprotinin treatment. The efficiency of TS2 and Serpine2 kd should be provided by qrt PCR and WB. TS2 kd promoted SERPINE2 expression should also be presented by qrt PCR and WB.
Figure 6: A, why ta use aSMA and not invasive activity as a readout here? There are many parameters leading to decreased aSMA expression upon kd; (1) why only MMP1 and Fibulin were selected as candidates? (2) the single kd control of the screen candidates is missing! (3) Can it be expected that all these matrisomal proteins are involved in aSMA expression regulation? I have doubts. C, D, E, why MMP1 was not also tested in these assays? F, Fibrillin is shown in the figure but not described in the text. It would be quite interesting to see whether Fibrillin kd has the same effect as TS14 kd on LTGF-β activation (which of course need to be shown experimentally). E, what is the meaning of αSMA intensity quantification? By IF staining of αSMA? PSC αSMA expression should be quantified by qrt PCR and WB. Also here, kd efficiency of TS14 and Fibulin2 should be provided by qrt PCR and WB.
Figure S5E should be part of figure 6, qrt PCR of Fibulin2 should be added.
Figure 5/6 and throughout: It is claimed that ADAMTS2 and ADAMTS14 regulate TGFβ bioavailability through SREPINE2-Plasmin and Fibulin2. As mentioned above, TGFβ activation is only mentioned in the schemes, but no experimental evidence is given. In addition, according to previous studies, ADAMTSs can activate latent TGFβ directly by interaction with the LAP of latent TGFβ. .
Figure 3B, C, and 6D: We are confused from the migration/invasion assays. Invasion should be based on migration of tumor cells, whereas in the migration assays only stellate cells seem to be active? Can you explain this to us? According to Figure 3B, stellate and cancer cells are cocultured in the chamber. Is this the same condition as for the experiment presented as figure 6D?
In summary, this study for the first time found that ADAMTS2 and ADAMTS14 have opposite roles on myofibroblast differentiation, which is shown by using chimeric spheroids of stellate and pancreatic cancer cells. The authors claim a therapeutic potential for pancreatic cancer by regulating ADAMTS2/14-mediated stellate cell activation, which should avoid cancer cell invasion. The approach is interesting and there is preliminary evidence, however the study has many gaps and requires substantive workload.
-
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 Carter and colleagues examines that role of cancer-associated fibroblasts (CAFs) in regulation of invasion in a 3D co-culture assay with epithelial cells. The authors propose that invasive chains of cancer cells are led by fibroblasts. The authors utilise a system of co-culture to create chimeric human-mouse fibroblast-cancer cell spheroids (both directions utilised, to eliminate species bias) to allow for in situ sequencing of the co-operating transcriptional programmes of each cell type during 3D invasion. From this powerful approach, this allowed the authors to identify two key two collagen-processing enzymes, ADAMTS2 and ADAMTS14, as contributing to CAF function in their system. The authors identify that these two enzymes have opposing roles in invasion, and map some of their key substrates in invasion, which extend beyond collagen-processing. The authors propose that one key function is to control the processing of TGFbeta, the latter of which is a regulator of the myofibroblast subpopulation of CAF. Overall, the findings of the manuscript are interesting, but need some further proof-of-principal demonstrations to extend their findings to support the claims within.
- The authors demonstrate a clear role of ADAMTS2 and ADAMTS14 in stellate function during differentiation and invasion. Is there any evidence of such changes in patient materials? Could the authors query publicly available databases of micro-dissected stroma vs epithelium to validate the translational relevance of their findings?
Major comments:
- Page no. 4, Line 71, The authors conclude that the invasion in the chimeric spheroids is "led by" stellate cells. This is a key concept in the manuscript. How do the authors define the "led by" phenomena? What is the frequency that this occurs?
- For Figure 2A and S2A, the text suggests that the heatmap represents the stellate vs cancer cell expression (as shown in Figure 1B and S1B) in the respective species but the labelling below the heatmap suggests they are all cancer cells (Mia, Pan, R2 and DT). Is this a typo? Could the authors clarify this?
- The text and the figures are lacking information about the cell line names used in the experiment, e.g, Figure 2C, 2D, 2SB, 2SC and 2SD does not indicate what cell line was used in the study. This is the same with other figures as well. Please indicate in all instances exactly which samples are queried.
- It's mentioned in the text that the authors have used the cancer and stellate cells in a 1:2 ratio but the numbers of stellate cells look different between different spheroids confocal images. e.g. The numbers look very different between the Miapaca2:PS1 vs Miapaca2:mPSC spheroids. Is this simply the representative images, or are their bona fide differences. This, in turn, would impact on claims of cells being 'led' by stellate cells. Can the authors clarify?
- While for most of the experiments the authors generated the chimeric spheroids first and then performed the respective experiments, it appears that for the invasion assay simply co-culture of Cancer cells and stellate cells was done. Is this correct? Have the authors tried performing the assay with the chimeric spheroids to see if the stellate cells still invade?
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The authors claim that ADAMTS2 and ADAMTS14 regulate the bioavailability of TGFB, and this is a key reason that these regulate CAF differentiation. However, there is no direct demonstration of this concept, which is conspicuous by absence. Could the authors either directly demonstrate this, or remove such notions from the results, and explicitly state that this is an untested speculation in discussion? Examples of this are:
- Line 173, authors state "ADAMTS2 facilitates TGFβ release through degradation of the plasmin inhibitor, SERPINE2 (Figure 5D)"
- Line 196 authors conclude "Together these data implicate 197 ADAMTS14 as a key regulator of TGFβ bioavailability (Figure 6F)."
- Line 240 states "This reduces the activation of Plasmin, preventing the release of TGFβ (Figure 5C)." Since this is just a model without detailed experiments, It will be better to propose rather than conclude.
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Figure S5C shows a less invasive phenotype in the NTCsi + ADAMTS14si spheroids compared to the NTCsi + NTCsi control. However, there appears no appreciable difference between NTCsi + ADAMTS14si and NTCsi + NTCsi spheroids' brightfield images in Figure 5SD. Could the authors comment on this?
Minor Comments:
- Page no. 2, Line 20 has an incomplete sentence "Crosstalk between cancer and stellate cells is pivotal in pancreatic cancer, resulting in differentiation 21 of stellate cells into myofibroblasts that drive."
- Figure 2C; Figure S2C and Figure S5E lack quantification for the western blots.
- Why did the authors choose to investigate the Metzincin family? Could the authors provide their reasoning to investigate these proteins, to the exclusion of other candidates?
- Info about the number of fields imaged per sample for the microscopy data is missing in the figure legends (e.g. Figure 2F and 2I, Figure 5SF).
- Any particular reason why the ADAMTS2 expression was not checked through Western blotting like ADAMTS14 in Figure S2B.
- The legends for Figure 3SC and 5SF mention that "Images are representative of at least two biological replicates". How many technical replicates were used? It would be useful if the relative intensity of the images is measured and plotted in a graph.
Significance
This work provides an examination of the cross talk between fibroblasts and cancer cells in a 3-Dimensional culture model of pancreatic tumour cell invasion. By using chimeric human-mouse spheroids, the authors are able to identify cell-type specific transcripts by bulk RNA sequencing in situ. This advance is not to be underestimated as a number of existing approaches for cell type-specific profiling (eg. single-cell sequencing) relies upon dissociation of cell communities prior to sequencing. It is very likely that transcriptional programmes change during this isolation process. This approach allows the authors to identify transcriptional co-operating programmes in situ. This data provides a resource to understand this key co-operation of these two cell types during tumourigenesis, and will be of interest to the pancreatic cancer field. In addition, the mapping of the key substrate of these enzymes provides further insights that may be useful in understanding the expanded target repertoire of these enzymes beyond collagen processing.
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Referee #1
Evidence, reproducibility and clarity
This study aims to explain the opposing contributions of stromal stellate cells/CAFs to PDAC. By first identifying stroma-specific proteases, followed by a process of candidate selection and elimination, the authors find that two specific metalloproteases that share enzymatic activity against collagen in fact have differential activity on TGFb availability. This could be interpreted as a way of shaping the CAF population and tumor-promotin or -restricting properties of the stroma.
There are several flaws that the authors could address to improve the manuscript:
- In the flow of experiments and analyses, there is a strange mix of fully unbiased discovery phases followed by functional experiments that do not consider all possible candidates to test, and vice versa. For instance, from the mixed-species transcript analysis, ADAMTS2 and -14 are chosen based on their shared collagenase activity based on literature. However, the authors then perform again a proteomics analysis to identify things from the entire matrisome that are cleaved by these enzymes? Then, for ADAMTS2 a co-silencing approach is done on one selected candidate (Serpine2), but for ADAMTS14 an siRNA screen is performed? The problem of this approach is that the rationale for some studied enzymes is very strong, where as for others it is not.
- The ECM is more than just collagen. Choosing these two metalloproteases based on their shared collagen substrate is an approach that perhaps oversimplifies the ECM a bit, and again, does not provide the strongest rationale that these metalloproteases are most likely to explain counteracting stromal activities on tumor growth and progression.
- Related to the above: How were the stellate cells used for the matrisome analysis grown? In the suspension setup or adherent? This will have a large impact on the outcome. Is there for instance hyaluronic acid in this matrix?
- Performing the species-specific transcript analysis both ways is a neat approach, but why did the authors ignore the opportunity to formally overlay/compare the two stromal gene sets to define likely candidates based on statistics?
Minor comments:
The bioinformatics Methods need more details on how reads were mapped to the different genomes. How many mismatches were allowed and was the mapping done separately or using for instance Xenofilter?
The authors use the knowledge on the activities of both ADAMTS2 and -14 on collagen as a rationale to choose these two. Is there really a need for the paragraph (and associated figures) from line 102 on?
Abstract, line 21; some words are missing?
Were the siRNA screen hits validated?
What is the genotype of the mouse cancer cells? KPC-derived?
Significance
The trick of dissecting tumor from stromal signals in spheroid cocultures by RNA-Seq is a cool trick, but not new and the authors should probably cite some prior work.
What this all means for patients (or in vivo tumors even) remains unclear. There is some debate on whether highly activated CAFs (ACTA2/aSMA+ cells, some call them myCAFs) are indeed tumor-restrictive or whether they promote invasion. The authors appear to argue the latter (which I can agree with) but without any translational work to show what the net outcome of this mechanism is, the study remains descriptive and perhaps of limited interest.
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Referee #2
Evidence, reproducibility and clarity
This study by Kordala et al reports the identification of new therapeutics to further improve the clinical outcomes of spinal muscular atrophy (SMA) patients. SMA is childhood neurological disease that is caused by insufficient levels of the survival motor neuron (SMN) protein. There are currently three approved therapies for SMA, yet the disease is not cured and many patients remain severely disabled. The authors conducted a screen of known epigenetic regulators to identify molecules that increase SMN protein. They identified MS023, which is a selectively PRMT inhibitor, that promotes SMN exon 7 inclusion and thus full length SMN protein. Importantly, MS023 improves the SMA phenotype alone or in combination with the SMN2 antisense oligonucleotide suggesting it can potentially be used by itself or in combinatorial approaches. While this is a generally well written paper with relatively straight forward experimental design there remains some concerns that should be addressed.
Major Concerns:
- The mechanism of action needs further clarification. Does MS023 work similarly to Risdaplam? Also, if Nusinersen is already interfering with hnRNPA1 how does MS023 augment the splicing.
- MS023 alone did not increase improve exon 7 inclusion in the spinal cord of treated SMA mice yet the protein levels were increased (Fig. 3D,F). Are there alternative mechanisms through which MS023 is acting?
- Further explanation of why MS023 did not improve exon 7 inclusion in the spinal cord but enhanced the effect of the ASO (Fig. 4B) is needed.
- Nusinersen has been shown to almost completely rescue the SMA phenotype in mice. Was the dose used here chosen to be suboptimal?
Minor Concern:
Many neurological diseases are now moving to a multimodal approach. The manuscript could be improved with further discussion of why MS023 would be an attractive option compared to other synergistic strategies being employed for SMA, including the most obvious of combining some of the already approved therapies.
Significance
This is a generally well done study that works through a screening methodology to identify a molecule that increase the levels of SMN. Mechanistic studies suggest that the compound works through inhibiting the recruitment of hnRNPA1 to the SMN2 gene, thus promoting inclusion of exon 7 and the production of full-length SMN protein.
The study does not provide definitive data that methyl transferase activity of PRMT promotes exon 7 exclusion or that the inhibitor changes the methylation state of any of the proteins involved. However, knockdown experiments does not exclude this possibility.
This study would be of general interest to wider audience if more detail was included regarding the current SMA landscape and how MS023 fits in with what is currently available. The transcriptome data was potentially very interesting since it provided clues on how MS023 is exerting its synergistic effect(neuroinflammation angle is relatively unique), but that data was only briefly discussed.
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Evidence, reproducibility and clarity
Summary
SMA is a severe, monogenetic, progressive neuromuscular disease that mostly affects young children. SMA is cause by homozygous loss of function of SMN1. The main modifier of disease severity - that ranges widely, from neonatal to adult onset - is the presence of a varying number of SMN2 copies in the human genome. Recently, several gene-targeting therapies for SMA have been approved. This has changed the outcome of SMA drastically for many patients, but, surprisingly, the effect of these treatments varies strongly between patients. This leads to significant uncertainty for patients, families and clinicians and poses a challenge to reliable prognosis.
One of the drugs that has been approved for treating SMA is the antisense oligonucleotide nusinersen (Spinraza). Nusinersen improves SMA outcomes by enhancing the splicing of SMN2 -transcribed pre-mRNA, leading to an increase in the inclusion of exon 7 leading to an increase in the availability of full-length, functional SMN protein. In the current manuscript, Kordala and colleagues investigate the effect of a library of 54 compounds (focused on modulating epigenetic regulators) on SMN2 splicing and SMN protein in an SMA type II patient fibroblast cell line. They found the Type I PMRT inhibitor, MS023 to dose-dependently increase full length SMN2 splicing SMN protein levels, by decreasing hnRNPA1 binding to SMN2 pre-mRNA. Next, they show that MS023 monotreatment of the severe 'Taiwanese' (+/- SMA type I) mouse model of SMA leads to improved survival and weight gain. Moreover, they show that combinatorial treatment of the same mouse model with MS023 and nusinersen, significantly further improves survival compared to both nusinersen and MS023 monotreatment. Finally, transcriptome analysis suggests that the majority of misregulated transcripts in SMA is rescued by both nusinersen an combinatorial treatment but, importantly, the rescue observed in the combinatorial group seems more complete.
Suggestions
The authors state in the abstract that "transcriptomic analysis revealed that MS023 treatment has very minimal off-target effects". However, their transcriptomic analyses do not contain a condition that investigates the effects of MS023 on the transcriptome in WT and SMA animals on its own. I belief this would have been an essential addition to support the conclusion on off-target effects of MS023, especially considering the benefits that the authors list in the discussion when compared to e.g. VPA. I agree with their comments about the unspecificity of such drugs; however, I don't belief their current transcriptomics analysis on MS023 fully support this conclusion either. It may not be feasible to include such an experiment in a revised version of the manuscript, but in this case the authors should reflect on the wording of their conclusions.
I agree with the authors that the effect of MS023 on SMN-FL RNA appears to be dose-dependent but I don't think the data fully supports that conclusion for SMN protein levels (compare e.g. 250 nM and 2.5 µM quantification). In fact, there are many inconsistencies between SMN RNA and SMN protein levels: in figure 3 (MS023 monotreatment), the authors observe in spinal cord no change in SMN RNA but a significant increase in SMN protein. In contrast, in the same figure, in muscle, both SMN RNA and protein increase significantly. This is a bit confusing and to me mostly means that the regulation of SMN RNA and protein expression in complex and likely depends on many more factors than PMRT activity and hnRNPA1 arginine methylation status. Indeed, the authors pick hnRNPA1 as a promising target from a list of proteins that contains 72 in total. Are there no other promising candidates in this list that would be able to explain the unclear and inconsistent correlation between SMN RNA splicing and SMN protein levels?
The in vitro work was based on the use of one primary fibroblast cell line. It would be relatively straightforward to characterized the effect of MS023 on e.g. type 1 and type 3 patient-derived lines, thus providing a clearer overview of the use of this type of drug in SMA patients of different types. Both through the Corriell repository (as used in the current paper) and surely also through biobanks at Oxford it should be relatively straightforward to obtain such cell lines and for the authors to extend their analyses to include patients of different types (and with varying SMN2 copy number).
The mechanism that the authors suggest in e.g. Fig. 2D about the interaction of hnRNPA1 with the SMN2-ISSN1 in relation to PMRT inhibition is very similar to how nusinersen prevents SMN2-ISSN1 binding of hnRNPA1 (as the authors mention in the discussion). How do the authors suggest this would work? Do they have suggestions for further experiments to investigate this interaction (e.g. using hnRNPA1 and nusinersen molecules with point mutations?)
Minor comments
Do I understand correctly that none of the screened molecules in figure 1 lead to significantly unregulated SMN protein levels (including MS023)? What causes the difference between figure 1 (no signficicant upregulation of SMN protein) vs figure 2 (a dose dependent increase of SMN protein)? Do the authors have an explanation for this difference? In relation to this point, I am somewhat surprised at the variability in protein quantifications in especially figures 1 and 2. In these figures, biological replicates are obtained from one cell line. Although I understand that there is not necessarily much benefit to including all western blots used for quantification in for example the supplementary files with the paper, it would be useful to see some examples for e.g. the western blots for the quantifications in fig. 1C. Similarly, I appreciate the complexity of the IPs and arginine-methylation specific blotting in fig 2E, but the current tightly cropped blots are not super convincing and the uncropped blots are not included in the supplementary data. Also how was this quantified; fig 2F lacks some indication of standard deviation or other indicator of reproducibility between measurements.
There are some what appear to be reference formatting errors (e.g. lines 17 and 20 on page 15 of the manuscript PDF amongst others).
The PDF version of Supplementary table 2 in its current format is not really usable or readable; an Excel version would be preferable.
Significance
The paper addresses an interesting question: it aims to improve the efficacy of existing drugs for SMA by identifying novel molecules that may improve the working mechanism of, in this case, nusinersen. Others have tried this before by using VPA, but the current molecule appears to be more specific. However, it would have been interesting to get more details on the effect of this novel compound: a wider range of cell lines, further mouse experiments (a control group in figs. 3 and 5) and analysis (e.g. pathological analysis of the neuromuscular system). It would in fact have been interesting to combine some of the analyses in the current work also with the other available SMN2 splicing modifier risdiplam: as risdiplam also modulates SMN2 splicing, MS023 might also have been suitable to improve risdiplam efficacy. Especially in the cell line the authors have used this would have been a relatively straightforward addition. I believe the paper may provide an interesting start, but without further analysis remains at that stage.
The audience to likely be most interest are mostly colleagues from the SMA field, as the mechanisms in the current manuscript focus very much on ISS-N1-regulated SMN2 splicing which is highly specific for SMA.
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Reply to the reviewers
Manuscript number: RC-2022-01785
Corresponding author(s): Amélie, Fradet-Turcotte, and Louis, Flamand
Title: The immediate early protein 1 of human herpesvirus 6B counteracts ATM activation in an NBS1-dependent manner
Our manuscript received positive and constructive comments from all three Reviewers. First, they unanimously agreed that the biology uncovered in our study is novel and of broad scientific interest, including researchers studying host-pathogen, DNA damage response and repair processes. They highlighted that the manuscript is well-written and presents clear, rigorous, and convincing data. Second, they provided constructive comments to strengthen our model and the biological relevance of our findings. Here, we provide an overview of our findings and a point-by-point reply explaining the revisions, additional experimentations and analyses planned to address the points raised by the referees.
1 - Description of the planned revisions
1.1 *The three Reviewers agreed that we convincingly show that HHV-6B IE1 binds to NBS1 and inhibits ATM activation; however, they all raised concerns about whether the IE1-dependent inhibition of ATM is required for HHV-6B replication and integration. *
We agree with the Reviewers that the biological data validating the impact of ATM on viral replication and integration could be solidified. Problematically, IE1 is essential to promote HHV-6B replication in infected cells, and thus any IE1 knockdown (KD) or knockout (KO) approach will generate data that are hard to interpret. As mentioned by Reviewers 1 and 3, the ideal experiment to address this concern would be to infect cells with an HHV-6B virus in which IE1 contains a small truncation or a mutation that specifically suppresses its ability to inhibit ATM. Creating IE1 deletion and single mutants in the HHV-6 genome is technically challenging and can only be achieved using herpesvirus bacterial artificial chromosome (BAC)(Warden et al., 2011). Although HHV-6A BAC was previously described (Borenstein & Frenkel, 2009; Tang et al., 2010), our multiple attempts at generating HHV-6B BAC remained unsuccessful. As an alternative, we will investigate if the inhibition of ATM by using the ATM inhibitor (KU-55933) or its depletion by an shRNA, impact HHV-6B replication and integration as proposed by Reviewers 1 and 3. Specifically, MOLT-3 cells will be either treated with 10 µM KU-55933 or depleted for ATM with shATM(Rodier et al., 2009) prior to infection. DMSO and shLUC will be used as controls, respectively. These experiments will allow us to determine if ATM inhibition enhances HHV-6B replication and/or integration.
1.2 Reviewer 2: "Although they have nicely mapped the interaction (between IE1 and NBS1), the authors have not yet defined the mechanism of ATM inhibition. They propose a number of possibilities in the discussion, but none are yet tested experimentally. The manuscript would be strengthened by further exploration of these possibilities. Does the sequence or proposed structure give any insights into interactions that could be relevant? Is IE1 phosphorylated by ATM, and could this affect the binding of other proteins?"
We thank the Reviewer for pinpointing that a deeper characterization of the mechanism of ATM inhibition would allow us to support our model. In the manuscript, we discuss the possibility that IE1 inhibits ATM activation by preventing the interaction between the FxF/Y motif of NBS1 and ATM. Although we do not detect a strong interaction between IE1 and ATM (Fig. 5A), we have not yet investigated if the ATM-inhibitory domain (ATMiD) is required for IE1 to prevent the recruitment of ATM by NBS1 at the LacO array (Fig. 5E). Thus, we will determine if an ∆ATMiD IE1 inhibits the interaction between NBS1 and ATM in this assay. If the ATMiD domain interferes with the interaction of NBS1 with ATM, we expect to see no inhibition of NBS1 activation of ATM in cells that express 3xFlag-HHV-6B IE1 ∆ATMiD.
Another possibility is that IE1 inhibits ATM activation indirectly by interacting with the nucleosome. The latter possibility is based on the finding that the C-terminal domain of HHV-5 IE1 contains an arginine-serine (RS) motif that interacts with the acidic patch of the nucleosome(Fang et al., 2016). Interestingly, HHV-6B IE1 sequence analysis reveals two RS motifs at positions 852-53 and 1033-34. Thus, the conserved RS residues (R852A/S853A and R1033A/S1034A) will be mutated in the ATMiD domain of HHV-6B IE1 (810-1078), and their ability to inhibit ATM activation will be quantified by immunofluorescence approach as described in Fig 6 D-E. In parallel, GST-tagged recombinant ATMiD of HHV-6B IE1 will be produced, and pulldown experiments will investigate their ability to bind to nucleosomes. We already have purified nucleosomes in the lab and have the expertise for this type of analysis(Galloy et al., 2021; Sitz et al., 2019).
Thanks to the Reviewer's comment, we performed sequence analyses for putative ATM phosphorylation sites (SQ/TQ) and found that the protein contains 6 of them, two of which are in the ATMiD of the protein. To determine if the viral protein is a substrate of ATM, we will immunoprecipitate IE1 from MOLT-3 infected cells and use the well-characterized pSQ/pTQ antibody in western blotting analyses. The immunoprecipitation will be done in denaturing conditions to avoid interference with other endogenous interactors of IE1. If the protein is phosphorylated in an ATM-dependent manner, we will test the impact of these mutants on ATM inhibition as done in Fig. 6 D-E.
Altogether, these experiments will allow us to refine our understanding of the mechanism by which HHV-6B IE1 inhibits ATM activation in host cells.
1.3* Reviewer 2: "Could the effects of IE1 be linked to other post-translational modifications? The literature suggests this protein to be SUMOylated. Is SUMOylation relevant to the effects on ATM activation?" *
The Reviewer is right. Our group showed that IE1 is sumoylated on K802R in a SUMO interacting motif (SIM)-dependent manner (V775, I776, V777)(Collin et al., 2020). In the LacO/LacR assays, we already showed that the K802R and SIM mutant (775AAA777) do not impact the interaction of IE1 with NBS1. Although the sumoylated site and the SIM lie outside of the ATMiD, we cannot rule out the possibility that this post-tranlationnal modification impacts ATM inhibition by IE1 throughout a conformational interference. To address this possibility, we will characterize the ability of the single and double K802R/SIM mutant proteins to inhibit the activation of ATM, as described in Fig 6 D-E.
2 - ____Description of the revisions already incorporated in the transferred manuscript
The following comments and all minor comments raised by the Reviewers have been incorporated into the transferred manuscript:
2.1 Reviewer 2: "In Figure 1, they look at micronuclei formation but MNi is not defined the main text."
We thank the Reviewer for noticing this mistake. MNi is now defined as micronuclei in line 138.
2.2 Reviewer 3: "As discussed by the authors, HHV-6B IE1 inhibits DSB signaling through NSB1, but we cannot know how this inhibition (might be increase genome instability of both host and virus) enhances viral replication and integration. The readers are easy to understand if the authors described it in the discussion or analyzed by KD or KO of IE1 in infected cells."
The Reviewer is right. We cannot rule out that increased genomic instability enhances viral replication. Thus, we add the following sentences to clarify this point in the discussion.
Line 371-374: "Finally, the model presented here assumes that NBS1 and ATM activity must be inhibited to prevent their detrimental effect on viral replication. However, it is impossible to rule out that enhanced viral replication and integration result from the increased level of genomic instability induced in host cells upon viral infection. Further studies will be required to address this question."
2.3 Reviewer 3: "Described in lines 354-356 are the case of lytic cycle only. In the lytic cycle, the infected cells will die soon after viral replication. and there is no chance to become tumor. However, the state of ciHHV-6 or latently infected cells can be affected by genome instability during IE1 expression. Please add discussion."
We thank the Reviewer for raising this important point. We agree that the real threat for the host cells regarding tumor development is genomic instability promoted by the expression of IE1 during latent infection or from an integrated form of the virus. Consistent with this possibility, our original manuscript contains this sentence in the abstract:
Line 60-62: "Interestingly, as IE1 expression has been detected in cells of subjects with the inherited chromosomally-integrated form of HHV-6B (iciHHV-6B), a condition associated with several health conditions, our results raise the possibility of a link between genomic instability and the development of iciHHV-6-associated diseases."
To further emphasize this point, the following sentence has now been added to the discussion:
Line 349-356: During the lytic cycle, the accumulation of genomic instability in the host cell genome is not a problem as these cells will die upon the lysis provoked by the virus to release new virus particles. However, more selective inhibition of ATM by IE1 during the latent cycle of HHV-6B or from iciHHV-6B would avoid a detrimental accumulation of genomic alterations in host cells. This model would be consistent with the fact that HHV-6B is not associated with a higher frequency of cancer development, as would be expected if global DSB signaling was inhibited in these cells. Alternatively, expression of IE1 upon the exit of latency may inhibit global DSB signaling, but this phenomenon is restricted to the early stages of the process, thereby minimizing the impact on the host cell's genomic stability.
2.4 Reviewer 3: Line 114, Miura et al (J Infect Dis 223:1717-1723 [2021]) should be cited.
This reference has been added in line 113. In the discussion, we also introduce the citation where we mention the link between HHV-6B integration and abortion, line 362 of the revised manuscript.
3 - ____Description of the revisions that will not be carried out
3.1 Reviewer 2: "Does it (HHV-6B IE1) also share other activities with herpesvirus proteins e.g. ubiquitinylation?"
IE1 shares very little sequence homology with proteins from other herpesviruses (except HHV-6A and HHV-7), meaning that deductions based on primary sequence analysis are very limited. Any attempt at understanding the function of HHV-6B IE1 by structure analysis prediction software did not predict any known function or domain. Thus, most of our knowledge of IE1 relies on experiments that used IE1 truncation (this study and (Jaworska et al., 2007)) and point mutants(Collin et al., 2020). The protein contains no conserved RING or HECT domain that would hint at an E3-ligase activity and does not share homology with other herpes proteins that promote ubiquitylation events, such as ICPO from HSV-1(Rodríguez et al., 2020). We believe that, at this point, there is not enough evidence to investigate further if HHV-6B IE1 has an E3-ligase activity.
3.2 Reviewer 3: Lines 52, "Expression of immediate early protein 1 (IE1) was sufficient to recapitulate this phenotype" is not right. The authors showed that IE1 blocked ATM signaling in transient experiments but they did not show any evidence in infected cells. Kock down or Kock out of IE1 is important to conclude it."
We agree with the Reviewer HHV-6B IE1 knockdown, or knockout, would allow us to conclude that IE1 is the only protein to target DSB signaling in the infected cells. As mentioned by the Reviewer (see point 3.3 and 1.1), IE1 is essential to promote HHV-6B replication in infected cells. Thus, any knockdown or knockout approach will generate data that are hard to interpret. In contrast, the generation of an HHV-6 genome containing truncation or point mutation that abolishes its ability to inhibit ATM signaling should allow us to bypass this issue. While we believe this question is important, human resource shortages prevent us from addressing this point in an acceptable time frame. Instead, we propose investigating the role of ATM activity in HHV-6B replication and integration. We also rephrased the sentence highlighted by Reviewer 3:
Line 51-52: "Expression of immediate early protein 1 (IE1) phenocopies this phenotype and blocks further homology-directed double-strand break (DSB) repair."
3.3 Reviewer 3: The authors did not analyze the effect of viral manipulation as they did not analyze KO or KD of IE1. Even if HHV-6B IE1 is essential for viral replication, they can use dominant negative mutant of IE1 or NSB1 determined in this manuscript.
Reviewer is right. As discussed in points 3.2 and 1.1, we haven’t tried to rescue IE1 knockdown, or knockout in infected cells. Rescue experiments of IE1 by transient transfection of dominant negative IE1 mutant would require a high level of transfection in MOLT-3 cells and small truncation or mutations of IE1 that revert the ATM inhibitory function of IE1. Screening additional sets of truncations/mutants of IE1 that abolish its ability to inhibit ATM and optimizing the poor transfection efficiency of the lymphoid cell line MOLT-3 will take time and resources that we don’t have at this moment. Thus, we believe that this point should be addressed in follow-up studies.
REFERENCES
Borenstein, R., & Frenkel, N. (2009). Cloning human herpes virus 6A genome into bacterial artificial chromosomes and study of DNA replication intermediates. Proceedings of the National Academy of Sciences of the United States of America, 106(45). https://doi.org/10.1073/pnas.0908504106
Collin, V., Gravel, A., Kaufer, B. B., & Flamand, L. (2020). The promyelocytic leukemia protein facilitates human herpesvirus 6B chromosomal integration, immediate-early 1 protein multiSUMOylation and its localization at telomeres. PLoS Pathogens, 16(7). https://doi.org/10.1371/journal.ppat.1008683
Fang, Q., Chen, P., Wang, M., Fang, J., Yang, N., Li, G., & Xu, R.-M. (2016). Human cytomegalovirus IE1 protein alters the higher-order chromatin structure by targeting the acidic patch of the nucleosome. ELife, 5. https://doi.org/10.7554/elife.11911
Galloy, M., Lachance, C., Cheng, X., Distéfano-Gagné, F., Côté, J., & Fradet-Turcotte. (2021). Approaches to study native chromatin-modifying activities and function. Frontiers in Cell and Developmental Biology, Section Epigenomics and Epigenetics, In Press.
Jaworska, J., Gravel, A., Fink, K., Grandvaux, N., & Flamand, L. (2007). Inhibition of Transcription of the Beta Interferon Gene by the Human Herpesvirus 6 Immediate-Early 1 Protein. Journal of Virology, 81(11), 5737–5748. https://doi.org/10.1128/jvi.02443-06
Rodier, F., Coppé, J. P., Patil, C. K., Hoeijmakers, W. A. M., Muñoz, D. P., Raza, S. R., Freund, A., Campeau, E., Davalos, A. R., & Campisi, J. (2009). Persistent DNA damage signalling triggers senescence-associated inflammatory cytokine secretion. Nature Cell Biology, 11(8). https://doi.org/10.1038/ncb1909
Rodríguez, M. C., Dybas, J. M., Hughes, J., Weitzman, M. D., & Boutell, C. (2020). The HSV-1 ubiquitin ligase ICP0: Modifying the cellular proteome to promote infection. In Virus Research (Vol. 285). https://doi.org/10.1016/j.virusres.2020.198015
Sitz, J., Blanchet, S. A. S. A., Gameiro, S. F. S. F., Biquand, E., Morgan, T. M. T. M., Galloy, M., Dessapt, J., Lavoie, E. G. E. G., Blondeau, A., Smith, B. C. B. C., Mymryk, J. S. J. S., Moody, C. A. C. A., & Fradet-Turcotte, A. (2019). Human papillomavirus E7 oncoprotein targets RNF168 to hijack the host DNA damage response. Proceedings of the National Academy of Sciences of the United States of America, 116(39), 19552–19562. https://doi.org/10.1073/pnas.1906102116
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Referee #3
Evidence, reproducibility and clarity
In this manuscript, the authors report that human herpesvirus 6B (HHV-6B) infection suppresses the host cell's ability to induce ATM-dependent signaling pathways. At least one of the viral proteins named IE1 block ATM signaling and further homology-directed double-strand break (DSB) repair in these cells. The ATM-dependent DNA damage response (DDR) is activated by infection of many viruses and suppresses their replications. Some of them induce the degradation of the MRE11/RAD50/NBS1 (MRN) complex and prevent subsequent DDR signaling. In the case of HHV-6B IE1, the N-terminal domain of it interacts with the MRN complex protein NBS1, the interaction of which might recruit IE1 to DSB and the C-terminal domain of IE1 inhibits ATM. The authors also showed that depletion of NBS1 enhanced HHV-6B replication. Viral integration of HHV-6B into the cellular chromosomes was enhanced by the NSB1 depletion in ATL-negative HeLa cells, supporting the models that the viral integration occurs via telomere elongation rather than through DNA repair.
Major comments
This manuscript is well written and will be of interest to the readers. The data seems convincing and statistical analysis is adequate. However, the role and significance of HHV-6B IE1 in infected cells was not analyzed well. If there are not analyzed, the data only show the role of the MRN complex or the only a single protein NSB1 for HHV-6B replication and they cannot conclude that HHV-6B IE1 hampers the ATM signaling for proper viral replication. I have a few comments listed below to improve this manuscript. All of them might be required for a couple of months.
- (i) Lines 52, "Expression of immediate early protein 1 (IE1) was sufficient to recapitulate this phenotype" is not right. The authors showed that IE1 blocked ATM signaling in transient experiment but they did not show any evidence in infected cells. Kock down or Kock out of IE1 is important to conclude it.
- (ii) In Fig7, the role of the other factors in the ATM-dependent DDR (such as ATM) should be analyzed by knock down or inhibitors.
- (iii) The authors did not analyze the effect of viral manipulation as thy did not analyze KO or KD of IE1. Even if HHV-6B IE1 is essential for viral replication, they can use dominant negative mutant of IE1 or NSB1 determined in this manuscript.
- (iv) As discussed by the authors, HHV-6B IE1 inhibit DSB signaling through NSB1, but we cannot know how this inhibition (might be increase genome instability of both host and virus) enhances viral replication and integration. The readers are easy to understand if the authors described it in the discussion or analyzed by KD or KO of IE1 in infected cells.
Minor comments
- (i) Described in lines 354-356 are the case of lytic cycle only. In the lytic cycle, the infected cells will die soon after viral replication. and there is no chance to become tumor. However, the state of ciHHV-6 or latently infected cells can be affected by genome instability during IE1 expression. Please add discussion.
- (ii) Line114, Miura et al (J Infect Dis 223:1717-1723 [2021]) should be cited.
Significance
HHV-6B is ubiquitous herpesvirus which cause exanthem subitem and encephalitis, although effective antiviral is not established yet. Characteristically, HHV-6B has ability to integrate its genome into host. How HHV-6B replicate and integrate its genome in host cells is one of the most important question in this field. I am basic virologist mainly focusing on this virus and believe this manuscript includes important notion for our field.
To counteract ATM-mediated signaling, many viruses induce the degradation of the MRN complex and prevent subsequent DDR signaling. The mechanism of HHV-6B IE1 described in this manuscript is unique and might be interested by the readers from many fields.
Furthermore, around 1% of human populations harbor chromosomally integrated HHV-6B in their genome. The pathogenesis of it is not completely understand but must be important not only for virologist but also all of us.
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Referee #2
Evidence, reproducibility and clarity
Viruses have evolved different strategies by which they manipulate the host DNA damage response (DDR) in order to propagate in infected cells. This study shows how the human herpesvirus 6B (HHV-6B) blocks homology-directed double-stranded DNA break repair by the immediate early protein 1 (IE1) which they demonstrate inhibits the host ATM kinase. They employ microscopy and cytometry approaches to probe genomic instability, signaling, and interactions between virus and host. They use infection of MOLT-3 cells and induction of IE1 in U2OS cells to examine these mechanisms and the effects on genome stability. They show inhibition of H2AX phosphorylation, and inhibition of homology-directed repair with reporter assays. They discovered that IE1 interacts with the cellular NBS1 protein, localizes to DNA breaks, and inhibits activation of ATM kinase. They map two distinct domains that promote NBS1 interaction and the inhibition of ATM activation. They show that depletion of NBS1 promotes lytic replication in MOLT-3 cells, and also decreases the frequency of integration, at least in some semi-permissive cells.
Major:
- Although they have nicely mapped the interactions, the authors have not yet defined the mechanism of ATM inhibition. They propose a number of possibilities in the Discussion but none are yet tested experimentally. The manuscript would be strengthened by further exploration of these possibilities. Does the sequence or proposed structure give any insights into interactions that could be relevant? Is IE1 phosphorylated by ATM and could this affect binding of other proteins?
- Could the effects of IE1 be linked to other post-translational modifications? The literature suggests this protein to be SUMOylated. Is SUMOylation relevant to the effects on ATM activation? Does it also share other activities with herpesvirus proteins e.g. ubiquitinylation?
- Are the effects on the lifecycle (lytic replication and integration) affected by ATM kinase in the same way as NBS1?
Minor:
- In Figure 1 they look at micronuclei formation but MNi is not defined the main text.
Significance
Overall, the manuscript is well written the experiments are performed in a rigorous manner, and the biology uncovered is of broad scientific interest. It is now known that a number of DNA viruses inhibit aspects of the cellular DNA sensing and repair machinery to overcome antiviral responses and promote infection. Understanding how this achieved by different viral systems provides insights into cellular DNA damage signaling and repair. It also informs about how viruses can trigger genomic instability. In this case, the authors have uncovered a novel way that the ATM kinase is inhibited during HHV-6B infection by the IE1 protein. They show that HHV-6B infection induces genomic instability. Integration of the HHV-6 genome results in inherited chromosomally-integrated (ici)HHV-6A/B. They have some data to show that virus replication is inhibited by NBS1 and that viral integration may be partially impacted. These results have implications for understanding viral integration and genomic instability with this human pathogen. They advance the field and expand our understanding of how viruses manipulate repair pathways and lead to genomic instability. Strengths include the rigorous analysis of interactions with IE1 and impacts on cellular pathways. Limitations include the lack of mechanism for inhibition and the weaker links to viral biology. The results will be on interest to those studying virus-host interactions as well as those studying repair pathways beyond virus infection.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript Collin and colleagues found that the human herpesvirus 6B (HHV-6B) causes genomic instability in host cells by suppressing the host cell's ability to induce ATM-dependent signaling pathways. The authors show that the immediate early protein 1 (IE1) of HHV-6B is sufficient to block homology-directed double-strand break (DSB) repair and ATM-mediated DNA damage signaling. Interestingly, the authors show that IE1 does not affect the stability of the MRN complex, but instead uses two distinct domains to inhibit ATM activation. Finally, the authors show that suppression of NBS1 is critical for the ability of HHV-6B to replicate in permissive cells. In contrast, suppression of NBS1 increases the rate of integration in semi permissive cells. Overall, this study provides a mechanistic insight into HHV-6B infection and viral integration into telomeres may promote genomic instability and the development of certain diseases associated with inherited chromosomally integrated form of HHV-6B.
Significance
Overall, this is a superb manuscript, the data are clear, well controlled, and well presented. This reviewer has only a minor suggestion/ comment.
The authors show convincingly that E1a can bind NBS1 and suppress ATM activation. However, it is not clear whether suppression of ATM is critical for HHV-6 replication. The ideal experiment would be an infection with a virus depleted of E1A (or expressing a defective E1A mutant). I realize that this would be a challenging experiment. An alternative experiment would be to test whether suppression of ATM has the same effect on HHV-6 replication and integration as NBS1 depletion.
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Reply to the reviewers
Manuscript number: RC-2022-01803
Corresponding author(s): Brittany A., Ahlstedt, Rakesh, Ganji, Sirisha Mukkavalli, Joao A., Paulo, Steve P., Gygi, Malavika, Raman
If you wish to submit a full revision, please use our "Full Revision" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]
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 insightful comments and agree that the many of these revision experiments will improve the strength of our manuscript. Some of these we have already completed or are in the process of completing which will be outlined below. In particular, the reviewers asked that we investigate the mechanistic link between increased translation and UPR induction. We have detailed the studies that we will perform to establish this connection in detail below.
Description of the planned revisions
Response to Reviewer 1:
- The authors need to express UBXN1 and mutants lacking either the UBX or UBA domain in UBXN1 knockout cells to test whether the ER stress phenotype (Figure 1) and the protein upregulation phenotype (Figure 5A-F) can be rescued. This would eliminate the possibility that the reported phenotypes are the off-target effects of CRISPR.
- We will express the Myc-tagged wildtype UBXN1 and UBX or UBA point mutants (used in translation rescue studies in Figure 6) into UBXN1 knockout (KO) cells to determine whether the ER stress phenotype can be rescued. We will determine the level of xbp1s by real-time PCR and BiP by immunoblot.
- The studies in Figure 5 A-F were completed in cells depleted of UBXN1 with siRNA, not the CRISPR knockout cells. Thus, it is unlikely an off-target effect of CRISPR. We will attempt rescue of this phenotype with the wildtype and mutant constructs.
For Figure 2, please indicate whether the repeat is a biological replicate or a technical replicate from RT-PCR.
- We apologize for the omission. The data from the RT PCR studies in Figure 2 are biological replicates – the figure legend and main text of the manuscript will be edited to clarify this.
In Figure 1A, the authors show that the knockout of UBXN1 causes an upregulation of phosphorylated eIF2alpha, which is known to suppress protein translation globally. In this regard, it is surprising to see the authors also concluded from Figure 7 that there is an upregulation of protein translation in UBXN1 knockout cells. The authors do not provide any explanation on how these seemingly contradictory phenotypes could be seen in the same cells.
- We will provide a detailed discussion of the apparent paradox between upregulation of phosphorylated eIF2a and increased protein translation. Several prior studies have demonstrated that elevated expression of ATF4 (as we observe in UBXN1 KO cells) activates a transcriptional program that restarts translation. This occurs through the upregulation of the phosphatase PPP1R15a that dephosphorylates eiF2a, as well as aminoacyl tRNA synthetases and ribosomal subunits. We propose that elevated ATF4 levels leads to premature translational restart in UBXN1 KO cells. In addition, our data suggests that UBXN1 represses translation upstream of UPR activation and thus and increase in protein translation dysregulates ER-proteostasis which hyperactivates the UPR.
Any evidence that UBXN1 is associated with translating ribosomes?
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We now have new data that UBXN1 is associated with 40S, 60S, and 80S ribosomal fractions as well as actively translating polysome fractions that we isolated by polysome purification. In agreement with our finding that the role of UBXN1 in repressing translation is independent of p97, p97 appears to associate largely with the 40S, 60S, and 80S ribosomal fractions but not with the actively translating polysomes. This data will be included in the revised manuscript. Response to Reviewer 2:
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Authors found that significant enrichment of the ER proteins in UBXN1 KO cells, while there is no change in the abundance of proteins in the cytosol or nucleus. Mitochondrial proteins are even down-regulated in UBXN1 KO cells. I found these observations very interesting. However, I was frustrated that authors did not investigated the reason why such differences are associated in UBXN1-suppressed cells. Authors demonstrate that depletion of UBXN1 resulted in suppression of protein synthesis, but did not address whether ER proteins are specifically repressed by UBXN1 or it represses translation globally, as noted in their Discussion section. Do the mRNAs encoding signal sequence at the N-terminus of their products are specifically translated in UBXN1-suppressed cells? Do the translations of mRNAs encoding mitochondria translocation signals are suppressed in UBXN1 KO cells? It should be possible to investigate these issues by using appropriate model ER- or mitochondrial proteins with or without specific signal sequences. Such kind of analysis should be necessary to support the claim of this manuscript.
- Previous studies by Luke Wiseman’s group showed that PERK activation resulted in hyperfusion of the mitochondria and loss of Tim17 leading to decreased mitochondrial import. We already show that mitochondrial proteins are downregulated (by TMT proteomics and by immunoblotting). We now have preliminary data that mitochondria are more fused in UBXN1 KO cells consistent with data from the Wiseman group. We will include this in the resubmission.
- In addition, we have re-analyzed our TMT proteomics data to parse out proteins with ER-signal sequences and define the topology of ER proteins (Type 1, 2, multimembrane spanning and luminal proteins) and those with mitochondrial targeting sequences. This data will be included in the revised manuscript.
Related to my previous comments, ER-targeted mRNAs are known to be degraded by a process termed RIDD in the case of ER stressed condition. Since the rapid degradation of mRNAs through RIDD functions to alleviate ER stress by preventing the continued influx of new polypeptides into the ER, I wondered why UBXN1 depletion greatly stimulates ER protein synthesis, escaping IRE1-dependent mRNA degradations. Does UBXN1 depletion suppress RIDD?
- In the revised manuscript, we will determine the relative mRNA abundance of the bona fide RIDD targets BLOC1S1 and CD59 by quantitative PCR in cells stressed with dithiothreitol (DTT). We will utilize previously published and validated primers for each target to quantify RIDD activity in wildtype and UBXN1 KO cells. These studies will address whether loss of UBXN1 impacts IRE1-dependent RIDD.
Authors mentioned that the elevated levels of ER proteins are not due to increased transcription of target genes. However, they only provided the quantification of prp transcript levels, which was unchanged between wildtype and UBXN1 KO cells. To support this important conclusion, it is necessary to provide whole transcriptome data to compare the expression levels of corresponding ER proteins (quantified by their proteomics data) and transcripts (quantified by, for an example, RNA-seq analysis).
- We thank the reviewer for this comment. Currently, we show that mRNA levels of Prp do not significantly change between control and siUBXN1 cells (Supplementary Figure 4). For a more comprehensive analysis, we will additionally assess the mRNA levels of the proteins we determinized to be significantly enriched in Figure 5 (AGAL, ALPP2 and TRAPa). RNA sequencing is currently beyond the scope of this study.
Authors claimed that UBXN1 loss is detrimental to cell viability and have elevated levels of the apoptosis in the face of ER stress. However, authors did not examine apoptotic cell death in UBXN1 KO cells. They only provided evidence for defective proliferation of cells and transient induction of CHOP expression, but these are not enough to support the ER-stress induced apoptosis.
- We will address the levels of apoptotic cell death in wildtype and UBXN1 KO cells by assessing PARP, caspase-3, or caspase-8 cleavage in these cells by immunoblot.
Authors showed that UBA domain of UBXN1 is critical for suppressing protein synthesis. Could you provide a bit more detailed discussion how UBA domain modulates protein translational events and promote expressions of ER-related proteins. Have you ever checked whether UBA domain of UBXN1 is necessary for suppressing UPR-specific target gene expressions?
- We will express the Myc-tagged wildtype UBXN1 and UBX or UBA point mutants (used in translation rescue studies in Figure 6) into UBXN1 knockout (KO) cells to determine whether the ER stress phenotype can be rescued.
- We will also include a discussion on how the UBA domain in UBXN1 may recognize distinct ubiquitylation events on ribosomes that modulate their abundance and function. Response to Reviewer 3:
(Major comments)
- My main reservation about the current manuscript is whether the UPR activation can be directly ascribed to the loss of UBXN1. The authors do not differentiate between acute depletion (through siRNA in Fig. 5) versus permanent UBXN1 knockout in most of the experiments. The latter may lead to extensive adaptation of the cellular proteome due to chronic stress. Prior studies from the authors have shown that UBXN1 knockout leads to loss of aggreasomes. This raises a major question whether the observed UPR activation can be directly attributed to UBXN1 loss or be an indirect result of adaptation in the knockout cells, for instance due to accumulation of BAG6 substrates in insoluble aggregates as the authors have shown previously (ref. 40). Along those lines, the authors already showed in the same study that UBXN1 knockout cells are more sensitive to proteotoxic stress.
- We agree with the reviewer that cells can adapt to CRISPR knockout. However, the IRE1a clustering studies found in Figure 1 were completed in the context of acute depletion of UBXN1 by siRNA and demonstrate a significant increase in IRE1a clustering when UBXN1 is depleted.
- We now have new data that that acute depletion of UBXN1 with siRNA results in a significant increase in BiP and ATF4 expression as well as ATF6 N-terminal processing.
- Furthermore, we have new data that acute depletion of UBXN1 with siRNA phenocopies UBXN1 KO in terms of increased puromycin incorporation into newly synthesized proteins.
- Thus, we will have both genetic knockout as well as siRNA acute depletion for all major studies. We will include these new studies in the revised manuscript.
The later results in the study nicely show that the repressed protein translation phenotype is dependent on the ubiquitin binding domain of UBXN1. These segregation-of-function mutants and complementation experiments could be easily used to more clearly distinguish whether the UPR activation can be directly attributed to UBXN1 and the increase in protein translation. For instance, can overexpression of UBXN1 in the knockout background suppress the UPR activation? Is the UBX-domain mutant capable of suppressing the UPR phenotype? These results would provide critical support as to whether the UPR activation is a direct result of the loss of UBXN1.
- We will express the Myc-tagged wildtype UBXN1 and UBX or UBA point mutants (used in translation rescue studies in Figure 6) into UBXN1 knockout (KO) cells to determine whether the ER stress phenotype can be rescued. We will determine the level of xbp1s by real-time PCR and BiP by immunoblot.
- To delineate the relationship between UPR activation and protein translation, we will halt protein synthesis with the translational elongation inhibitor cycloheximide and assess UPR activation in wildtype and UBXN1 KO cells. If increased protein translation in UBXN1 KO cells is what causes UPR activation, we anticipate that cycloheximide will rescue UPR activation in UBXN1 KO cells back to wildtype levels.
Similarly, the authors use transient siRNA knockdown of UBXN1 in Fig. 5 and Supp. Fig. 4, but do not reassess the UPR activation under these conditions. It would be important to validate that the acute UBXN1 knockdown can recapitulate the UPR activation phenotype.
- Please see comment 1 above.
I am puzzled by the interpretation of the AGAL degradation experiments in Supplemental Figure 4F. Clearly, the rate of AGAL degradation is much faster in WT cells than in UBXN1 knockout cells as indicated by the slope of the curves between 2-4 hours. I disagree with the interpretation that UBXN1 knockout does not impact AGAL turnover. It is not valid to make the comparison at 9 hours because hardly any AGAL substrate is remaining. Importantly, this experiment raises a larger question: Are other ER client degradation rates affected by the UBXN1 knockout? And is the UPR activation more generally due to accumulation of misfolded ER proteins? Their prior publication (ref. 40) evaluated several ERAD clients where UBXN1 was dispensable, but it could be possible that UBXN1 has a more specialized client pool. Showing quantification of the PrP CHX chase would also be helpful - from the single replicate it looks like more PrP remaining in the UBXN1 knockout at 8 hours (Supp. Figure 4G).
- Our previous ERAD reporter study using three distinct ERAD clients that are routinely used to assess ERAD found no role for UBXN1 in ERAD (Ganji et al MCB 2018). We do agree with the reviewer that UBXN1 may have discrete roles in regulating the degradation of select p97 ER clients. Determining this in an unbiased and comprehensive manner would require pulse chase SILAC proteomics or similar methodologies which are beyond the scope of the current study. We will therefore evaluate whether loss of UBXN1 affects the rate of degradation of additional ER-client proteins that we identified via TMT. Additionally, we will include a quantification of PrP cycloheximide chase.
It would be helpful for the manuscript to clearly distinguish between 1) upregulation of ER proteostasis factors because of ER stress/UPR, and 2) upregulation of secreted clients (AGAL, PrP) which may be partly due to increased translation rates but could also be due to reduced degradation. Many of the hits from the proteomics experiments are ER proteostasis factors that are part of the adaptive stress response (SEC61B, SEC63, CANX, SSR1/2/3, STT3B, RPN1, RPN2, SEC61A1 - compare to ref 12: most are direct IRE1/XBP1s targets). Their increased expression does not lead to increased ER stress as they are involved in the resolution of ER stress. It appears to be circular logic that increased expression of UPR targets would lead to more UPR activation. Currently, the authors do not clearly disentangle the increased expression of endogenous ER proteins from the proteomics experiment versus overexpression of exogenous secreted clients.
- We identify many ER proteins with increased abundance in UBXN1 KO cells that are not transcriptional targets of the IRE1-UPR pathway. We will re-format the TMT data to more comprehensively characterize the proteins that we identify (known UPR transcriptional targets, membrane embedded, soluble clients etc.).
- We will change the language in the current manuscript to clearly demarcate the difference between an increase of ER proteostasis factors in response to ER stress, and the upregulation of secreted proteins. Additionally, we will emphasize the secretory proteins that are significantly enriched in UBXN1 KO cells in our proteomics figures to demonstrate the increase of non-ER stress responsive clients.
The authors should tone down on broad generalizations, for instance in lines 306-309: ER aggregation was only observed for a single client protein (AGAL). Further, only a single mitochondrial protein was observed to be downregulated (TOMM20).
- We have included the quantifications of the relative expression levels of three mitochondrial proteins, two of which are significantly reduced (TOMM20 and CYC1).
- Additionally, we have new data where we immunoblotted for additional mitochondrial import factors and observed significant reduction of the mitochondrial proteins TIMM23 and TOMM70A which will be included in the revised manuscript.
- We also plan to examine the levels of the TIMM17A subunit of the TIMM23 complex in UBXN1-depleted cells. TIMM17A is degraded in response to ER stress to prevent protein import into the mitochondria. (Rainbolt, T. et al. Cell Metab 2013)
- The language of the manuscript will be changed to tone down on broad generalizations. (Minor comments)
Does UBXN1 localization to the ER/microsomes fraction depend on p97? What happens in UBX-domain mutant?
- We will isolate ER-microsomes from UBXN1 KO cells where we have expressed wildtype and UBX/UBA domain mutants to address if localization is dependent on ubiquitin or p97 interaction.
In Fig. 1A it is surprising that no BiP is detected at 0 hours as BiP is highly expressed even in the absence of ER stress. Can the authors comment on this discrepancy.
- We provide low exposures of the immunoblots as the UBXN1 KO cells have very high levels of BiP compared to control. We will provide alternative blots where the BiP levels at t=0 in control cells is more obvious.
The authors use different ER stressors interchangeably: DTT, Tunicamycin, Thapsigargin. While all results in UPR activation, they do so through different mechanisms and with slight nuances that may be worth considering for the experiments and interpretations.
- We thank the reviewer for this comment and agree that these stressors can impact the ER and UPR activation in distinct ways. Our rationale for using these agents interchangeably was to demonstrate the UPR induction in UBXN1 null cells occurs irrespective of the type of stress.
- DTT is a severe stressor and we used tunicamycin and thapsigargin in some assays (imaging etc.) as they are less toxic and more amenable to downstream analysis. We will include text that explains our rationale better.
Line 198: "Hierarchical clustering analysis demonstrates that the gene expression pattern observed in UBXN1 KO cells more closely resembles wildtype cells stressed with DTT than untreated wildtype cells based on similar log2 fold change values (Figure 2)." Where is this clustering shown?
- We apologize that this was not clear in the figure. We will edit the figure to make the clustering more obvious.
What are the downregulated UPR genes in Fig. 2, and may this hold significance?
- The reviewer points out an interesting observation. Many of the downregulated transcripts are ERAD components. The significance of this is presently unclear and we would require RNA-seq analysis to make a more educated conclusion. However, this finding may point to an environment that has a greater need to induce folding than degradative components. We will include a discussion of this in the revision.
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.
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.
Response to Reviewer 1:
- Taking the increased protein translation phenotype as an example, does this indicate UBXN1 is a translation suppressor for those ER-associated proteins?
- We thank the reviewer for this comment. We are indeed very interested in determining whether UBXN1 represses the translation of ER proteins. We are in the process of identifying proteins that are translated in UBXN1 null cells using O-propargyl-puromycin (OPP) labelling and mass spectrometry. However, given the timeframe for these studies, this cannot be accomplished in this revision.
How can UBXN1 selectively inhibit the translation of a subset of proteins?
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Recent studies suggest that ribosome populations are quite heterogeneous, and ribosome associated proteins can help tune translation of select proteins. For example, pyruvate kinase muscle (PKM) associates with ER docked ribosomes to regulate the translation of ER proteins in particular. We find that UBXN1 is present on ER membranes and localizes to polysomes and thus may regulate the translation of specific proteins. Studies are underway to test this hypothesis but are beyond the scope for this present study. Response to Reviewer 2:
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Authors found that significant enrichment of the ER proteins in UBXN1 KO cells, while there is no change in the abundance of proteins in the cytosol or nucleus. Mitochondrial proteins are even down-regulated in UBXN1 KO cells. I found these observations very interesting. However, I was frustrated that authors did not investigated the reason why such differences are associated in UBXN1-suppressed cells. Authors demonstrate that depletion of UBXN1 resulted in suppression of protein synthesis, but did not address whether ER proteins are specifically repressed by UBXN1 or it represses translation globally, as noted in their Discussion section. Do the mRNAs encoding signal sequence at the N-terminus of their products are specifically translated in UBXN1-suppressed cells? Do the translations of mRNAs encoding mitochondria translocation signals are suppressed in UBXN1 KO cells? It should be possible to investigate these issues by using appropriate model ER- or mitochondrial proteins with or without specific signal sequences. Such kind of analysis should be necessary to support the claim of this manuscript.
- Please see comment 1 above.
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Referee #3
Evidence, reproducibility and clarity
Summary:
Ahlstedt et al. investigate a new role for the p97 adapter protein UBXN1 in negatively regulating the ER unfolded protein response. The study starts from the observations that knockdown of UBXN1 in a previously generated HeLa cell line leads to induction of unfolded protein response markers, and the knockout cells display more pronounced UPR activation upon ER stress. This elevated UPR signaling renders the UBXN1 cells more prone to cell death. Global proteomics experiments similarly show an increased abundance of ER localized proteins, although it is not clearly delineated which of those are the result of UPR activation. The authors then probe the expression of two secretory client proteins, alpha-galactosidase (AGAL) and prion protein (PrP) and find that UBXN1 transient knockdown leads to ER accumulation of the two proteins and increased aggregation upon ER stress. The authors claim that degradation of these ER client proteins in unaffected by the UBXN1 knockdown, but accumulation may instead be due to increased protein translation. Indeed, they surprisingly find that UBXN1 knockout leads to constitutively elevated protein translation. This result points to a previously unknown role of UBXN1 in repressing protein synthesis. Complementation with UBXN1 mutants demonstrate that the translation repression is dependent on the ubiquitin binding activity of UBXN1 but that p97 is dispensable. Further investigation into the molecular mechanism for the translation repression remains reserved for a future manuscript.
Major comments:
- My main reservation about the current manuscript is whether the UPR activation can be directly ascribed to the loss of UBXN1. The authors do not differentiate between acute depletion (through siRNA in Fig. 5) versus permanent UBXN1 knockout in most of the experiments. The latter may lead to extensive adaptation of the cellular proteome due to chronic stress. Prior studies from the authors have shown that UBXN1 knockout leads to loss of aggreasomes. This raises a major question whether the observed UPR activation can be directly attributed to UBXN1 loss or be an indirect result of adaptation in the knockout cells, for instance due to accumulation of BAG6 substrates in insoluble aggregates as the authors have shown previously (ref. 40). Along those lines, the authors already showed in the same study that UBXN1 knockout cells are more sensitive to proteotoxic stress.
- The later results in the study nicely show that the repressed protein translation phenotype is dependent on the ubiquitin binding domain of UBXN1. These segregation-of-function mutants and complementation experiments could be easily used to more clearly distinguish whether the UPR activation can be directly attributed to UBXN1 and the increase in protein translation. For instance, can overexpression of UBXN1 in the knockout background suppress the UPR activation? Is the UBX-domain mutant capable of suppressing the UPR phenotype? These results would provide critical support as to whether the UPR activation is a direct result of the loss of UBXN1.
- Similarly, the authors use transient siRNA knockdown of UBXN1 in Fig. 5 and Supp. Fig. 4, but do not reassess the UPR activation under these conditions. It would be important to validate that the acute UBXN1 knockdown can recapitulate the UPR activation phenotype.
- I am puzzled by the interpretation of the AGAL degradation experiments in Supplemental Figure 4F. Clearly, the rate of AGAL degradation is much faster in WT cells than in UBXN1 knockout cells as indicated by the slope of the curves between 2-4 hours. I disagree with the interpretation that UBXN1 knockout does not impact AGAL turnover. It is not valid to make the comparison at 9 hours because hardly any AGAL substrate is remaining. Importantly, this experiment raises a larger question: Are other ER client degradation rates affected by the UBXN1 knockout? And is the UPR activation more generally due to accumulation of misfolded ER proteins? Their prior publication (ref. 40) evaluated several ERAD clients where UBXN1 was dispensable, but it could be possible that UBXN1 has a more specialized client pool. Showing quantification of the PrP CHX chase would also be helpful - from the single replicate it looks like more PrP remaining in the UBXN1 knockout at 8 hours (Supp. Figure 4G).
- It would be helpful for the manuscript to clearly distinguish between 1) upregulation of ER proteostasis factors because of ER stress/UPR, and 2) upregulation of secreted clients (AGAL, PrP) which may be partly due to increased translation rates but could also be due to reduced degradation. Many of the hits from the proteomics experiments are ER proteostasis factors that are part of the adaptive stress response (SEC61B, SEC63, CANX, SSR1/2/3, STT3B, RPN1, RPN2, SEC61A1 - compare to ref 12: most are direct IRE1/XBP1s targets). Their increased expression does not lead to increased ER stress as they are involved in the resolution of ER stress. It appears to be circular logic that increased expression of UPR targets would lead to more UPR activation. Currently, the authors do not clearly disentangle the increased expression of endogenous ER proteins from the proteomics experiment versus overexpression of exogenous secreted clients.
- The authors should tone down on broad generalizations, for instance in lines 306-309: ER aggregation was only observed for a single client protein (AGAL). Further, only a single mitochondrial protein was observed to be downregulated (TOMM20).
Minor comments
- Does UBXN1 localization to the ER/microsomes fraction depend on p97? What happens in UBX-domain mutant?
- In Fig. 1A it is surprising that no BiP is detected at 0 hours as BiP is highly expressed even in the absence of ER stress. Can the authors comment on this discrepancy.
- The authors use different ER stressors interchangeably: DTT, Tunicamycin, Thapsigargin. While all results in UPR activation, they do so through different mechanisms and with slight nuances that may be worth considering for the experiments and interpretations.
- Line 198: "Hierarchical clustering analysis demonstrates that the gene expression pattern observed in UBXN1 KO cells more closely resembles wildtype cells stressed with DTT than untreated wildtype cells based on similar log2 fold change values (Figure 2)." Where is this clustering shown?
- What are the downregulated UPR genes in Fig. 2, and may this hold significance?
Significance
General assessment: The authors broadly characterize the UPR activation in the UBXN1 knockout cells, looking both at gene targets by Western blot and qPCR, and characterize the activation of individual sensors (ATF6 cleavage and IRE1alpha clustering). Proteomics results further corroborate the upregulation of ER-localized proteins, although the robustness of the findings is surprising considering that only 2 replicates were included in the mass spectrometry experiment. Most other experiments are technically sound, for instance the puromycilation translation assays. One of the key limitations of the is that the authors fail to make use of their extensive prior toolset on UBXN1, particularly the segregation-of-function mutations for p97 and ubiquitin binding, as well as the knockdown cell lines with inducible overexpression of UBXN1 to rescue the phenotypes. These tools could probe a direct involvement of UBXN1 in the UPR repression, and whether this activity is truly independent of p97. A related limitation is that results are often over-interpreted and too far generalized (see examples above), or wrongly interpreted (see AGAL degradation rates).
Advance: The AAA+ ATPase VCP/p97 has many divergent cellular roles that are in part mediated by a variety of different adaptor proteins. The authors have previously discovered the important role for UBXN1 in recruiting p97 to mislocalized cytosolic proteins targeted to the BAG6 complex. The current study now aims to establish a new role for UBXN1 in regulating the unfolded protein response. As it stands, the findings that UBXN1 knockdown results in UPR activation and impacts translation rates are solid but largely descriptive in nature. These findings merit reporting but require that the authors tone down their conclusions about a direct role for UBXN1 as a regulator of the UPR. Alternatively, if the authors choose to stick with their current model for a direct involvement of UBXN1, they need to establish the mechanistic link more clearly.
Audience: In the current form, the manuscript should appeal to a broad biochemistry and cell biology readership interested in topics related to proteostasis, protein quality control, and stress signaling.
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Referee #2
Evidence, reproducibility and clarity
RC-2022-01803 "UBXN1 maintains ER proteostasis and represses UPR activation by modulating translation independently of the p97 ATPase" By Ahlstedt et al.
Comments to the Author
UBXN1 is a VCP adaptor UBX domain protein which is known to be involved in elimination of ubiquitylated cytosolic proteins bound to the BAG6 complex. In this study, authors demonstrated that cells depleted of UBXN1 have elevated UPR activation, even without external ER stresses. Cells devoid of UBXN1 have significant and global up-regulation of UPR-specific target genes, and these cells are more sensitive to ER stress than their wildtype counterparts. Using quantitative tandem mass tag proteomics of UBXN1 deleted cells, authors found that significant enrichment of the abundance of ER proteins involved in protein translocation, protein folding, quality control, and the ER stress response in an ERAD-independent manner. Notably, they observed no change in the abundance of proteins in the cytosol or nucleus, and significant decrease in the expression of several mitochondrial proteins when UBXN1 was depleted. Authors further demonstrate that UBXN1 is a translation repressor, and its UBA domain is critical for suppressing protein synthesis. Thus, increased influx of proteins into the ER in UBXN1 KO cells causes UPR activation. Authors concluded that they have identified a new regulator of protein translation and ER proteostasis.
My specific comments were provided as follows.
Comments
- Authors found that significant enrichment of the ER proteins in UBXN1 KO cells, while there is no change in the abundance of proteins in the cytosol or nucleus. Mitochondrial proteins are even down-regulated in UBXN1 KO cells. I found these observations very interesting. However, I was frustrated that authors did not investigated the reason why such differences are associated in UBXN1-suppressed cells. Authors demonstrate that depletion of UBXN1 resulted in suppression of protein synthesis, but did not address whether ER proteins are specifically repressed by UBXN1 or it represses translation globally, as noted in their Discussion section. Do the mRNAs encoding signal sequence at the N-terminus of their products are specifically translated in UBXN1-suppressed cells? Do the translations of mRNAs encoding mitochondria translocation signals are suppressed in UBXN1 KO cells? It should be possible to investigate these issues by using appropriate model ER- or mitochondrial proteins with or without specific signal sequences. Such kind of analysis should be necessary to support the claim of this manuscript.
- Related to my previous comments, ER-targeted mRNAs are known to be degraded by a process termed RIDD in the case of ER stressed condition. Since the rapid degradation of mRNAs through RIDD functions to alleviate ER stress by preventing the continued influx of new polypeptides into the ER, I wondered why UBXN1 depletion greatly stimulates ER protein synthesis, escaping IRE1-dependent mRNA degradations. Does UBXN1 depletion suppress RIDD?
- Authors mentioned that the elevated levels of ER proteins are not due to increased transcription of target genes. However, they only provided the quantification of prp transcript levels, which was unchanged between wildtype and UBXN1 KO cells. To support this important conclusion, it is necessary to provide whole transcriptome data to compare the expression levels of corresponding ER proteins (quantified by their proteomics data) and transcripts (quantified by, for an example, RNA-seq analysis).
- Authors claimed that UBXN1 loss is detrimental to cell viability and have elevated levels of the apoptosis in the face of ER stress. However, authors did not examine apoptotic cell death in UBXN1 KO cells. They only provided evidence for defective proliferation of cells and transient induction of CHOP expression, but these are not enough to support the ER-stress induced apoptosis.
- Authors showed that UBA domain of UBXN1 is critical for suppressing protein synthesis. Could you provide a bit more detailed discussion how UBA domain modulates protein translational events and promote expressions of ER-related proteins. Have you ever checked whether UBA domain of UBXN1 is necessary for suppressing UPR-specific target gene expressions?
Significance
Although the discovery in this manuscript might be potentially interesting for broad audience, the presented study did not provide enough mechanistic insights and their data lacks vital evidences to support their conclusion. I found that the data are preliminary to discuss the validity of this finding. The inadequacy of these points makes this manuscript unsuitable for publication at this stage.
My expertise is cell biology and biochemistry for protein quality control.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, Ahlstedt et al. study UBXN1, an adaptor of the p97/VCP AAA ATPase, using a cell line deficient for UBXN1. They found that the knockout of UBXN1 activates ER stress and sensitizes cells to ER stress-induced cell death. They used a proteomic approach to analyze the change in the global proteome in UBXN1 knockout cells. Interestingly, they found many proteins are upregulated in UBXN1 knockout cells, which appears to be regulated at a post-transcriptional level. Using puromycin labeling, they found that protein translation appears to be upregulated in UBXN1 knockout cells.
Major comments:
The conclusions of the manuscript are generally well supported by experimental data, which are of high quality. The presentation is clear. In my opinion, a few issues need to be addressed to further strengthen their conclusions. 1. The authors need to express UBXN1 and mutants lacking either the UBX or UBA domain in UBXN1 knockout cells to test whether the ER stress phenotype (Figure 1) and the protein upregulation phenotype (Figure 5A-F) can be rescued. This would eliminate the possibility that the reported phenotypes are the off-target effects of CRISPR. 2. For Figure 2, please indicate whether the repeat is a biological replicate or a technical replicate from RT-PCR. 3. In Figure 1A, the authors show that the knockout of UBXN1 causes an upregulation of phosphorylated eIF2alpha, which is known to suppress protein translation globally. In this regard, it is surprising to see the authors also concluded from Figure 7 that there is an upregulation of protein translation in UBXN1 knockout cells. The authors do not provide any explanation on how these seemingly contradictory phenotypes could be seen in the same cells.
Significance
p97/VCP is an important member of the AAA ATPase family that has a variety of functions. It interacts with a collection of adaptor proteins that all contain a UBX domain. These adaptors help to link the ATPase to the correct substrate in cells. The best-established function of p97/VCP is its role in ERAD, in which it acts together with its adaptors Ufd1-Npl4 and UBXD8 to extract retrotranslocated proteins from the ER for proteasomal degradation. UBXN1 is not required for ERAD. Instead, it appears to be a negative regulator of ERAD. Previous studies have also implicated it in mitophagy (Mengus C., Autophagy, 2022) and aggresome formation (from this group). Overall, the published studies did not pinpoint the precise cellular function of UBXN1.
This work characterizes the cellular phenotypes associated with UBXN1 loss of function. The information reported here is important, but the biological significance is limited. This is mainly because the authors entirely rely on a genetic approach. While the reported phenotypes associated with UBXN1 deficiency is solid, it is unclear what the underlying mechanisms are. It is not clear whether or not these phenotypes are interconnected, nor is it clear whether UBXN1 is a direct regulator of these processes. Taking the increased protein translation phenotype as an example, does this indicate UBXN1 is a translation suppressor for those ER-associated proteins? How can UBXN1 selectively inhibit the translation of a subset of proteins? Any evidence that UBXN1 is associated with translating ribosomes?
In summary, because of the limited mechanistic insights on UBXN1 function, the study may only be interesting to a specialized audience.
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Reply to the reviewers
- Reviewer #1 (Evidence, reproducibility and clarity (Required))*
Summary: ER+ breast cancer is the most common form of cancer. Targeting ER-alpha transcriptional cofactors present one potential method to target the disease. The authors demonstrate that MYSM1 is a histone deubiquitinase and a novel ER cofactor, functioning by up-regulating ER action via histone deubiquitination. Loss of MYSM1 attenuated cell growth and increase breast cancer cell lines' sensitivity to anti-estrogens. The authors, therefore, propose MYSM1 as a potential therapeutic target for endocrine resistance in Breast cancer. *
*Major Comments: *
The data as presented is convincing, and the evidence for the role of MYSM1 as a co-activator of ER-alpha is extensive. Given the amount of data, I do not believe any additional experiments are needed. I could not find any description of ethics for the patient samples used.
Response: Appreciate for the positive response from the reviewer. According to the important suggestions, the ethics approval for the patient specimens have been included in the “Materials and methods” part.
Minor Comments:
The data as presented is convincing, and the evidence for the role of MYSM1 as a co-activator of ER-alpha is extensive. Given the amount of data, I do not believe any additional experiments are needed. I could not find any description of ethics for the patient samples used.
- Response: Appreciate for the positive response from the reviewer. According to the important suggestions, the ethics approval for the patient specimens have been included in the “Materials and methods” part.
(1)- Figure 4C - is the increase of binding in response to Estrogen significant? It is an important control to show for MCF7 as Fig 4B is in T47D.
Response: According to the comments from reviewers, we conducted statistical difference analysis in Figure 4C, our results have shown that the recruitment of MYSM1 or ERa on c-Myc ERE region is significantly increased upon E2 treatment in MCF-7 cells.
*(2)- Figure 6 - Can we clarify that B = Before, A = After *
Response: Apologize for the unclear description in Figure 6. As clarified by the reviewer, “B” represents before AI treatment, “A” represents after AI treatment. We have included the description in the “Figure legends” section.
(3)- The use of Fig EV was confusing to me, I assume it means supplementary?
Response: Thank you for your question. Since our priority affiliate journal is belong to EMBO Press, this manuscript was written according to the relevant requirements and “EV” is the abbreviation of “Expanded View”, which is the same as that of the supplementary figures.
Reviewer #1 (Significance (Required)): - Discovery science to understand the regulation of the ER is critical in discovering new opportunities to target breast cancer. As far as I can tell this is the first study where MYSM1 is a co-regulator of the ER. - The significance would be greatly increased if the manuscript identified opportuinities to target the ER via this pathway using existing compounds. However, it is reasonable to consider this is beyond the scope of this study.
Response: According to your valuable suggestion, we thus turned to screen the commercially-available compound in ZINC database to find the compounds that could spatially interact with MYSM1 protein, thereby inhibiting the activity of MYSM1. We plan to perform the additional biological function experiments to explore the effect of MYSM1-targeting compounds on the sensitivity of breast cell lines to anti-estrogen treatment.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
*Below I outline a few suggestions that can help clarify specific aspects of the study. *
Fig. 2: Ideally a rescue study with a wild-type and catalytically mutant MYSM1 should be performed.
Response: Thank you for your suggestion. To address this point, we will perform a rescue study with a wild-type and catalytically mutant MYSM1 in the breast cancer cells with stable knocked down of MYSM1 to examine the corresponding protein expression of ERa target genes.
What is the ERa interactome in the presence and absence of MYSM1? Proteomics studies upon shMYSM1 should be performed. Alternatively, a better characterization of ERa-containing complexes upon shMYSM1 should be performed.
Response: We agree with the reviewer’s suggestion to functionally address the influence of MYSM1 on ERa interactome. In breast cancer cells with the presence or absence of MYSM1, Co-IP experiments will be conducted to examine the influence of MYSM1 on the interaction between ERa and KAT2B, EP300 and CREBBP complex, which are predicted from String database.
*Fig. 3: Does MYSM1 control its own protein via deubiquitination? *
Response: We thank the reviewer for this suggestion and it provides us with a novel perspective upon MYSM1 investigation of whether MYSM1 is the deubiqutination substrate of itself. We would first transfect MYSM1-FL or MYSM1-ΔMPN plasmids and detect whether the endogenous MYSM1 expression changes. Next step, ubiquitination assays will be performed to determine whether MYSM1 control its own protein via deubiquitination.
*Fig. 4: I propose that the authors perform MYSM1 ChIP-Seq to better show the MYSM1 distribution and overlap with ERa distribution. *
Response: Appreciate for the reviewer for the valuable and important comments. ChIP-seq will be additionally performed in MCF-7 cells with MYSM1 antibody to examine the MYSM1 occupation on global chromatin in response to E2 and to show its overlap with ERa distribution.
Fig. 7. Is there a correlation between MYSM1 mRNA and protein levels in cancer and physiological samples? How is the MYSM1 transcriptionally regulated in physiological and cancer cells?
Response: We thank the reviewer for raising this issue. We will detect MYSM1 mRNA and protein levels in breast cancer and physiological samples, along with physiological and breast cancer cells. Statistics for MYSM1 transcriptional level will be further displayed.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
*Luan et al performed a detailed analysis on the potential coactivator MYSM1 and its role in regulating the expression of ER and ER-dependent genes by being a deubiquitinase of ER as well the repressive mark, H2Aub1. This study has demonstrated an excellent work on the biochemistry aspect of the story with meticulous work on the role of specific domains of MYSM1 and ER and how they interact and how the deubiquitination process is regulated. This was identified initially in Drosophila models, but eventually and promptly explored in multiple breast cancer cell lines and patient samples. *
*Major Comments: *
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- It is really exciting to see how MYSM1 regulates ER activity and it looks like expression of ER is the first event of regulation by MYSM1's. However, H3Ac would be the very intermediate event of ER activity. This brings a question of whether ER complex itself is affected by MYSM1 - for example, does MYSM1 affect p300, SWI/SNF and other ER-associated coactivator binding? Does it affect chromatin accessibility? Which exact histone mark of H3Ac is affected, as different proteins are involved in the acetylation of histones. *
Response: Appreciate the reviewer for the valuable questions. The Co-IP and ChIP experiments will be conducted respectively to assess the influence of MYSM1 on the binding of ERa with its associated co-activators and their recruitments on EREs upon MYSM1 knockdown. In addition, ChIP assays will also be performed to determine the effect of MYSM1 on histone modification levels (H3K9ac, H3K27ac, et al). MNase assay will be further performed to examine the function of MYSM1 on chromatin accessibility.
- The regulation of MYSM1 is mainly shown on promoters of ER regulated genes. However, ER primarily bind to enhancers. Is there any general effect on enhancers? *
Response: Thank you for your comments. We will perform ChIP assays to detect the regulation of MYSM1 on ERa binding to enhancers of ERa regulated genes in breast cancer cells.
3. MYSM1 is not the complex usually cells prefer to deubiquitinate H2Aub, but BAP1. What is the role of BAP1 here? Are they redundant or any cross-talk?
Response: Concerning this interesting question, it has been reported that BAP1 co-activator function correlated with increased H3K4me3 and concomitant deubiquitination of H2Aub at target genes. However, BAP1 has not been reported as an ERa co-regulator so far. Moreover, the interaction between ERa and BAP1 cannot be predicted using the STRING database. Whether BAP1 plays a similar role as MYSM1 in breast cancer and how MYSM1 cooperates with the other DUBs to regulate the genome-wide landscape of histone H2A ubiquitination and the gene expression profiles of different mammalian cell types remains to be elusive. It would be necessary to further study in the future.
- Effect of MYSM1 on histone marks on the EREs - only one ERE is shown. Multiple EREs should be validated by qPCR. Enhancers should also be focused. Does it affect H3K27ac or H3K4me1?*
Response: Thank you for your suggestions. ChIP experiments will be conducted to examine the effect of MYSM1 on histone marks on multiple EREs of ERa target genes. Furthermore, we will focus on the effect on MYSM1 on hitone marks (H3K27ac and H3K4me1 levels, et al) on enhancers of ERa target genes.
- It is clear that MYSM1 is required for the response to antiestrogen therapies. However, the link to resistance is not completely clear. This should be investigated with multiple Tamoxifen resistant cell lines. There is one cell line used, but it is responding to tamoxifen even at lower concentrations in Crystal violet assays. MYSM1 overexpression in nonresponders doesn't mean that their activity is also more. Binding analyses should be analysed in proper Tamoxifen-resistant cell lines. Usually, Tamoxifen is used or works at concentrations from 100 nM - 1 uM in vitro to see the transcriptional effects. However, the authors claim that these are very high concentrations, but actually they aren't the concentrations which promote toxicity.*
Response: We thank reviewer for the valuable comments. According to your suggestion, we will construct Tamoxifen-resistant MCF-7 or T47D cell lines carrying stable knockdown of MYSM1 to perform the biological function experiments with appropriate Tamoxifen concentrations to further confirm the effect of MYSM1 on the sensitivity of cells to anti-estrogen. In addition, we will examine the expression of MYSM1 and ERa target genes or histone H2Aub levels in nonresponders samples to preliminarily determine the activity of MYSM1 in AI-resistant samples.
- Discussion about DUB inhibitors - how specific are these? Would they be useful to target MYSM1 activity and thus ER regulation in nonresponders or resistant cell lines? This would add up strongly on the clinical potential of the study. *
Response: The DUB inhibitors mentioned in discussion are specific to USP14 and UCHL5, but not MYSM1. We thus turned to screen the commercially-available compound in ZINC database to find the compounds that could spatially interact with MYSM1 protein, thereby inhibiting the activity of MYSM1. We plan to perform the additional biological function experiments to explore the effect of MYSM1-targeting compounds on the sensitivity of breast cell lines to anti-estrogen treatment.
- OPTIONAL: ChIP-seq analyses on the factors would be more informative to look at the unbiased mechanisms including enhancers. *
Response: We appreciate your important comments. We plan to perform ChIP-seq in MCF-7 cells with MYSM1 antibody to examine the MYSM1 occupation on global chromatin in response to E2 and to show its overlap with ERa distribution.
- Number of replicates aren't clear in figure legends. Are they biological or technical replicates?*
Response: We thank for your comments. We have included the number of replicates in the “materials and methods” and “Figure legends” sections.
*Minor comments: *
- Please give page numbers and line numbers in the manuscript.*
Response: We have given page numbers and line numbers in the revised manuscript.
- Title - "MYSM1 co-activates ER action". "Action" is not needed to be mentioned here.*
Response: We have modified the title according to the reviewer’s suggestion. The title has been modified as below: “MYSM1 acts as a novel co-activator of ERα via histone and non-histone deubiquitination to confer antiestrogen resistance in breast cancer”.
- Abstract talks about the work on Drosophila mainly, but apart from the first experiment, everything else is done on mammalian cell culture and also clinically relevant patient samples. *
Response: Thank you for your important comments. We have modified the abstract contents with breast cancer-derived cell lines instead of Drosophila experimental system.
- Abstract Line 13 - the work is done many ER regulated genes and not gene.*
Response: We've modified the text into “ERa-regulated genes” in Abstract section.
- Pg 6 first paragraph - What/how many mutants were screened here? *
Response: Thank you for your suggestion. In this study, about 300 fly lines carrying loss of function mutants obtained from Bloomington Stock Center were used for screening.
- CoIP protocol is not clear. It says followed with manufacturer instructions but no kit information is provided.*
Response: Apologize for the misrepresentation. Co-IP experiments were performed as that in the previous study. We have corrected the description for CoIP protocol and cited our previous study in the Materials and Methods section.
- Fig. 1H, etc - can you show a zoomed in or DAPI removed (from merge) picture to show the interactions clearly? It's hard to follow the yellow co-interaction spots as they are hidden behind the blue colour. Any kind of quantification analyses would be wonderful.*
Response: Thank you for your suggestion, we have merged the red and green colours to precisely show the co-location of MYSM1 and ERa.
- Fig. EV1H - can you link this with the results from Fig. 1F to discuss if the delta SANT-MYSM1 lost the interaction with ER also in the IF studies? *
Response: Thank you for your question. Commonly, the fluorescence intensity of confocal results mainly represents the amount of ectopic expression of MYSM1 or ERa, Co-IP experiments more exactly represent the association between proteins. It would be better to pick up the similar cell number in confocal experiments to assess the intensity of protein interaction. We will repeat the confocal again to show the exact fluorescence intensity.
- Pg 7 - 3-4th line from last - These lines should move above where AF1 and AF2 are introduced. According to Fig. 1G, the interaction of AF2 and MYSM1 is important. Why do we see an effect on AF1 as well in Fig. 2B?*
Response: Thank you for your comments. The GST ERa-AF1 and GST ERa-AF1 fusion proteins contain 29-180aa and 282-595aa of ERa truncated mutants respectively, while the ERa-AF1 and ERa-AF2 expression plasmids used in luciferase assay in Fig 2B encode 1-282aa and 178-595aa fragments. We can see the ERa-AF1 mutant in Fig 2B contains more amino acid segments than that in GST ERa-AF1 in Fig. 1G. We speculate that MYSM1 may interact with the extra segment (180aa-282aa) to upregulate ERa-AF1 induced transcription. To make it clear, we have included relevant description in the text along with a schematic representation of ERa, ERa-AF1, and ERa-AF2 plasmids used in luciferase reporter assays in Fig EV2B and in materials and methods section.
- It's confusing to have HEK and breast cancer cell line datasets swapped inconsistently between main figures and Supplementary figures. It would be nice to keep them consistent. *
Response: We have reverse the order of Fig 2B and Fig EV2C to maintain the consistency of the cell line datasets.
- RPMI is spelled wrong in Pg. 19. *
Response: We have corrected the spelling error of RPMI.
- How long is the estrogen treatment done in each experiment? What is the concentration? This should be mentioned in the figure legends. 12 or 24 hrs time point is a later stage of estrogen receptor induction. Even 1-3 hrs would be sufficient to promote a stronger effect on RNA transcription than that of these later time points. What you are looking at is all effect on later time points and the effect should be observed on earlier time points to observe dynamic and immediate effects. p-values are required for the comparison on no E2 vs E2 here.*
Response: We appreciate your valuable comment. We have rephrased the description on estrogen treatment in “Material and methods” and “Discussion” parts to more clearly state that E2 (100nM) was given for 4-6h in the experiments detecting transcriptional levels, while 16-18h in the experiments detecting translation levels. In addition, p-values have included to display the change of MYSM1 and ERa recruitment on ERE region upon E2 treatment.
- Fig. 2G - effect on c-Myc after MYSM1 knockdown is not clear comparing to the previous WB in 2E.*
Response: We will replace a clear image in Fig 2G to show the change of c-Myc protein expression after MYSM1 knockdown.
- Pg. 8 - start of the last paragraph - "Unexpectedly, in Co-IP experiment as shown in Figure 2E and F" - These are not Co-IP experiments. *
Response: Apologize for the writing error. We have re-written the sentence “Unexpectedly, in western blot experiments as shown in Figure 2E and F” in line 229.
- Fig. 3C and E - Quantification with comparison needed.*
Response: Relative ERa levels were semi-quantified by densitometry and normalized by the relative expression of 0 hour to compare the ERa degradation rate in Fig 3C and E.
- Pg 10 - subtitle - multiple gene promoters have been looked, but the subtitle says "gene". Only ERE for c-MYC is looked at, but it says EREs.*
Response: We have modified the word “genes” and “ERE” in correct forms in the text.
- MYSM1 is in the nucleus in IF even before E2 treatment, however it is recruited after estrogen treatment in ChIP assays. Explain why there is a difference seen here. What other targets they might bind to in the nucleus?*
Response: The aim of ChIP experiments is to examine the recruitment of MYSM1 protein on the DNA in the presence of E2, while IF results represent the MYSM1 subcellular distribution in the nucleus even in the absence of E2. MYSM1 has been reported to bind to promoters of numerous target genes, including Ebf1 in B cell progenitors, Pax5 in naïve B cells, miR150 in B1a cells, Id2 in NK cell progenitors, Flt3 in dendritic cell precursors, and Gfi1 in hematopoietic stem and progenitor cells. In our study, we plan to perform ChIP-seq to further show its potential binding elements on the global genome in ER-positive breast cancer.
- Pg. 10 last line - the sentence should be combined with comma.*
Response: Thank you for pointing this out, we have combined a comma in the sentence.
- Fig. 5H - What about Ki67 which is a proliferative marker for cancer cell growth?*
Response: We will further perform IHC experiments to compare Ki67 expression in the shCtrl and shMYSM1 group of xenograft tumors from nude mice.
- Pg 12 - Samples were used from patients treated with AI adjuvant treatment. A small summary of details are needed here including n, arm, details of administration, etc even though mentioned in Methods.*
Response: We have restated the patients’ condition and administration details in lines 342-250.
- MYSM1 is upregulated in nonresponders, but it is also downregulated in responders which is ignored. What would this mean mechanistically? Don't patients need MYSM1 for the response or after treatment? Does estrogen inhibition regulate MYSM1 upstream? *
Response: Appreciate for your important questions. The changes of intracellular environment caused by AI treatment are complicated and varied. The mechanism underlying such a phenomenon is largely unclear. We plan to perform western blot and ubiquitination assays to compare the expression and activity of MYSM1 in endocrine-resistant breast cancer cells treated or untreated with endocrine drugs to identify the effects of estrogen inhibition on MYSM1 expression. Moreover, we will detect whether MYSM1 expression is correlated with cell cycle and cell proliferation states.
- Pg 13 - Is this data associated with any trial? More details are needed. *
Response: We appreciate for your helpful comment. We have rearranged the logic of the article in order to clarify our reasoning for presenting this data. The modified contents included in lines 367-371 in the modified version are followed below: The regulation of MYSM1 on ERa action indicates that MYSM1 acts as a novel ERa co-activator, suggesting that MYSM1 may play an important role in breast cancer. We then conducted western blot and IHC experiments to estimate MYSM1 expression and the correlation between MYSM1 expression and clinicopathologic factors of the patients.
- Last lines of Pg 15 - These were already introduced in the results. *
Response: We thank reviewer for their highlighting this redundancy in our text. We have simplified the text in lines 442-444.
- Pg 16 - third last line of the first paragraph - makes typo.*
Response: Thanks for pointing out this typo. We have corrected the word “make” in line 456.
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Referee #3
Evidence, reproducibility and clarity
Luan et al performed a detailed analysis on the potential coactivator MYSM1 and its role in regulating the expression of ER and ER-dependent genes by being a deubiquitinase of ER as well the repressive mark, H2Aub1. This study has demonstrated an excellent work on the biochemistry aspect of the story with meticulous work on the role of specific domains of MYSM1 and ER and how they interact and how the deubiquitination process is regulated. This was identified initially in Drosophila models, but eventually and promptly explored in multiple breast cancer cell lines and patient samples.
Major Comments:
- It is really exciting to see how MYSM1 regulates ER activity and it looks like expression of ER is the first event of regulation by MYSM1's. However, H3Ac would be the very intermediate event of ER activity. This brings a question of whether ER complex itself is affected by MYSM1 - for example, does MYSM1 affect p300, SWI/SNF and other ER-associated coactivator binding? Does it affect chromatin accessibility? Which exact histone mark of H3Ac is affected, as different proteins are involved in the acetylation of histones.
- The regulation of MYSM1 is mainly shown on promoters of ER regulated genes. However, ER primarily bind to enhancers. Is there any general effect on enhancers?
- MYSM1 is not the complex usually cells prefer to deubiquitinate H2Aub, but BAP1. What is the role of BAP1 here? Are they redundant or any cross-talk?
- Effect of MYSM1 on histone marks on the EREs - only one ERE is shown. Multiple EREs should be validated by qPCR. Enhancers should also be focused. Does it affect H3K27ac or H3K4me1?
- It is clear that MYSM1 is required for the response to antiestrogen therapies. However, the link to resistance is not completely clear. This should be investigated with multiple Tamoxifen resistant cell lines. There is one cell line used, but it is responding to tamoxifen even at lower concentrations in Crystal violet assays. MYSM1 overexpression in nonresponders doesn't mean that their activity is also more. Binding analyses should be analysed in proper Tamoxifen-resistant cell lines. Usually, Tamoxifen is used or works at concentrations from 100 nM - 1 uM in vitro to see the transcriptional effects. However, the authors claim that these are very high concentrations, but actually they aren't the concentrations which promote toxicity.
- Discussion about DUB inhibitors - how specific are these? Would they be useful to target MYSM1 activity and thus ER regulation in nonresponders or resistant cell lines? This would add up strongly on the clinical potential of the study.
- OPTIONAL: ChIP-seq analyses on the factors would be more informative to look at the unbiased mechanisms including enhancers.
- Number of replicates aren't clear in figure legends. Are they biological or technical replicates?
Minor comments:
- Please give page numbers and line numbers in the manuscript.
- Title - "MYSM1 co-activates ER action". "Action" is not needed to be mentioned here.
- Abstract talks about the work on Drosophila mainly, but apart from the first experiment, everything else is done on mammalian cell culture and also clinically relevant patient samples.
- Abstract Line 13 - the work is done many ER regulated genes and not gene.
- Pg 6 first paragraph - What/how many mutants were screened here?
- CoIP protocol is not clear. It says followed with manufacturer instructions but no kit information is provided.
- Fig. 1H, etc - can you show a zoomed in or DAPI removed (from merge) picture to show the interactions clearly? It's hard to follow the yellow co-interaction spots as they are hidden behind the blue colour. Any kind of quantification analyses would be wonderful.
- Fig. EV1H - can you link this with the results from Fig. 1F to discuss if the delta SANT-MYSM1 lost the interaction with ER also in the IF studies?
- Pg 7 - 3-4th line from last - These lines should move above where AF1 and AF2 are introduced. According to Fig. 1G, the interaction of AF2 and MYSM1 is important. Why do we see an effect on AF1 as well in Fig. 2B?
- It's confusing to have HEK and breast cancer cell line datasets swapped inconsistently between main figures and Supplementary figures. It would be nice to keep them consistent.
- RPMI is spelled wrong in Pg. 19.
- How long is the estrogen treatment done in each experiment? What is the concentration? This should be mentioned in the figure legends. 12 or 24 hrs time point is a later stage of estrogen receptor induction. Even 1-3 hrs would be sufficient to promote a stronger effect on RNA transcription than that of these later time points. What you are looking at is all effect on later time points and the effect should be observed on earlier time points to observe dynamic and immediate effects. p-values are required for the comparison on no E2 vs E2 here.
- Fig. 2G - effect on c-Myc after MYSM1 knockdown is not clear comparing to the previous WB in 2E.
- Pg. 8 - start of the last paragraph - "Unexpectedly, in Co-IP experiment as shown in Figure 2E and F" - These are not Co-IP experiments.
- Fig. 3C and E - Quantification with comparison needed.
- Pg 10 - subtitle - multiple gene promoters have been looked, but the subtitle says "gene". Only ERE for c-MYC is looked at, but it says EREs.
- MYSM1 is in the nucleus in IF even before E2 treatment, however it is recruited after estrogen treatment in ChIP assays. Explain why there is a difference seen here. What other targets they might bind to in the nucleus?
- Pg. 10 last line - the sentence should be combined with comma.
- Fig. 5H - What about Ki67 which is a proliferative marker for cancer cell growth?
- Pg 12 - Samples were used from patients treated with AI adjuvant treatment. A small summary of details are needed here including n, arm, details of administration, etc even though mentioned in Methods.
- MYSM1 is upregulated in nonresponders, but it is also downregulated in responders which is ignored. What would this mean mechanistically? Don't patients need MYSM1 for the response or after treatment? Does estrogen inhibition regulate MYSM1 upstream?
- Pg 13 - Is this data associated with any trial? More details are needed.
- Last lines of Pg 15 - These were already introduced in the results.
- Pg 16 - third last line of the first paragraph - makes typo.
Significance
- The study seems to be novel as MYSM1 is never studied before as a coactivator for ER. This expands the wealth of knowledge we have on coactivators which can be explored for its potential targeting to treat advanced breast cancers. The study seems to be support the biochemical aspects of ER interaction, but vaguely uncovers the functional or epigenetic mechanisms.
- Studies on coactivators/coregulators of ER is very important, as modulating ER alone is not efficient enough to solve the puzzle of antiestrogen resistance. The expression/activity levels of the coregulators are very important as these can be modulated in cancers due to epigenetic reprogramming during resistance and mutations on these genes dominate. They can also serve as potential targets especially when cells don't respond to classical ER targeting therapies.
- Strength - Biochemical analyses of the interactions and detailed mechanistic information
- Limitation - Studies are very much limited to the biochemical regulation on ER and not on the molecular or epigenetic mechanisms. Association of MYSM1 in resistance mechanisms isn't clear.
- Audience - this can be interesting for both basic research and clinical audience. Biochemical knowledge would help people to understand how a nonclassical deubiquitinase can promote nuclear receptor associated transcription by targeting genomic and nongenomic targets simultaneously. Clinically this study would be relevant if the MYSM1-ER interaction can be targeted using DUB inhibitors, as requested.
- Area of expertise of the reviewer - breast cancer, nuclear receptors, estrogen receptor biology, epigenetics, bioinformatics
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Referee #2
Evidence, reproducibility and clarity
Below I outline a few suggestions that can help clarify specific aspects of the study.
Fig. 2: Ideally a rescue study with a wild-type and catalytically mutant MYSM1 should be performed. What is the ERa interactome in the presence and absence of MYSM1? Proteomics studies upon shMYSM1 should be performed. Alternatively, a better characterization of ERa-containing complexes upon shMYSM1 should be performed.
Fig. 3: Does MYSM1 control its own protein via deubiquitination?
Fig. 4: I propose that the authors perform MYSM1 ChIP-Seq to better show the MYSM1 distribution and overlap with ERa distribution.
Fig. 7. Is there a correlation between MYSM1 mRNA and protein levels in cancer and physiological samples? How is the MYSM1 transcriptionally regulated in physiological and cancer cells?
Significance
This is a very comprehensive study characterizing the role of MYSM1 deubiquitinase in ERa transcriptional programs in breast cancer systems. Breast cancer therapy is an unmet need and the role of deubiquitinases warrants further investigation. This accounts for the high significance of the story.
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Referee #1
Evidence, reproducibility and clarity
Summary:
ER+ breast cancer is the most common form of cancer. Targeting ER-alpha transcriptional cofactors present one potential method to target the disease. The authors demonstrate that MYSM1 is a histone deubiquitinase and a novel ER cofactor, functioning by up-regulating ER action via histone deubiquitination.
Loss of MYSM1 attenuated cell growth and increase breast cancer cell lines' sensitivity to anti-estrogens. The authors, therefore, propose MYSM1 as a potential therapeutic target for endocrine resistance in Breast cancer.
Major Comments:
- The data as presented is convincing, and the evidence for the role of MYSM1 as a co-activator of ER-alpha is extensive.
- Given the amount of data, I do not believe any additional experiments are needed.
- I could not find any description of ethics for the patient samples used.
Minor
- Figure 4C - is the increase of binding in response to Estrogen significant? It is an important control to show for MCF7 as Fig 4B is in T47D.
- Figure 6 - Can we clarify that B = Before, A = After
- The use of Fig EV was confusing to me, I assume it means supplementary?
Significance
- Discovery science to understand the regulation of the ER is critical in discovering new opportunities to target breast cancer. As far as I can tell this is the first study where MYSM1 is a co-regulator of the ER.
- The significance would be greatly increased if the manuscript identified opportuinities to target the ER via this pathway using existing compounds. However, it is reasonable to consider this is beyond the scope of this study.
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- Feb 2023
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
We apologize for the delay in resubmitting this revised manuscript. We faced a number of challenges over the previous year unrelated to this project that slowed progress on completing the necessary revisions. However, we are happy to report we have addressed all of the reviewer’s valuable comments in this revised submission through the including of 27 new or improved figure panels and significant adaptations to the text. We highlight these changes below.
REVIEWER #1.
Reviewer #1 General Comments. “This study investigates changes in mitochondrial morphology in response to ER stress due to pharmacological inhibition or genetic dysfunction in vitro via two different cell models (MEFs and HeLa cells). The authors specifically implicate the PERK branch of the ER-stress induced pathway in this process based on the observation that mitochondria elongate in response to thapsigargin (Tg) treatment which is blocked by the pathway inhibitors GSK and ISRIB or by genetic ablation of Perk/PERK. Homozygous knockout cells lacking PERK exhibit a fragmented mitochondrial phenotype even in the absence of Tg, which is rescued by expression of the wildtype but not a hypomorphic allele (PERKPSP). One of the more interesting suppositions of this manuscript is that mitochondrial elongation is dependent on the abundance of phosphatidic acid (PA); treatment with Tg provokes an increase in mitochondrial PA, but PA does not accumulate in mitochondria from cells co-treated with GSK, an inhibitor of PERK. This correlation suggests that increased mitochondrial PA accumulation is PERK-dependent. In addition, predicted manipulation of PA levels achieved by a gain of function expression of the lipase Lipin diminished mitochondrial elongation in response to ER stress. Similar results were obtained by PA-PLA1 overexpression, a cytosolic lipase that converts PA into lysophosphatidic acid (LPA). To further describe the mechanistic link between ER stress and mitochondrial morphology, the authors found that PRELID1, which transports PA from the OMM to the intermembrane space, and TIM17A, a component of the protein translocation machinery, were stabilized by loss of PERK or YME1L [and possibly an effect of ATF4], regardless of ER stress via Tg treatment. The authors also report that Tg treatment prevents OPA1 cleavage in cells treated with CCCP, an uncoupler of the proton gradient, suggesting that the effect due to Tg treatment is not through ER stress but decreased mitochondrial fusion via mito-stress induced OPA1 cleavage. To address this, cells were treated with ionomycin which induces mitochondrial fragmentation independent of DRP1. The authors observed an increase in mitochondrial fragmentation in the presence of ionomycin. However, co-treatment with Tg prevented fragmentation, as did overexpression of mitoPLDGFP, which converts cardiolipin to PA on the OMM. These results support a model in which, under ER stress conditions, PERK activation leads to translational attenuation, which leads to a decrease in the steady state levels of PRELID1 via YME1L-dependent degradation and to the accumulation of PA on the OMM. Based on published work this PA accumulation is expected to inhibit the mitochondrial division dynamin, DRP1. The authors tested this by examining the dependence of mitochondrial elongation on PRELID1.”
“Perturbances in PERK signaling evoke an alteration in mitochondrial morphology and have been extensively reported on, due to their clinical implications on neurodegenerative disorders such as Alzheimer's disease. The present work provides insight into the molecular basis for Stress Induced Mitochondrial Hyperfusion (SIMH) which can be triggered by ER stress. The authors find that this process occurs downstream of PERK and proceeds through accumulation of PA in the OMM by stabilization of Prelid, a mitochondrial resident protein that transports PA from the OMM to IMM for cardiolipin synthesis. The evidence of this work represents a substantial addition to the field of mitochondrial dynamics/SIMH and the Unfolded Protein Response”
“The novelty of this work is in the inclusion of PRELID1 downstream of PERK signaling pathway for transmission of ER stress to the mitochondria, a process that involves phosphatidic acid (PA). Some studies have addressed how phosphatidic acid is a modulator and a signal in mitochondrial physiology. The role of the lipids in mitochondrial dynamics represent an important and emerging field that needs to be explored in order to understand how metabolites control mitochondrial fusion/fission.”
__Our Response to Reviewer #1 General Comments. __We thank the reviewer for the positive comments related to our manuscript. We address specific comments brought up by the reviewer in our revised manuscript as highlighted below. We combined specific comments related to the same point in this response to best manage the various points brought up by the reviewer.
Reviewer #1 Comment #1. __The Reviewer__ brought up the quality of our images numerous times in their review. A few examples are included below.
“Image quality of mitochondria is sub par and the images do not always appear representative of/match the accompanying histograms. When using a single fluorescent marker (mito-GFP), the images should be in grey scale.”
“In several images there is substantial background GFP signal resulting in images that are fuzzy on the high quality PDF (printout is unintelligible). Example: Figure 2, Mock+veh. Example: Figure S2I, Mock+veh, +PA-PLA Tg. Example: Figure 3C mock+veh”
“Images from prior paper (Lebeau J, et al. 2018) are of much higher quality and is much easier to discern mitochondrial”
“Mitochondrial morphology doesn't appear uniform even within the same cell so how is this accounted for in scoring of mitochondrial morphology? Also, how are authors scoring mitochondrial morphology? Due to the inconsistencies in the chosen images, we feel this manuscript would benefit from addition of a supplementary figure showing examples for each cell model expressing mtGFP (i.e. HeLa and MEFs) depicting the fragmented, tubular and elongated mitochondria. This should be able to be constructed from images already collected for these analyses that weren't already used in the paper.”
__Our Response to Reviewer #1 Comment #1. __In the revised manuscript, we improved the quality of the images and converted all images to greyscale, as suggested by the reviewer.
As described in Materials and Methods, we quantified mitochondrial morphology by cell, scoring whether a cell has primarily fragmented, tubular, or elongated mitochondria morphology. This scoring was performed by at least two blinded researchers for at least 3 independent experiments with a total of >60 cells/condition counted across all experiments. Scores for individual experiments were then combined and averaged. Statistics were calculated from these averaged scores. In the revised manuscript, the images presented are representative of each individual condition. In addition, we now include new panels showing the quantification of total cells counted/condition across all individual replicates by a representative researcher for the main text figures (e.g., see Fig. S1C). This provides an alternative representation of the observed phenotype across the individual experiments for these key figures.
As suggested by the reviewer, in the revised submission we also now provide representative images of cells with primarily fragmented, tubular, and elongated mitochondria for both MEF and HeLa cells (Fig. S1A,B). We appreciate this suggestion as we feel it improves the clarity of our manuscript.
Reviewer #1 Comment #2. ____“Mitochondria in Perk-/- MEFs are highly fragmented, which is potentially inconsistent with previous work (Lebeau J, et al. 2018) performed by the same research group. Can the authors comments on this discrepancy? Also, do the authors interpret this fragmentation to mean that Perk is required to maintain mitochondrial elongation in the absence of exogenous ER stress (Tg)? If so, the authors should test whether expression of a dominant negative version of DRP1 rescues this fragmented morphology. This would be an additional critical test of the authors' model.”
“Vehicle treated Perk-/- cells have fragmented morphology which is different from Figure 2F in above publication by same group. Can the authors explain this discrepancy?”
Our Response to Reviewer #1 Comment #2. In our previous publication, we did not quantify mitochondrial morphology in Perk-deficient cells. However, as reported in this current manuscript, we find that Perk-deficient cells display higher amounts of fragmented mitochondria, as compared to Perk+/+ MEFs (Fig. 1B,C). We quantified this result across 5 independent experiments. Moreover, we found that reconstitution with PERKWT restored tubular mitochondrial morphology in Perk-deficient cells, demonstrating that this effect can be attributed to loss of PERK.
With respect to the increase in mitochondrial fragmentation observed in Perk-deficient MEFs, we attribute this to reduced mitochondrial membrane potential observed in these cells. We now show that Perk-deficient MEFs show 50% reductions in TMRE staining, as compared to controls. We include this data in the revised manuscript as __Fig. S1D __and the accompanying text below.
Line 91. “*Perk-/- MEFs showed increases in fragmented mitochondria in the absence of treatment (Fig. 1B,C and Fig. S1C). This corresponds with reductions in the mitochondrial membrane potential in Perk-deficient cells, as measured by tetramethylrhodamine ethyl ester (TMRE) staining (Fig. S1D). This suggests that the increase of fragmentation in these cells can be attributed to mitochondrial depolarization. Tg-induced mitochondrial elongation was also impaired in Perk-deficient cells (Fig. 1B,C and Fig. S1C).”. *
Reviewer #1 Comment #3. “The authors postulate that mitochondrial elongation in response to Perk activation is specifically outer membrane PA-dependent negative regulation of DRP1. However, PA is readily convertible to other phospholipids, notably CL and LPA, both of which positively regulate mitochondrial fusion. The authors do not measure abundance of other phospholipids, particularly LPA or CL in their targeted lipidomics experiments, only PC. The authors need to consider this alternate possibility.”
Reviewer #1 Comment #3. __Overexpression of PA-PLA1 (which converts PA to LPA) blocks ER stress induced mitochondrial elongation (__Fig. S2L-O). This indicates that the observed Tg-dependent increase in mitochondrial elongation are unlikely to be attributed to increases in LPA. mitoPLD converts CL to PA at the outer mitochondrial membrane. Since mitoPLD overexpression increases mitochondrial elongation (Fig. 3A,B), this again suggests that CL is not a major driver of mitochondrial elongation. These results combined with the sensitivity of ER stress induced mitochondrial elongation to two different PA lipases strongly support a model whereby increases in PA contribute to ER stress induced mitochondrial elongation.
In the revised manuscript, we include measurements of CL in mitochondria isolated from MEFmtGFP cells treated with Tg and/or depleted of Prelid1. As expected, reductions of PRELID1 decrease CL in isolated mitochondria (Fig. S5C). Treatment with Tg reduced CL to similar extents in mitochondria isolated from MEFmtGFP cells expressing non-silencing shRNA. However, we did not observe further reductions of CL in Prelid1-depleted cells. This is consistent with a model whereby ER stress-dependent reductions in PRELID1 decrease PA trafficking across the IMS and lead to reductions in CL synthesis. These results are discussed in the revised manuscript as below:
Line 214. “PRELID1 traffics PA from the outer to inner mitochondrial membrane, where it serves as a precursor to the formation of cardiolipin.56,66,67 Thus, reductions in PRELID1 should decrease cardiolipin. To test this, we shRNA-depleted Prelid1 from MEFmGFP cells and monitored cardiolipin in isolated mitochondria in the presence or absence of ER stress. We confirmed efficient PRELID1 knockdown by immunoblotting (Fig. S5A). Importantly, Prelid1 depletion did not alter Tg-induced reductions of TIM17A or increases of ATF4. Further, Tg-dependent increases in PA were observed in Prelid1-depleted MEFmtGFP cells (Fig. S5B). These results indicate that loss of PRELID1 does not impair PERK signaling in these cells. Prelid1 depletion reduced cardiolipin in mitochondria isolated from MEFmtGFP cells (Fig. S5B). Treatment of MEFmtGFP cells expressing non-silencing shRNA with Tg for 3 h also reduced cardiolipin to levels similar to those observed in Prelid1-deficient cells. However, Tg did not further reduce cardiolipin in Prelid-depleted cells. These results are consistent with a model whereby ER stress-dependent reductions in PRELID1 limit PA trafficking across the inner mitochondrial membrane and contribute to reductions in cardiolipin during acute ER stress”
Reviewer #1 Comment #4. “In Figure 5, the authors found very little difference in mitochondrial elongation following knockdown of Prelid1 (comparison between vehicle only conditions), which is potentially inconsistent with their model as decreased PRELID1 should lead to increased OMM PA [and subsequently mitochondrial fusion/elongation]. Therefore, these findings do not adequately support the authors' main model.”
Our Response to Reviewer #1 Comment #4. __Our model predicts that ER stress induced mitochondrial elongation is mediated through a process involving both PERK kinase-dependent increases in total PA and YME1L-dependent PRELID1 degradation induced downstream of PERK-dependent translation attenuation (see __Fig. 6). Thus, we predict that PRELID1 degradation is required, but not sufficient, to promote mitochondrial elongation. Our results showing that PRELID1 depletion does not basally disrupt mitochondrial morphology or inhibit Tg-induced mitochondrial elongation are consistent with this model. Moreover, we show that genetic Prelid1 depletion rescues Tg-induced mitochondrial elongation in cells co-treated with the PERK signaling inhibitor ISRIB – a compound that blocks PERK-dependent PRELID1 degradation (Fig. 4D), but not increases in PA (Fig. 2B, S2E,F) – in both MEFmtGFP and HeLa cells (Fig. 5A-D). This is consistent with our proposed model whereby PRELID1 degradation is required but not sufficient for promoting mitochondrial elongation. We make this point clearer in the revised manuscript.
Line 259: “Interestingly, Prelid1 depletion did not basally influence mitochondrial morphology or inhibit Tg-induced mitochondrial elongation (Fig. 5A,B and Fig. S5E). This indicates that reduction of PRELID1, on its own, is not sufficient to increase mitochondrial elongation, likely reflecting the importance of PERK kinase-dependent increases in PA in this process.53”
Reviewer #1 Comment #5. “The manuscript requires more careful editing - there were grammatical and punctuation errors.”
“… the text needs considerable editing to make the language clearer and formal whereas the figures are not always presented in a manner that is easily absorbed by the reader. Representative microscopy images chosen do not always match the corresponding graphical summary and are not clear even on PDF version compared to (Lebeau J, et al. 2018 - full citation above).”
__Our Response to Reviewer #1 Comment #5. __We carefully edited the revised manuscript.We also confirmed that representative images match the observed quantifications.
Reviewer #1 Comment #6. “In order to further investigate the contribution PRELID1-dependent accumulation of PA in the OMM and its role in mitochondrial elongation, the authors should investigate the abundance of PA (and other lipids) in Perk, Prelid, Yme1l KO mutants. These experiments should quantitatively complement the results in Figure 5. KD of Prelid would be expected to increase mitochondrial elongation but there is no difference compared to WT in Figure 5.”
Our Response to Reviewer #1 Comment #6. __We thank the reviewer for this comment and now include new data to further demonstrate that co-treatment with the PERK kinase inhibitor GSK2656157 inhibits Tg-dependent increases in PA, while the PERK signaling inhibitor ISRIB does not (__Fig. 2B __and __Fig. S2A-E). Further, it is published that Perk-deletion inhibits ER stress-induced increases in PA, while knockin cells expressing the non-phosphorylatable eIF2a S51A mutant do not (Bobrovnikova-Marjon et al (2012) Mol Cell Biol). This is consistent with a model whereby PERK-dependent increases in PA are attributed to a PERK kinase-dependent, yet eIF2a phosphorylation-independent, mechanism. In the revised manuscript, we include additional quantification of PA across other genetic manipulations, as requested. Notably, we confirm that Lipin1 overexpression reduced basal PA and prevents Tg-dependent increases in PA (Fig. 2C, Fig. S2F,G). Further, we show that PRELID1 depletion does not significantly impact Tg-dependent increases of PA (Fig. S5B).
However, it is important to highlight that our work is specifically monitoring how acute ER stress-dependent PERK activation impacts mitochondria. Genetic manipulations that target many of the core components of these pathways are well established to globally disrupt many aspects of mitochondrial biology. Thus, these types of genetic manipulations often confound our ability to accurately monitor the contribution of specific stress-responsive signaling pathways in adapting mitochondria in response to acute insults. For example, a recent publication demonstrates that deletion of Perk impairs ER-mitochondrial phospholipid transport through mechanism independent of PERK kinase activity (Sassano et al (2023) J Cell Biol). While this problem can be limited if specific perturbations do not basally disrupt the phenotype being monitored (e.g., PRELID1 depletion does not significantly impact basal mitochondrial morphology; Fig. 5), our ability to evaluate how stress-responsive signaling regulates mitochondria in response to acute insults (e.g., ER stress) still requires temporal control to properly evaluate how these pathways impact aspects of mitochondrial biology. It is for this reason that we paired PRELID1 depletion with pharmacologic interventions that can be used to temporally inhibit PERK signaling (e.g., ISRIB, GSK), allowing us to best define the specific role for PERK-dependent reductions PRELID1 in promoting mitochondrial elongation in response to ER stress.
Reviewer #1 Comment #7. “Title of the subsection: "hypomorphic PERK variants inhibit ER..." is inappropriate since authors only investigated a single hypomorphic variant (PSP). KO mutant is a null not hypomorphic mutant”
__Our Response to Reviewer #1 Comment #7. __We agree and have made the suggested change in the revised manuscript.
Reviewer #1 Comment #8. “Can the authors elaborate on the possible biological relevance for the inhibition of OPA1 cleavage via Tg treatment?”
Our Response to Reviewer #1 Comment #8. __We show that Tg pretreatment inhibits mitochondrial depolarization induced by CCCP (__Fig. S3G). Thus, the impaired CCCP-induced, OMA1-dependent OPA1 processing observed in response to pretreatment with Tg likely reflects disruptions in mitochondrial uncoupling afforded by this treatment. We make this point clearer in the revised manuscript.
Line 170: “However, Tg pretreatment inhibited CCCP-induced proteolytic cleavage of the inner membrane GTPase OPA1 (Fig. 3C) – a biological process upstream of DRP1 in mitochondrial fragmentation induced by membrane uncoupling.43-47,64 This appears to result from Tg-dependent increases in mitochondrial membrane polarity (Fig. S3G), preventing efficient uncoupling in CCCP-treated cells and precluding our ability to determine whether Tg pretreatment directly impairs DRP1 activity under these conditions..”
Reviewer #1 Comment #9. “PRELID is a known short-lived protein; can the authors elaborate on possible additional impact due to 3-6 hr Tg treatment which is sufficient to induce expression of ATF4 target genes (Figure S2G).”
Our Response to Reviewer #1 Comment #9. PRELID1 is a short-lived mitochondrial protein that is rapidly degraded in response to acute ER insults. As demonstrated in Fig. 4 of our manuscript, this reduction is mediated by the IMM protease YME1L downstream of PERK-regulated translation attenuation. This 3-6 h timecourse corresponds with the translational attenuation induced downstream of PERK-dependent eIF2a phosphorylation following treatment with Tg and corresponds with the loss of PRELID1 observed in Tg-treated cells.
Note that the increase in ATF4 noted by the reviewer reflects the fact that ATF4 (and related proteins) are preferentially translated following eIF2a phosphorylation due to the presence of uORFs in their promoter. Thus, while global protein translation (including PRELID1 translation) is reduced by eIF2a phosphorylation, proteins like ATF4 are selectively translated.
Reviewer #1 Comment #10. “Thapsigargin induced ER stress does not only activate PERK arm of the ISR, correct? Could the authors comment on this?”
__Our Response to Reviewer #1 Comment #10. __I believe the reviewer is asking whether Tg treatment activates other arms of the integrated stress response (ISR). At the short timepoints used in this work (3-6 h), Tg-dependent increases in ISR signaling can be fully attributed to PERK signaling. This is evident as Perk deletion or inhibition blocks markers of ISR signaling in cells treated with Tg for these shorter timepoints (e.g., __Fig. 4E __of this paper; Harding et al (2002) Mol Cell and Lebeau et al (2018) Cell Reports). While other ISR kinases can be activated in response to more prolonged ER stress, the ISR activation observed in these shorter treatments with Tg are well established to be attributed to PERK activity.
Tg does induce all three arms of the unfolded protein response (i.e., ATF6, IRE1, and PERK) in the 3-6 h timeframe used in this manuscript. We previously showed that pharmacologic inhibition of ATF6 and IRE1 activity does not influence Tg-induced mitochondrial elongation (Lebeau et al (2018) Cell Reports). However, as reproduced in this manuscript, inhibition of PERK signaling blocks ER stress induced mitochondrial elongation. We make this point clearer in the revised manuscript.
Line 86. “Pharmacologic inhibition of PERK signaling, but not other arms of the UPR, blocks mitochondrial elongation induced by ER stress.39”
Reviewer #1 Comment #11. “*Addition of drugs and duration (3-6 hrs) likely very toxic to cells; how does this treatment affect viability? Unhealthy cells will have unhealthy mitochondria so it's hard to be confident that subtle morphological differences are specific. Why do authors use 3 hrs Tg-treatment after initially using 6 hrs in Figure 1? Would be helpful to assay toxicity and mitochondrial morphology of thapsigargin and other drugs in WT vs. Perk KO MEFs over time.” *
__Our Response to Reviewer #1 Comment #11. __Thapsigargin (Tg) is toxic to cells, but apoptosis is observed in cell culture models only after much longer treatments 24-72 h. We are using Tg to monitor how cells respond to acute ER stress. We chose the short 3-6 h timecourse because this is sufficient to induce PERK-dependent translation attenuation independent of cell death. Consistent with this, we observe no reductions in cellular viability or death in the short 3-6 h treatments used in this study. This timecourse is standard in the field when monitoring cellular changes induced by acute ER stress.
Reviewer #1 Comment #12. “Previously, an increase in fragmentation was observed at 0.5 hours but this subsided by 6 hours in WT (Lebeau J, et al. 2018) but is this the same for Perk KO MEFs?”
Our Response to Reviewer #1 Comment #12. __The increase in mitochondrial fragmentation observed following Tg treatment results from the rapid increase of mitochondrial Ca2+ induced by this treatment (Hom et al (2007) J Cell Phy). Consistent with this, we have found that pharmacologic inhibition of PERK signaling using the compound ISRIB, does not inhibit mitochondrial fragmentation in MEFmtGFP cells treated for 30 min with Tg. Since Perk-deficient MEFs already show increased fragmentation (__Fig. 1B,C), monitoring mitochondrial morphology in Perk-deficient cells treated with Tg for 30 min is unlikely to reveal additional insights into the mechanism outlined in this manuscript.
Reviewer #1 Comment #13. “How much protein was loaded per lane and what was the percentage of polyacrylamide gel? Please clarify details in methodology.”
Our Response to Reviewer #1 Comment #13. We loaded 100 µg of protein for our immunoblotting experiments. We used 10% or 12% SDS-PAGE gels. We included this information in the revised Materials and Methods.
Reviewer #1 Comment #14. “Figure 1A is virtually identical to Figure 2A (with exception of "MEF A/A") from previous publication: Lebeau J, Saunders JM, Moraes VWR, Madhavan A, Madrazo N, Anthony MC, Wiseman RL. The PERK Arm of the Unfolded Protein Response Regulates Mitochondrial Morphology during Acute Endoplasmic Reticulum Stress. Cell Rep. 2018 Mar 13;22(11):2827-2836. doi: 10.1016/j.celrep.2018.02.055. PMID: 29539413; PMCID: PMC5870888.”
Our Response to Reviewer #1 Comment #14. __Yes. __Fig. 1A is a cartoon showing PERK-dependent regulation of mitochondria and the specific pharmacologic and genetic manipulations used in this paper to alter this pathway. This is adapted from our previous manuscript (Lebeau et al (2018) Cell Reports). We properly reference this adaptation in the revised manuscript. We feel it is important to show this figure to specifically highlight how different manipulations influence this signaling pathway.
Reviewer #1 Comment #15. “If the authors' hypothesis is correct, overexpression of PRELID1 should have same effect as overexpression of Lipin”
Our Response to Reviewer #1 Comment #15. Overexpressed PRELID1 will be sensitive to the same rapid YME1L-dependent degradation observed for the endogenous protein. Thus, overexpressing PRELID1 would be expected to have no effect (or a very minor effect) on mitochondrial morphology in Tg-treated cells. We show that Lipin1 overexpression basally increases mitochondrial fragmentation and blocks Tg-induced mitochondrial elongation (Fig. 2). Identical results were observed in cells overexpressing the alternative PA lipase PA-PLA1 (Fig. S2). We feel that these data, in combination with others shown in our manuscript, strongly support the dependence of this process on PA levels and localization.
Reviewer #1 Comment #16. “What is the selective marker used for HeLa cells expressing mitoPLDGFP since the HeLa parental cell background already expressed a mitochondrial targeted GFP, we assume it was puromycin but this was not clear in the Figure legend or methods? If so, it would be helpful to clarify this. If not, how can the authors observe a difference in morphology if the selectable marker is the same? Indeed, mitoPLDGFP is expressed, detectable by immunoblot, but this is on a cell population level so no way of knowing whether the specific cells scored expressed mitoPLDGFP unless another selectable marker was used (i.e. should have used CFP, RFP, etc.).”
“The authors state "Note the expression of mitoPLDGFP did not impair our ability to accurately monitor mitochondrial morphology in these cells." in Figure 3 legend and again basically the same in S3: "Note that the expression of the mitoPLDGFP did not impair our ability to monitor mitochondrial morphology in these cells." Could the authors explain their reasoning here?”
__Our Response to Reviewer #1 Comment #16. __We co-transfected the mitochondrial localized mitoPLD-GFP with mtGFP in HeLa cells using calcium phosphate transfection. In using this approach, we (and others) have consistently found that this method leads to the efficient transfection of cells with both plasmids. Thus, cells will express both mitoPLD-GFP and mtGFP. We used mitoPLD-GFP because we were reproducing published experiments (Adachi et al (2016) Mol Cell) and we wanted to use the same overexpression plasmid used in these previous studies. It is clear from our images that the presence of GFP-tagged mitoPLD did not influence our ability to accurately monitor mitochondrial elongation in these cells. Further, the robust increase in mitochondrial elongation observed in cells overexpressing mitoPLD-GFP and the further increase in elongation observed upon co-treatment with Tg demonstrate the effectiveness of this assay. This is consistent with published results (Adachi et al (2016) Mol Cell).
Reviewer #1 Comment #17. ____“Figure S4C: the authors show that Tg treatment on MEF mtGFP cells for distinct hours to determine PRELID levels. However, in the Results section states that this treatment was with CHX, could the authors please check this and correct?”
Our Response to Reviewer #1 Comment #17. __The data shown in __Fig. S4C from the previous version is in Tg-treated cells. We corrected this in the revised manuscript.
Reviewer #1 Comment #18. “Figure 6: A schematic representation should be a graphic summary of all findings reported in the text with no text except where absolutely essential. A good model should be easily understood without reading any description since all concepts were supported in the main text and by experimentation.”
*“The model also contains some inaccuracies. The suggestion is that the authors re-do the model and clarify some aspects such as: *
*The model suggests that ISRIB inhibits PRELID1 directly but there is no evidence for this whereas PRELID is directly regulated by YME1L (also typo here in figure: "Yme1" no "l"). *
*This model incorrectly uses inhibition symbols; for example, mutation of Perk does not inhibit its activity as GSK does. The KO does not have Perk so cannot perform its function. These are not the same. *
Similarly, the lipases (Lipin and PA-PLA1) should be depicted instead as altering flux of PA away from OMM not as inhibition.
The authors should connect PA accumulation in the OMM graphically to mitochondrial elongation [instead of through text]. If the authors consider the numbered labels convenient, please use just the number and place the description in the figure legend instead.”
Our Response to Reviewer #1 Comment #18. __We have adapted our model shown in __Fig. 6 and the accompanying legend to address points brought up by the reviewer. In particular, because the reviewer found it difficult to follow how specific manipulations impacted specific steps, we removed those parts from the revised figure for clarity.
__Reviewer #1 Comment #19. __The reviewer made many suggestions to improve the Materials and Methods section of this manuscript in their review, which we do not include here for space considerations.
__Our Response to Reviewer #1 Comment #19. __We have addressed all of the reviewer’s comments regarding the Materials and Methods section in our revised manuscript.
Reviewer #1 Comment #20. The reviewer made many suggestions about the presentation of our figures that we do not include here for space considerations.
Our Response to Reviewer #1 Comment #20. __We have addressed all of the reviewer’s comments regarding the Figures__ in our revised manuscript.
REVIEWER #2.
Reviewer #2 General Comments. “Previous studies have shown that ER stress increases amounts of phosphatidic acid (PA) (PMID: 22493067) and induces elongation of mitochondria through the protein and lipid kinase PERK (PMID: 29539413, work by Wiseman's lab). The current work reports that ER stress by thapsigargin promotes the degradation of a mitochondrial protein PRELID1, which transfers PA from the outer membrane to the inner membrane. An inner membrane protease, YME1L, was identified as responsible for this degradation of PRELID1. Consistent with the notion that PA is required for the morphological change, overexpression of a PA phosphatase (Lipin) or a PA phospholipase (PA-PLA1) decreased ER-stress-induced mitochondrial elongation.”
“Overall, this manuscript is a nice extension of the authors' previous work and investigates the molecular mechanism underlying the regulation of mitochondrial elongation induced by ER stress. However, the current data do not strongly support the role of PRELID1 in either ER-stress-mediated PA level elevation or mitochondrial elongation, as described in Specific comments. The authors should address these points.”
__Our Response to Reviewer #2 General Comments. __We thank the reviewer for the thorough and careful read of our manuscript. We address the specific points brought up by the reviewer in our revised manuscript, as described below.
Reviewer #2 Comment #1. “The authors report that PRELID1 knockdown did not promote mitochondrial elongation under either normal or ER-stress conditions (Fig. 5). If PRELID1 plays a vital role in mitochondrial elongation, PRELID1 depletion will restore elongation. Therefore, the presented data argue against the authors' conclusion. Since PRELID1 has multiple homologs, including PRELID3B, which is also a short-lived protein like PRELID1, these homologs might redundantly function in PA transport, especially when PRELID1 is absent. Therefore, the authors need to knock them down simultaneously. This possibility is consistent with the previous authors' data that YME1L depletion decreases ER-stress-induced mitochondrial elongation (PMID: 29539413). YME1L knockdown may rescue multiple short-lived PRELID1 homologs.”
Our Response to Reviewer #2 Comment #1. __Our model indicates that ER stress-dependent increases in mitochondrial elongation require two steps: 1) PERK kinase-dependent increases in total PA and 2) YME1L-dependent degradation of PRELID1 downstream of PERK-dependent translation attenuation. Thus, it is not surprising that PRELID1 depletion did not induce mitochondrial elongation on its own. However, we do demonstrate that depletion of PRELID1 rescues Tg-induced mitochondrial elongation in cells co-treated with the PERK signaling inhibitor ISRIB – a compound that specifically blocks Tg-dependent PRELID1 degradation, but not PERK kinase dependent increases in total PA (__Fig. 6). This demonstrates that PRELID1 reductions are required, but not sufficient for promoting mitochondrial elongation. We make this point more clear in the revised manuscript.
Line 259: “Interestingly, Prelid1 depletion did not basally influence mitochondrial morphology or inhibit Tg-induced mitochondrial elongation (Fig. 5A,B and Fig. S5E). This indicates that reduction of PRELID1, on its own, is not sufficient to increase mitochondrial elongation, likely reflecting the importance of PERK kinase-dependent increases in PA in this process.53”
With respect to PRELID3B/SLMO2. This lipid transporter is primarily associated with trafficking phosphatidylserine (PS) from the outer to the inner mitochondrial membrane, where it is then converted to phosphatidylethanolamine (PE). As alluded to by the reviewer, we found that SLMO2, like PRELID1, is also a short-lived mitochondrial protein that is rapidly degraded by YME1L downstream of PERK-dependent translation attenuation. We have also found that Tg treatment disrupts mitochondrial PE levels through a PERK-dependent mechanism on a similar timescale to that observed for PA changes. However, shRNA depletion of SLMO2 in HeLa cells – a condition that mimics the reductions in SLMO2 observed during ER stress – increases basal mitochondrial fragmentation and inhibits Tg-induced mitochondrial elongation. Since chronic, genetic reductions in SLMO2 (which mirror the acute reduction in SLMO2 observed during ER stress) show opposite impacts on mitochondrial morphology to that observed upon Tg treatment, we interpreted this result to indicate that SLMO2 reductions are likely not involved in PERK-dependent regulation of mitochondrial elongation during acute ER stress. In contrast, depletion of PRELID1 is sufficient to rescue Tg-induced mitochondrial elongation in cells co-treated with ISRIB (Fig. 5A-D) – a compound that selectively blocks ER stress-dependent reductions in PRELID1. This implicates reductions in PRELID1 in this process. We are continuing to define the specific impact of PERK-dependent regulation of SLMO2 on mitochondrial morphology, ultrastructure, and/or function in work outside the scope of this current manuscript, but we felt it most appropriate to focus this manuscript on PA-dependent morphology remodeling based on the presented data.
Reviewer #2 Comment #2. “Another possibility is that since a previous study has shown that PERK-produced PA activates the mTOR-AKT pathway (PMID: 22493067), this signaling pathway may contribute to mitochondrial morphology in addition to PRELID1. The authors should test the combined effects of mTOR-AKT inhibition in ER-stress-induced mitochondrial elongation.”
Our Response to Reviewer #2 Comment #2. __As highlighted by the reviewer, PERK-dependent increases in PA can influence mTOR and AKT activity. To test this, we monitored mTOR-dependent S6K phosphorylation and AKT phosphorylation in MEFmtGFP and HeLa cells treated with Tg for 3 h. While we did observe increases in S6K phosphorylation in Tg-treated MEFmtGFP cells, mTOR activity was not changed in Tg-treated HeLa cells. AKT phosphorylation was not affected in MEFmtGFP or HeLa cells (not shown). We include these mTOR data in the revised manuscript (see __Fig. S3C,D). Since we observe PERK-dependent mitochondrial elongation in both MEFmtGFP and HeLa cells, we interpret these results to indicate that PA-dependent increases in mTOR activity is not primarily responsible for ER stress dependent increases in mitochondrial elongation across cell types. We describe these results in the revised manuscript.
Line 156: “In contrast, PERK-dependent increases in PA can activate mTOR during ER stress.53 Consistent with this, we observe Tg-dependent increases in mTOR-dependent S6K phosphorylation in MEFmtGFP cells (Fig. S3C). However, despite increasing PA and promoting mitochondrial elongation, Tg did not increase S6K phosphorylation in HeLa cells (Fig. S3D). These results suggest that PERK-dependent alterations in mTOR activity are unlikely to be primary contributors to ER stress induced mitochondrial elongation across cell types.”
Reviewer #2 Comment #3. “The authors' model suggests the loss of PRELID1 increases PA levels in the mitochondrial outer membrane (Fig. 6). The authors should test PA levels in mitochondria isolated from cells depleted for PRELID1 and its homologs (simultaneously). Since PA that is transported to the inner membrane is actively converted to other phospholipids, such as CDP-DAG, elevated levels of PA are likely seen if the outer membrane to inner membrane transport is blocked.
Our Response to Reviewer #2 Comment #3. __We agree with the reviewer it is important to evaluate how PERK-dependent degradation of PRELID1 impacts other phospholipids dependent on PA trafficking to the IM where it can be converted to other lipids, most notably cardiolipin (CL). In the revised manuscript, we now show measurements of CL in MEFmtGFP cells treated with Tg and/or depleted of Prelid1. As expected, reductions in PRELID1 decrease CL in isolated mitochondria (__Fig. S5C). Treatment with Tg reduced CL to similar extents in MEFmtGFP-treated cells expressing non-silencing shRNA. However, we did not observe further reductions of CL in Prelid1-depleted cells. This is consistent with a model whereby ER stress-dependent reductions in PRELID1 decrease PA trafficking across the IMS and lead to reductions in CL synthesis. These results are discussed in the revised manuscript as below:
Line 214. “PRELID1 traffics PA from the outer to inner mitochondrial membrane, where it serves as a precursor to the formation of cardiolipin.56,66,67* Thus, reductions in PRELID1 should decrease cardiolipin. To test this, we shRNA-depleted Prelid1 from MEFmGFP cells and monitored cardiolipin in isolated mitochondria in the presence or absence of ER stress. We confirmed efficient PRELID1 knockdown by immunoblotting (Fig. S5A). Importantly, Prelid1 depletion did not alter Tg-induced reductions of TIM17A or increases of ATF4. Further, Tg-dependent increases in PA were observed in Prelid1-depleted MEFmtGFP cells (Fig. S5B). These results indicate that loss of PRELID1 does not impair PERK signaling in these cells. Prelid1 depletion reduced cardiolipin in mitochondria isolated from MEFmtGFP cells (Fig. S5C). Treatment of MEFmtGFP cells expressing non-silencing shRNA with Tg for 3 h also reduced cardiolipin to levels similar to those observed in Prelid1-deficient cells. However, Tg did not further reduce cardiolipin in Prelid-depleted cells. These results are consistent with a model whereby ER stress-dependent reductions in PRELID1 limit PA trafficking across the inner mitochondrial membrane and contribute to reductions in cardiolipin during acute ER stress.” *
We are continuing to define how PERK signaling influences other mitochondrial phospholipids during conditions of ER stress in work outside the scope of this manuscript. Notably, we are continuing to evaluate how ER stress and PERK signaling influences aspects of cardiolipin synthesis in response to both acute and chronic ER stress. Further, as discussed above, we are determining how PERK-dependent reductions in PRELID3B/SLMO2 influence PS trafficking and subsequent PE synthesis at the IM and the implications of these changes on mitochondrial biology. Initial experiments indicate that PERK signaling reduces PE during ER stress, indicating that other phospholipids can be influenced by this pathway. However, we view this work as being outside the scope of the current manuscript focused specifically on defining the impact of PA remodeling on mitochondrial morphology.
Reviewer #2 Comment #4. “The authors need to test whether Lipin and PA-PLA1 overexpression decreased PA levels in mitochondria treated with thapsigargin. The current manuscript only shows the effect of Lipin and PA-PLA1 on PA levels in whole-cell lysate without ER stress (Fig. S2F).”
Our Response to Reviewer #2 Comment #4. __We agree. In the revised manuscript, we now show that Lipin overexpression blocks Tg-dependent increases in PA (__Fig. 2C). Identical experiments are also shown for Prelid1-depleted cells (Fig. S5B).
Reviewer #2 Comment #5. “The authors propose that PA inhibits DRP1 in mitochondrial division under ER stress. It has been shown that PA blocks DRP1 after recruitment to mitochondria (PMID: 27635761). Does thapsigargin induce mitochondrial accumulation of DRP1?”
Our Response to Reviewer #2 Comment #5. __The reviewer is correct that our results suggest that ER stress promotes mitochondrial elongation through a model involving PA-dependent inhibition of mitochondrial fission at the outer membrane. In the revised manuscript, we now show that Tg treatment does not significantly influence the recovery of DRP1 in mitochondrial fractions (__Fig. S3A). Further, we recapitulate results from previous publications showing that Tg does not significantly influence DRP1 phosphorylation at either S637 or S616 (Fig. S3B). This indicates that DRP1 localization and posttranslational modification does not appear affected by Tg treatment. However, we do show that Tg pretreatment inhibits DRP1-dependent mitochondrial fission induced by ionomycin (Fig. 3D,E). Combined with other results, our data are consistent with a model whereby PERK-dependent increases in PA and PRELID1 degradation leads to the accumulation of PA on the OM where it can inhibit DRP1 activity (Fig. 6). We make this point clearer in the revised manuscript.
Line 154: “However, as reported previously39, Tg did not influence DRP1 phosphorylation at either S637 or S616 (Fig. S3A) or alter the amount of DRP1 enriched in mitochondrial fractions from MEFmtGFP cells (Fig. S3B).”
REVIEWER #3.
Reviewer #3 General Comments. “The authors investigated signaling pathways and molecular mechanisms leading to mitochondrial dysfunction after ER stress. This study extends their previous publication (Lebeau et al., 2018) by providing evidence on how PERK regulates mitochondrial structure and function in response to ER stress. Some key findings are that PERK induces mitochondrial elongation by increasing and retaining phosphatidic acid (PA) in the outer mitochondrial membrane which is important for cell adaptation and survival. This process requires PERK-dependent translational attenuation through YME1L-PRELID dependent mechanism. This is a very strong study with compelling evidence.”
“This study adds to our current knowledge on how ER stress affects mitochondria adaptation and proteostasis, which may contribute to the pathogenesis and progression of numerous neurodegenerative diseases. Specifically, this study establishes a new role for PERK in mitochondrial adaptive remodeling focused on trafficking and accumulation of phospholipids. Identifying molecular markers like PERK and its involvement with PRELID, YME1L, and PA to regulate mitochondrial remodeling during ER stress is important to understand the effects of drug-targeting this ER stress-responsive factor.”
__Our Response to Reviewer #3 General Comments. __We thank the reviewer for the enthusiastic comments about our manuscript. We address the reviewers remaining concerns as outlined below.
Reviewer #3 Comment #1. “Only one minor point should be addressed: In Fig S2G & H, the authors indicate that "Lipin1 overexpression did not significantly influence increases of ATF4 protein". The blots show a decrease in ATF4 in Tg-treated HeLa cells. The same effect is observed in Fig. S3F showing reduction in ATF4, but the authors described it as the "overexpression of mitoPLD did not significantly impact other aspects of PERK signaling in Tg-treated cells". The quantification of the blots or indication that the blots were quantified should be clarified and noted (at least in the legend).”
Our Response to Reviewer #3 Comment #1. __We agree. We now include quantification of ATF4 in immunoblots from HeLA cells overexpressing lipin1 and treated with Tg (__Fig. S2J). As we suggested, these results confirm that Tg treatment does not significantly influence ATF4 expression in these cells. In addition, we now include additional data showing that lipin overexpression does not significantly reduce Tg-dependent expression of ISR target genes including Asns or Chop (Fig. S2I). This further supports other findings in the manuscript showing that different manipulations do not significantly impact ISR signaling (evident by ATF4 expression or TIM17A or PRELID1 degradation).
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Referee #3
Evidence, reproducibility and clarity
The authors investigated signaling pathways and molecular mechanisms leading to mitochondrial dysfunction after ER stress. This study extends their previous publication (Lebeau et al., 2018) by providing evidence on how PERK regulates mitochondrial structure and function in response to ER stress. Some key findings are that PERK induces mitochondrial elongation by increasing and retaining phosphatidic acid (PA) in the outer mitochondrial membrane which is important for cell adaptation and survival. This process requires PERK-dependent translational attenuation through YME1L-PRELID dependent mechanism.
This is a very strong study with compelling evidence. Only one minor point should be addressed: In Fig S2G & H, the authors indicate that "Lipin1 overexpression did not significantly influence increases of ATF4 protein". The blots show a decrease in ATF4 in Tg-treated HeLa cells. The same effect is observed in Fig. S3F showing reduction in ATF4, but the authors described it as the "overexpression of mitoPLD did not significantly impact other aspects of PERK signaling in Tg-treated cells". The quantification of the blots or indication that the blots were quantified should be clarified and noted (at least in the legend).
Significance
This study adds to our current knowledge on how ER stress affects mitochondria adaptation and proteostasis, which may contribute to the pathogenesis and progression of numerous neurodegenerative diseases. Specifically, this study establishes a new role for PERK in mitochondrial adaptive remodeling focused on trafficking and accumulation of phospholipids. Identifying molecular markers like PERK and its involvement with PRELID, YME1L, and PA to regulate mitochondrial remodeling during ER stress is important to understand the effects of drug-targeting this ER stress-responsive factor.
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Referee #2
Evidence, reproducibility and clarity
Summary
Previous studies have shown that ER stress increases amounts of phosphatidic acid (PA) (PMID: 22493067) and induces elongation of mitochondria through the protein and lipid kinase PERK (PMID: 29539413, work by Wiseman's lab). The current work reports that ER stress by thapsigargin promotes the degradation of a mitochondrial protein PRELID1, which transfers PA from the outer membrane to the inner membrane. An inner membrane protease, YME1L, was identified as responsible for this degradation of PRELID1. Consistent with the notion that PA is required for the morphological change, overexpression of a PA phosphatase (Lipin) or a PA phospholipase (PA-PLA1) decreased ER-stress-induced mitochondrial elongation.
Specific comments
- The authors report that PRELID1 knockdown did not promote mitochondrial elongation under either normal or ER-stress conditions (Fig. 5). If PRELID1 plays a vital role in mitochondrial elongation, PRELID1 depletion will restore elongation. Therefore, the presented data argue against the authors' conclusion. Since PRELID1 has multiple homologs, including PRELID3B, which is also a short-lived protein like PRELID1, these homologs might redundantly function in PA transport, especially when PRELID1 is absent. Therefore, the authors need to knock them down simultaneously. This possibility is consistent with the previous authors' data that YME1L depletion decreases ER-stress-induced mitochondrial elongation (PMID: 29539413). YME1L knockdown may rescue multiple short-lived PRELID1 homologs.
- Another possibility is that since a previous study has shown that PERK-produced PA activates the mTOR-AKT pathway (PMID: 22493067), this signaling pathway may contribute to mitochondrial morphology in addition to PRELID1. The authors should test the combined effects of mTOR-AKT inhibition in ER-stress-induced mitochondrial elongation.
- The authors' model suggests the loss of PRELID1 increases PA levels in the mitochondrial outer membrane (Fig. 6). The authors should test PA levels in mitochondria isolated from cells depleted for PRELID1 and its homologs (simultaneously). Since PA that is transported to the inner membrane is actively converted to other phospholipids, such as CDP-DAG, elevated levels of PA are likely seen if the outer membrane to inner membrane transport is blocked.
- The authors need to test whether Lipin and PA-PLA1 overexpression decreased PA levels in mitochondria treated with thapsigargin. The current manuscript only shows the effect of Lipin and PA-PLA1 on PA levels in whole-cell lysate without ER stress (Fig. S2F).
- The authors propose that PA inhibits DRP1 in mitochondrial division under ER stress. It has been shown that PA blocks DRP1 after recruitment to mitochondria (PMID: 27635761). Does thapsigargin induce mitochondrial accumulation of DRP1?
Significance
Overall, this manuscript is a nice extension of the authors' previous work and investigates the molecular mechanism underlying the regulation of mitochondrial elongation induced by ER stress. However, the current data do not strongly support the role of PRELID1 in either ER-stress-mediated PA level elevation or mitochondrial elongation, as described in Specific comments. The authors should address these points.
Audience ER stress, mitochondrial dynamics, membrane lipids, proteases
My Expertise mitochondrial dynamics, lipid biology
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Referee #1
Evidence, reproducibility and clarity
Summary:
This study investigates changes in mitochondrial morphology in response to ER stress due to pharmacological inhibition or genetic dysfunction in vitro via two different cell models (MEFs and HeLa cells). The authors specifically implicate the PERK branch of the ER-stress induced pathway in this process based on the observation that mitochondria elongate in response to thapsigargin (Tg) treatment which is blocked by the pathway inhibitors GSK and ISRIB or by genetic ablation of Perk/PERK. Homozygous knockout cells lacking PERK exhibit a fragmented mitochondrial phenotype even in the absence of Tg, which is rescued by expression of the wildtype but not a hypomorphic allele (PERKPSP). One of the more interesting suppositions of this manuscript is that mitochondrial elongation is dependent on the abundance of phosphatidic acid (PA); treatment with Tg provokes an increase in mitochondrial PA, but PA does not accumulate in mitochondria from cells co-treated with GSK, an inhibitor of PERK. This correlation suggests that increased mitochondrial PA accumulation is PERK-dependent. In addition, predicted manipulation of PA levels achieved by a gain of function expression of the lipase Lipin diminished mitochondrial elongation in response to ER stress. Similar results were obtained by PA-PLA1 overexpression, a cytosolic lipase that converts PA into lysophosphatidic acid (LPA). To further describe the mechanistic link between ER stress and mitochondrial morphology, the authors found that PRELID1, which transports PA from the OMM to the intermembrane space, and TIM17A, a component of the protein translocation machinery, were stabilized by loss of PERK or YME1L [and possibly an effect of ATF4], regardless of ER stress via Tg treatment. The authors also report that Tg treatment prevents OPA1 cleavage in cells treated with CCCP, an uncoupler of the proton gradient, suggesting that the effect due to Tg treatment is not through ER stress but decreased mitochondrial fusion via mito-stress induced OPA1 cleavage. To address this, cells were treated with ionomycin which induces mitochondrial fragmentation independent of DRP1. The authors observed an increase in mitochondrial fragmentation in the presence of ionomycin. However, co-treatment with Tg prevented fragmentation, as did overexpression of mitoPLDGFP, which converts cardiolipin to PA on the OMM. These results support a model in which, under ER stress conditions, PERK activation leads to translational attenuation, which leads to a decrease in the steady state levels of PRELID1 via YME1L-dependent degradation and to the accumulation of PA on the OMM. Based on published work this PA accumulation is expected to inhibit the mitochondrial division dynamin, DRP1. The authors tested this by examining the dependence of mitochondrial elongation on PRELID1.
Major comments:
- Are the key conclusions convincing?
A considerable amount of work was performed by the authors in preparation of this manuscript and while we find the model exciting, there are several issues that need to be addressed in order for the model to be sufficiently supported.
- Image quality of mitochondria is sub par and the images do not always appear representative of/match the accompanying histograms. When using a single fluorescent marker (mito-GFP), the images should be in grey scale.
- Mitochondria in Perk-/- MEFs are highly fragmented, which is potentially inconsistent with previous work (Lebeau J, et al. 2018) performed by the same research group. Can the authors comments on this discrepancy? Also, do the authors interpret this fragmentation to mean that Perk is required to maintain mitochondrial elongation in the absence of exogenous ER stress (Tg)? If so, the authors should test whether expression of a dominant negative version of DRP1 rescues this fragmented morphology. This would be an additional critical test of the authors' model.
- The authors postulate that mitochondrial elongation in response to Perk activation is specifically outer membrane PA-dependent negative regulation of DRP1. However, PA is readily convertible to other phospholipids, notably CL and LPA, both of which positively regulate mitochondrial fusion. The authors do not measure abundance of other phospholipids, particularly LPA or CL in their targeted lipidomics experiments, only PC. The authors need to consider this alternate possibility.
- In Figure 5, the authors found very little difference in mitochondrial elongation following knockdown of Prelid1 (comparison between vehicle only conditions), which is potentially inconsistent with their model as decreased PRELID1 should lead to increased OMM PA [and subsequently mitochondrial fusion/elongation].
- The manuscript requires more careful editing - there were grammatical and punctuation errors.
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? In Figure 5, the authors found very little difference in mitochondrial elongation following knockdown of Prelid1 (comparison between vehicle only conditions), which is potentially inconsistent with their model as decreased PRELID1 should lead to increased OMM PA [and subsequently mitochondrial fusion/elongation]. Therefore, these findings do not adequately support the authors' main model.
- 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.
- a. In order to further investigate the contribution PRELID1-dependent accumulation of PA in the OMM and its role in mitochondrial elongation, the authors should investigate the abundance of PA (and other lipids) in Perk, Prelid, Yme1l KO mutants. These experiments should quantitatively complement the results in Figure 5. KD of Prelid would be expected to increase mitochondrial elongation but there is no difference compared to WT in Figure 5.
- b. The main premise is that ER-stress activates PERK which in turn leads to increased abundance of PA at the OMM in a PRELID1-dependent manner. PA has been shown to inactivate DRP1, resulting in decreased fission (and mitochondrial elongation). The authors should test their model by expressing a dominant negative allele of DRP1 to see if it rescues the fragmented morphology of Perk KO mutant.
- 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.
- a. The authors have all the necessary cell line and methods in hand, so we consider these experiments to be doable.
- Are the data and the methods presented in such a way that they can be reproduced?
- a. Not all are described in a way that could be easily reproduced (see specific comments below).
- Are the experiments adequately replicated and statistical analysis adequate?
- a. The foundation of this paper is based on qualitative analysis of confocal fluorescence microscopy images, but the chosen images are often not of high quality so performing statistical analysis in these cases is misleading. Also, each imaging-based experiment was performed three times, but with only 20 cells for each replicate. Does this represent sufficient statistical power?
Specific major comments by section
Introduction - No additional major comments.
Results - Title of the subsection: "hypomorphic PERK variants inhibit ER..." is inappropriate since authors only investigated a single hypomorphic variant (PSP). KO mutant is a null not hypomorphic mutant.
Discussion - Can the authors elaborate on the possible biological relevance for the inhibition of OPA1 cleavage via Tg treatment? - PRELID is a known short-lived protein; can the authors elaborate on possible additional impact due to 3-6 hr Tg treatment which is sufficient to induce expression of ATF4 target genes (Figure S2G). - Thapsigargin induced ER stress does not only activate PERK arm of the ISR, correct? Could the authors comment on this?
Methods - Addition of drugs and duration (3-6 hrs) likely very toxic to cells; how does this treatment affect viability? Unhealthy cells will have unhealthy mitochondria so it's hard to be confident that subtle morphological differences are specific. Why do authors use 3 hrs Tg-treatment after initially using 6 hrs in Figure 1? Would be helpful to assay toxicity and mitochondrial morphology of thapsigargin and other drugs in WT vs. Perk KO MEFs over time. Previously, an increase in fragmentation was observed at 0.5 hours but this subsided by 6 hours in WT (Lebeau J, et al. 2018) but is this the same for Perk KO MEFs? Figures/supplementary figures - General: - In several images there is substantial background GFP signal resulting in images that are fuzzy on the high quality PDF (printout is unintelligible). - Example: Figure 2, Mock+veh. - Example: Figure S2I, Mock+veh, +PA-PLA Tg. - Example: Figure 3C mock+veh. - Mitochondrial morphology doesn't appear uniform even within the same cell so how is this accounted for in scoring of mitochondrial morphology? Also, how are authors scoring mitochondrial morphology? Due to the inconsistencies in the chosen images, we feel this manuscript would benefit from addition of a supplementary figure showing examples for each cell model expressing mtGFP (i.e. HeLa and MEFs) depicting the fragmented, tubular and elongated mitochondria. This should be able to be constructed from images already collected for these analyses that weren't already used in the paper. - Images from prior paper (Lebeau J, et al. 2018) are of much higher quality and is much easier to discern mitochondrial phenotype. - How much protein was loaded per lane and what was the percentage of polyacrylamide gel? Please clarify details in methodology. - Figure 1: - See general comments. - Figure 1A is virtually identical to Figure 2A (with exception of "MEF A/A") from previous publication: Lebeau J, Saunders JM, Moraes VWR, Madhavan A, Madrazo N, Anthony MC, Wiseman RL. The PERK Arm of the Unfolded Protein Response Regulates Mitochondrial Morphology during Acute Endoplasmic Reticulum Stress. Cell Rep. 2018 Mar 13;22(11):2827-2836. doi: 10.1016/j.celrep.2018.02.055. PMID: 29539413; PMCID: PMC5870888. - Figure 1B: the complemented Perk KO + vehicle should be similar to WT vehicle, but those images look quite different, even so, the respective bars are equal. - Vehicle treated Perk-/- cells have fragmented morphology which is different from Figure 2F in above publication by same group. Can the authors explain this discrepancy? - Figure S1: - No additional major comments. - Figure 2: - See general comments. - If the authors' hypothesis is correct, overexpression of PRELID1 should have same effect as overexpression of Lipin. ● Figure S2: - Images in Figure S2I are not representative of corresponding bars in Figure S2J (specifically vehicle treated panels). The "+PA-PLA1+Tg" panel instead appears fragmented (in comparison with other images). - Do authors have clearer images to substitute for CHX-treated panels? ● Figure 3: - What is the selective marker used for HeLa cells expressing mitoPLDGFP since the HeLa parental cell background already expressed a mitochondrial targeted GFP, we assume it was puromycin but this was not clear in the Figure legend or methods? If so, it would be helpful to clarify this. If not, how can the authors observe a difference in morphology if the selectable marker is the same? Indeed, mitoPLDGFP is expressed, detectable by immunoblot, but this is on a cell population level so no way of knowing whether the specific cells scored expressed mitoPLDGFP unless another selectable marker was used (i.e. should have used CFP, RFP, etc.). - The authors state "Note the expression of mitoPLDGFP did not impair our ability to accurately monitor mitochondrial morphology in these cells." in Figure 3 legend and again basically the same in S3: "Note that the expression of the mitoPLDGFP did not impair our ability to monitor mitochondrial morphology in these cells." Could the authors explain their reasoning here? - Figure S3: - Same as in Figure 3; "mock+Veh" appears more fragmented than tubular so is there a more representative image that the authors can show? - Figure 4: - No major comments. - Figure S4: - Figure S4C: the authors show that Tg treatment on MEF mtGFP cells for distinct hours to determine PRELID levels. However, in the Results section states that this treatment was with CHX, could the authors please check this and correct? - Figure 5: - 5C: PLKO NS shRNA +Tg appears more fragmented than tubular; do the authors have a more representative image? - Figure S5: - No major comments. - Figure 6: - A schematic representation should be a graphic summary of all findings reported in the text with no text except where absolutely essential. A good model should be easily understood without reading any description since all concepts were supported in the main text and by experimentation. - The model also contains some inaccuracies. The suggestion is that the authors re-do the model and clarify some aspects such as: - The model suggests that ISRIB inhibits PRELID1 directly but there is no evidence for this whereas PRELID is directly regulated by YME1L (also typo here in figure: "Yme1" no "l"). - This model incorrectly uses inhibition symbols; for example, mutation of Perk does not inhibit its activity as GSK does. The KO does not have Perk so cannot perform its function. These are not the same. Similarly, the lipases (Lipin and PA-PLA1) should be depicted instead as altering flux of PA away from OMM not as inhibition. - The authors should connect PA accumulation in the OMM graphically to mitochondrial elongation [instead of through text]. If the authors consider the numbered labels convenient, please use just the number and place the description in the figure legend instead.
Minor comments:
- Specific experimental issues that are easily addressable.
- a. Yes, please see specific examples below.
- Are prior studies referenced appropriately?
- a. References appeared adequate except in the Materials and Methods section (see specific examples below).
- Are the text and figures clear and accurate?
- a. No, the text needs considerable editing to make the language clearer and formal whereas the figures are not always presented in a manner that is easily absorbed by the reader. Representative microscopy images chosen do not always match the corresponding graphical summary and are not clear even on PDF version compared to (Lebeau J, et al. 2018 - full citation above).
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
- a. Yes, please see specific examples below.
Specific minor comments by section
Introduction - This section contains minor grammatical errors and awkward writing which should be rephrased to be more concise. For example: - Incorrect use of commas (ex: absence of commas on page 3, bottom of paragraph 3).
Results - Overall, this section contains many grammatical errors and awkward language but these are unevenly distributed as some subsections are well written and thoroughly edited whereas others need closer inspection. For example: - No period at end of first subsection title; this should be consistent throughout. - Text not consistently written in past tense/passive voice. - Post-translational should be hyphenated (page 5, 2x on bottom of page). - The use of dashes to conjoin thoughts is too casual and sentences should be restructured with the aid of parentheses or semicolons only when necessary (ex: page 6, paragraph 2 through page 7). - Homogenize the use of hyphens in all sentences such as: ER stress-induced, ER stress-dependent.
Discussion
- Minor grammatical errors and awkward wording throughout; description of ideas should be more concisely written. For example:
- Page 13, paragraph 1: "Thus, an improved understanding of how different PERK-dependent alterations to mitochondrial morphology and function integrate will provide additional insight to the critical importance of this pathway in regulating mitochondria during conditions of ER stress."
- Page 13, paragraph 2: "Further investigations will be required to determine the specific impact of altered PERK signaling on mitochondria morphology and function in the context of these diseases to reveal both the pathologic and potentially therapeutic implications of PERK activity on the mitochondrial dysfunction observed in the pathogenesis of these disorders."
- Awkward/oxymoronic word choices. For example:
- Page 11, paragraph 2: "...GSK2606414 reduces Tg-dependent increases of PA..." could be written as "... blocks/limits Tg-dependent increase of PA..." instead.
- What is evidence that ionomycin is completely independent of DRP1?
Methods
- Please provide more description or a reference for the method used for CRISPR/Cas9 gene editing (page 15, paragraph 1).
- Since different versions of chemicals are often available from the same company (for example in solution vs. powder, as a salt, different purities, etc.) it would be helpful for the authors to also include the catalog number for the purchased drugs and analytical standards (page 16, paragraph 1).
- The authors did an excellent job of blinding these images and utilizing several researchers to score each. However, we feel that 20 cells per biological replicate (~60 total per condition) is insufficient when mitochondrial morphology in chosen representative images is unclear. We think it is reasonable to request the authors to score additional images they collected as part of this investigation.
- The below two sentences contain some redundancies and should be combined/rephrased (page 16, paragraph 2).
- "Three different researchers scored each set of images and these scores were averaged for each individual experiment. All quantifications shown were performed for at least 3 independent experiments, where averages in morphology quantified from each individual experiment were then combined."
- Incorrect units, for example: "500g" should be "500 x g" on page 16, paragraph 3 and "g" should be italicized. Same for "200g" on page 17, paragraph 1.
- Inconsistent abbreviation of chemicals, for example:
- Chloroform and hydrochloric acid but not methanol in methods on page 17, paragraph 1. Also, the "l" in "HCL" should be lowercase.
- "Solvents" (2x) on page 17, paragraph 2 should be singular not plural.
- What does RT stand for on page 17, paragraph 2?
- Tris buffered saline is abbreviated incorrectly as "TB" then correctly later in the same paragraph as "TBS" on page 18, paragraph 3.
- Paragraph 4 on page 18 should be indented to be consistent with formatting of previous methods sections.
- To remove any ambiguity, catalog numbers should be included for antibodies (also consider including the lot number as there can be lot to lot variability).
- What percentage of tween v/v was supplemented in TBS buffer? Different concentrations of tween can impact antibody binding and would beneficial to include for reproducibility.
- Please indicate the incubation time and conditions for the secondary antibodies.
- The abbreviation for phosphate buffered saline is "PBS" not "PBD" (page 19, paragraph 1).
- Could the authors state clearly the reference transcript used for RT-qPCR (assumed is RIBOP)?
- Sometimes GIBCO is capitalized, sometimes not (Gibco), which should also be consistent.
- Who is the supplier for CCCP and what is the catalog number? Similarly, what is the catalog number for TMRE (both on page 19, paragraph 3)?
- Student's t-test is capitalized and possessive (similar to Tukey's) on page 19, paragraph 4.
Figures/supplementary figures
- General:
- With respect to the lines overlaying histograms scoring mitochondrial morphology for designating statistical significance [with color-coded asterisks]:
- It is assumed that the bars of the histogram being compared are those at the ends of each line but these aren't aligned perfectly. Please tidy up the figure by shifting these and consider capping lines to make more clear.
- It appears that the authors provide these lines at all instances of statistically significant differences whether the comparison is important to their conclusions or not; including only the necessary comparisons will reduce the noise of these figures and make them easier to absorb and interpret. For example:
- Figure 1C: why is comparison being made only for KO vs. complemented (+veh) - difference between KO and WT not statistically significant? Also, wouldn't the difference between WT and KO +Tg percent fragmented be statistically significant? The comparisons being made appear arbitrary or if not, was not clearly stated (same criticism for 2D, 3B, 3D, etc.).
- The authors appear to use "transfection" and "transduction" interchangeably such that it is unclear whether expression of transgenes or shRNA is stably vs. transiently expressed. It would help if the authors could clarify their language here as well.
- With respect to the lines overlaying histograms scoring mitochondrial morphology for designating statistical significance [with color-coded asterisks]:
- Figure 1:
- Figure 1A - PERK is membrane bound not soluble; should this not be represented in the model? Model colors are not easily distinguishable from each other on printout and should be upgraded.
- Figure 1C - phenotypic scoring is not easy to interpret; perhaps authors could rearrange the figure such that each treatment is adjacent since that is the more interesting comparison? All cells in figure 1 are MEFs so delete "MEFs" below Perk+/+ and Perk -/-.
- Figure S1:
- How much protein was loaded per lane and what percentage of polyacrylamide gel was used?
- Figure 2:
- See general comments.
- Figure 2A - extra letter/typo in "Fold Change."
- Why do authors switch to HeLa cells after measuring PA content in MEFs?
- Figure S2:
- Authors are now including ns for "not significant" and the p value where before they were not before. The intent for including the p-value in S2B appears to be because it suggests a trend towards statistical significance (actually a bit surprised it is not based on SEM error bars; authors should recheck their calculations) which is inappropriate. Either provide all the p-values, possibly as a separate table or none at all.
- Now including double headed error bars for S2D-E which is inconsistent with rest of manuscript.
- What is standard error for vehicle treated cells in 3B, 3D, and 3E? Given the above mistake it's reasonable to suspect that the error bars were omitted by accident.
- Figure 3:
- Title should have hyphen for "stress-induced" and ionomycin shouldn't be capitalized.
- Now using double headed error bars for 3B which is inconsistent with majority of other figures.
- Figure S3:
- Title should have hyphen for "stress-induced" and ionomycin shouldn't be capitalized.
- Figure 4:
- What is the purpose of including 4A? This depicts a concept which is not particularly difficult to grasp, was not experimentally shown in this manuscript, and is somewhat redundant with Figure 6. We recommend removing from Figure 4 and combining with Figure 6.
- Since all cells used in Figure 4 were MEFs, the authors can remove "MEFs" from figure and just include genotype.
- Figure 4C: typo in Yme1l - has two 1's.
- Figure S4:
- See general comments.
- Figure 5:
- Figure 5C: What does PLKO abbreviation stand for in the control line? pLKO.1 vector (see methods but not explained further).
- Figure S5:
- Figure S5A-B: KD clearly worked but how efficient is unclear (quantitatively, i.e. 50, 90%, etc.?). The authors could perform serial dilutions of protein (i.e. 5, 10, 20 ug of the same samples for SDS-PAGE/immunoblot) or RT-qPCR. If knockdown is incomplete, this could explain the discrepancy in Figure 5 where depletion of Prelid should result in elongation [via OMM depletion of PA].
- Figure 6:
- This is a more appropriate location for panel 4A.
Significance
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
- a. Perturbances in PERK signaling evoke an alteration in mitochondrial morphology and have been extensively reported on, due to their clinical implications on neurodegenerative disorders such as Alzheimer's disease. The present work provides insight into the molecular basis for Stress Induced Mitochondrial Hyperfusion (SIMH) which can be triggered by ER stress. The authors find that this process occurs downstream of PERK and proceeds through accumulation of PA in the OMM by stabilization of Prelid, a mitochondrial resident protein that transports PA from the OMM to IMM for cardiolipin synthesis. The evidence of this work represents a substantial addition to the field of mitochondrial dynamics/SIMH and the Unfolded Protein Response.
- Place the work in the context of the existing literature (provide references, where appropriate).
- a. The novelty of this work is in the inclusion of PRELID1 downstream of PERK signaling pathway for transmission of ER stress to the mitochondria, a process that involves phosphatidic acid (PA). Some studies have addressed how phosphatidic acid is a modulator and a signal in mitochondrial physiology. The role of the lipids in mitochondrial dynamics represent an important and emerging field that needs to be explored in order to understand how metabolites control mitochondrial fusion/fission.
References
Yoshihiro Adachi, Kie Itoh, Tatsuya Yamada, Kara L. Cerveny, Takamichi L. Suzuki, Patrick Macdonald, Michael A. Frohman, Rajesh Ramachandran, Miho Iijima, Hiromi Sesaki. Coincident Phosphatidic Acid Interaction Restrains Drp1 in Mitochondrial Division. Molecular Cell. Volume 63, Issue 6. 2016. Pages 1034-1043. https://doi.org/10.1016/j.molcel.2016.08.013
Huang H, Gao Q, Peng X, Choi SY, Sarma K, Ren H, Morris AJ, Frohman MA. piRNA-associated germline nuage formation and spermatogenesis require MitoPLD profusogenic mitochondrial-surface lipid signaling. Dev Cell. 2011 Mar 15;20(3):376-87. https://doi.org/10.1016/j.devcel.2011.01.004 3. State what audience might be interested in and influenced by the reported findings. - a. Audiences of the fields such as Mitochondrial dynamics, UPR, lipid metabolism, neurodegenerative diseases, ER-stress response, Integrated Stress Response. 4. 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. - a. Mitochondrial morphology, mtDNA inheritance, mitochondrial metabolism, fluorescence/indirect immunofluorescence microscopy
- Are the key conclusions convincing?
A considerable amount of work was performed by the authors in preparation of this manuscript and while we find the model exciting, there are several issues that need to be addressed in order for the model to be sufficiently supported.
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Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.
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Reply to the reviewers
We thank all the reviewers for having raised constructive criticism to fortify the main message and improve the clarity of the manuscript. We appreciate that all reviewers found that our work addresses an important topic and is of interest to a broad audience. We believe that we have thoroughly addressed the concerns of the reviewers, especially with regard to 1) performing another SMC3 chromatin immunoprecipitation and sequencing (ChIP-seq) replicate and control, 2) including a later time point for the transcriptional data, and 3) performing additional characterization of the growth phenotype of the SMC3 conditional knockdown.
Reviewer #1
(Evidence, reproducibility and clarity (Required)):*
Summary The present work by Rosa et al., provides convincing data about the presence and functional relevance of the cohesin complex in Plasmodium falciparum blood stages. In accordance with other organisms, the composition of the cohesin complex containing SMC1, SMC3 RAD21 and putatively STAG could be confirmed via pulldown and mass spectrometry. Basic characterization of endogenous tagged SMC3 demonstrated the expression and nuclear localization during IDC, as well as the relatively stable accumulation at centromeric regions, consistent with the known cohesin function in chromatid separation. Furthermore, dynamic and stage-dependent binding to intergenic regions observed in ChIPseq and major transcriptome aberrations upon knockdown of SMC3 (__Response: __As we regularly perform ChIP-seq experiments in the lab, we have generated multiple negative control datasets. In our opinion, the most stringent negative control for an HA-tagged protein is performing ChIP with an HA antibody in a WT strain. We have recently published an in-depth analysis of this (and other) negative ChIP-seq controls (Baumgarten & Bryant, 2022, https://doi.org/10.12688/openreseurope.14836.2). We show in this publication that non-specific ChIP-seq experiments (such as negative controls) result in an over-representation of HP1-heterochromatinized regions due to differences in sonication efficiency of heterochromatin and technical challenges with mapping regions with high levels of homology. In the anti-HA in WT ChIP negative control (performed at 12hpi), we do not see any enrichment at centromeric regions, but rather at heterochromatinized regions where clonally variant gene families are located. We performed peak calling analysis and found no significant overlap between the negative control ChIP-seq and the SMC3-3HA ChIP-seq data at 12hpi.
In addition, we have now performed a second biological replicate of the SMC3-3HA ChIP-seq with a different clone at all time points. We compared this data to that from the original clone and found significant overlap of the peaks called (see what is now Table 4 and Supp. Fig. 3A). We generated a stringent list of peaks that were shared between both clones at each time point and repeated all downstream analyses (see what are now Tables 5-8). We found that our conclusions were largely unchanged. Text describing these experiments and analyses have been added throughout the results section.
- Proposed mechanism of repressive effect of SMC3 early in IDC on genes, that get de-repressed in late stages: To claim this mode of function, it would be necessary to include a KD on late stage parasites. If there is an early repressive role of SMC3, upregulated genes should not be affected by late SMC3-KD. __Response: __To be clear, we are most interested in the transcriptional role of SMC3 during interphase, where results are not confounded by its potential role in mitosis. However, we did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to the manuscript (see Tables 11-13). Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi (see what is now Supp. Fig. 5B). Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.
To address the question of whether genes that are upregulated upon depletion of SMC3 at early stages are affected at the 36hpi time point, we performed differential expression analysis of the SMC3-3HA-glmS parasites with and without glucosamine at 36hpi (we have added this data in Table 11). Again, significantly up- and down-regulated genes were not filtered using the WT dataset. With this analysis, we see only three genes from the list of invasion-related genes (Hu et al., 2010) that are up-regulated, but none of them have a significant q-value (Tab 5 of Table 18). Thus, depletion of SMC3 in late stage parasites does not lead to up-regulation of the same genes that are upregulated at 12 and 24hpi. We have added this information to the text (Line 273).
Furthermore, the hypothesized repressive effect of SMC3 does not explain the numerous genes downregulated in KD.
__Response: __As we state on line 350, we do not observe enrichment of SMC3 at downregulated genes, suggesting an indirect or secondary effect of SMC3 KD on these genes.
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Due to the fact, that the KD was induced at the exact same timepoint and analysed 12h and 24h after induction it is possible that identified, differentially expressed genes at 24h are not directly regulated by SMC3, but rather due to a general deregulation of gene expression. Did the authors attempt to analyse gene expression upon induction at ring, trophozoite and schizont stage? Response: __As we state on line 230, in order to achieve SMC3 KD at the protein level, we had to treat the parasite with glucosamine for two cell cycles (approximately 96 hours). After two cell cycles of glucosamine treatment, the parasites were tightly synchronized and sampled 12 and 24 hours later. Thus, SMC3 KD takes place over the course of multiple days, but parasites are collected after stringent synchronization. Giemsa staining and bioinformatic analysis (line 250) of the RNA-seq data from parasites (with or without glucosamine) harvested at 12 and 24 hpi show that these parasites were synchronous and that there were no gross differences in genome-wide transcript levels. It is certainly possible that differentially expressed genes at 12 or 24hpi are not directly regulated by SMC3, and this is precisely why we perform ChIP-seq of SMC3: to provide evidence of direct involvement via binding, as stated on line 281. __
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*Based on rapid parasite growth, the authors hypothesize a higher invasion rate due to upregulation of invasion genes. This hypothesis is not supported by quantitative invasion assays or quantification of invasion factors on the protein level. An alternative explanation could be a shorter cell cycle (__Response: __We have repeated the growth curve analysis with additional clones and no longer observe a growth phenotype in the SMC3 knockdown condition. We have added images of Giemsa-stained parasites from the knockdown time course we performed to what is now Supp. Fig. 5A. We see no obvious differences in cell morphology caused by glucosamine treatment in the WT or SMC3-3HA-glmS parasites.
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Correlation of SMC3-occupancy/ATAC/expression profile of the exemplary genes rap2 and gap45 (Figure 4C,D,E): is this representative for all upregulated genes? __Response: __SMC3 occupancy shown at rap2 and gap45 is representative for all upregulated genes (see Fig. 4A and B). It is difficult to provide a general representation of the average expression profiles of all up-regulated genes over the course of the IDC, but Fig. 3E shows that the vast majority of up-regulated genes normally reach their peak expression in late stage parasites. With regard to ATAC-seq profiles, we have performed a metagene analysis of chromatin accessibility (data taken from (Toenhake et al., 2018)) at all up-regulated genes at time points that closely correspond to the time points used in our study: 15, 25, and 35, and 40 hpi (new Fig. 4C). This metagene analysis confirms what we observe at individual genes: increasing chromatin accessibility over the course of the IDC at these genes’ promoters. While metagene analyses offer important information, we always try to show the raw data (as in new Figs. 4D-F) from individual examples as proof of principle.
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Given that SMC3 appears to be not essential for parasite growth, the authors could generate a null mutant for SMC3, which might allow for easier analysis of differences in gene regulation, cell cycle progression and/or invasion efficiency. __Response: __As we explain on line 327, very little cohesin is required for normal growth and/or mitosis in our study and two studies in S. cerevisiae and D. melanogaster. However, SMC3 is essential in S. cerevisiae. We were unable to knock out SMC3, and a recent mutagenesis study suggests that SMC3 and SMC1 are essential to the parasite during the intraerythrocytic developmental cycle (Zhang et al. Science, 2018). This is why we chose an inducible knockdown system.
*Reviewer #1 (Significance (Required)):
Own opinion The authors provide a basic characterization of the cohesin component SMC3 using NGS methods to investigate chromatin binding sites and its potential influence on gene expression. *
__Response: __We respectfully disagree that our study offers only a basic characterization of SMC3. We combine IFA, mass spectrometry, and both ChIP-seq and RNA-seq of SMC3 across the entire intraerythrocytic developmental cycle to provide the most detailed and comprehensive functional analysis of SMC3 in P. falciparum to date.
The localisation of SMC3 at centromers as described previously (Batugedara 2020) was confirmed. However, the dynamic binding to other regions in the genome, potentially mediated by other proteins, could not be resolved unequivocal with only one replicate of ChIPseq per time point.
__Response: __With regard to the replicates for ChIP-seq, please see our response to this same point above.
Similarly, the RNAseq data demonstrate the relevance of SMC3 for gene expression, but no clear picture of a regulatory mechanism can be drawn at his point. Lacking information about the mode of binding as well as the setup of transcriptome analysis (only two time-shifted sampling points after simultaneous glmS treatment for 96h resulting in incomplete knockdown) cannot definitely elucidate, if SMC3/cohesin is a chromatin factor that affects transcription of genes in general or a specific repressor of stage-specific genes. __Response: __We agree that we have not established a regulatory mechanism for how SMC3 achieves binding specificity. However, the combination of inducible knockdown (as SMC3 is essential to the cell cycle) and differential expression analysis with ChIP-seq from the same time points across the intraerythrocytic developmental cycle is the most stringent and standard approach in the field of epigenetics for determining the direct role of a chromatin-associated protein in gene expression. We provide a detailed explanation of how the transcriptome analysis was set up in the Results (lines 229-234) and Materials and Methods (lines 715-719) section. With regard to our sampling points being “time-shifted,” we provide bioinformatic analysis (line 246-251, what is now Supp. Fig. 5B) of the RNA-seq data from untreated and glucosamine-treated parasites showing highly similar “ages” with regard to progression through the intraerythrocytic developmental cycle. While we of course also monitor progression through the cell cycle with Giemsa staining (Supp. Fig. 5A), this bioinformatic analysis is the most stringent method of determining specific times in the cell cycle.
*The work will be interesting to a general audience, interested in gene regulation and chromatin remodelling
The reviewers are experts in Plasmodium cell biology and epigenetic regulation.*
Reviewer #2
(Evidence, reproducibility and clarity (Required)):
Rosa et al, Review Commons The manuscript by Rosa et al. addresses the function of the cohesion subunit Smc3 in gene regulation during the asexual life cycle of P. falciparum. Cohesin is a conserved protein complex involved in sister chromatin cohesion during mitosis and meiosis in eukaryotic cells. Cohesin also modulates transcription and DNA repair by mediating long range DNA interactions and regulating higher order chromatin structure in mammals and yeast. In P. falciparum, the Cohesin complex remains largely uncharacterized. In this manuscript, the authors present mass spectrometry data from co-IPs showing that Smc3 interacts with Smc1 and a putative Rad21 orthologue (Pf3D7_1440100, consistent with published data from Batugedara et al and Hilliers et al), as well as a putative STAG domain protein orthologue (PF3D7_1456500). Smc3 protein appears to be most abundant in schizonts, but ChIPseq indicates predominant enrichment of Smc3 in centromers in ring and trophozoite stages. In addition, Smc3 dynamically binds with low abundance to other loci across the genome; however, the enrichment is rather marginal and only a single replicate was conducted for each time point making the data interpretation difficult. Conditional knock-down using a GlmS ribozyme approach indicates that parasites with reduced levels of Smc3 have a mild growth advantage, which is only evident after five asexual replication cycles and which the authors attribute to the transcriptional upregulation of invasion-linked genes following Smc3 KD. Indeed, Smc3 seems to be more enriched upstream of genes that are upregulated after Smc3 KD in rings than in downregulated genes, indicating that Smc3/cohesin may have a function in supressing transcription of these schizont specific genes until they are needed. The manuscript is concise and very well written, however it suffers from the lack of experimental replicates for ChIP experiments and a better characterization of the phenotype of conditional KD parasites. * Major comments • In the mass spectrometry analysis, many seemingly irrelevant proteins are identified at similar abundance to the putative rad21 and ssc3 orthologues, and therefore the association with the cohesion complex seems to be based mostly on analogy to other species rather than statistical significance. Hence, it would be really nice to see a validation of the novel STAG domain and Rad21 proteins, for example by Co-IP using double transgenic parasites.*
__Response: __While our IP-MS data did not yield high numbers of peptides, the top most enriched proteins were SMC3 and SMC1. As we state on line 157, two previous studies have already shown a robust interaction between SMC1, SMC3, and RAD21 in Plasmodium, supporting the existence of a conserved cohesin complex. While the identification of the STAG domain-containing protein is interesting, the purpose of our IP-MS was less about redefining the cohesin complex in P. falciparum and more about confirming that the epitope-tagged SMC3 we generated was incorporated correctly into the cohesin complex and was specifically immunoprecipitated by the antibody we later use for western blot, immunofluorescence, and ChIP-seq analyses. However, to validate the results of ours and others’ mass spectrometry results, we generated two new parasite strains – SMC1-3HA-dd and STAG-3HA-dd – and an antibody against SMC3 (see what is now Supp. Fig. 1). We performed co-IP and western blot analysis with these strains and show an interaction between SMC1 and SMC3 and STAG and SMC3 (see what is now Supp. Fig. 2). This information has been added to the manuscript on lines 162-167.
- *The ChIPseq analysis presented here is based on single replicates for each of the three time points. The significance cutoffs for the peaks are rather high (q __Response: __In our experience, a significance cutoff of FDR As we regularly perform ChIP-seq experiments in the lab, we have generated multiple negative control datasets. In our opinion, the most stringent negative control for an HA-tagged protein is performing ChIP with an HA antibody in a WT strain. We have recently published an in-depth analysis of this (and other) negative ChIP-seq controls (Baumgarten & Bryant, 2022, https://doi.org/10.12688/openreseurope.14836.2). We show in this publication that non-specific ChIP-seq experiments (such as negative controls) result in an over-representation of HP1-heterochromatinized regions due to differences in sonication efficiency of heterochromatin and technical challenges with mapping regions with high levels of homology. In the anti-HA in WT ChIP negative control (performed at 12hpi), we do not see any enrichment at centromeric regions, but rather at heterochromatinized regions where clonally variant gene families are located. We performed peak calling analysis and found no significant overlap between the negative control ChIP-seq and the SMC3-3HA ChIP-seq data at 12hpi.
In addition, we have now performed a second biological replicate of the SMC3-3HA ChIP-seq with a different clone at all time points. We compared this data to that from the original clone and found significant overlap of the peaks called (see what is now Table 4 and Supp. Fig. 3A). We generated a stringent list of peaks that were shared between both clones at each time point and repeated all downstream analyses (see what are now Tables 5-8). We found that our conclusions were largely unchanged. Text describing these experiments and analyses have been added throughout the results section.
The SMC3 ChIP from Batugedara et al., 2020 was performed with an in-house generated antibody (not a commercially available, widely validated antibody as we use) at a single time point in the IDC: trophozoites. Batugedara et al. performed one replicate and did not have an input sample for normalization. Rather, it seems that they incubated beads, which were not bound by antibody or IgG, with their chromatin and used any sequenced reads from this beads sample to subtract from their SMC3 ChIP signal as means of normalization. According to ENCODE ChIP-seq standards, this is not a standard nor stringent way of performing ChIP-seq and the subsequent analysis. Because they did not generate a dataset for their ChIP input, it is not possible to call peaks as we do in our study and compare those peaks with ours.
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The authors argue that during schizogony, cohesin may no longer be required at centromers, explaining the low ChIPsignal at this stage (Line 301). However, during schizogony parasites undergo repeated rounds of DNA replication (S-phase) and mitosis (M-phase) to generate multinucleated parasites; and concentrated spots of Smc3 are observed in each nucleus in schizonts by IFA. In turn, the strong presence of Smc3 at centromers in ring stage parasites is surprising, particularly since the Western Blot in Figure 1D shows most expression of Smc3 in schizonts and least in rings; and Smc3 is undetectable in rings by IFA. Yet, the ChIP signal shows very strong enrichment at centromers, long before S phase produces sister chromatids. What could be the reason for this discrepancy? Again, ChIP replicates and controls would be helpful in distinguishing technical problems with the ChIP from biologically relevant differences. __Response: __We discuss in lines 337-342 not that cohesin is no longer required at centromeres during schizogony, but that its removal from centromeres may be required specifically for separation of sister chromatids, as is seen in other eukaryotes. We also discuss that the unique asynchronous mitosis in Plasmodium may lead to a mixed population of parasites at the time point sampled where there may be some centromeres with SMC3 present and some where it is absent to promote sister chromatid separation. Even though SMC3 may be evicted from centromeres to promote sister chromatid separation, it is likely re-loaded onto centromeres once this process is complete. This is most likely why we see foci of SMC3 in each nucleus of mature schizonts by IFA. With regard to the discrepancy between SMC3 levels in rings seen in total nuclear extracts (by western blot) and at centromeres (by ChIP-seq): the total level of a protein in the nucleus does not necessarily dictate the genome-wide binding pattern or the level of enrichment of that protein at specific loci in the genome. Moreover, if one molecule of SMC3 binds to each centromere, 14 molecules would be needed in a ring stage parasite while over 500 would be needed in a schizont (assuming that there are ~36 merozoites present). SMC3 binds to centromeres in interphase cells in other eukaryotes as well, and we speculate that this binding may play a role in the nuclear organization of centromeres, as we discuss starting on line 333.
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It is surprising that a conserved protein like Smc3 shows such a subtle phenotype, given that it is predicted to be essential and its orthologues have a function in mitosis. Generally, only limited data are presented to characterize the Smc3 KD parasites, and more detail should be included. For example validation of the parasite line using a PCR screen for integration and absence of wt, parasite morphology after KD, and/or analysis of the KD parasites for cell cycle status. __Response: __First, we have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B). As we discuss on line 342, very little intact cohesin complex seems to be required for normal growth and mitosis in S. cerevisiae and D. melanogaster, which is probably why we do not see an obvious growth or morphological phenotype. Because we could not generate SMC3 knockout parasites, there may be just enough SMC3 left to perform its vital function in our KD strain. We have added PCR data to demonstrate integration of the 3HA tag- and glmS ribozyme-encoding sequence in the clonal strains we are using for all experiments (see what is now Supp. Fig. 1A). Sanger sequencing was performed on these PCR products to confirm correct sequences. We also added images of Giemsa-stained parasites in untreated and glucosamine-treated parasites at all time points to demonstrate a lack of an obvious morphological phenotype in SMC3 KD parasites (see what is now Supp. Fig. 5A).
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Synchronization was performed at the beginning of the growth time course, which would be expected to result in a stepwise increase in parasitemia every 48 hours; however, the parasitemia according to Fig. 4F rises steadily, which would indicate that the parasites are actually not very synchronous. __Response: __We did indeed tightly synchronize these parasites and hope that the stepwise increase in parasitemia is seen better in our new growth curve analysis (see what is now Supp. Fig. 4B).
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The question of whether Smc3 causes a shorter parasite life cycle (quicker progression) or more invasion is important and could be experimentally addressed by purifying synchronous schizont stage parasites and determining their invasion rates as well as morphological examination of the Giemsa smears over the time course. __Response: __We have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B).
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Please also compare Smc3 transcriptional levels in transgenic parasites to those in wt parasites to rule out that the genetic modification has lead to artificial upregulation of Smc3 transcription. __Response: __We have added this data to what is now Supp. Fig. 4C, showing that there is no significant difference in SMC3 transcript levels between WT and SMC3-3HA-glmS strains. We have added this information to the text of the manuscript (Line 243). As we also generated an SMC3 antibody, we could demonstrate that there is no appreciable difference in SMC3 protein levels between WT and SMC3-3HA-glmS strains (see what is now Supp. Fig. 1D).
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According to Figure S2, even more genes were deregulated at the 12 hpi time point in the WT parasites than in Smc3 parasites, and even to a much higher extent. What "transcriptional age" did the WT control parasites have at each time point? __Response: __We have now included the transcriptional age of all strains, replicates, and treatments in what is now Supp. Fig. 5B. At the 12 hpi time point in particular, regardless of glucosamine treatment, the SMC3-3HA-glmS and WT parasites were highly synchronous. The only large discrepancy we see in transcriptional age is between untreated and glucosamine-treated WT parasites at 36 hpi, which is why we did not include this time point in our transcriptional analysis. We were also surprised by the number of genes that were de-regulated with simple glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.
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A negative correlation with transcription is well established in S. cerevisiae, particularly at inducible genes. How does Smc3 enrichment generally look like for genes that show maximal expression at each of the time point? __Response: __We have performed a metagene analysis of SMC3 enrichment at all genes at each respective time point, which we divided into quartiles of expression based on their FPKM values in the RNA-seq data from the corresponding time point in untreated SMC3-3HA-glmS parasites. This quartile analysis considers all genes, including genes that are not transcribed at all and regardless of whether a gene has a significant SMC3 peak or is differentially expressed upon SMC3 knockdown. At the 12 hpi time point, we do see an inverse correlation between SMC3 enrichment and gene transcription level, but this enrichment is most pronounced across genes bodies. We see the highest SMC3 enrichment at genes in the 4th (lowest) quartile category. For the other two time points, we do not see any obvious pattern of SMC3 enrichment with regard to transcriptional status.
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Line 590: according to the methods, a 36 hpi KD time point was also harvested. Why are the data not shown/analysed? __Response: __To be clear, we are most interested in the transcriptional role of SMC3 during interphase, where results are not confounded by its potential role in mitosis. However, we did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to the manuscript (see Tables 11-13). Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi (see what is now Supp. Fig. 5B). Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.
Minor Comments • Line 103/104: the hinge domain and ATPase head domain are mentioned, please annotate these in Figure 1A.
__Response: __We have annotated the hinge and ATPase domains.
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Figure 1D: the kDa scale is missing from the H3 WB. __Response: __We have added a kDa scale.
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What is the scale indicated by different colors in Fig. 2A? __Response: __The different colors (blue, coral, and green) only represent the 12, 24, and 36hpi time points, respectively. This color scheme is used throughout the manuscript. If the reviewer is referring to the color gradation within each circos plot, this does not indicate a specific scale. The maximum y-axis value for all circos plots is 24, as indicated in the figure legend.
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Line 189: it would also be interesting how many peaks are "conserved" between the different time points studied, so not only to compare the gene lists of closest genes but also the intersecting peaks and then the closest genes to the intersecting peaks. __Response: __We have added this information in Table 7 and in the manuscript starting on Line 203. Using the new dataset of consensus peaks between two replicates, there were 88 genes associated with an SMC3 peak across all three time points, most of which were close to a centromeric region.
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What is the distribution of the peaks over diverse genetic elements, such as gene bodies, introns, convergent/ divergent/ tandem intergenic regions? In yeast, cohesion is particularly enriched in convergent intergenic regions, so it would be interesting to see how this behaves in P. falciparum. __Response: __We would have liked to define how many peaks were in intergenic versus genic regions of the genome, but the dataset of “genes” from PlasmoDB includes UTRs. Thus, we would need a better annotation of the genome to perform this analysis. Regardless, we calculated the average SMC3 peak enrichment (shared between both replicates) in intergenic regions between convergent and divergent genes (see what is now Supp. Fig. 3B and Table 6). As we now state in the manuscript on line 198, we see a slight enrichment in regions between convergent genes at all time points, but the differences were not significant.
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Line 130 intra-chromosomal interactions (word missing) __Response: __Thank you for pointing this out. We have corrected this.
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Contrary to Figure 1D, the WB in Figure 3A indicates strong expression of Smc3 in rings. Please comment on this discrepancy. __Response: __While extracts from all time points were run on the same western blot in Fig. 1D and thus developed for the same amount of time, this was not the case for Fig. 3A. In Fig. 3A, the samples were run on different blots and exposed for different times, so while we can compare SMC3-HA levels between – and + glucosamine for each time point, the levels at 12 hpi cannot be quantitatively compared to those at 24 or 36hpi.
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What time point after glucosamine addition represents the WB in Fig. 3A? __Response: __The “12hpi” parasites were sampled approximately 108 hours post glucosamine addition and the “24hpi” parasites sampled approximately 120 hours post glucosamine addition. Basically, the parasites were treated with glucosamine for 96 hours, synchronized, and then harvested 12 and 24 hours later.
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Line 233 / Suppl Figure 3: Isn't it a bit concerning that the untreated control parasites at 24 hpi statistically corresponded to 18-19 hpi? And to what timepoint did the wt parasites correspond? __Response: __We are not concerned by this, and we have included the WT parasites in what is now Supp. Fig. 5B for better comparison. In the analysis presented in Supp. Fig. 5B, regardless of glucosamine presence or absence, the differences among replicates and strains at 12 and 24hpi are, in our opinion, minimal, amounting to one or two hours of the 48-hour IDC. In our extensive experience with RNA-seq across the P. falciparum lDC, this synchronization is extremely tight. As we describe on line 430 of the Materials and Methods, there is a ±3 hour window in our synchronization method, meaning that parasites harvested at 24hpi could be anywhere from 21-27hpi. In addition, the dataset that was used for comparison (from Bozdech et al., 2003) was generated in 2003 in a different laboratory using different strains with microarray. While comparing more recent RNA-seq data to this classic study has become well-established practice and is useful for comparing transcriptional age between replicates and strains, it is inevitable that the calculated “hpi” from (Bozdech et al., 2003) will differ somewhat from our experimental “hpi”. We have indeed seen this small discrepancy in predicted transcriptional age in several of our RNA-seq datasets (unrelated to this study) from trophozoites harvested at 24hpi.
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Line 264: "whether naturally or via knockdown" - the meaning of this sentence is not entirely clear __Response: __We are referring to depletion of SMC3 at promoters, either naturally (i.e. lack of binding at the promoter at 36hpi that is not the result of SMC3 knockdown, as we show in Fig. 4B) or via SMC3 knockdown, which is not natural but artificial.
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Figure 4 Legend: A, B, C etc. are mixed up. Response: Thank you for pointing this out. We have corrected this.
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Figure 4D: the differences seem to be marginally significant, even not significant at all (q=0.8) for gap45 at 12hpi. __Response: __If one defines a significance cutoff of q = 0.05 (as is common practice in differential expression analyses), then the differences are significant. For a small minority of invasion genes (such as gap45), we do observe significance at either 12 hpi or 24 hpi, but not both. Thus, we have removed the word “significant” from the descriptions of each dataset in Tab 1 of what is now Table 18. however, we do not believe that this rules out a role for SMC3 at such a gene during interphase. What is now Table 18 offers a longer list of invasion-related genes, most of which are more “significantly” affected than rap2 and gap45.
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Figure 4F shows FACS data using SYBR green as a DNA stain. The authors could exploit this data to look at the relative DNA content per cell as a measure of parasite stage, since more mature parasites will have more DNA (mean fluorescence intensity). How did the corresponding parasite cultures look in Giemsa smears? Response: We have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B). We have added images of Giemsa-stained parasites in untreated and glucosamine-treated parasites at all time points to demonstrate a lack of an obvious morphological phenotype in SMC3 KD parasites (see what is now Supp. Fig. 5A).
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Are RNAseq replicates biological replicates from independent experiments or technical replicates? __Response: __RNA-seq replicates are technical replicates from the same parasite clone.
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Why does the number of genes analysed for differential gene expression differ between the comparisons? __Response: __If the reviewer is referring to the discrepancy between the total number of genes for different time points [for example, between what is now Table 9 (12hpi) and Table 10 (24hpi)], this is because in the RNA-seq/differential expression analysis, there have to be reads mapping back to a gene in order for that gene to be included in the analysis. Thus, if a gene is not transcribed at a given time point in the treated or untreated samples, it will not be included in the analysis. Gene transcription fluctuates significantly over the course of the IDC, so different time points will have different total numbers of transcribed genes.
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Line 372: Do you mean the proteins or the genes? AP2-I has a peak at 24 hpi and 36 hpi, and its interacting AP2 factor Pf3D7_0613800 at all time points. __Response: __We are referring to the genes. With the new ChIP-seq analysis including the second replicate, there are no consensus SMC3 peaks associated with ap2-I, bdp1, or Pf3D7_0613800 (see what is now Table 7).
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Line 480: no aldolase was shown. __Response: __We have removed this sentence.
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Line 838: include GO analysis in methods __Response: __We have added this.
Reviewer #2 (Significance (Required)): The paper addresses the function of the cohesin complex in gene regulation of malaria parasites for the first time. Due to the conserved nature of the complex, the data may be interesting for a broad audience of scientists interested in nuclear biology and cell division/ gene regulation.
Reviewer #3
(Evidence, reproducibility and clarity (Required)):
*Summary:
In the presented manuscript by Rosa et al. the authors investigate the longstanding question of how P. falciparum achieves the tight transcriptional regulation of its genome despite the apparent absence of many canonical sequence specific transcription factor families found in other eukaryotes. To do this the authors investigate the role of the spatial organization of the genome in this context, by performing a functional characterization of the conserved cohesion subunit SMC3 and its putative role in transcriptional regulation in P. falciparum. Using Cas9 mediated genome editing the authors generated a SMC3-3xHA-glmS parasite line, which they subsequently used to show expression of the protein over the asexual replication cycle by western blot and IFA analysis. In addition, using co-IP experiments coupled with mass spectrometry they identified the additional components of the cohesion complex also found in other eukaryotes as interaction partners of SMC3 in the parasite, thereby confirming the presence of the conserved cohesin complex in P. falciparum. By using a combination of ChIP-seq and RNA-seq experiments in SMC3 knockdown parasites the authors furthermore show that a reduction of SMC3 resulted in the up-regulation of a specific set of genes involved in invasion and egress in the early stages of the asexual replication cycle and that this up-regulation in transcription is correlated with a loss of SMC3 enrichment at these genes. From these observations the authors conclude, that SMC3 binds dynamically to a subset of genes and works as a transcriptional repressor, ensuring the timely expression of the bound genes. Overall, the presented data is intriguing, of high quality and very well presented. However, there are some points, which should be addressed to bolster the conclusions drawn by the authors.
Major points: I was not able to find the deposited datasets in the BioProject database under the given accession number. This should obviously be addressed and would have been nice to be able to have a look at these datasets also for the review process. *__Response: __We apologize for not giving the reviewers access. As the manuscript has been made available as a pre-print (which includes data accession numbers), but has not yet been published, we have not activated access to the data on the database.
*SMC3-ChIP-seq experiments:
"168 were bound by SMC3 across all three time points (Fig. 2D). However, most SMC3-bound genes showed a dynamic binding pattern, with a peak present at only one or two time points (Fig. 2B,D)."
Here it would be interesting to actually have more than one replicate of each of these ChIP-seq time points. This could provide a better idea of how "dynamic" these binding patterns actually are. Furthermore, I was missing a list of these 168 genes, which are constantly bound by SMC3. Anything special about those? What actually happens to this subset of genes in the SMC3 knockdown parasites? Do they show similar transcriptional changes?*
__Response: __We have now performed a second biological replicate of the SMC3-3HA ChIP-seq with a different clone at all time points. We compared this data to that from the original clone and found significant overlap of the peaks called (see what is now Table 4 and Supp. Fig. 3A). We generated a stringent list of peaks that were shared between both clones at each time point and repeated all downstream analyses (see what are now Tables 5-8). We found that our conclusions were largely unchanged. Text describing these experiments and analyses have been added throughout the results section. Using the new dataset of consensus peaks between two replicates, there were 88 genes associated with an SMC3 peak across all three time points (see what is now Table 7). The genes that are associated with an SMC3 peak at all time points are, in general, those closest to centromeric/pericentromeric regions and show no obvious functional relationship to each other. Out of these 88 genes, four are significantly up- or downregulated at 12 hpi and 26 are significantly up- or downregulated at 24 hpi. The most significantly downregulated of these genes in both datasets is smc3 itself.
*SMC3-knockdown experiments:
In Sup. Fig. 1 there is a double band in the HA-western blot in the 2nd cycle -GlcN. sample. This second band is absent in all other HA-western shown. Have the authors any idea where that second band comes from?*
__Response: __As the reviewer says, we do not see this second band in most of our western blots. It is possible that it is just a small amount of degradation in the lysate.
In Figure 3A, the WB data shown is slightly contrasting the RNA-seq quantification (3B). The knock-down on protein level seems to be stronger in the 12 hpi samples here than in the 24 hpi samples. Although the band for HA-SMC3 is stronger at the 12 hpi TP there's no band visible in the + GlcN. sample. There's however in the 24 hpi samples. Could the authors comment on this?
Response: __With regard to the discrepancy of the knockdown and protein versus RNA level, it is quite common for transcript levels to not agree with protein levels. This is why we always confirm a transcriptional knockdown with western blot analysis using appropriate loading controls. We are not sure why there is a more dramatic knockdown of SMC3 at 12hpi than at 24hpi, as these samples came from the same culture, but were simply harvested 12 hours apart. __
*"Comparison of our RNA-seq data to the time course transcriptomics data from (Painter et al., 2018) revealed that SMC3 depletion at 12 hpi caused downregulation of genes that normally reach their peak expression in the trophozoite stage (18-30 hpi), with the majority of upregulated genes normally reaching their peak expression in the schizont and very early ring stages (40-2 hpi) (Fig. 3E). At 24 hpi, a similar trend is observed, with most downregulated genes normally peaking in expression in trophozoite stage (24-32 hpi) and the majority of upregulated genes peaking in expression at very early ring stage (2 hpi) (Fig. 3F)."
I'm not fully convinced by these presented results/conclusions. This dataset would greatly benefit from the inclusion of additional later time points.*
__Response: __To be clear, we are most interested in the transcriptional role of SMC3 during interphase, where results are not confounded by its potential role in mitosis. However, we did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to the manuscript (see Tables 11-13). Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi (see what is now Supp. Fig. 5B). Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.
We performed differential expression analysis of the SMC3-3HA-glmS parasites with and without glucosamine at 36hpi (we have added this data in Table 11). Again, significantly up- and down-regulated genes were not filtered using the WT dataset. With this analysis, we see only three genes from the list of invasion-related genes (Hu et al., 2010) that are up-regulated, but none of them have a significant q-value (Tab 5 of Table 18). Thus, depletion of SMC3 in late stage parasites does not lead to up-regulation of the same genes that are upregulated at 12 and 24hpi. We have added this information to the text (Line 277).
*The presented upregulation of the egress and invasion related genes is hard to pinpoint to be a direct effect of transcriptional changes due to the SMC3 knockdown. While there's a slight upregulation of these genes they still seem to be regulated in their normal overall transcriptional program as shown in Figure 4D/E. *
__Response: __We provide evidence of a direct effect of SMC3 binding by combining differential expression analysis performed upon SMC3 knockdown with SMC3 ChIP-seq at corresponding time points. As we show in what is now Fig. 4C and D, promoter accessibility of these egress/invasion genes correlates with their transcriptional activity. However, SMC3 binding to the promoters of these same genes shows inverse correlation with their transcriptional activity (what is now Fig. 4B and D). While we believe that SMC3 does contribute to the repression of these genes at specific time points during the cell cycle, it is highly likely that SMC3 is just one protein of many that regulates these genes. Moreover, and especially since we do not see a growth phenotype in the SMC3 KD, it is possible that another protein or even SMC1 could compensate for loss of SMC3 at these promoter regions. We now state these possibilities on lines 346 383 of the Discussion.
*So the changes could in theory also be explained by the differences in cell cycle progression which are present between +/- GlcN. cultures (Sup. Fig. 3). The presented normalization to the microarray data is a well-established practice to correct for this but, as presented seems to have its limitation with these parasite lines (line 233, glucosamine treated parasites harvested at 24 hpi correspond statistically to approximately 18-19 hpi (Supp. Fig. 3).) *
__Response: __In the analysis presented in what is now Supp. Fig. 5B, regardless of glucosamine presence or absence, the differences among replicates and strains at 12 and 24hpi are, in our opinion, minimal, amounting to one or two hours of the 48-hour IDC. In our extensive experience with RNA-seq across the P. falciparum lDC, this synchronization is extremely tight. As we describe on lines 416-421 of the Materials and Methods, there is a ±3 hour window in our synchronization method, meaning that parasites harvested at 24hpi could be anywhere from 21-27hpi. In addition, the dataset that was used for comparison (from Bozdech et al., 2003) was generated in 2003 in a different laboratory using different strains with microarray. While comparing more recent RNA-seq data to this classic study has become well-established practice and is useful for comparing transcriptional age between replicates and strains, it is inevitable that the calculated “hpi” from (Bozdech et al., 2003) will differ somewhat from our experimental “hpi”. We have indeed seen this small discrepancy in predicted transcriptional age in several of our RNA-seq datasets from trophozoites harvested at 24hpi.
By including additional later time points, one could actually follow the expression profiles over the whole cycle and elucidate if there's an actual transcriptional up-regulation of the genes, or if the + GlcN. parasites show a faster cell cycle progression, with a shifted peak expression timing compared to the - GlcN. parasites. __Response: __We did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to what is now Supp. Fig. 5. Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi. Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.
*"These genes show SMC3 enrichment at their promoter regions at 12 and 24 hpi, but not at 36 hpi (Fig. 4C), and depletion of SMC3 resulted in upregulation at both 12 and 24 hpi (Fig. 4D). Comparison of the SMC3 ChIP-seq data with published Assay for Transposase-Accessible Chromatin using sequencing (ATAC-seq) data (Toenhake et al., 2018) and mRNA dynamics data (Painter et al., 2018) from similar time points in the IDC revealed that SMC3 binding at the promoter regions of these genes inversely correlates with chromatin accessibility (Fig. 4C) and their mRNA levels (Fig. 4E), which both peak in schizont stages. These data are consistent with a role of SMC3 in repressing this gene subset until their appropriate time of expression in the IDC."
The presented correlations certainly make an intriguing point towards the authors conclusion that SMC3/cohesin depletion from the promoter regions of the genes results in a de-repression of these genes and their transcriptional activation. However, the SMC3 knockdown is not complete and only up to 69% as presented on RNA level in these parasites. Therefore a control experiment which needs to be done is to actually show the loss of SMC3 from the presented activated example genes in the knockdown parasites. This could easily be done by ChIP-qPCR or even ChIP-seq, to get a global picture of the actual changes in SMC3 occupation in the knockdown parasites in correlation with changes in transcript levels. *__Response: __While SMC3-3HA-glmS knockdown is not complete at the RNA level, it is fairly robust at the protein level, especially at 12hpi (Fig. 3A).
*"These data suggest that SMC3 knockdown results in a faster progression through the cell cycle or a higher rate of egress/invasion."
The authors could greatly strengthen their conclusions by investigating this thoroughly. Pinpointing the observed phenotype to an actual increase in invasion or egress would add to the authors main conclusion that the loss of SMC3 de-regulates the timing of gene expression for these invasion related genes thereby increasing their transcript levels and thus leading to a higher rate of egress/invasion. To determine cell cycle progression simple comparisons between DNA content using a flow cytometer at timepoints together with visual inspection of Giemsa stained blood smears would give a ggod indication towards changes in cell cycle progression. In addition invasion/egress assays by counting newly invaded rings per schizont could reveal, if there are changes in the rate of egress/invasion upon SMC3 knockdown.*
Response: __We have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B). We have added images of Giemsa-stained parasites from the knockdown time course we performed to what is now Supp. Fig. 5A. We see no obvious differences in cell morphology caused by glucosamine treatment in the WT or SMC3-3HA-glmS parasites. As we discuss on line 327, very little intact cohesin complex seems to be required for normal growth and mitosis in S. cerevisiae and D. melanogaster, which is probably why we do not see an obvious growth or morphological phenotype. We believe that SMC3 is probably only a part of a complex controlling transcription of these invasion or egress genes. Thus, the up-regulation of these genes upon SMC3 KD might not be enough to lead to a significant growth or invasion phenotype. __
*Minor points:
In the MM section on the Cas9 experiments it says dCas9 where it should be Cas9 (line 425)*
__Response: __Thank you for pointing this out. We have corrected this.
It would be great to add which HP1 antibody was used in which dilution in the IFAs to the MM section. __Response: __We have added this information to the Materials and Methods section.
In Figure 4C for the gap45 gene there's is some green peak floating around which should not be there. __Response: __Thank you for pointing this out, we have corrected it.
*Reviewer #3 (Significance (Required)):
Significance: The manuscript investigates a very timely topic by trying to uncover new molecular mechanisms of transcriptional regulation in P. falciparum. Investigating the role of the cohesin complex/SMC3 in this context provides valuable new insights to the field. While the first part with the description of the SMC3 cell line and the co-IP experiments largely confirms published data on the existence and composition of the cohesin complex in Plasmodium and its enrichment at the centromeres, the second part is especially intriguing since it investigates the molecular function of SMC3 in more detail. The results pointing to a role of SMC3/cohesin as a transcriptional repressor are of great interest to the field and will open up new concepts for future investigation.*
*Audience: The work is particularly interesting for people interested in gene regulatory processes in Plasmodium and Apicomplexan parasites in general. At the same time it also nicely points towards shared principles of gene regulation to other eukaryotes in relation to the spatial organization of the genome making the work also very interesting for a broader audience with interest in the general principles of gene regulatory processes in eukaryotic organisms.
Expertise: P. falciparum epignetics and chromatin biology / gene regulation / Cas9 gene editing*
CROSS-CONSULTATION COMMENTS
All reviewers agree that the paper addresses an important topic and provides convincing evidence for enrichment of the cohesin component Smc3 at P. falciparum centromers. In contrast, evidence for a function of Smc3 as a transcriptional repressor of genes in the first part of the parasite life cycle is less well supported. All reviewers agree that the statistical significance of the ChIP experiments needs to be impoved by including biological replicates. In addition, the phenotype of the conditional knock-down should be analysed in more detail by clarifying whether faster cell cycle progression or higher invasion rate are responsible for the observed growth adavantage. Inclusion of transcriptional data from a later time point in addition to the presented data for 12 hpi and 24 hpi was also requested by all reviewers. Finally, several inconsistencies require clarification.
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Referee #3
Evidence, reproducibility and clarity
Summary:
In the presented manuscript by Rosa et al. the authors investigate the longstanding question of how P. falciparum achieves the tight transcriptional regulation of its genome despite the apparent absence of many canonical sequence specific transcription factor families found in other eukaryotes. To do this the authors investigate the role of the spatial organization of the genome in this context, by performing a functional characterization of the conserved cohesion subunit SMC3 and its putative role in transcriptional regulation in P. falciparum.
Using Cas9 mediated genome editing the authors generated a SMC3-3xHA-glmS parasite line, which they subsequently used to show expression of the protein over the asexual replication cycle by western blot and IFA analysis. In addition, using co-IP experiments coupled with mass spectrometry they identified the additional components of the cohesion complex also found in other eukaryotes as interaction partners of SMC3 in the parasite, thereby confirming the presence of the conserved cohesin complex in P. falciparum. By using a combination of ChIP-seq and RNA-seq experiments in SMC3 knockdown parasites the authors furthermore show that a reduction of SMC3 resulted in the up-regulation of a specific set of genes involved in invasion and egress in the early stages of the asexual replication cycle and that this up-regulation in transcription is correlated with a loss of SMC3 enrichment at these genes. From these observations the authors conclude, that SMC3 binds dynamically to a subset of genes and works as a transcriptional repressor, ensuring the timely expression of the bound genes.
Overall, the presented data is intriguing, of high quality and very well presented. However, there are some points, which should be addressed to bolster the conclusions drawn by the authors.
Major points:
I was not able to find the deposited datasets in the BioProject database under the given accession number. This should obviously be addressed and would have been nice to be able to have a look at these datasets also for the review process.
SMC3-ChIP-seq experiments:
"168 were bound by SMC3 across all three time points (Fig. 2D). However, most SMC3-bound genes showed a dynamic binding pattern, with a peak present at only one or two time points (Fig. 2B,D)."
Here it would be interesting to actually have more than one replicate of each of these ChIP-seq time points. This could provide a better idea of how "dynamic" these binding patterns actually are. Furthermore, I was missing a list of these 168 genes, which are constantly bound by SMC3. Anything special about those? What actually happens to this subset of genes in the SMC3 knockdown parasites? Do they show similar transcriptional changes?
SMC3-knockdown experiments:
In Sup. Fig. 1 there is a double band in the HA-western blot in the 2nd cycle -GlcN. sample. This second band is absent in all other HA-western shown. Have the authors any idea where that second band comes from?
In Figure 3A, the WB data shown is slightly contrasting the RNA-seq quantification (3B). The knock-down on protein level seems to be stronger in the 12 hpi samples here than in the 24 hpi samples. Although the band for HA-SMC3 is stronger at the 12 hpi TP there's no band visible in the + GlcN. sample. There's however in the 24 hpi samples. Could the authors comment on this?
"Comparison of our RNA-seq data to the time course transcriptomics data from (Painter et al., 2018) revealed that SMC3 depletion at 12 hpi caused downregulation of genes that normally reach their peak expression in the trophozoite stage (18-30 hpi), with the majority of upregulated genes normally reaching their peak expression in the schizont and very early ring stages (40-2 hpi) (Fig. 3E). At 24 hpi, a similar trend is observed, with most downregulated genes normally peaking in expression in trophozoite stage (24-32 hpi) and the majority of upregulated genes peaking in expression at very early ring stage (2 hpi) (Fig. 3F)."
I'm not fully convinced by these presented results/conclusions. This dataset would greatly benefit from the inclusion of additional later time points. The presented upregulation of the egress and invasion related genes is hard to pinpoint to be a direct effect of transcriptional changes due to the SMC3 knockdown. While there's a slight upregulation of these genes they still seem to be regulated in their normal overall transcriptional program as shown in Figure 4D/E. So the changes could in theory also be explained by the differences in cell cycle progression which are present between +/- GlcN. cultures (Sup. Fig. 3). The presented normalization to the microarray data is a well-established practice to correct for this but, as presented seems to have its limitation with these parasite lines (line 233, glucosamine treated parasites harvested at 24 hpi correspond statistically to approximately 18-19 hpi (Supp. Fig. 3).) By including additional later time points, one could actually follow the expression profiles over the whole cycle and elucidate if there's an actual transcriptional up-regulation of the genes, or if the + GlcN. parasites show a faster cell cycle progression, with a shifted peak expression timing compared to the - GlcN. parasites.
"These genes show SMC3 enrichment at their promoter regions at 12 and 24 hpi, but not at 36 hpi (Fig. 4C), and depletion of SMC3 resulted in upregulation at both 12 and 24 hpi (Fig. 4D). Comparison of the SMC3 ChIP-seq data with published Assay for Transposase-Accessible Chromatin using sequencing (ATAC-seq) data (Toenhake et al., 2018) and mRNA dynamics data (Painter et al., 2018) from similar time points in the IDC revealed that SMC3 binding at the promoter regions of these genes inversely correlates with chromatin accessibility (Fig. 4C) and their mRNA levels (Fig. 4E), which both peak in schizont stages. These data are consistent with a role of SMC3 in repressing this gene subset until their appropriate time of expression in the IDC."
The presented correlations certainly make an intriguing point towards the authors conclusion that SMC3/cohesin depletion from the promoter regions of the genes results in a de-repression of these genes and their transcriptional activation. However, the SMC3 knockdown is not complete and only up to 69% as presented on RNA level in these parasites. Therefore a control experiment which needs to be done is to actually show the loss of SMC3 from the presented activated example genes in the knockdown parasites. This could easily be done by ChIP-qPCR or even ChIP-seq, to get a global picture of the actual changes in SMC3 occupation in the knockdown parasites in correlation with changes in transcript levels.
"These data suggest that SMC3 knockdown results in a faster progression through the cell cycle or a higher rate of egress/invasion."
The authors could greatly strengthen their conclusions by investigating this thoroughly. Pinpointing the observed phenotype to an actual increase in invasion or egress would add to the authors main conclusion that the loss of SMC3 de-regulates the timing of gene expression for these invasion related genes thereby increasing their transcript levels and thus leading to a higher rate of egress/invasion. To determine cell cycle progression simple comparisons between DNA content using a flow cytometer at timepoints together with visual inspection of Giemsa stained blood smears would give a ggod indication towards changes in cell cycle progression. In addition invasion/egress assays by counting newly invaded rings per schizont could reveal, if there are changes in the rate of egress/invasion upon SMC3 knockdown.
Minor points:
In the MM section on the Cas9 experiments it says dCas9 where it should be Cas9 (line 425)
It would be great to add which HP1 antibody was used in which dilution in the IFAs to the MM section.
In Figure 4C for the gap45 gene there's is some green peak floating around which should not be there.
Significance
The manuscript investigates a very timely topic by trying to uncover new molecular mechanisms of transcriptional regulation in P. falciparum. Investigating the role of the cohesin complex/SMC3 in this context provides valuable new insights to the field. While the first part with the description of the SMC3 cell line and the co-IP experiments largely confirms published data on the existence and composition of the cohesin complex in Plasmodium and its enrichment at the centromeres, the second part is especially intriguing since it investigates the molecular function of SMC3 in more detail. The results pointing to a role of SMC3/cohesin as a transcriptional repressor are of great interest to the field and will open up new concepts for future investigation.
Audience:
The work is particularly interesting for people interested in gene regulatory processes in Plasmodium and Apicomplexan parasites in general. At the same time it also nicely points towards shared principles of gene regulation to other eukaryotes in relation to the spatial organization of the genome making the work also very interesting for a broader audience with interest in the general principles of gene regulatory processes in eukaryotic organisms.
Expertise:
P. falciparum epignetics and chromatin biology / gene regulation / Cas9 gene editing
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Referee #2
Evidence, reproducibility and clarity
Rosa et al, Review Commons
The manuscript by Rosa et al. addresses the function of the cohesion subunit Smc3 in gene regulation during the asexual life cycle of P. falciparum. Cohesin is a conserved protein complex involved in sister chromatin cohesion during mitosis and meiosis in eukaryotic cells. Cohesin also modulates transcription and DNA repair by mediating long range DNA interactions and regulating higher order chromatin structure in mammals and yeast. In P. falciparum, the Cohesin complex remains largely uncharacterized. In this manuscript, the authors present mass spectrometry data from co-IPs showing that Smc3 interacts with Smc1 and a putative Rad21 orthologue (Pf3D7_1440100, consistent with published data from Batugedara et al and Hilliers et al), as well as a putative STAG domain protein orthologue (PF3D7_1456500). Smc3 protein appears to be most abundant in schizonts, but ChIPseq indicates predominant enrichment of Smc3 in centromers in ring and trophozoite stages. In addition, Smc3 dynamically binds with low abundance to other loci across the genome; however, the enrichment is rather marginal and only a single replicate was conducted for each time point making the data interpretation difficult. Conditional knock-down using a GlmS ribozyme approach indicates that parasites with reduced levels of Smc3 have a mild growth advantage, which is only evident after five asexual replication cycles and which the authors attribute to the transcriptional upregulation of invasion-linked genes following Smc3 KD. Indeed, Smc3 seems to be more enriched upstream of genes that are upregulated after Smc3 KD in rings than in downregulated genes, indicating that Smc3/cohesin may have a function in supressing transcription of these schizont specific genes until they are needed. The manuscript is concise and very well written, however it suffers from the lack of experimental replicates for ChIP experiments and a better characterization of the phenotype of conditional KD parasites.
Major comments
- In the mass spectrometry analysis, many seemingly irrelevant proteins are identified at similar abundance to the putative rad21 and ssc3 orthologues, and therefore the association with the cohesion complex seems to be based mostly on analogy to other species rather than statistical significance. Hence, it would be really nice to see a validation of the novel STAG domain and Rad21 proteins, for example by Co-IP using double transgenic parasites.
- The ChIPseq analysis presented here is based on single replicates for each of the three time points. The significance cutoffs for the peaks are rather high (q < 0.05). Therefore, the relevance of the marginally enriched dynamic peaks (average relative enrichment of <1.2 fold for genes upregulated in rings 12 hpi in Figure 4A and B) does not appear to be very robust. Even in ChIPseq experiments using non-immune IgG, hundreds of peaks are usually called with MACS2 with a similar magnitude. So, to substantiate the data for extra-centromeric peaks convincingly, replicates and more stringent statistics are necessary. In addition, the authors should also compare their data to published PfSmc3 ChIP data from Batugedara et al 2020 (GSE116219).
- The authors argue that during schizogony, cohesin may no longer be required at centromers, explaining the low ChIPsignal at this stage (Line 301). However, during schizogony parasites undergo repeated rounds of DNA replication (S-phase) and mitosis (M-phase) to generate multinucleated parasites; and concentrated spots of Smc3 are observed in each nucleus in schizonts by IFA. In turn, the strong presence of Smc3 at centromers in ring stage parasites is surprising, particularly since the Western Blot in Figure 1D shows most expression of Smc3 in schizonts and least in rings; and Smc3 is undetectable in rings by IFA. Yet, the ChIP signal shows very strong enrichment at centromers, long before S phase produces sister chromatids. What could be the reason for this discrepancy? Again, ChIP replicates and controls would be helpful in distinguishing technical problems with the ChIP from biologically relevant differences.
- It is surprising that a conserved protein like Smc3 shows such a subtle phenotype, given that it is predicted to be essential and its orthologues have a function in mitosis. Generally, only limited data are presented to characterize the Smc3 KD parasites, and more detail should be included. For example validation of the parasite line using a PCR screen for integration and absence of wt, parasite morphology after KD, and/or analysis of the KD parasites for cell cycle status.
- Synchronization was performed at the beginning of the growth time course, which would be expected to result in a stepwise increase in parasitemia every 48 hours; however, the parasitemia according to Fig. 4F rises steadily, which would indicate that the parasites are actually not very synchronous.
- The question of whether Smc3 causes a shorter parasite life cycle (quicker progression) or more invasion is important and could be experimentally addressed by purifying synchronous schizont stage parasites and determining their invasion rates as well as morphological examination of the Giemsa smears over the time course.
- Please also compare Smc3 transcriptional levels in transgenic parasites to those in wt parasites to rule out that the genetic modification has lead to artificial upregulation of Smc3 transcription.
- According to Figure S2, even more genes were deregulated at the 12 hpi time point in the WT parasites than in Smc3 parasites, and even to a much higher extent. What "transcriptional age" did the WT control parasites have at each time point?
- A negative correlation with transcription is well established in S. cerevisiae, particularly at inducible genes. How does Smc3 enrichment generally look like for genes that show maximal expression at each of the time point?
- Line 590: according to the methods, a 36 hpi KD time point was also harvested. Why are the data not shown/analysed?
Minor Comments
- Line 103/104: the hinge domain and ATPase head domain are mentioned, please annotate these in Figure 1A.
- Figure 1D: the kDa scale is missing from the H3 WB.
- What is the scale indicated by different colors in Fig. 2A?
- Line 189: it would also be interesting how many peaks are "conserved" between the different time points studied, so not only to compare the gene lists of closest genes but also the intersecting peaks and then the closest genes to the intersecting peaks.
- What is the distribution of the peaks over diverse genetic elements, such as gene bodies, introns, convergent/ divergent/ tandem intergenic regions? In yeast, cohesion is particularly enriched in convergent intergenic regions, so it would be interesting to see how this behaves in P. falciparum.
- Line 130 intra-chromosomal interactions (word missing)
- Contrary to Figure 1D, the WB in Figure 3A indicates strong expression of Smc3 in rings. Please comment on this discrepancy.
- What time point after glucosamine addition represents the WB in Fig. 3A?
- Line 233 / Suppl Figure 3: Isn't it a bit concerning that the untreated control parasites at 24 hpi statistically corresponded to 18-19 hpi? And to what timepoint did the wt parasites correspond?
- Line 264: "whether naturally or via knockdown" - the meaning of this sentence is not entirely clear
- Figure 4 Legend: A, B, C etc. are mixed up.
- Figure 4D: the differences seem to be marginally significant, even not significant at all (q=0.8) for gap45 at 12hpi.
- Figure 4F shows FACS data using SYBR green as a DNA stain. The authors could exploit this data to look at the relative DNA content per cell as a measure of parasite stage, since more mature parasites will have more DNA (mean fluorescence intensity). How did the corresponding parasite cultures look in Giemsa smears?
- Are RNAseq replicates biological replicates from independent experiments or technical replicates?
- Why does the number of genes analysed for differential gene expression differ between the comparisons?
- Line 372: Do you mean the proteins or the genes? AP2-I has a peak at 24 hpi and 36 hpi, and its interacting AP2 factor Pf3D7_0613800 at all time points.
- Line 480: no aldolase was shown.
- Line 838: include GO analysis in methods
Referees cross-commenting
All reviewers agree that the paper addresses an important topic and provides convincing evidence for enrichment of the cohesin component Smc3 at P. falciparum centromers. In contrast, evidence for a function of Smc3 as a transcriptional repressor of genes in the first part of the parasite life cycle is less well supported. All reviewers agree that the statistical significance of the ChIP experiments needs to be impoved by including biological replicates. In addition, the phenotype of the conditional knock-down should be analysed in more detail by clarifying whether faster cell cycle progression or higher invasion rate are responsible for the observed growth adavantage. Inclusion of transcriptional data from a later time point in addition to the presented data for 12 hpi and 24 hpi was also requested by all reviewers. Finally, several inconsistencies require clarification.
Significance
The paper addresses the function of the cohesin complex in gene regulation of malaria parasites for the first time. Due to the conserved nature of the complex, the data may be interesting for a broad audience of scientists interested in nuclear biology and cell division/ gene regulation.
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Referee #1
Evidence, reproducibility and clarity
Summary
The present work by Rosa et al., provides convincing data about the presence and functional relevance of the cohesin complex in Plasmodium falciparum blood stages. In accordance with other organisms, the composition of the cohesin complex containing SMC1, SMC3 RAD21 and putatively STAG could be confirmed via pulldown and mass spectrometry. Basic characterization of endogenous tagged SMC3 demonstrated the expression and nuclear localization during IDC, as well as the relatively stable accumulation at centromeric regions, consistent with the known cohesin function in chromatid separation. Furthermore, dynamic and stage-dependent binding to intergenic regions observed in ChIPseq and major transcriptome aberrations upon knockdown of SMC3 (<70% mRNA reduction via glmS-system) suggest an important function in transcriptional regulation. The underlying mechanism of gene regulation by cohesin via the creation of chromatin clusters or DNA loops as well as its specificity to target sites remain speculation.
Major criticism
- Accuracy of ChIPseq with only one replicate per time point (and lacking negative controls without antibody) is not convincing. The authors should include more replicates.
- Proposed mechanism of repressive effect of SMC3 early in IDC on genes, that get de-repressed in late stages: To claim this mode of function, it would be necessary to include a KD on late stage parasites. If there is an early repressive role of SMC3, upregulated genes should not be affected by late SMC3-KD. Furthermore, the hypothesized repressive effect of SMC3 does not explain the numerous genes downregulated in KD.
- Due to the fact, that the KD was induced at the exact same timepoint and analysed 12h and 24h after induction it is possible that identified, differentially expressed genes at 24h are not directly regulated by SMC3, but rather due to a general deregulation of gene expression. Did the authors attempt to analyse gene expression upon induction at ring, trophozoite and schizont stage?
- Based on rapid parasite growth, the authors hypothesize a higher invasion rate due to upregulation of invasion genes. This hypothesis is not supported by quantitative invasion assays or quantification of invasion factors on the protein level. An alternative explanation could be a shorter cell cycle (<48h), as the different cell cycle progression estimation of KD/WT could indicate (SuppFigure 3). Giemsa-stain images of KD/WT parasites should be included to show normal stage development over time.
- Correlation of SMC3-occupancy/ATAC/expression profile of the exemplary genes rap2 and gap45 (Figure 4C,D,E): is this representative for all upregulated genes?
- Given that SMC3 appears to be not essential for parasite growth, the authors could generate a null mutant for SMC3, which might allow for easier analysis of differences in gene regulation, cell cycle progression and/or invasion efficiency.
Significance
Own opinion
The authors provide a basic characterization of the cohesin component SMC3 using NGS methods to investigate chromatin binding sites and its potential influence on gene expression. The localisation of SMC3 at centromers as described previously (Batugedara 2020) was confirmed. However, the dynamic binding to other regions in the genome, potentially mediated by other proteins, could not be resolved unequivocal with only one replicate of ChIPseq per time point. Similarly, the RNAseq data demonstrate the relevance of SMC3 for gene expression, but no clear picture of a regulatory mechanism can be drawn at his point. Lacking information about the mode of binding as well as the setup of transcriptome analysis (only two time-shifted sampling points after simultaneous glmS treatment for 96h resulting in incomplete knockdown) cannot definitely elucidate, if SMC3/cohesin is a chromatin factor that affects transcription of genes in general or a specific repressor of stage-specific genes.
The work will be interesting to a general audience, interested in gene regulation and chromatin remodelling
The reviewers are experts in Plasmodium cell biology and epigenetic regulation.
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Reply to the reviewers
The authors do not wish to provide a response at this time. The full point-by-point reply is attached together with the manuscript files.
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Referee #3
Evidence, reproducibility and clarity
Review Commons recommends including the following components in referee reports:
- Evidence, reproducibility and clarity
Summary:
Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2.
The manuscript by Awoniyi et al is an elegant study that addresses the protein composition of the lipid rafts upon BCR activation. The authors use an elegant system, employing the enzyme ascorbate peroxidase (APEX2), which in cellulo generates short-lived biotin radicals, that in turn randomly bind to proteins in their vicinity (10-20 nm) within 1 min. APEX2 is furthermore fused with the 7-amino acid sequence MGCVCSS, which allows its targeting to lipid rafts (Raft-APEX2) and with an mCherry marker. Using modern microscopy methods as well as quantitative mass-spectrometry proteomics, the authors provide a spatially and temporally resolved dynamic insight into the changes within the lipid raft and. are able to enrich multiple proteins in the lipid rafts previously not associated with BCR signaling. Furthermore, they identify Golga3 and Vti1b as proteins proximally responding to BCR activation possibly enabling vesicle transport.
The manuscript is generally well written, the study is well-conceived and well-controlled. Nevertheless, the authors may answer some important questions (see below)
Major comments:
• Are the key conclusions convincing?
Yes, the key conclusions of the study are convincing and based on elegant experiments
• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
• 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.
• In Figure 2, the HEL-specific A20 B cells are stimulated with anti-IgM F(ab)'2. While, beyond a doubt, anti-IgM F(ab)'2 is a potent stimulus, which triggers BCR signaling activation, I am curious why the authors chose it over the HEL antigen.
• Describing figures 4 and 5, the authors state that they did not identify prominent BCR signaling pathway regulators. My major concern here is that the authors employ cancerous B cells for their analyses. The lipid raft composition and proteins recruited to the rafts in these cells may vary from those in primary wild-type B cells. While the authors do keep in mind that the signaling protein composition may vary between cell lines, it may vary even more between lymphoma B cell line and primary wild-type cells. Therefore, it may be beneficial to verify the expression of the "unexpected" proteins, such as Golga3, Kif20a, and Vtib1b in primary cells using immunofluorescence analyses similar to the ones presented in Fig 6.
• The authors mention in the discussion, that Syk was not identified in their data set. This is surprising as Syk has been attributed with an important role in the proximal BCR signaling (Kulathu et al, https://doi.org/10.1111/j.1600-065X.2009.00837.x)
• Would it be possible to detect Syk using the immunofluorescence technique from Figure 6?
• Additionally, as stated in the text, A20 cells express endogenous IgG2a. Have the authors tried to conduct similar experiments stimulating with anti-IgG antibodies instead of anti-IgM F(ab)'2?
• Have the authors tried to co-express the IgD-BCR to mimic mature peripheral B cells?
• 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 cannot estimate the cost but if conducted, some experiments might take several months
• 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.
• Are prior studies referenced appropriately?
Yes
• Are the text and figures clear and accurate?
Yes, but, if possible, please provide the data instead of writing "data not shown"
• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
Fig. 1D and Supp. Fig. S1C: the authors state that after IgM cross-linking, the non-transfected and Raft-APEX2-transfected cells showed "indistinguishable" p-Tyr levels. From my perspective, the Raft-APEX2-transfected cells show higher levels of p-Tyr. It is possible to quantify it?
Some paragraph titles are very short and descriptive (e.g. Proteomic analysis, membrane-proximal proteome etc.). It could improve the reading if the paragraph titles consisted of respective key findings
Significance
2. Significance
• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
• This study dissects in a spatio-temporal manner the early events upon BCR stimulation and the enrichment of various proteins in the vicinity of lipid rafts. While conceptually not novel, the study provides novel methodology to address this question. This is technically relevant and worth to be published after a major revision.
• Place the work in the context of the existing literature (provide references, where appropriate).
*This study prominently overlooks a bulk of literature that supports the BCR dissociation activation model and does not comment that (reviewed in Maity et al, Volume 1853, Issue 4, April 2015, Pages 830-840)
• State what audience might be interested in and influenced by the reported findings.
The findings of this manuscript are specifically interesting for researchers who study early events of B cells activation, specifically the changes in the membrane composition and early BCR signaling
• 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.
Immunology, Molecular and Cell Biology
Referee Cross-commenting
I agree totally that "the article would greatly benefit from a follow-up investigation on the functional/physiological relevance of the proposed players", however only if this is easily done with the CRISP mediated knock out as mentioned by both reviewers. In addition it s interesting to see data on cells stimulated with the antigen instead of anti IgM fab'2.
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Referee #2
Evidence, reproducibility and clarity
Summary
Awoniyi et al. utilizes APEX2-mediated proximity proteomics to investigate the protein composition of lipid rafts and their dynamics in the context of B cell receptor (BCR) signaling. The authors add a 7 amino acid guide sequence to an APEX2-mCherry construct to specifically target the fusion protein into lipid raft plasma membrane domains and thereby spatially label and identify contained proteins. While a larger number of lipid raft-related proteins were verified, the study focuses on a smaller subset that is proposed to be specifically related to BCR signaling. Unexpectedly, this approach suggests key players of BCR signaling to be excluded from lipid rafts in an inducible manner. Finally, two of the identified proteins, Golga3 and Vti1b, were further investigated by immunofluorescence microscopy. Since both proteins are shown to be recruited to the plasma membrane and to colocalize with antigen, the authors propose Golga3 and Vti1b as novel targets of BCR activation and drivers of subsequent antigen internalization.
Major Comments
- A major claim of this study is that the majority of BCR signaling proteins (including CD79a and CD79b as parts of the BCR as well as BLNK) get excluded from lipid rafts upon stimulation. Moreover, many components of the endocytosis/vesicle trafficking pathways have been identified and the authors raise interesting points regarding the BCR as signaling platform versus the BCR as antigen internalization complex. This is intriguing and could even be explored further (e.g. by presenting Figure S3 in the main manuscript). However, the claim that Vti1b and Golga3 (and possibly Kif20) play key roles in the endocytic processes underlying BCR/antigen endocytosis and subsequent processing needs further verification e.g. by gene targeting experiments. In its present form, the manuscript links these proteins to B cell activation but does not convincingly back up the implied functional relevance to antigen/BCR endocytosis and/or trafficking leading to antigen presentation via MHC II.
- It should be explained why the proteomic experiments were conducted using anti-IgM antibodies as opposed to the more physiological stimulation via HEL antigen, used for the microscopy studies.
- Even though it is the central approach, the number of figures derived from the APEX2 proteomic experiments is quite high and should be condensed. For example, Figures 4 and 5 could be merged.
- Figure 1D/E and Figure S1C seem to be the same pictures.
- In contrast to Golga3, Vti1b is not mentioned in Figure 4 and the authors should explain why this particular protein was chosen for further investigation among all others (as opposed to proteins enriched upon anti-IgM treatment).
- In Figures 6 and S4, the most apparent changes in Golga3 staining appear to be the increased (cytoplasmic and peripheral) vesicle size and intensity. For the analysis and quantitation of peripheral Golga3 staining, a tubulin-based masking algorithm was used to segment the image. This raises three concerns: 1) The tubulin staining that was used for masking appears to be rather blurry and the expected microtubule network is barely visible. 2) More information is needed on how the masking algorithm treated Golga3 vesicles touching the mask border. Based on the images in S4, there seems to be substantial overlap between (visibly peripheral) Golga3 vesicles and tubulin, so this will likely have an impact on quantification results. 3) Authors should comment on the overall increase in Golga3 upon activation.
Minor Comments
- While the APEX2 construct is globally targeted into the lipid raft environment, the study uses this approach to investigate proteins that are in the proximity of the IgM-BCR. The authors mention in the discussion that there have been "challenges" to target the BCR directly. It may be beneficial to briefly discuss those problems the authors have been facing with.
- Figure 5B: It will be informative to show the BCR-induced (fold change) enrichment of Golga3 and Vti1b (and Kif20) in relation to IgM /kappa LC and the "classical" BCR signaling-related players.
- Figure 6AB: Please clearly indicate that unmasked images are displayed, but masked images were quantified for Golga3 staining.
- Figure 6CD: Since the quantification protocol of vesicle positioning involves nuclear staining, please depict respective DAPI stainings.
- Figure S1D: It should be indicated that AF633-streptavidin was used for the flow cytometry experiment in Figure S1D (x axis).
Significance
Overall, the presented study offers an interesting approach and provides a novel, unbiased view on BCR-mediated lipid raft dynamics. The method is appealing in its technicality and its presentation, and hence, might attract the attention of a larger community working on plasma membrane localization of signaling platforms. It proposes two candidate signaling proteins and verifies their BCR-dependent colocalization with lipid rafts and antigen. While Golga3 and Vti1b are novel and interesting target proteins in the context of BCR activation, a functional assessment of these proteins is not presented. Certainly, the article would greatly benefit from a follow-up investigation on the functional/physiological relevance of the proposed players. As it stands, the manuscript largely remains on the level of exploration.
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Referee #1
Evidence, reproducibility and clarity
This is an interesting study identifying membrane RAFT associated proteins in a mouse B cell line, before and after BCR stimulation, using a proximity biotinylation method. This method relies on the expression of an biotinylating enzyme APEX2 with a RAFT targeting domain that is activated by H2O2 addition. The system is well controlled by comparing transfected to non-transfected cells and by titrating H2O2 etc. The expected anti-IgM induced recruitment of the BCR to the RAFT domain is well documented in this system. The authors identify by proteome analysis over 1600 proteins in proximity to the membrane-targeted APEX2, most of which are constitutively labelled, i.e. do not change upon BCR stimulation. Only a minority of proteins (less than 100) changes dynamically between resting and stimulated state. Some results are surprising, as the authors discuss, as the known players of the BCR signalling pathway hardly change in their Raft association. Interesting is also the exclusion of signalling proteins such as Btk, BLNK and Ig-alpha/Ig-beta from BCR clusters upon activation. The strength of the system is that the APEX2 system causes a biotinylation with 1 min, which is an advantage to other systems and that the authors analyse 3 time points after BCR stimulation. The data are thoroughly analysed and discussed. The following points should be addressed: 1. Why did the authors not use the HEL antigen to stimulate their cells, as the A20 line expresses a Ag-specific BCR? Would this not be more physiological than Fab2-anti IgM? 2. Many proteins of pathways like RNA transport, Spliceosome, mRNA surveillance, mismatch repair etc. are identified. Although the authors try to explain some of these data, they should also consider unspecific labelling or unspecific enrichment of these proteins which have nothing to do with raft association. This should be more openly discussed. 3. The authors follow up two proteins that dynamically change during activation, Golga3 and Vti1b, and demonstrate their membrane association upon activation. This is of course relevant. What is missing, is some genetic studies. CRISPR-mediated KO is not difficult to do in cell lines. Have the authors produced such mutants for these two genes and analysed possible phenotypes in BCR signalling or other aspects? This would certainly strengthen the study.
Significance
This is a unique approach to globally identify proteins associated with the BCR in Rafts upon BCR stimulation. Comparable studies with other methods have been published before for B cell lines. Gupta et al. used quantitative proteomics of isolated RAFT-associated proteins before and after BCR stimulation. They also found that the association of most proteins to RAFTs was not changed after BCR stimulation. Saeki et al. used a proteomic approach in another B cell line to identify RAFT associated proteins, but without comparing stimulated to unstimulated cells. The approach used here has the advantage of not selecting only membrane bound proteins, but equally identifiying cytosolic proteins in vicinity to the Raft as well. Furthermore, dynamic changes are better analysed than in the other two studies. Therefore, the findings are relevant and a good advance in the field.
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Reply to the reviewers
Thank you for conducting the peer-review of our manuscript. We really appreciate the constructive criticism of the reviewers, and we are happy to note the positive appreciation of our core findings regarding the role of the decapping machinery during apical hook and lateral root formation and the identification of ASL9 as a target of the decapping machinery. However, both reviewers note we over-interpretate about the function of ASL9 in cytokinin and auxin responses which is not always supported by our data. Based on their feedback, we have toned down our claims and performed additional experiments and analyses and addressed all the comments raised by both reviewers. We hope this substantially revised and improved version of our manuscript will be better accepted.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In this manuscript, the authors describe the role of the mRNA decay machinery in apical hook formation during germination in darkness in A.thaliana. As reported, this machinery is predominantly described in literature in stress response processes, whereas little is known about its involvement during developmental processes. In detail, the authors demonstrated, via RNA immunoprecipitation (RIP) and genetic experiments, the direct regulation of the LATERAL ORGAN BOUNDARIES DOMAIN 3 (LBD3)/ASYMMETRIC LEAVES 2-19 LIKE 9 (ASL9) mRNA stability by the mRNA decapping machinery subunits DCPs. According to the manuscript, ASL9 controls apical hooking, LR development and primary root growth is regulating cytokinin signalling and hence its regulation helps to maintain a correct balance of auxin/cytokinin. Indeed, they showed an impair apical hooking and LR defects both in mRNA decapping mutants, where they observed more capped ASL9 compared to WT, and in ASL9 over-expressor lines. Moreover, they reported a largely restoration of over-expressor lines phenotype in the arr10-5arr12-1 double mutants. This work present simple but interesting data that corroborate the authors hypothesis.
Our response: We thank the reviewer for acknowledging the significance of our findings although we wonder what it´s meant by “simple data”. Through a combination of (complicated) genetics, phenotyping, cell imaging and molecular biology, we have provided mechanistic evidence on the function of the decapping machinery during 2 different post embryonic developmental events. Please see our detailed answers to the reviewer’s comments in the following.
Nonetheless, I have both major comments and minor comments to improve the manuscript: MAJOR COMMENTS: 1. I am a bit concerned by the fact that cytokinin, auxin, LBD3, ARR12 and ARR10 have been largely involved in vasculature development and that the obtained results might be due to their role in vasculature development more than in LBD3 mRNA decapping process. Authors should provide evidence that their results are independent from vasculature defects present in those backgrounds or in case discuss this possibility.
__Our response: __We are a bit puzzled on how vasculature development could explain the apical hook phenotype observed in the decapping mutant. Data like the rapid assembly of P-bodies upon IAA (Fig. 3C) treatments and the overall decreased DR5 signal in dcp mutants (Fig.S5&6) are all consistent with a process precluding vasculature formation. However, we still discuss the possibility that the developmental defects observed in mRNA decapping mutants and ASL9 overexpressor might be related to the vasculature development in these plants (Line 239-244).
The interaction between the described players and auxin is not clear. From the reported experiments it is difficult to understand what authors wants to report as in S4 and S5 are reported experiments not fully described in the text (authors report about introgression of DR5::GFP in dcp1 and 2 mutants, but SD4 reports ACC treatments of DR5::GFP,dcp2 mutants and SD5 of 7 dpg root meristems of this strain ). Please describe and discuss better the experiment. Also, to this reviewer it is difficult to understand whether the absence of auxin activity in the dcp2 mutants hypocotyl is merely an effect of the lack of the hook formation in this background or a cause. Please clarify this point including new experiments (axr1 or axr3 mutants might help in understand this point).
__Our response: __We follow the reviewer’s suggestions and trust we now describe and discuss Fig S5&6 (old Fig S4&S5) clear in Line 188-193. As axr1 has been published with apical hook and lateral root defect (old Line 42, new Line 39&169), we did not repeat it in new experiments but emphasize it in Line 169.
Authors conclude that mRNA decapping is also involved in root growth. However, they do not report direct evidences regarding root growth but mostly regarding the mere root lenght at a precise developmental stage. Please eliminate this point or provide new experiments (e.g., root length and root meristem activity over time)
__Our response: __We follow the reviewer’s suggestions and eliminate the data regarding to primary root growth (Fig. 3-6 &S2)
Regarding root growth defects, these might be due to defect in the vasculature development, please analyse this point or report new experiments (e.g., vasculature analysis of dcp1,2 mutants or tissue specific expression of DCP2).
__Our response: __We largely agree with the reviewer, all the decapping components DCP1, DCP2, DCP5 and PAT1 exhibit high expression in xylem cells and low expression in procambium cells (Brady et al., 2007) indicating functions of decapping components in vasculature development. However, we did not include this knowledge in our manuscript since we decided to eliminate the primary root growth data (Fig.3-6&S2).
For consistency the last paragraph of result section: "ASL9 directly contributes to apical hooking, LR formation and primary root growth" should be part of the result section entitled "Accumulation of ASL9 suppresses LR formation and primary root growth". Authors should move this result in the paragraph before "Interference of a cytokinin pathway and/or exogenous auxin restores developmental defects of ASL9 over-expressor and mRNA decay deficient mutants".
__Our response: __We agree thus we reorganize the result sections and move "ASL9 directly contributes to apical hooking and LR formation" before "Interference of a cytokinin pathway and/or exogenous auxin restores developmental defects of ASL9 over-expressor and mRNA decay deficient mutants" (Line 152).
I suggest being consistent in the description of the statistical analysis. In particular: - I suggest reporting the meaning of ANOVA letters and the P-value in each figure as sometimes these information are missing, especially in Fig.2.
__Our response: __We used ANOVA letters when comparing among genotypes and treatments, for example Fig 2A; and we used stars when comparing to controls, for example old Fig 2F. For consistency, we use letters for all the statistical analysis now and we report the meaning of the letters clearly in the figure legends (Fig. 1-6, S1-5&7). However, we think that putting the P-values in each figure would not be reader-friendly, and thus we have not done this.
- in Fig.S3 please report the statistical significance on bars and the statistical analysis performed.
__Our response: __We thank the reviewer for pointing it out, we report the statistical analysis now in new Fig. S2 (old Fig. S3).
MINOR COMMENTS: L31- please replace "normal" with "proper"
__Our response: __We thank the reviewer for the suggestion, now we replace "normal" with "proper"(Line 30)
L42-please report the acronym of axr1
__Our response: __The acronym of axr1 is correctly reported (Line 40).
L57, L59-please include the entire name of DCP2 and XRN
__Our response: __The entire name of DCP2 and XRN are correctly included (Line 55 &57).
-Please report how many plants were analysed in legend or in methods section
__Our response: __The numbers of plants in analysis are now reported in figure legends (Fig. 1-6, S1,2&7).
-Please report how many transgenic independent lines were obtained in methods section
__Our response: __The numbers of transgenic independent lines are now reported in methods (Line 292)
- Please, try to change the colours of the graph in Fig.S2A-B, as it quite difficult to distinguish light grey shades.
__Our response: __We thank the reviewer’s suggestions, the colours of new Fig.S3&4 (old Fig.S2) are changed.
- In Fig. 5A and S5A scale bars are missing.
__Our response: __We thank the reviewer for pointing this out, scale bars are correctly added in new Fig 4 &S6 (old Fig 5 &S5).
Reviewer #1 (Significance (Required)): The manuscript is interesting and analyse important and overlooked aspects of the role of mRNA decapping in development. Nonetheless experiments reported are not particularly innovative and not always sound. Also authors analysis are a bit superficial probably because they decide to utilize too many systems in their research (root development, hook development and lateral root development).
Our response: We thank the reviewer again for acknowledging the significance of our findings and hope we satisfied the reviewer with our answers above. However, we would like to ask what is the purpose of writing “experiments are not particularly innovative”? We admit we used established and robust experiments which we found sufficient to answer the overlooked aspects of the role of mRNA decpping in apical hook and lateral root development as also noted by the reviewer, but maybe we simply don't understand the comment.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Major Comments 1. My main concern is about the authors' conclusions on the role of mRNA decay and ASL9/LBD3 in the control over cytokinin and auxin responses. I don't think that based on the data presented the authors may do the conclusions stated on lines 184-185, see also the points below.
__Our response: __We agree thus we tone down our conclusion in our new manuscript (Line 197-199), see answers below for detail.
The conclusion about the role of ASL9 and its direct involvement in the apical hook formation and lateral root development/main root growth is a bit exaggerated, based on rather tiny effects mediated by the introduction of asl9-1 into the dcp5-1. Rather, the data suggest that misregulation of other transcripts in the mRNA decay-deficient lines might be responsible for the observed defects. That is also apparent from slightly different phenotypes seen in dcp5-1/pat triple compared to oxASL9 (Fig. 3A). The strong dependency of oxASL9 phenotype on the presence of functional ARR10 and ARR12 implies cytokinin signaling-dependent mechanism of ASL9/LBD3 action (see also point 3 below). Considering the aforementioned phenotype differences between the dcp5-1/pat triple and oxASL9, it would be interesting to see the possible dependence of the mRNA decay-deficient line phenotypes on the cytokinin signaling, too.
__Our response: __We note restoration of dcp5-1 developmental defects in asl9 backgrounds is partial, indicating other ASLs or non-ASLs also contributing to apical hook and lateral root development (old Line 224-225, new Line 229-230 &234-235). We also note that partial suppression is a common phenomenon when studying discrete developmental traits. Two such examples could include the knockout of TPXL5 which partially suppressed the increase of LR density in the hy5 mutant and the introduction of a point mutation in SnRK2.6 in the gsnor1-3/ost1-3 double-mutant partially suppressed the effect of gsnor1-3 on ABA-induced stomatal closure (Qian et al., 2022 The Plant Cell doi.org/10.1093/plcell/koac358; Wang et al., 2015 PNAS 112, 613). In addition to such discrete developmental traits, more dramatic phenotypes like autoimmunity may also only be partially suppressed (Zhang et al., 2012 CH&M 11, 253). However, we agree that it’s interesting to check the dependence of cytokinin signaling of the developmental defects in mRNA decay-deficient mutants. Unfortunately, we were only able to cross arr10 arr12 into dcp5-1. This line showed similar partial restoration of dcp5-1 developmental defects as seen for dcp5-1asl9-1. Overall, these data indicates that contribution of mRNA decapping targeting ASL9 transcripts during apical hook and LR formation depends on ARR10 and ARR12 (Fig. 4&6, Line 180-186).
Also the hypothesis on the upregulation of cytokinin signaling in the mRNA decay mutants and Col-0/oxASL9 is very indirect and should be tested using e.g. TCSn:GFP. The type A ARRs (RRAs) are not only the negative regulators of cytokinin signaling, but also the cytokinin primary response genes. Thus, the downregulation of RRAs could mean the downregulation of the cytokinin signaling pathway in the mRNA decay mutants and/or Col-0/oxASL9. The latter seems to be the case as shown recently (Ye et al., 2021).
__Our response: __We thank the reviewer for suggesting a different annotation of our result regarding to type-A ARRs. Ye et al reported accumulation of ASL9/LBD3 induced downregulation of cytokinin pathway based on weaker ARR5 and TCSn-GFP signal(Ye et al., 2021). However, the fact that knocking out cytokinin signaling activator genes ARR10 and ARR12 largely restored developmental defects in ASL9 over-expressors lead to the hypothesis of upregulated cytokinin signaling in ASL9 over-expressors (Fig 5). Therefore, we substitute “upregulation” with “misregulation” for cytokinin signaling to compromise in our new manuscript (Line 174).
The hypothesis on the causal link between the observed auxin-related defects and upregulated cytokinin signaling (Discussion, lines 214-216) is more than speculation. This could be tested by introducing arr10 arr12 into the dcp2-1/DR5-GFP and/or dcp5-1/DR5-GFP.
__Our response: __We thank the reviewer for the suggestions, due to time and funds management, we decided to check auxin related gene expression in dcp5-1arr10-5arr12-1 mutants instead of making transgenic plants in triple mutant. The repressed expression of SAUR23 and TAR2 in dcp5-1 is partially restored (Fig. S4), indicating possible repression of auxin signaling caused by upregulated cytokinin signaling. However, for consistency in cytokinin signaling description, we tone down the hypothesis on the link between auxin-related defects and cytokinin signaling (Line 218-220).
Compared to the text/quantification of the effect of asl9-1 mutant on the hook formation (Fig. S1D), I see exaggerated hook formation both in the presence and absence of ACC in asl9-1, at least on the figures shown in Fig. S1C. Are the shown seedlings not representative?
__Our response: __We thank the reviewer for pointing our mistakes out, the shown seedlings are representative but mislabeled and the mistakes are corrected now in our new manuscript (Fig. S1C).
Minor Comments 1. Syntax problem in the sentence on lines 45-46 (?).
__Our response: __We thank the reviewer for pointing it out, syntax problem of this sentence is solved now in new manuscript (Line 41-44).
The sentence on lines 48-49 should be rephrased. It implies the cytokinins regulate the amount of RRBs, which is not correct (cytokinins control phosphorylation of RRBs, not their abundance, RRAs are not TFs).
__Our response: __We now rephrase the sentence in a correct way (Line 46)
In the FL for Fig. 2F there is mentioned that MYC-YFP was used as a control compared to the main text mentioning YFP-WAVE (?).
__Our response: __We thank the reviewer for pointing this out, the YFP-WAVE line we used is MYC-YFP transgenic plants, we now include this information in our manuscript (Line 136) and for consistency we changed MYC-YFP to YFP-WAVE in Fig. 2F.
Naito et al. (2007) suggest ASL9 as a target of cytokinin signaling, but I don't think they imply the involvement of ASL9 in the cytokinin signaling as mentioned e.g. on line 166 (?)
__Our response: __We largely agree with the reviewer thus we also cite Ye’s paper here in our new manuscript (Line 165)
References Ye L, Wang X, Lyu M, Siligato R, Eswaran G, Vainio L, Blomster T, Zhang J, Mahonen AP. 2021. Cytokinins initiate secondary growth in the Arabidopsis root through a set of LBD genes. Curr Biol 31(15): 3365-3373 e3367.
Reviewer #2 (Significance (Required)):
The authors provide interesting data suggesting possible role of mRNA decay machinery in the hook and lateral root formation and main root growth via decapping-mediated control over ASL9/LBD3 transcript abundance. Based on the observed interaction of the observed phenotypes with hormonal regulations, the authors' conclude mechanistic link between the mRNA decay/ASL9 and cytokinin and auxin responses.
Our response: We thank the reviewer for acknowledging the significance of our findings.
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Referee #2
Evidence, reproducibility and clarity
Major Comments
- My main concern is about the authors' conclusions on the role of mRNA decay and ASL9/LBD3 in the control over cytokinin and auxin responses. I don't think that based on the data presented the authors may do the conclusions stated on lines 184-185, see also the points below.
- The conclusion about the role of ASL9 and its direct involvement in the apical hook formation and lateral root development/main root growth is a bit exaggerated, based on rather tiny effects mediated by the introduction of asl9-1 into the dcp5-1. Rather, the data suggest that misregulation of other transcripts in the mRNA decay-deficient lines might be responsible for the observed defects. That is also apparent from slightly different phenotypes seen in dcp5-1/pat triple compared to oxASL9 (Fig. 3A). The strong dependency of oxASL9 phenotype on the presence of functional ARR10 and ARR12 implies cytokinin signaling-dependent mechanism of ASL9/LBD3 action (see also point 3 below). Considering the aforementioned phenotype differences between the dcp5-1/pat triple and oxASL9, it would be interesting to see the possible dependence of the mRNA decay-deficient line phenotypes on the cytokinin signaling, too.
- Also the hypothesis on the upregulation of cytokinin signaling in the mRNA decay mutants and Col-0/oxASL9 is very indirect and should be tested using e.g. TCSn:GFP. The type A ARRs (RRAs) are not only the negative regulators of cytokinin signaling, but also the cytokinin primary response genes. Thus, the downregulation of RRAs could mean the downregulation of the cytokinin signaling pathway in the mRNA decay mutants and/or Col-0/oxASL9. The latter seems to be the case as shown recently (Ye et al., 2021).
- The hypothesis on the causal link between the observed auxin-related defects and upregulated cytokinin signaling (Discussion, lines 214-216) is more than speculation. This could be tested by introducing arr10 arr12 into the dcp2-1/DR5-GFP and/or dcp5-1/DR5-GFP.
- Compared to the text/quantification of the effect of asl9-1 mutant on the hook formation (Fig. S1D), I see exaggerated hook formation both in the presence and absence of ACC in asl9-1, at least on the figures shown in Fig. S1C. Are the shown seedlings not representative?
Minor Comments
- Syntax problem in the sentence on lines 45-46 (?).
- The sentence on lines 48-49 should be rephrased. It implies the cytokinins regulate the amount of RRBs, which is not correct (cytokinins control phosphorylation of RRBs, not their abundance, RRAs are not TFs).
- In the FL for Fig. 2F there is mentioned that MYC-YFP was used as a control compared to the main text mentioning YFP-WAVE (?).
- Naito et al. (2007) suggest ASL9 as a target of cytokinin signaling, but I don't think they imply the involvement of ASL9 in the cytokinin signaling as mentioned e.g. on line 166 (?)
References
Ye L, Wang X, Lyu M, Siligato R, Eswaran G, Vainio L, Blomster T, Zhang J, Mahonen AP. 2021. Cytokinins initiate secondary growth in the Arabidopsis root through a set of LBD genes. Curr Biol 31(15): 3365-3373 e3367.
Significance
The authors provide interesting data suggesting possible role of mRNA decay machinery in the hook and lateral root formation and main root growth via decapping-mediated control over ASL9/LBD3 transcript abundance. Based on the observed interaction of the observed phenotypes with hormonal regulations, the authors' conclude mechanistic link between the mRNA decay/ASL9 and cytokinin and auxin responses.
-
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
In this manuscript, the authors describe the role of the mRNA decay machinery in apical hook formation during germination in darkness in A.thaliana. As reported, this machinery is predominantly described in literature in stress response processes, whereas little is known about its involvement during developmental processes. In detail, the authors demonstrated, via RNA immunoprecipitation (RIP) and genetic experiments, the direct regulation of the LATERAL ORGAN BOUNDARIES DOMAIN 3 (LBD3)/ASYMMETRIC LEAVES 2-19 LIKE 9 (ASL9) mRNA stability by the mRNA decapping machinery subunits DCPs. According to the manuscript, ASL9 controls apical hooking, LR development and primary root growthis regulating cytokinin signalling and hence its regulation helps to maintain a correct balance of auxin/cytokinin. Indeed, they showed an impair apical hooking and LR defects both in mRNA decapping mutants, where they observed more capped ASL9 compared to WT, and in ASL9 over-expressor lines. Moreover, they reported a largely restoration of over-expressor lines phenotype in the arr10-5arr12-1 double mutants.
This work present simple but interesting data that corroborate the authors hypothesis. Nonetheless, I have both major comments and minor comments to improve the manuscript:
Major comments
- I am a bit concerned by the fact that cytokinin, auxin, LBD3,ARR12 and ARR10 have been largely involved in vasculature development and that the obtained results might be due to their role in vasculature development more than in LBD3 mRNA decapping process. Authors should provide evidence that their results are independent from vasculature defects present in those backgrounds or in case discuss this possibility.
- The interaction between the described players and auxin is not clear. From the reported experiments it is difficult to understand what authors wants to report as in S4 and S5 are reported experiments not fully described in the text (authors report about introgression of DR5::GFP in dcp1 and 2 mutants, but SD4 reports ACC treatments of DR5::GFP,dcp2 mutants and SD5 of 7 dpg root meristems of this strain ). Please describe and discuss better the experiment. Also, to this reviewer it is difficult to understand whether the absence of auxin activity in the dcp2 mutants hypocotyl is merely an effect of the lack of the hook formation in this background or a cause. Please clarify this point including new experiments (axr1 or axr3 mutants might help in understand this point).
- Authors conclude that mRNA decapping is also involved in root growth. However, they do not report direct evidences regarding root growth but mostly regarding the mere root lenght at a precise developmental stage. Please eliminate this point or provide new experiments (e.g., root length and root meristem activity over time)
- Regarding root growth defects, these might be due to defect in the vasculature development, please analyse this point or report new experiments (e.g., vasculature analysis of dcp1,2 mutants or tissue specific expression of DCP2).
- For consistency the last paragraph of result section: "ASL9 directly contributes to apical hooking, LR formation and primary root growth" should be part of the result section entitled "Accumulation of ASL9 suppresses LR formation and primary root growth". Authors should move this result in the paragraph before "Interference of a cytokinin pathway and/or exogenous auxin restores developmental defects of ASL9 over-expressor and mRNA decay deficient mutants".
- I suggest being consistent in the description of the statistical analysis. In particular:
- I suggest reporting the meaning of ANOVA letters and the P-value in each figure as sometimes these information are missing, especially in Fig.2.
- in Fig.S3 please report the statistical significance on bars and the statistical analysis performed.
Minor comments
L31- please replace "normal" with "proper"
L42-please report the acronym of axr1
L57, L59-please include the entire name of DCP2 and XRN
- Please report how many plants were analysed in legend or in methods section
- Please report how many transgenic independent lines were obtained in methods section
- Please, try to change the colours of the graph in Fig.S2A-B, as it quite difficult to distinguish light grey shades.
- In Fig. 5A and S5A scale bars are missing.
Significance
The manuscript is interesting and analyse important and overlooked aspects of the role of mRNA decapping in development. Nonetheless experiments reported are not particularly innovative and not always sound. Also authors analysis are a bit superficial probably because they decide to utilize too many systems in their research (root development, hook development and lateral root development).
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Reply to the reviewers
Revision Plan
Manuscript number: RC-2022-01765
Corresponding author(s): Dr. Huiqing Zhou (Radboud University)
1. General Statements [optional]
We like to thank the editor and reviewers for their constructive comments and suggestions for improving the manuscript. We here address the comments point-by-point using the template of the revision plan.
2. Description of the planned revisions
Reviewer #1:
- While the study is complete and describes well, a strong conclusion, including validation of the role of some TFs such as FOSL2 through knock out experiments in model organisms or cell culture will elevate the paper more (optional). *
To address this point, we will perform siRNA knockdown experiments of TFs identified in our study, including FOSL2, in primary LSCs, and examine the transcriptional consequences of knocking down these TFs by RNA-seq or RT-qPCR analyses.
Reviewer #2:
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- The findings provide an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. Although the presented predictions are interesting, what is missing is an examination of the functional significance of the findings. * Indeed, we fully agree with the reviewer that additional functional examinations are important and relevant and would strengthen the manuscript. We propose to do the following functional analyses to further demonstrate the importance of the key TFs.
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Immunostaining of the key TFs in the human cornea and in LSCs and KCs.
- As described above, we will perform siRNA experiments for key TFs identified in our study, followed by RNA-seq or RT-qPCR analysis, to assess the transcriptional program controlled by these key TFs.
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The gene regulatory network controlled by these tested TFs will be analysed, to examine the interplay of these TFs in transcriptional regulation and in cell fate determination. Reviewer #2:
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Also, the findings indicate an interaction between FOXL2 and other TFS is important for maintaining the corneal epithelium. These interesting predictions indicate an important role for FoxL2 in corneal function. It would be important to verify these predictions by experimental studies, for example, by presenting the association of FOXL2 with the predicted co-factors and presenting data on the effect of the identified mutation on FOXL2 transcriptional activity.
*
We assume that Reviewer #2 refers to FOSL2 instead of FOXL2. We agree with this reviewer’s suggestion to functionally address the importance of FOSL2 in the cornea. In order to answer this, we plan to perform FOSL2 staining and FOSL2 siRNA knockdown in LSCs, followed by RNA-seq, as described above. This will show the FOSL2 importance in LSCs and in cornea, and will identify the affected downstream gene networks.
Regarding the clinical effect of the specific FOSL2 variant reported in our study, we agree that functional validation would strengthen our work even more. We believe that the main message of the study is the use of integrative omics analyses to uncover new transcription factors involved in corneal and limbal fates, and to highlight new candidate genes in corneal disease. Therefore we feel that the disease mechanism behind the specific FOSL2 variant, albeit interesting, is beyond the scope of this study. Nonetheless, we reinforced the pathogenicity of the variant with various in silico prediction platforms (supplementary table 9). Interestingly, a recent study reported that FOSL2 truncating mutations are involved in a new syndrome with ectodermal defects and cataract. This is in line with our findings that FOSL2 is an important shared TF in both LSCs and KCs, and strengthens the predicted role of FOSL2 in the epithelium of the eye and associated diseases. We have included additional discussion on this study in the Discussion line 662-668.
3. Description of the revisions that have already been incorporated in the transferred manuscript
Reviewer #2:
In Figure 1, the authors compare the transcriptome and epigenome (ATAC-seq and histone modifications) of basal KCs from skin donors and cultured LSCs established from limbal biopsies. The authors should clarify the source of the cells in the published studies - specifically, why more data were needed and if these were comparable to their datasets.
We have included the cell sources and cultured conditions from the published studies and added additional columns in the supplementary tables 1, 2 and 3. Briefly, LSC publicly available samples were extracted from post-mortem cornea and cultured in DMEM/F12, or KSFM.
Regarding the questions on the necessity of incorporating more data, our reasoning was two-fold. First of all, we have taken an integrated approach to perform our analysis, using both our own and publicly available datasets. We see this as a strength, as the most important differences between cell types that determine cell fates should be consistent with cells generated from different donors and labs. Second, we choose to generate more data in our own lab in order to make sure to have comparisons without the influence of technical differences between publicly available datasets. We include text about this approach in the Discussion (lines) 578-580. Furthermore, to show that the datasets we used are consistent and can be integrated, we have performed a PCA correlation analysis for the RNA-seq analysis (supplementary figures 1A&1B lines 834-837), and added a spearman correlation analysis for the ATAC-seq datasets (supplementary figure 5F & lines 818-820). Both indicated clear biological signal similarities between cell types across different labs and techniques.
Reviewer #2:
3.Next, they compared the transcriptomes of LSCs and KCs to the transcription profile of LSCs from two aniridia patients and control. They need to specify the stage of the donors' disease and provide details on the control samples.
Both aniridia samples were from patients of stage 4 on the Lagali Stages (Lagali, N. et al. (2020) ‘Early phenotypic features of aniridia-associated keratopathy and association with PAX6 coding mutations’, The Ocular Surface, 18(1), pp. 130–140. We have included this information in Material and Methods (lines 738-739). For healthy control cells, no information regarding the stage and gender is available, as they are from anonymous individuals. We added more information on the aniridia and control samples regarding the culture conditions and passage numbers (lines 747:750).
Reviewer #2:
- In addition, and as indicated above, when combining published datasets, one should clarify whether the methods of collecting/growing the cells and the disease stage are comparable. This is important with samples from aniridia as it is unclear if the patient LSCs survive the isolation or if other cells take over.*
Healthy LSC cells used in the direct comparison with aniridia LSC cells were grown using the same expansion and culture conditions. Furthermore, the method of culture, extraction and expansion between the earlier published aniridia cell data and our data are exactly the same (lines 735:750). As described above, we have included the cell sources from the aniridia samples, and added additional columns in the supplementary table 1.
Reviewer #2:
- It would be valuable to the community if the presented data were also provided online in a web tool so that CRE activity or gene expression could be easily examined.*
We have expanded the UCSC track hub to highlight the identified variable CRE elements. This will enable a searchable tool for differential CREs close to genes of interest between KCs and LSCs. We have furthermore added a sentence to explicitly mention the presence of this track hub in the result section (lines 248-249).
4. Description of analyses that authors prefer not to carry out
Reviewer #1:
- By identifying differential cis regulatory elements in two cells, they identify TFs that are associated with overexpression or repression of genes of interest. However, this approach of relying solely upon nearest genes of CREs is very cursory and the authors could have used methods such as Activity-by-Contact to establish CREs and their target genes and then assessed their correlation with expression (optional). Activity-by-Contact incorporation would be an exciting inclusion in the data analysis, and for the next step in GRN modelling. However, this is out of the scope of this manuscript. In addition, we would like to point out that we did not solely rely on the method of mapping CREs to the nearest genes. Instead, for H3K27ac and ATAC-seq signals, our analysis uses a weighted TSS distance method, within windows of up to 100kb, similar to the method ANANSE and other published gene regulatory network tools. For H3K4me3 and H3K27me3 marks which correlate far better with an expression of the closest genes, we use a window of 2kb at the closest gene.
Reviewer #2:
When ATAC-seq was combined with histone modification analyses, about a third of these regions showed different characteristics, inferring tissue-specific activities. These data may be valuable for identifying tissue-specific cis-regulatory elements (CREs) for the key TFs. This, however, remains to be examined experimentally.
It is not fully clear to us what ‘experimentally examination’ was referred to by this reviewer, whether to test these tissue-specific CREs individually or globally. We agree that it is important to test tissue-specific CREs experimentally to examine their function, e.g., which genes they are regulating, and which role they play in tissue-specificity. However, this is out of the scope of this manuscript.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Multi-omics analyses identify transcription factor interplay in corneal epithelial fate determination and disease The authors of this manuscript describe their work on identifying transcriptional regulators and their interplay in cornea using limbal stem cells and epidermic using keratinocytes. This is a very well written and well described comprehensive manuscript. The authors performed various analyses which were in line with logical workflow of the research question. The authors begin by first identifying differential gene expression signals for the two tissues along with enriched biological processes using GSEA and PROGENy. The strength of this manuscript also includes usage of epigenetic data to determine the cell fate and its drivers. The authors study various epigenetic assays and correlate them expression levels of TFs and genes to identify regulatory patterns that mark differences between LSCs and KCs. By identifying differential cis regulatory elements in two cells, they identify TFs that are associated with overexpression or repression of genes of interest. However, this approach of relying solely upon nearest genes of CREs is very cursory and the authors could have used methods such as Activity-by-Contact to establish CREs and their target genes and then assessed their correlation with expression (optional). In logical progression, the authors use gene regulatory networks using to compare LSC and KC with Embryonic Stem Cells (ESC) to identify most influential TFs to differentiate them. Along with identifying key TFs, they also identify TF regulatory hierarchy to find TFs that regulate other TFs in context-specific manner. They identify "p63, FOSL2, EHF, TFAP2A, KLF5, RUNX1, CEBPD, and FOXC1 are among the shared epithelial TFs for both LSCs and KCs. PAX6, SMAD3, OTX1, ELF3, and PPARD are LSC specific TFs for the LSC fate, and HOXA9, IRX4, CEBPA, and GATA3 were identified as KC specific TFs." And "p63, KLF4 and TFAP2A can potentially co-regulate PAX6 in LSCs." To compare in vitro findings with in vivo results, they also generate single cell data and identify specific TFs that may play pathobiological role in disease development and progression. While the study is complete and describes well, a strong conclusion, including validation of role of some TFs such as FOSL2 through knock out experiments in model organisms or cell culture will elevate the paper more (optional). This study merits publication in high quality journal (IF:10-15)
Reviewer #1 (Significance (Required)):
The study is very significant not only in the context of corneal disease biology. The imbalance in interplay of TFs is often envisaged behind disease development but very few efforts of detailed analysis are undertaken. This study is performed very well and the methods are described in clear manner. Appropriate statistical methods are used where required.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The study by Smits et al. presents detailed multi-omics (transcripts, ATAC-seq, histone marks) analyses comparing human limbal stem cells (LSCs) to skin keratinocytes (KCs). The authors compared these two cell types because they have a shared origin in the epidermal progenitors and because LSC diseases occasionally accompany a transition to KC-like phenotypes. The authors analyzed the "omics" data using several bioinformatic analysis tools. Their analyses resulted in a detailed list of the critical transcription factors (TFs) and their gene regulatory networks shared between the two lineages and those unique to either LSCs or KCs.
The findings provide an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. Although the presented predictions are interesting, what is missing is an examination of the functional significance of the findings. Also, as detailed below, there is a need to clarify the source of the cells used for the different analyses.
Comments and suggestions: 1. In Figure 1, the authors compare the transcriptome and epigenome (ATAC-seq and histone modifications) of basal KCs from skin donors and cultured LSCs established from limbal biopsies. The authors should clarify the source of the cells in the published studies - specifically, why more data were needed and if these were comparable to their datasets. 2. Next, they compared the transcriptomes of LSCs and KCs to the transcription profile of LSCs from two aniridia patients and control. They need to specify the stage of the donors' disease and provide details on the control samples. In addition, and as indicated above, when combining published datasets, one should clarify whether the methods of collecting/growing the cells and the disease stage are comparable. This is important with samples from aniridia as it is unclear if the patient LSCs survive the isolation or if other cells take over. The finding that LSC genes are reduced in aniridic LSCs may suggest that the cells resemble KCs, although specific KC genes are not elevated. 3. Figure 2: The authors characterized the regulatory regions in the two cell types based on ATAC-seq and histone marks. Based on ATAC-seq, 80% of the open areas were shared between the two lineages. When ATAC-seq was combined with histone modification analyses, about a third of these regions showed different characteristics, inferring tissue-specific activities. These data may be valuable for identifying tissue-specific cis-regulatory elements (CREs) for the key TFs. This, however, remains to be examined experimentally. 4. It would be valuable to the community if the presented data were also provided online in a web tool so that CRE activity or gene expression could be easily examined. 5. Using motif predictions, the authors point to the TF families that likely control the differential CREs (Figure 3). Next, the authors constructed the gene regulatory network based on the (ANANSE) pipeline, which integrates CRE and TF motif predictions with the expression of TFs and their target genes. To gain further insight into the shared gene regulatory networks, they compared each to similar data from embryonic stem cells. Their analysis further suggests shared TFs regulating each other and some of the tissue-specific transcription factors. Differential gene expression of the TFs was partially validated by analyzing available single-cell data (Figure 4). 6. In the final section of the study, the authors aimed to identify TFs in LSCs that are relevant to corneal disease. They examined whether the LSC TFs are bound to genes associated with LSC deficiency and inherited corneal diseases. To accomplish this task, the authors incorporated single-cell data on corneal gene expression and available datasets on genetic analyses of families. Through this analysis, they identified a mutation in FOSL2 that may be causing corneal opacity in the carriers. Also, the findings indicate an interaction between FOXL2 and other TFS is important for maintaining the corneal epithelium. These interesting predictions indicate an important role for FoxL2 in corneal function. It would be important to verify these predictions by experimental studies, for example, by presenting the association of FOXL2 with the predicted co-factors and presenting data on the effect of the identified mutation on FOXL2 transcriptional activity.
Reviewer #2 (Significance (Required)):
The analysis provides an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. The results predict a role for FoxL2 in corneal function.
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Referee #2
Evidence, reproducibility and clarity
The study by Smits et al. presents detailed multi-omics (transcripts, ATAC-seq, histone marks) analyses comparing human limbal stem cells (LSCs) to skin keratinocytes (KCs). The authors compared these two cell types because they have a shared origin in the epidermal progenitors and because LSC diseases occasionally accompany a transition to KC-like phenotypes. The authors analyzed the "omics" data using several bioinformatic analysis tools. Their analyses resulted in a detailed list of the critical transcription factors (TFs) and their gene regulatory networks shared between the two lineages and those unique to either LSCs or KCs.
The findings provide an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. Although the presented predictions are interesting, what is missing is an examination of the functional significance of the findings. Also, as detailed below, there is a need to clarify the source of the cells used for the different analyses.
Comments and suggestions:
- In Figure 1, the authors compare the transcriptome and epigenome (ATAC-seq and histone modifications) of basal KCs from skin donors and cultured LSCs established from limbal biopsies. The authors should clarify the source of the cells in the published studies - specifically, why more data were needed and if these were comparable to their datasets.
- Next, they compared the transcriptomes of LSCs and KCs to the transcription profile of LSCs from two aniridia patients and control. They need to specify the stage of the donors' disease and provide details on the control samples. In addition, and as indicated above, when combining published datasets, one should clarify whether the methods of collecting/growing the cells and the disease stage are comparable. This is important with samples from aniridia as it is unclear if the patient LSCs survive the isolation or if other cells take over. The finding that LSC genes are reduced in aniridic LSCs may suggest that the cells resemble KCs, although specific KC genes are not elevated.
- Figure 2: The authors characterized the regulatory regions in the two cell types based on ATAC-seq and histone marks. Based on ATAC-seq, 80% of the open areas were shared between the two lineages. When ATAC-seq was combined with histone modification analyses, about a third of these regions showed different characteristics, inferring tissue-specific activities. These data may be valuable for identifying tissue-specific cis-regulatory elements (CREs) for the key TFs. This, however, remains to be examined experimentally.
- It would be valuable to the community if the presented data were also provided online in a web tool so that CRE activity or gene expression could be easily examined.
- Using motif predictions, the authors point to the TF families that likely control the differential CREs (Figure 3). Next, the authors constructed the gene regulatory network based on the (ANANSE) pipeline, which integrates CRE and TF motif predictions with the expression of TFs and their target genes. To gain further insight into the shared gene regulatory networks, they compared each to similar data from embryonic stem cells. Their analysis further suggests shared TFs regulating each other and some of the tissue-specific transcription factors. Differential gene expression of the TFs was partially validated by analyzing available single-cell data (Figure 4).
- In the final section of the study, the authors aimed to identify TFs in LSCs that are relevant to corneal disease. They examined whether the LSC TFs are bound to genes associated with LSC deficiency and inherited corneal diseases. To accomplish this task, the authors incorporated single-cell data on corneal gene expression and available datasets on genetic analyses of families. Through this analysis, they identified a mutation in FOSL2 that may be causing corneal opacity in the carriers. Also, the findings indicate an interaction between FOXL2 and other TFS is important for maintaining the corneal epithelium. These interesting predictions indicate an important role for FoxL2 in corneal function. It would be important to verify these predictions by experimental studies, for example, by presenting the association of FOXL2 with the predicted co-factors and presenting data on the effect of the identified mutation on FOXL2 transcriptional activity.
Significance
The analysis provides an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. The results predict a role for FoxL2 in corneal function.
-
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Referee #1
Evidence, reproducibility and clarity
Multi-omics analyses identify transcription factor interplay in corneal epithelial fate determination and disease The authors of this manuscript describe their work on identifying transcriptional regulators and their interplay in cornea using limbal stem cells and epidermic using keratinocytes. This is a very well written and well described comprehensive manuscript. The authors performed various analyses which were in line with logical workflow of the research question. The authors begin by first identifying differential gene expression signals for the two tissues along with enriched biological processes using GSEA and PROGENy. The strength of this manuscript also includes usage of epigenetic data to determine the cell fate and its drivers. The authors study various epigenetic assays and correlate them expression levels of TFs and genes to identify regulatory patterns that mark differences between LSCs and KCs. By identifying differential cis regulatory elements in two cells, they identify TFs that are associated with overexpression or repression of genes of interest. However, this approach of relying solely upon nearest genes of CREs is very cursory and the authors could have used methods such as Activity-by-Contact to establish CREs and their target genes and then assessed their correlation with expression (optional). In logical progression, the authors use gene regulatory networks using to compare LSC and KC with Embryonic Stem Cells (ESC) to identify most influential TFs to differentiate them. Along with identifying key TFs, they also identify TF regulatory hierarchy to find TFs that regulate other TFs in context-specific manner. They identify "p63, FOSL2, EHF, TFAP2A, KLF5, RUNX1, CEBPD, and FOXC1 are among the shared epithelial TFs for both LSCs and KCs. PAX6, SMAD3, OTX1, ELF3, and PPARD are LSC specific TFs for the LSC fate, and HOXA9, IRX4, CEBPA, and GATA3 were identified as KC specific TFs." And "p63, KLF4 and TFAP2A can potentially co-regulate PAX6 in LSCs." To compare in vitro findings with in vivo results, they also generate single cell data and identify specific TFs that may play pathobiological role in disease development and progression. While the study is complete and describes well, a strong conclusion, including validation of role of some TFs such as FOSL2 through knock out experiments in model organisms or cell culture will elevate the paper more (optional). This study merits publication in high quality journal (IF:10-15)
Significance
The study is very significant not only in the context of corneal disease biology. The imbalance in interplay of TFs is often envisaged behind disease development but very few efforts of detailed analysis are undertaken. This study is performed very well and the methods are described in clear manner. Appropriate statistical methods are used where required.
-
-
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
This manuscript describes studies that indicate roles for the ALK and LTK receptors in neuronal polarity, cortical patterning and behavior in mice. I really liked the study and overall think that it deserves publication in a high-ranking journal. It reports important and novel results and benefits from a comprehensive analysis at multiple levels, including cell biological, biochemical and behavior. The points raised below are suggestions for consideration at the discretion of the authors.
We thank the reviewer for the positive and enthusiastic comments on our study and especially for noting that it is appropriate for publication in a high-ranking journal. We greatly appreciate the valuable suggestions, the majority of which we have incorporated into the revised manuscript.
- The term "DKO" appears in the Introduction without explanation. I assume this means double KO mice lacking both receptors from birth. It should be indicated here, just in case.
We have added text at the first appearance of DKO (ie results section) to indicate that this refers to double knockout mice that lack both Ltk and Alk from birth.
- The last paragraph of the Introduction is redundant with the Abstract. This is a stylistic question, which is up to the authors. Nevertheless, as a suggestion, they could take the opportunity here to explain the rationale of the study and why they did what they did._
We have made some modifications to provide an indication of the rationale for the studies.
- Is "single cell in situ mRNA analysis" standard in situ hybridization or something else? Why is it called "single-cell"? It could be misleading.
This was a typographical error and has been corrected to single molecule in situ.
- In Fig. S1B, could the authors please include expression patterns of LTK in adult brain? It'd seem that is the most relevant place to look given the analysis that follows in the paper.
We have replaced the previous panels with new plots (now Fig. S1G) showing the relative expression of Ltk, Alk and their ligand, Alkal2 in embryos (E15.5), newborn (P0) and post-natal Day 2 (P2) and Day 7 (P7) and in adults both in the cortex and whole brain. The results confirm that Alk and Ltk are both expressed in the cortex and brain but in varying patterns with Alk expression decreasing with age and Ltk increasing, particularly in the cortex. In contrast, Alkal2 expression is relatively constant throughout.
Related comments #5, #7, #8 and #9.
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I have an issue in general in the first part of the manuscript with regards to the labeling of cortical layers. How were CP, IZ and SVZ/VZ defined? Specific markers should be used to identify their actual boundaries. Guesswork from the DAPI pattern (if that is what was used) is not really appropriate.
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In Fig. 1F, again, how were the boundaries between the cortical areas (dotted lines) determined? This is particularly important for the mutant sections....
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In Fig. S3C-F, the all-critical quantification of Ctip2 cells at P2 seems to be missing in this figure. It would important to provide this in light of the comments above. Again, the same problem with the layer boundaries is clear here.....
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In Figure 2A and B, % positive cells is plotted but we are not told what is the reference (100%) level. ... Also, the idea of drawing a little rectangle in the IZ and CP and counting only there is flawed. ...Finally, again, we are not told how the boundaries of the different cortex areas were established. ...
Response to related comments #5, #7, #8 and #9.
As exemplified in the related comments above, the reviewer indicated that they “__have an issue in general in the first part of the manuscript with regards to the labeling of cortical layers.”
We thank the reviewer for this insightful comment. Development of the mouse cortex follows a stereotypical pattern, thus we used a combination of DAPI ( ie nuclear density is characteristic of some layers), and layer specific markers (Satb2, Ctip2, Pax6, Sox2, Tbr2) to label the cortical layers. While this is generally acceptable for wild type mice, we agree with the reviewer’s comment that this may not be appropriate in mutant mice. Accordingly, we have now taken a more unbiased approach and repeated all of the quantitation after creating equally sized bins that span the entire cortical length and have plotted the quantitation by bin location. The general location of layers in WT mice has been marked on the images for reference. Our conclusions that there are defects in early patterning that are resolving by ~P7 is unchanged.
With this re-quantitation, some of the previous reviewer comments within #5, 7, 8 and 9 no longer apply (ie a missing plot, box placement being subjective, etc) and so have not been responded to. With regards to the question of what is the reference (ie 100%) for the plots showing the y-axis as % positive; this was determined based on the total number of DAPI+ cells counted in each region. This information has been added to the legends and methods along with details of the new quantitation method.
- Comparing Fig. 1 and Fig. S2, there would seem to be little or no additive nor synergistic effects of the double mutation, as the phenotype in the DKO appears to be completely attributable to the Ltk KO. What does this mean? Providing the expression patterns of the two receptors at the ages used here (i.e., P2 and P7) would also be helpful.
The relative contribution of Alk or Ltk in comparison to the DKO, varies as a function of age (E15.5, P2, P7) that generally correlates with their level of expression, as per the Reviewer’s suggestion. For example, at E15.5, a reduction in the number of Sox2+ or Tbr2+ cells is observed for either Alk or Ltk knockouts alone, with a more prominent reduction in the case of Alk alone, and with the DKOs showing the greatest reduction. In contrast, when examining Ctip2 levels at P2, the loss of Ltk alone yields a stronger effect. In agreement with these observations, analysis of mRNA expression levels show that Alk levels are highest in the embryonic cortex and brain and steadily decline until adulthood, while Ltk expression increases with maximal levels occurring post-natally. As indicated for our reply to comment #4, we have now added plots showing the relative level of expression of Alk and Ltk at various ages from embryos to adults (Fig S1G).
- At the end of page 8, it is concluded that Alk/Ltk promote neuronal migration. Is this a cell-autonomous effect? Given the very sparse expression of these receptors (Fig S1), cell-autonomy (which is being implied by the authors) is not at all clear. Is the migration of Alk+ cells affected in the Ltk mutant? Vice-versa?
In our analysis of mRNA expression using RNAscope we originally included a widefield image that depicts the entire cortex where it is difficult to see expression at the cell level. We now also provide a magnified image of the E15.5 SVZ/VZ that shows that most cells do express the receptors (Fig. S1B). Thus, the results are consistent with the idea that the defect in migration is a cell autonomous effect.
- In Fig. S4A, as every cell in these panels bears probe signal, it'd be important to present a negative control, perhaps from KO cultures or wild type cells lacking receptor expression in the same field as expressing cells. At a 75%, 1 in 4 cells in any field should be receptor-negative.
As requested, we now provide images with a wider field of view that includes negative cells.
- Figure S4B is difficult to interpret in the absence of Tau and MAP2 markers, as GFP does not discriminate between axons and dendrites.
In the original submission we quantitated Tau-1 and MAP2 co-stained neurons in many experiments to demonstrate that Ltk/Alk act on axons, but in some cases, we used Tuj1 to more easily visualize and quantitate neurites. Nevertheless, as requested by the reviewers, in the revised manuscript we have repeated and replaced most of the results with Tuj1 or phalloidin staining with experiments using Tau-1 and MAP2 antibodies, including Fig. 5B-D and Fig. 6A-D and G as well as for Fig. S4B. The new data is consistent with our results using Tuj1 staining and further support our conclusions that Ltk/Alk act via Igf1-r to regulate neuronal polarity.
In general, the authors are recommended to show more than one cell per condition in their figures. Readers need to be convinced that these are robust phenotypes easily observed on many cells in the same field.
Due to space constraints, we included only a single representative image for each condition and then provided quantitation to support our conclusions. We have numerous images for all of the presented data and could provide a collage for all panels if considered appropriate. In the meantime, we have added additional images for several experiments in the Main Figures (Fig. 5A-D, Fig. 6A, C) and in Suppl. Figure S4A, B, C where sufficient space was readily available.
- In Fig. S4C and D, do the KO neurons become bipolar? I don't see examples of multipolar neurons in the images provided.
Upon siRNA mediated knockdown of Ltk and/or Alk, we observe about 50% of the neurons are bipolar (ie display the typical wild type single axon phenotype) while roughly 40% display the multiple axon phenotype. With the exception of the control (siCTL), the images provided were selected to show neurons with multiple axons. However, in some of the images, the arrowheads pointing to the axons were inadvertently omitted. These have now been added.
- Is there a way to quantify the effects shown in Fig. 3E?
We attempted to quantitate the number and direction of neurites in the brain sections but because this is a dense tissue, even with Golgi staining, we found it impossible to trace individual neurites back to the cell body and thus were unable to quantitate the effects. As an alternative, we have provided additional images (Fig. S3B) from distinct mice to support our observations of aberrant horizontal neurites in the adult cortex.
- The DKO display a dramatically different behavior phenotype compared to single Kos. How can this result be explained given that DKOs are indistinguishable from single KOs in all other parameters studied?
The reviewer is correct, that the single KO mice do not manifest noticeable behavioural defects except when older and challenged with the most demanding task, the Puzzle box, which measures complex executive functions. We speculate that alternative cortical re-wiring in the single knockouts is sufficient to maintain normal circuitry that cannot be compensated when both Ltk and Alk receptors are deleted. It is also possible that Ltk/Alk regulated signalling events, besides Igf-1r/PI3K could contribute to the behavioural defects observed in the DKO mice, such as the ALK-LIMK-cofilin pathway which regulates synaptic scaling mentioned by the reviewer (Zhou et al., Cell Rep. 2021). Nevertheless, the strong phenotype of the DKOs confirms that Ltk/Alk are important for proper brain function, thus our preference is to retain the behavioural data in the manuscript but to discuss that alternative Ltk/Alk pathways could contribute to the phenotype (which we have now incorporated into the text).
- At the end of the behavior section, the authors attribute the phenotypes observed to defects in neuronal polarization. Given that polarization was only studied in vitro, it may be a premature to conclude that neurons fail to polarize in vivo in the absence of direct evidence showing this.
We agree and have modified the text to remove this inaccurate assertation.
- Regarding P-AKT studies, it would be interesting to assess the effects of the ALK7LTK ligands (e.g., from conditioned medium) on the levels of P-AKT in WT neurons.
We agree that this would be interesting and we had attempted this experiment, but found that treatment of WT cortical neurons with medium conditioned with the ALKAL2 ligand did not change the levels of pAKT under our experimental conditions (namely 20-30 min treatment with ACM). Because the data is negative, it makes it difficult to make a firm conclusion, but if true, it is possible that other pathways might be involved when WT cortical neurons are stimulated with ligand.
- In the mid part of page 14, the sentence "Treatment of WT cortical neurons with AG1024 at a dose (1 μM) at which only IGF-1R but not InsR was inhibited restored the single axon phenotype in DKO neurons" is confusing. Treatment performed in WT neurons but assessed in DKO neurons? This must be a typo.
Thank you for pointing out this typo. It has been corrected.
- For completion, it would be informative to test whether IGF-1 antagonizes the effects of ALK and LTK ligands in axon formation.
As suggested, we performed the requested experiment (with 3 independent repeats). In brief, four hours post-plating neurons were treated with control or ALKAL2-conditioned media and Igf-1 was added after 1 hour. Neurons were fixed at 36 hours, stained for MAP2 and Tau-1 and axons (Tau-1+) quantitated. Consistent with our previous findings, Igf-1 promotes the formation of multiple axons while ligand inhibits axon formation. In the ligand-treated neurons, addition of Igf-1 did not result in a statistically-significant change in the number of axons. These findings are consistent with our model that activation of Ltk/Alk promotes a decrease in cell-surface Igf1-r. This data has been added to the manuscript (Fig. 7J).
- The quality of the blot provided to illustrate levels of activated Igf-1r in Fig. 7A is clearly suboptimal. It is not apparent from that blot that phosphorylation of Igf1r is increased in the mutant neurons as the band intensities are indistinguishable. Was this performed in cortex extracts or cultured neurons? Is it affected by treatment with ALK/LTK ligands?
We apologize for a labelling error that has caused confusion for both reviewers. We have replaced the blots and corrected the labels. We have noted in the legend that the experiments were performed using cultured cortical neurons.
- Given the physical interaction between ALK/LTK and IGF-R1, these receptors are presumably co-internalized upon ligand treatment, or? Does treatment with IGF1 induces internalization of ALK or LTK?
This is a very interesting question. Unfortunately, due to the lack of suitable antibodies for the mouse versions of Alk or Ltk, we are not able to perform these experiments in cortical neurons with endogenous receptor expression. However, our co-immunoprecipitation experiments and in vitro kinase assays, indicate that only versions of LTK and/or ALK with active kinase domains can interact with IGF-1R and that the activated LTK/ALK receptors then phosphorylate IGF-1R and trigger IGF-1R internalization (Fig. 7 and Fig. 8 model). Thus, we would expect that treatment with IGF-1 in the absence of LTK/ALK activation will not affect LTK/ALK internalization but will trigger IGF-1R endocytosis.
- The last paragraph in the Results section may be more appropriate for Discussion to avoid repetition. But it is of course up to the authors to decide on stylistic issues.
We prefer to include a summary of the experimental findings and the model figure at the end of the results.
- There is a discussion of possible redundancies between ALK and LTK in the Discussion section which appears to contradict itself. It is first stated (end of p. 18) that the two receptors are not redundant but both required for function. But in p. 19, the significant behavioral phenotypes observed in DKO mice, but not in single KO mice, are attributed to redundancy and compensation between the receptors. This needs some clarification. It's difficult to understand how there can be redundancy for behavior but not for structure or function.
We have clarified in the discussion, that both receptors are required in the context of neuronal polarity and migration whereas in the case of behaviour, compensatory mechanisms in neural circuitry or perhaps non-redundant Igf-1r independent pathways result in a strong phenotype only in DKO and can compensate for single but not double knockouts.
Reviewer #1 (Significance):
see above
Reviewer #2 (Evidence, reproducibility and clarity):
Christova et al. analyzed single and double knockout mice for Alk and Ltk to investigate their function in the nervous system and describe defects in cortical development and behavioral deficits. The defects in the formation of cortical layers suggest a delay in radial migration. In culture, 40% of cortical neurons from knockout embryos extend multiple axons. The mechanism responsible for this phenotype is explored in some detail. The authors conclude that Alk and Ltk function non-redundantly to regulate the Igf-1 receptor (Igf-1r). Inactivation of Alk or Ltk increases surface expression and activity of Igf-1r, which induces the formation of multiple axons. The authors propose that Alk and Ltk interact with Igf-1r and promote its endocytosis after activation by their ligand Alkal2, thereby preventing the formation of additional axons. However, the defects in neurogenesis, migration and behavior may have a different cause and should not be attributed only to Igf-1r.
We would like to thank the reviewer for all the insightful comments and suggestions which we feel have strengthened our study.
We appreciate the reviewer’s acknowledgement that we have shown that Igf-1r is in involved in Alk/Ltk-mediated regulation of axon outgrowth. To provide evidence that Igf-1r is also important for Ltk/Alk regulated migration in vivo, we explored the effect of the Igf-1r inhibitor, PPP on the migration of neurons in WT and DKO mice by BrdU labelling. Excitingly, this analysis revealed that PPP administration resulted in a partial rescue of the migration defect in Ltk/Alk DKO mice, with BrdU+ neurons being localized to the most superficial layers in P2 mice (Fig. 6F). Thus, these data are consistent with our model that loss of Ltk/Alk can disrupt both neuronal polarity and migration via IGF-1r. We do agree with the reviewer that we have not directly shown that the behavioural defects can be attributed to Igf-1r and it is certainly possible that other pathways or mechanisms may be involved in the complex phenotype. We have updated the manuscript and discuss the potential involvement of other pathways in the discussion.
Major comments<br /> 1) The role of Alk/Ltk in suppressing the formation of multiple axons is demonstrated by culturing neurons from knockout mice, suppression with siRNAs and treatment with inhibitors. These experiments consistently show that about 40% of cultured neurons extend more than one axon when Alk, Ltk or both are inactivated. Single and double knockout mice are largely normal with the exception of a delay in the formation of distinct cortical layers. The phenotypes of the knockout lines indicate a function in cortical development but Alk and Ltk are not "indispensable" as suggested (p. 18)._
We will modify the wording to remove the statement that Alk and Ltk are “indispensable” for cortical patterning and rather will indicate that the receptors ‘contribute’ to the timing of cortical patterning.
The morphology of cortical neurons was analyzed by Golgi staining. A few potential axons (Fig. 3E) were identified only by an absence of dendritic spines and their aberrant trajectory. These results indicate that there are ectopic extensions in the cortex but do not demonstrate that neurons extend multiple axons also in vivo. It has to be confirmed that these extensions are positive for axon-specific markers and that several axons originate from one soma to demonstrate a multiple axon phenotype in vivo. A quantification of the number of neurons with multiple axons would be required to conclude that this phenotype occurs at a similar frequency in vivo.
As indicated in response to reviewer #1, we attempted to quantitate the Golgi stained images but found it impossible to trace individual neurites to the cell body and thus could not unambiguously identify and quantitate axons. Accordingly, and as suggested by the reviewer, we have modified our conclusion to simply state there are aberrant extensions in the cortex in vivo. Although we were unable to do quantitation, to further support our conclusions, we have provided additional Golgi stained images of WT and DKO mice from an independent experiment (Fig. S3B).
2) According to the model presented in Fig. 7, Alkal2 activates Alk and Ltk, which stimulate the endocytosis of Igf-1r and thereby prevents the formation of additional axons. A quantification of Igf-1r surface levels by the biotinylation of surface proteins and Western blot shows an increase in knockout neurons. The authors suggest that Alk/Ltk activation stimulates Igf-1r endocytosis but do not demonstrate this directly. An increase in surface expression could also result from a stimulation of exocytosis or recycling.
We showed that ligand-induced activation of Ltk/Alk in WT neurons resulted in a loss of biotin-labelled cell-surface Igf-1r, which is strongly indicative of increased internalization and cannot be explained by exocytosis. However, the reviewer is correct, that we cannot exclude the possibility that changes in exocytosis or recycling might also occur and that in the unstimulated DKO neurons, the increase in surface expression of Igf-1r could also result from a stimulation of exocytosis or recycling. Indeed, several papers (Laurino et al, 2005, PMID: 16046480; Oksdath et al, 2017, PMID: 27699600; Quiroga et al, 2018, PMID: 29090510) have reported that exocytosis mediated transport of IGF-1R and activation of IGF-1R/PI3K pathway is essential for the regulation of membrane expansion during axon formation. Accordingly, we have modified the discussion text to incorporate this possibility.
3) The localization of Alk, Ltk and Alkal2 was determined by in situ hybridization. The signals are weak and it is not clear if they are specific because a negative control is missing. An analysis by immunofluorescence staining would be more informative.
RNAscope is designed so that a single molecule of RNA is visualized as a punctuate signal dot with high specificity. In lower magnification images, such as those we showed to provide an overall view of expression in the cortex, it is difficult to discern the individual ‘dots’, particularly for genes with low expression, giving the impression that the signal is weak. However, at high magnification (63X) the signals are readily visible as seen in a new panel in Fig. S1B). We also neglected to mention that positive probes with all 3 labels (POLR2A: Channel C1, PPIB: Channel C2, UBC:Channel C3) as well as a negative probe (Bacterial dap gene) supplied by the manufacturer were used on our samples to validate specificity. We have corrected the oversight and have now added this information to the methods section.
Regarding immunofluorescence, we have rigorously tested numerous commercially-available antibodies and have undertaken repeated attempts to produce our own antibodies that recognize mouse Ltk or Alk, and are appropriate for immunofluorescence, but have had no success. The high specificity enabled by the RNAscope technology is thus currently the most reliable way we can examine expression, with the added advantage that we can simultaneously assess expression of both receptors and the ligand in an individual cell within a section.
Alk appears to be expressed mainly in the ventricular zone (VZ) while Ltk shows a low expression in the SVZ and the cortical plate (CP). This expression pattern is not consistent with a function in regulating axon formation in multipolar neurons, which extend axons in the lower intermediate zone (IZ) (Namba et al., Neuron 2014) and not in the VZ or SVZ (p. 18).
It is well described that multipolar neurons can be found in the SVZ, while bipolar neurons are preferentially in the IZ. Neurons expressing Ltk, Alk and their ligand, Alkal2 can be found in both compartments (albeit levels appear higher in the SVZ), thus we feel our results are consistent with a role for the receptors in regulating neuronal polarization.
It is also essential to analyze the subcellular localization of Alk and Ltk at least in cultured neurons. Ltk has been reported as an ER-resident protein that regulates the export from the ER (Centonze et al., 2019), which would not be consistent with the model.
Unfortunately, the lack of antibodies with mouse reactivity prevents us from analyzing the subcellular localization of Alk and Ltk in cultured neurons. As mentioned by the reviewer, LTK has been reported as an ER-resident protein (in cancer cells) and similarly, many other tyrosine kinase receptors including IGF1R, have been reported to be localized to diverse intracellular compartments like Golgi, nucleus or mitochondria (reviewed in Rieger and O’Connor, 2021, Front Endocrinol:PMID: 33584548). However, since extracellular ligands for LTK and ALK are known, we feel it is a reasonable expectation that they will have a role as cell-surface receptors. Understanding the functions of RTK receptors and the interplay between the various compartments would nevertheless be an interesting area for future research.
4) The results convincingly show that an increased activity of Igf-1r is responsible for the formation of additional axons by cultured knockout neurons. The model in Fig. 7 explains how Alk/Ltk suppress the formation of multiple axons in culture but a key question remains to be addressed: why does Igf-1r remain active in the future axon? Are Alk/Ltk restricted to or selectively activated in dendrites? It is important to determine if Alk and Ltk are absent from the future axon before or after neuronal polarity is established.
We thank the reviewer for acknowledging that we have provided convincing data that increased activity of Igf-1r is responsible for the formation of multiple axons. Addressing why Igf-1r remains active in the future axon and if and how Ltk/Alk are selectively activated in dendrites and axons are all excellent questions, which we plan to pursue in future work, particularly when antibodies for Alk and Ltk become available.
Which cells produce Alkal2 in neuronal cultures and in vivo?_ _These points can be easily addressed and should be investigated.
We have confirmed that Alkal2 is expressed in the isolated cortical neurons, consistent with our demonstration that siRNA-mediated abrogation of Alkal2 expression in cultured neurons regulates polarity and that ligand levels do not change in Ltk/Alk double knock out mice (Fig. S1G and S6A). Whether other non-neuronal cell types also express Alkal2 would be an interesting future direction.
Why does an increase of Igf-1r surface expression in knockout neurons result in a stimulation of Igf-1r autophosphorylation? Neurons are cultured in a defined medium without Igf-1 and increased surface levels by themselves should not lead to an increased activity.
We have not mechanistically determined why/how Igf-1r displays enhanced autophosphorylation in DKO neurons. Thus, we can only speculate about possibilities. Perhaps there are low levels of Igf-1 in the cortical cell extracts, or is produced by the cortical neurons; there may be compensatory mechanisms engaged when Ltk/Alk are lost to ensure neuronal survival, or perhaps the increase in cell-surface Igf-1r promotes ligand-independent activation of receptors in the absence of ligand.
The results presented in this manuscript are consistent with a role of Igf-1r in the formation of multiple axons in the absence of Alk/Ltk. However, inhibition of Igf-1r by various means does not prevent axon formation in controls. Igf-1 has been implicated in axon formation (Sosa at al., 2006) but a knockout of Igf-1r does not result in a loss of axons but a reduction of axon length in cultured neurons (Jin et al., PLoS One 2019). Axon-specific markers are used only for some experiments but not in Figs. 3D, 5B-D and 6 where the neuronal marker Tuj1 does not allow the unambiguous identification of axons. Staining with an axonal marker and a quantification of axon length are required to distinguish between a block in axon formation and a reduction in axon growth in Figs. 3A, 5 and 6.
In the original submission we quantitated Tau-1 and MAP2 co-stained neurons in many experiments to demonstrate that Ltk/Alk act on axons, but in some cases we used Tuj1 to more easily visualize and quantitate neurites. Nevertheless, as requested by the reviewers, in the revised manuscript we have repeated and replaced most of the results with Tuj1 or phalloidin staining with experiments using Tau-1 and MAP2 antibodies, including Fig. 5B-D and Fig. 6A-D and G, as well as for Fig. S4B requested by reviewer #1). The new data is consistent with our results using Tuj1 staining and further support our conclusions that Ltk/Alk act via Igf1-r to regulate neuronal polarity. With regards to Fig. 3D, we have been experiencing ongoing technical issues in generating human stem cell derived cortical neurons and have been unable to undertake Tau1/MAP2 staining of the human cortical neurons. Given that the point being made is minor, we have removed this panel from the paper.
With regards to the comment on that inhibition of Igf1-r did not prevent basal axon formation: in our prior quantitation of WT neurons in which Igf1-r was inhibited using either siIgf1-r or PPP, we noticed a trend towards an increase in the number of neurons with no axons, but this was not statistically significant. Upon the repeat of experiments and re-quantitation with Tau-1/MAP2 co-staining, we do see a statistically-significant increase in the number of WT neurons without axons. This is in agreement with several prior studies (including one cited by the reviewer) indicating Igf1-r is important for neuronal polarity (Sosa, 2006; PMID:16845384, Neito Guil 2017 PMID:28794445). The text has been modified accordingly.
5) The analysis with layer specific markers and BrdU labeling reveals defects in the formation of cortical layers that suggest a delay in neuronal migration. The number of Sox2+ and Tbr2+ cells is lower in knockout neurons indicating a possible reduction in the number of proliferating progenitors and a defect in neurogenesis (Fig. 1). The number of neurons positive for layer-specific markers or BrdU was quantified as the percent of DAPI-positive cells. This does not allow distinguishing between a change in the distribution and a reduction in the number of neurons due to defects in neurogenesis. It would be more informative to quantify the total number Ctip+, Satb2+ or BrdU+ cells in the VZ, SVZ, IZ and CP._
In the in vivo BrdU labelling experiment, we did not co-stain sections with DAPI. However, in the immunofluorescence analysis in mice of the same ages, we did determine the total number of cells (ie by DAPI) that is shown in the plots in Fig. 1A and Fig. S2A/B. These results show that there are a similar number of cells in WT and mutant SVZ/VZ, consistent with the notion that there is a change in distribution rather than in reduction in the number of neurons due to defective neurogenesis. We neglected to mention this important point in the results and have now modified the text accordingly.
6) The deficits observed in behavioral tests do not correlate with the defects in neuronal development. While the single knockouts show defects in cortical development only the double knockout displays behavioral deficits. The behavioral phenotype could be completely independent of Igf-1r. Alk has been implicated in regulating retrograde transport (Fellows et al., EMBO Rep. 2020) and synaptic scaling (Zhou et al., Cell Rep. 2021). Since there is no clear correlation between structural and behavioral changes these data are not obviously linked to the other results.
The reviewer is correct, that the single KO mice do not manifest noticeable behavioural defects except when older and challenged with the most demanding task, the Puzzle box, which measures complex executive functions. We speculate that alternative cortical re-wiring in the single knockouts is sufficient to maintain normal circuitry that cannot be compensated when both Ltk and Alk receptors are deleted. However, we do agree that Ltk/Alk regulated signalling events, besides Igf-1r/PI3K could contribute to the behavioural defects observed in the DKO mice, such as the ALK-LIMK-cofilin pathway which regulates synaptic scaling as cited by the reviewer (Zhou et al., Cell Rep. 2021). Nevertheless, the strong phenotype of the DKOs confirms that Ltk/Alk are important for proper brain function, thus our preference is to retain the behavioural data in the manuscript but to discuss that alternative Ltk/Alk pathways could contribute to the phenotype (which we have now incorporated into the text).
It should be noted that the study by Fellows et al in EMBO Rep 2020 shows Igf1-r, not ALK regulates retrograde transport so we have not included this study in the updated text.
Minor comments
1) Fig. 3 shows defects in the corpus callosum where axons are restricted to the upper half in the wild type but not the knockout. These results could indicate a guidance defect but do not show a "failure in axon migration through the corpus callosum" (p. 17). It is also not demonstrated "that the aberrant axon tracts may be the result of effects on neuronal morphology" (p. 19). Without additional experiments to trace axonal projections e.g. by DiI labeling it is not possible to determine the actual cause for the observation shown in Fig. 3F._
We agree with the reviewer and have modified the concluding sentence so that the defects are described without attributing the cause to the defects on neuronal morphology.
2) Active kinases from SignalChem are used for the in vitro kinase assays. The increased phosphorylation of Igf-1r could also result from a stimulation of auto-phosphorylation and not a direct phosphorylation by Ltk. Previous results indicate that phosphorylation of Y1250/1251 leads to increased internalization and degradation (Rieger et al., Sci. Signal. 2020), which would be an alternative explanation how Alk/Ltk regulate surface expression. Antibodies that are specific for Igf-1r phosphorylation at Y1135/1136 or Y1250/1251 could address this possibility (Rieger at al., Sci. Signal. 2020).
It is rather surprising that for the Igf-1r, which is such a well-studied receptor, the mechanisms that regulate trafficking, exocytosis recycling, etc are so poorly understood and that this topic is currently an active area of investigation. The focus of our study was on understanding the role of Ltk/Alk in the brain and as part of this effort we demonstrated that Ltk/Alk can control neuronal polarity through Igf-1r phosphorylation. We believe that shedding light on the detailed mechanism of how enhanced Igf-1r phosphorylation induced by Ltk/Alk activation regulates Igf-1r trafficking is an exciting project for future work, but we feel that to thoroughly investigate this question is beyond the scope of the current study. We have, nevertheless, highlighted these points with additional references in the discussion.
3) The specificity of the siRNAs has to be verified in neurons by rescue experiments and the suppression of the targeted proteins confirmed by immunofluorescence staining.
We agree that rescue experiments are the gold standard, and we attempted to do this. However, we found that nucleofection of both siRNAs and cDNAs encoding either EGFP alone or Ltk/Alk was highly toxic to neurons with few surviving the treatment. As an alternative we used a pool of siRNAs, to minimize off-target effects and used genetic KOs or chemical inhibitors to verify the observations.
4) The position of molecular weight markers is missing for most Western blots.
We added the position of molecular weight markers for all the western blots in the revised manuscript.
5) It is not indicated which conditions show a significant difference in Fig. 6.
We thank the reviewer for pointing this out. We added the significant differences to all figures, including Fig. 6.
6) Why does the Western blot in Fig. 7A show a double band with the anti-phospho-Igf-1r antibody in the knockout? Which of the bands was used for the quantification?
We apologize for a labelling error that has caused confusion for both reviewers. We have replaced the blots and corrected the labels.
7) Details of the plasmids used and information (catalog number) for recombinant GST-Ltk and His-Igf-1r should be included in Materials and Methods.
The additional information and catalog numbers have been added to the Materials and Methods.
Reviewer #2 (Significance):
The receptor tyrosine kinase Alk has been studied mainly for its involvement in several types of cancer but the physiological functions of Alk and its close relative Ltk remain poorly understood. The regulation of Igf-1r is an interesting and important result to understand the physiological function of Alk and Ltk. However, several points have to be addressed before the manuscript would be suitable for publication.
We thank the reviewer for indicating that this is interesting and important study. We trust that the additional data and clarifications provided, have addressed the reviewers concerns.
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Referee #2
Evidence, reproducibility and clarity
Christova et al. analyzed single and double knockout mice for Alk and Ltk to investigate their function in the nervous system and describe defects in cortical development and behavioral deficits. The defects in the formation of cortical layers suggest a delay in radial migration. In culture, 40% of cortical neurons from knockout embryos extend multiple axons. The mechanism responsible for this phenotype is explored in some detail. The authors conclude that Alk and Ltk function non-redundantly to regulate the Igf-1 receptor (Igf-1r). Inactivation of Alk or Ltk increases surface expression and activity of Igf-1r, which induces the formation of multiple axons. The authors propose that Alk and Ltk interact with Igf-1r and promote its endocytosis after activation by their ligand Alkal2, thereby preventing the formation of additional axons. However, the defects in neurogenesis, migration and behavior may have a different cause and should not be attributed only to Igf-1r.
Major comments
- The role of Alk/Ltk in suppressing the formation of multiple axons is demonstrated by culturing neurons from knockout mice, suppression with siRNAs and treatment with inhibitors. These experiments consistently show that about 40% of cultured neurons extend more than one axon when Alk, Ltk or both are inactivated. Single and double knockout mice are largely normal with the exception of a delay in the formation of distinct cortical layers. The phenotypes of the knockout lines indicate a function in cortical development but Alk and Ltk are not "indispensable" as suggested (p. 18). The morphology of cortical neurons was analyzed by Golgi staining. A few potential axons (Fig. 3E) were identified only by an absence of dendritic spines and their aberrant trajectory. These results indicate that there are ectopic extensions in the cortex but do not demonstrate that neurons extend multiple axons also in vivo. It has to be confirmed that these extensions are positive for axon-specific markers and that several axons originate from one soma to demonstrate a multiple axon phenotype in vivo. A quantification of the number of neurons with multiple axons would be required to conclude that this phenotype occurs at a similar frequency in vivo.
- According to the model presented in Fig. 7, Alkal2 activates Alk and Ltk, which stimulate the endocytosis of Igf-1r and thereby prevents the formation of additional axons. A quantification of Igf-1r surface levels by the biotinylation of surface proteins and Western blot shows an increase in knockout neurons. The authors suggest that Alk/Ltk activation stimulates Igf-1r endocytosis but do not demonstrate this directly. An increase in surface expression could also result from a stimulation of exocytosis or recycling.
- The localization of Alk, Ltk and Alkal2 was determined by in situ hybridization. The signals are weak and it is not clear if they are specific because a negative control is missing. An analysis by immunofluorescence staining would be more informative. Alk appears to be expressed mainly in the ventricular zone (VZ) while Ltk shows a low expression in the SVZ and the cortical plate (CP). This expression pattern is not consistent with a function in regulating axon formation in multipolar neurons, which extend axons in the lower intermediate zone (IZ) (Namba et al., Neuron 2014) and not in the VZ or SVZ (p. 18).<br /> It is also essential to analyze the subcellular localization of Alk and Ltk at least in cultured neurons. Ltk has been reported as an ER-resident protein that regulates the export from the ER (Centonze et al., 2019), which would not be consistent with the model.
- The results convincingly show that an increased activity of Igf-1r is responsible for the formation of additional axons by cultured knockout neurons. The model in Fig. 7 explains how Alk/Ltk suppress the formation of multiple axons in culture but a key question remains to be addressed: why does Igf-1r remain active in the future axon? Are Alk/Ltk restricted to or selectively activated in dendrites? Which cells produce Alkal2 in neuronal cultures and in vivo? These points can be easily addressed and should be investigated. It is important to determine if Alk and Ltk are absent from the future axon before or after neuronal polarity is established. Why does an increase of Igf-1r surface expression in knockout neurons result in a stimulation of Igf-1r autophosphorylation? Neurons are cultured in a defined medium without Igf-1 and increased surface levels by themselves should not lead to an increased activity.<br /> The results presented in this manuscript are consistent with a role of Igf-1r in the formation of multiple axons in the absence of Alk/Ltk. However, inhibition of Igf-1r by various means does not prevent axon formation in controls. Igf-1 has been implicated in axon formation (Sosa at al., 2006) but a knockout of Igf-1r does not result in a loss of axons but a reduction of axon length in cultured neurons (Jin et al., PLoS One 2019). Axon-specific markers are used only for some experiments but not in Figs. 3D, 5B-D and 6 where the neuronal marker Tuj1 does not allow the unambiguous identification of axons. Staining with an axonal marker and a quantification of axon length are required to distinguish between a block in axon formation and a reduction in axon growth in Figs. 3A, 5 and 6.
- The analysis with layer specific markers and BrdU labeling reveals defects in the formation of cortical layers that suggest a delay in neuronal migration. The number of Sox2+ and Tbr2+ cells is lower in knockout neurons indicating a possible reduction in the number of proliferating progenitors and a defect in neurogenesis (Fig. 1). The number of neurons positive for layer-specific markers or BrdU was quantified as the percent of DAPI-positive cells. This does not allow distinguishing between a change in the distribution and a reduction in the number of neurons due to defects in neurogenesis. It would be more informative to quantify the total number Ctip+, Satb2+ or BrdU+ cells in the VZ, SVZ, IZ and CP.
- The deficits observed in behavioral tests do not correlate with the defects in neuronal development. While the single knockouts show defects in cortical development only the double knockout displays behavioral deficits. The behavioral phenotype could be completely independent of Igf-1r. Alk has been implicated in regulating retrograde transport (Fellows et al., EMBO Rep. 2020) and synaptic scaling (Zhou et al., Cell Rep. 2021). Since there is no clear correlation between structural and behavioral changes these data are not obviously linked to the other results.
Minor comments
- Fig. 3 shows defects in the corpus callosum where axons are restricted to the upper half in the wild type but not the knockout. These results could indicate a guidance defect but do not show a "failure in axon migration through the corpus callosum" (p. 17). It is also not demonstrated "that the aberrant axon tracts may be the result of effects on neuronal morphology" (p. 19). Without additional experiments to trace axonal projections e.g. by DiI labeling it is not possible to determine the actual cause for the observation shown in Fig. 3F.
- Active kinases from SignalChem are used for the in vitro kinase assays. The increased phosphorylation of Igf-1r could also result from a stimulation of auto-phosphorylation and not a direct phosphorylation by Ltk. Previous results indicate that phosphorylation of Y1250/1251 leads to increased internalization and degradation (Rieger et al., Sci. Signal. 2020), which would be an alternative explanation how Alk/Ltk regulate surface expression. Antibodies that are specific for Igf-1r phosphorylation at Y1135/1136 or Y1250/1251 could address this possibility (Rieger at al., Sci. Signal. 2020).
- The specificity of the siRNAs has to be verified in neurons by rescue experiments and the suppression of the targeted proteins confirmed by immunofluorescence staining.
- The position of molecular weight markers is missing for most Western blots.
- It is not indicated which conditions show a significant difference in Fig. 6.
- Why does the Western blot in Fig. 7A show a double band with the anti-phospho-Igf-1r antibody in the knockout? Which of the bands was used for the quantification?
- Details of the plasmids used and information (catalog number) for recombinant GST-Ltk and His-Igf-1r should be included in Materials and Methods.
Significance
The receptor tyrosine kinase Alk has been studied mainly for its involvement in several types of cancer but the physiological functions of Alk and its close relative Ltk remain poorly understood. The regulation of Igf-1r is an interesting and important result to understand the physiological function of Alk and Ltk. However, several points have to be addressed before the manuscript would be suitable for publication.
-
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Referee #1
Evidence, reproducibility and clarity
This manuscript describes studies that indicate roles for the ALK and LTK receptors in neuronal polarity, cortical patterning and behavior in mice. I really liked the study and overall think that it deserves publication in a high-ranking journal. It reports important and novel results and benefits from a comprehensive analysis at multiple levels, including cell biological, biochemical and behavior. The points raised below are suggestions for consideration at the discretion of the authors.
- The term "DKO" appears in the Introduction without explanation. I assume this means double KO mice lacking both receptors from birth. It should be indicated here, just in case.
- The last paragraph of the Introduction is redundant with the Abstract. This is a stylistic question, which is up to the authors. Nevertheless, as a suggestion, they could take the opportunity here to explain the rationale of the study and why they did what they did.
- Is "single cell in situ mRNA analysis" standard in situ hybridization or something else? Why is it called "single-cell"? It could be misleading.
- In Fig. S1B, could the authors please include expression patterns of LTK in adult brain? It'd seem that is the most relevant place to look given the analysis that follows in the paper.
- I have an issue in general in the first part of the manuscript with regards to the labeling of cortical layers. How were CP, IZ and SVZ/VZ defined? Specific markers should be used to identify their actual boundaries. Guesswork from the DAPI pattern (if that is what was used) is not really appropriate.
- Comparing Fig. 1 and Fig. S2, there would seem to be little or no additive nor synergistic effects of the double mutation, as the phenotype in the DKO appears to be completely attributable to the Ltk KO. What does this mean? Providing the expression patterns of the two receptors at the ages used here (i.e., P2 and P7) would also be helpful.
- In Fig. 1F, again, how were the boundaries between the cortical areas (dotted lines) determined? This is particularly important for the mutant sections, as apparent cortical thickness would be easily be affected by the plane of the section. Simply assuming that the CP is of equal thickness than the one in the WT may be incorrect. I feel the authors cannot just place dotted lines in the figure without explaining the criteria that was used to determine their location. Also, there is a significant (many fold) increase in Ctip2 cells in the IZb of the mutant (1F) that it's not explained in the text. The quantification of Ctip2 cells in the CP and IZa of the mutant is missing in the histogram. It should be indicated, even if very low. Again, the key point here is the criteria used for the<br /> boundaries between areas. May be what it's marked as IZa in the mutant is still part of the CP, in which case the number of Ctip2 cells would be increased there, not decreased, as claimed in the text.
- In Fig. S3C-F, the all-critical quantification of Ctip2 cells at P2 seems to be missing in this figure. It would important to provide this in light of the comments above. Again, the same problem with the layer boundaries is clear here. The Ltk KO would have normal levels of Ctip2 cells if the CP thickness were to be larger (due to e.g., the plane of the section not being perfectly perpendicular to the brain surface).
- In Figure 2A and B, % positive cells is plotted but we are not told what is the reference (100%) level. Was it the total number of cells in the entire cortex (including SVZ and VZ)? That cannot be the case, since CP+IZ in WT alone reaches almost 100%. What is 100% here please? Also, the idea of drawing a little rectangle in the IZ and CP and counting only there is flawed. The values would change drastically depending on where the rectangle is placed. They need to count the whole field of view, as it was done in the previous figures. Finally, again, we are not told how the boundaries of the different cortex areas were established. As explained earlier, distance from the surface (or from<br /> the bottom) of the cortex would be greatly affected by the plane of the section. This problem will need a more satisfying solution for the data to be interpreted in the way it has been done.
- At the end of page 8, it is concluded that Alk/Ltk promote neuronal migration. Is this a cell-autonomous effect? Given the very sparse expression of these receptors (Fig S1), cell-autonomy (which is being implied by the authors) is not at all clear. Is the migration of Alk+ cells affected in the Ltk mutant? Vice-versa?
- In Fig. S4A, as every cell in these panels bears probe signal, it'd be important to present a negative control, perhaps from KO cultures or wild type cells lacking receptor expression in the same field as expressing cells. At a 75%, 1 in 4 cells in any field should be receptor-negative.
- Figure S4B is difficult to interpret in the absence of Tau and MAP2 markers, as GFP does not discriminate between axons and dendrites. In general, the authors are recommended to show more than one cell per condition in their figures. Readers need to be convinced that these are robust phenotypes easily observed on many cells in the same field.
- In Fig. S4C and D, do the KO neurons become bipolar? I don't see examples of multipolar neurons in the images provided.
- Is there a way to quantify the effects shown in Fig. 3E?
- The DKO display a dramatically different behavior phenotype compared to single Kos. How can this result be explained given that DKOs are indistinguishable from single KOs in all other parameters studied?
- At the end of the behavior section, the authors attribute the phenotypes observed to defects in neuronal polarization. Given that polarization was only studied in vitro, it may be a premature to conclude that neurons fail to polarize in vivo in the absence of direct evidence showing this.
- Regarding P-AKT studies, it would be interesting to assess the effects of the ALK7LTK ligands (e.g., from conditioned medium) on the levels of P-AKT in WT neurons.
- In the mid part of page 14, the sentence "Treatment of WT cortical neurons with AG1024 at a dose (1 μM) at which only IGF-1R but not InsR was inhibited restored the single axon phenotype in DKO neurons" is confusing. Treatment performed in WT neurons but assessed in DKO neurons? This must be a typo.
- For completion, it would be informative to test whether IGF-1 antagonizes the effects of ALK and LTK ligands in axon formation.
- The quality of the blot provided to illustrate levels of activated Igf-1r in Fig. 7A is clearly suboptimal. It is not apparent from that blot that phosphorylation of Igf1r is increased in the mutant neurons as the band intensities are indistinguishable. Was this performed in cortex extracts or cultured neurons? Is it affected by treatment with ALK/LTK ligands?
- Given the physical interaction between ALK/LTK and IGF-R1, these receptors are presumably co-internalized upon ligand treatment, or? Does treatment with IGF1 induces internalization of ALK or LTK?
- The last paragraph in the Results section may be more appropriate for Discussion to avoid repetition. But it is of course up to the authors to decide on stylistic issues.
- There is a discussion of possible redundancies between ALK and LTK in the Discussion section which appears to contradict itself. It is first stated (end of p. 18) that the two receptors are not redundant but both required for function. But in p. 19, the significant behavioral phenotypes observed in DKO mice, but not in single KO mice, are attributed to redundancy and compensation between the receptors. This needs some clarification. It's difficult to understand how there can be redundancy for behavior but not for structure or function.
Significance
see above
-
-
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-
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
The manuscript from Li et al. describes the authors' attempt to redirect the exocytic Rab Sec4 to endocytic vesicles by fusing the GEF-domain of Sec2 to the CUE domain of the endosomal GEF Vps9, which binds to ubiquitin. The authors show that the localization of the Sec2GEF-GFP-CUE construct is slightly shifted from polarized towards non-polarized sites. Sec2GFP-CUE positive structures acquire Sec4 and Sec4 effectors like exocytic vesicles but are less motile and show delayed plasma membrane fusion. Expression of Sec2GEF-GFP-CUE was enhanced if expressed in a subset of secretory and endocytic mutants and cause delayed Mup1 uptake from the plasma membrane. As Vps9, Sec2GEF-GFP-CUE accumulated on Class E compartments in vps4Δ strains.<br /> The authors ask here whether vesicular identity is largely predetermined by the correct localization of the specific GEFs of small GTPases and thus localization of the Rab. Although this an interesting hypothesis, the authors observed that endocytic traffic was not reversed by relocating Sec4 to these vesicles. This seems to be due to the strong affinity of the Sec2 GEF-domain for Sec4 but probably also due to the rather weak relocalization via the CUE domain. Thus, only a portion of Sec2 was displaced from its native site. Since the efficiency of this rewiring was not defined, it remains unclear whether the observed mild effects indeed speak against the assumed dominant role of the GEFs and small GTPases in shaping organelle identity or whether they are rather due to an inefficient relocalization.
Our data demonstrate a dramatic relocalization of Sec2-GEF-GFP-CUE relative to Sec2-GEF-GFP. In the case of Sec2-GEF-GFP or Sec2-GEF-GFP-CUE M419D the cytoplasmic pool is predominant and only 30% of cells exhibit a detectable concentration, while in the case of Sec2-GEF-GFP-CUE 80% of cells show bright puncta and there is little or no detectable cytoplasmic pool (Fig 1A). Clearly the CUE domain can function as a localization domain that relies upon ubiquitin binding. Furthermore, half of the Sec2-GEF-GFP-CUE puncta colocalize with Vps9 (Fig S1). The high cytoplasmic background of Vps9 could mask additional colocalization, therefore we reexamined colocalization in a vps4__D_ _mutant in which the Vps9 cytoplasmic pool is reduced due to increased association with the expanded Class E late endosomes. In this situation we observe about 80% colocalization with Vps9 as well as substantial colocalization with Ypt51 and Vps8 (Fig 2). We now also show significant colocalization with PI(3)P (Fig S3D). Thus, our data demonstrate that addition of the CUE domain does indeed relocalize Sec2GEF to endocytic membranes. The Sec2 GEF activity then leads to the recruitment of Sec4 and Sec4 effectors, including Myo2 which in turn leads to their delivery to polarized sites. We now show by EM that the bright Sec2-GEF-GFP-CUE puncta correlate with clusters of 80 nm vesicles (Fig 5B). Our data argues that these are hybrid compartments carrying both endocytic and exocytic markers. We have restructured our paper to help clarify and emphasize this key point.
Specific comments:<br /> 1. The authors state decidedly that the recruitment of Vps9 occurs ubiquitin-dependent via the CUE-domain. While the CUE-domain is the only known and a likely localization determinant of Vps9, it was not a strong localization determinant. Apart from being present in some puncta, Vps9 localized strongly to the cytosol (Paulsel et al. 2013, Nagano et al. 2019). Shideler et al. also showed that ubiquitin-binding is not required for Vps9 function in vivo, which indicates that other localizing mechanisms may play a role e. g. by positive feedback of GEF-domain-Rab5 interactions which might be initiated by the other Rab5-GEF Muk1 or as suggested by transport from the Golgi (Nagano et al. 2019). These observations indicate that the CUE-domain is a rather weak recruitment domain, which was not discussed in this manuscript. The localization of the Sec2GEF-GFP-control to the polarized sites in 30% of the cells furthermore suggests that the used Sec2GEF-GFP-CUE retains some native localization via the GEF-domain. Since the relocation efficiency of Sec2GEF-GFP-CUE was not defined, the obtained phenotypic effects allow for only vague conclusions. Although the mild endo- and exocytosis defects as well as the accumulation of Sec2GEF-GFP-CUE at Class E compartments indicate that the CUE-domain indeed conferred some relocation to endosomes, this was not shown for the sec2Δ strain e. g. by looking at colocalizations with endocytic versus exocytic markers and comparing their relative abundance at the Sec2GEF-GFP-CUE-positive structures. While some of the Sec2GEF-GFP-CUE-positive structures colocalized with Mup1 in the Mup1-uptake assay, it would be important to clarify how many endosomal properties are retained and how many exocytic properties are gained by these chimeric vesicles e. g. by looking for the presence of specific phosphoinositides, or Rab5 and Rab5 effectors. A competition between endosomal and the acquired exocytic factors could also be another possible explanation for the immobility of the Sec2GEF-GFP-CUE structures and less efficient recruitment of Sec4 effectors in addition to the proposed lack of PI4P.
As summarized above, we observed dramatic relocalization of Sec2GEF that was strongly dependent upon the ability of the CUE domain to bind to ubiquitin. We also observed colocalization with Ypt51 and Vps8 as well as transient colocalization with internalized Mup1. We now also show significant colocalization with PI(3)P (Fig S3D). Full length Vps9 is probably subject to additional levels of regulation, perhaps autoinhibitory in nature, however our construct contains only the CUE domain which can clearly function as an efficient localization domain on its own. The high cytoplasmic pool of Vps9 reflects the rapid turnover of its ubiquitin binding sites, since it is efficiently recruited to membranes in vps4__D_ cells. The relocalized Sec2GEF domain was quite effective in recruiting Sec4 as well as most known Sec4 effectors. The recruitment of Myo2 leads to localization to sites of polarized growth. All of our studies were done in a sec2__D _background except for the analysis of dominant growth effects, as now explicitly stated at the beginning of the Results section.
- While the colocalization of the Sec2GEF-GFP-CUE-signal with Sec4 indicates that this GEF-construct is generally active, it remains unclear whether the activity of the tagged constructs differ from that of the wild type Sec2 protein. This could be analyzed in vitro via a MANT-GDP GEF-activity assay (Nordmann et al., 2010). Again, it remains unclear how much of the Sec2GEF-Sec4 colocalization represents the retained native localization versus synthetic localization at chimeric endo-exocytic vesicles.
The structure and nucleotide exchange mechanism of the Sec2 GEF domain have been thoroughly analyzed in prior studies and are well understood. There is no reason to think that the constructs we generated here would alter the exchange activity as the fusions are far removed from the Sec4 binding site and our analysis here confirms that they are active in vivo. We do not feel that there would be much to be gained by doing in vitro exchange assays and it would entail a great deal of work.
- The authors mention that tagging with GFP increases the stability of the expressed constructs. However, it remains unclear whether this is also the case for the other tags (NeonGreen, mCherry) used in the other experiments. Are the constructs expressed at similar levels?
We have compared the levels of the various tagged constructs and they appear to be similar (Fig S5A).
- In Figure 5: The incomplete colocalization of Sec2GEF-GFP-CUE with Vps9 is explained by the short-timed accessibility of ubiquitin moieties. Apart from the likely retained native localization or weak CUE-domain-function, this observation could also be due to competition between Vps9 and Sec2GEF-GFP-CUE for the available ubiquitin target structures.
As previously shown, Vps9 normally displays a prominent cytoplasmic pool. Deletion of Vps4 leads to recruitment of this pool to expanded endosomes through an increase in the lifetime of the ubiquitin binding sites. The high cytoplasmic background in VPS4 cells could obscure some colocalization with Sec2GEF-GFP-CUE and indeed we observe increased colocalization in vps4__D_ _cells in which the cytoplasmic pool of Vps9 has been recruited to endosomes. Expression of Sec2GEF-GFP-CUE does not appear to significantly alter the localization of Vps9.
Minor remarks:<br /> 1. Fig. 3C do not contain the arrowheads as indicated in the legend, making it harder to interpret.
These have been added.
- The image chosen for Sec2-GFP in Fig. 4B suggests less colocalization between Sec2-GFP and Sec8 than between Sec2GEF-GFP-CUE and Sec8. They rather look next to each other.
The images initially chosen were not representative. We have replaced them with better images from the same experiment.
- Figure 5: While resolution limits are possibly reached regarding endosomes, it might be interesting to check by thin section electron microscopy whether and how class E compartment formation is affected by Sec2GEF-GFP-CUE expression.
We have now done EM using permanganate fixation of both VPS4 and vps4__D_ cells (Fig 5B and below). In both backgrounds Sec2GEF-GFP-CUE expression leads to the formation of clusters of 80 nm vesicles that appear to correlate with the fluorescent puncta visible by light microscopy. The vps4__D _cells have in addition curved linear membrane structures that represent class E endosomes (see images at end of this file). The class E endosomes appear similar in cells expressing Sec2GEF-GFP-CUE, Sec2-GFP or Sec2. We did not observe any obvious spatial relationship between the class E structures and the vesicle clusters.
- Discussion: "Furthermore, delivery of Mup1-GFP to the vacuole was slowed in Sec2GEF-GFP-CUE cells..." - The authors studied "the clearance of Mup1-GFP from the plasma membrane" and not vacuolar delivery. They did not show much vacuolar localization.
We now include quantitation of Mup1-GFP at both the plasma membrane and vacuole (Fig 6 and Fig S8). This shows a reduced rate of depletion from the plasma membrane and a delayed appearance in the vacuole.
Literature:<br /> Nagano, M., Toshima, J. Y., Siekhaus, D. E., & Toshima, J. (2019): Rab5-mediated endosome formation is regulated at the trans-Golgi network. Nature Communications Biology, 2 (1), 1-12.<br /> Nordmann, M., Cabrera, M., Perz, A., Bröcker, C., Ostrowicz, C., Engelbrecht-Vandré, S., & Ungermann, C. (2010): The Mon1-Ccz1 complex is the GEF of the late endosomal Rab7 homolog Ypt7. Current Biology, 20(18), 1654-1659.<br /> Paulsel, A. L., Merz, A. J., & Nickerson, D. P. (2013): Vps9 family protein Muk1 is the second Rab5 guanosine nucleotide exchange factor in budding yeast. Journal of Biological Chemistry, 288 (25), 18162-18171.<br /> Shideler, T., Nickerson, D. P., Merz, A. J., & Odorizzi, G. (2015): Ubiquitin binding by the CUE domain promotes endosomal localization of the Rab5 GEF Vps9. Molecular Biology of the Cell, 26 (7), 1345-1356.
Reviewer #1 (Significance):
- see above
- has some deficits in interpretation as the Rab relocalization was not complete and thus conclusions are limiting
Reviewer #2 (Evidence, reproducibility and clarity):
This paper tries to address a fundamental question in cell biology, namely, what machinery is sufficient to tell a vesicle know where to go and what to do when it gets there. Several groups have shown that localization of some Rab/Ypt GEFs to an orthogonal compartment can lead to redirecting a Rab/Ypt to that membrane, where they can bind their partners abnormally. This story tries to explore what happens next.
Here, Novick and colleagues took a part of the SEC2 GEF for secretory vesicle SEC4 Rab/Ypt and anchored it to endocytic structures to ask whether that was enough to relocalize those structures and drive inappropriate trafficking events. A challenge and advantage in the study is the fact that not all of the GEF relocalized-and that enables the cells to survive as SEC4p is needed for cell growth and membrane delivery--but this incomplete relocalization complicates phenotypic analysis--some SEC4 is on secretory vesicles and some is relocalized apparently to endocytic structures. Another challenge is that the two compartments both show "polarized" distributions so it is hard to know what compartment the reader is looking at, in a given figure. This makes the story very challenging to digest for a non-yeast expert trying to understand the conclusions.
The authors show that the CUE domain can serve to partially localize SEC2GEF-GFP-CUE and this function relies on its ability to interact with ubiquitin. The localization is distinct from that of full length Sec2, nonetheless "many structures bearing Sec2GEF-GFP-CUE localize close to the normal sites of cell surface growth despite their abnormal appearance". The authors conclude that SEC4p and its effectors were recruited to these puncta with variable efficiency and the puncta were static; normal secretion was not blocked. This is not really a surprise as some SEC4p is still directed to secretory granules and cells do not show a vesicle accumulation phenotype by EM. Missing seems to be a clear-cut visual assay for exocytosis of secretory granules or endocytic structures despite attempts to include live cell imaging.
We now show that the bright Sec2GEF-GFP-CUE_ puncta correspond to clusters of 80nm vesicles (Fig 5B). Our FRAP analysis demonstrates that Sec2GEF-GFP-CUE _is able to enter into pre-existing, bleached puncta (Fig 1E). One interpretation is that the vesicle cluster remains static, while individual vesicles enter and exit the cluster.
The authors showed that SEC2-GFP-CUE structures fail to acquire Sro7 and do not seem to be able to assemble a complex with the tSNARE SEC9. Is this because Sro7 is being retained on the remaining secretory vesicles that also have SEC4 and other effectors that may be recruited to those structures by coordinate recognition?
We demonstrate that at least half of the Sec2GEF-GFP-CUE puncta colocalize with Vps9 and this becomes even more evident in a vps4__D_ _mutant (Fig 2A). There is also substantial colocalization with the Rab5 homolog Ypt51, the endocytic marker Vps8 and PI(3)P (Fig 2 and Fig S3D). Nearly all of these puncta also colocalize with Sec4 and most of its downstream effectors. Thus, it seems that we have generated a hybrid compartment, as we intended. The surprise is how well the cells can cope with this situation. One possible explanation is offered in the Discussion: In yeast the TGN is thought to play the role of the early endosome and may be the site of Vps9 membrane recruitment. Thus Sec2GEF-GFP-CUE might be initially recruited to the TGN and the hybrid vesicles formed from this compartment might function to bring secretory cargo from the TGN to the cell surface just like normal secretory vesicles, with the caveat that the presence of endocytic machinery is somewhat inhibitory to Sro7 function, slowing fusion.
There seem to be no issues with data as presented; a diagram of the SEC2-GFP-CUE would help the reader as would use of terms "secretory vesicle" and "endocytic vesicle" and how they were always distinguished rather than "polarized structure" which cannot distinguish these compartments.
We have tried to be careful in our use of terms. We refer to the Sec2-GFP-CUE puncta using the unbiased terms “structures” or “puncta” until we show EM demonstrating that these puncta represent clusters of 80 nm vesicles.
CROSS-CONSULTATION COMMENTS<br /> The two assessments come to the same conclusion--I agree that better definition of the precise phenotypes could be valuable but the limitation of incomplete relocalization will be hard to overcome in the absence of enormous effort.
Reviewer #2 (Significance):
This story represents a valiant effort and presents clean data but the impact and significance of the findings are limited due to the difficult phenotypic starting points (SEC4 in two places), and lack powerful exo- or endocytosis assays and better compartment-specific markers.
The work will be of interest to yeast cell biologists studying the secretory and endocytic pathways. My expertise is mammalian cell biology of the secretory and endocytic pathways.
-
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Referee #2
Evidence, reproducibility and clarity
This paper tries to address a fundamental question in cell biology, namely, what machinery is sufficient to tell a vesicle know where to go and what to do when it gets there. Several groups have shown that localization of some Rab/Ypt GEFs to an orthogonal compartment can lead to redirecting a Rab/Ypt to that membrane, where they can bind their partners abnormally. This story tries to explore what happens next.
Here, Novick and colleagues took a part of the SEC2 GEF for secretory vesicle SEC4 Rab/Ypt and anchored it to endocytic structures to ask whether that was enough to relocalize those structures and drive inappropriate trafficking events. A challenge and advantage in the study is the fact that not all of the GEF relocalized-and that enables the cells to survive as SEC4p is needed for cell growth and membrane delivery--but this incomplete relocalization complicates phenotypic analysis--some SEC4 is on secretory vesicles and some is relocalized apparently to endocytic structures. Another challenge is that the two compartments both show "polarized" distributions so it is hard to know what compartment the reader is looking at, in a given figure. This makes the story very challenging to digest for a non-yeast expert trying to understand the conclusions.
The authors show that the CUE domain can serve to partially localize SEC2GEF-GFP-CUE and this function relies on its ability to interact with ubiquitin. The localization is distinct from that of full length Sec2, nonetheless "many structures bearing Sec2GEF-GFP-CUE localize close to the normal sites of cell surface growth despite their abnormal appearance". The authors conclude that SEC4p and its effectors were recruited to these puncta with variable efficiency and the puncta were static; normal secretion was not blocked. This is not really a surprise as some SEC4p is still directed to secretory granules and cells do not show a vesicle accumulation phenotype by EM. Missing seems to be a clear-cut visual assay for exocytosis of secretory granules or endocytic structures despite attempts to include live cell imaging.
The authors showed that SEC2-GFP-CUE structures fail to acquire Sro7 and do not seem to be able to assemble a complex with the tSNARE SEC9. Is this because Sro7 is being retained on the remaining secretory vesicles that also have SEC4 and other effectors that may be recruited to those structures by coordinate recognition?
There seem to be no issues with data as presented; a diagram of the SEC2-GFP-CUE would help the reader as would use of terms "secretory vesicle" and "endocytic vesicle" and how they were always distinguished rather than "polarized structure" which cannot distinguish these compartments.
Referees cross-commenting
The two assessments come to the same conclusion--I agree that better definition of the precise phenotypes could be valuable but the limitation of incomplete relocalization will be hard to overcome in the absence of enormous effort.
Significance
This story represents a valiant effort and presents clean data but the impact and significance of the findings are limited due to the difficult phenotypic starting points (SEC4 in two places), and lack powerful exo- or endocytosis assays and better compartment-specific markers.
The work will be of interest to yeast cell biologists studying the secretory and endocytic pathways. My expertise is mammalian cell biology of the secretory and endocytic pathways.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
The manuscript from Li et al. describes the authors' attempt to redirect the exocytic Rab Sec4 to endocytic vesicles by fusing the GEF-domain of Sec2 to the CUE domain of the endosomal GEF Vps9, which binds to ubiquitin. The authors show that the localization of the Sec2GEF-GFP-CUE construct is slightly shifted from polarized towards non-polarized sites. Sec2GFP-CUE positive structures acquire Sec4 and Sec4 effectors like exocytic vesicles, but are less motile and show delayed plasma membrane fusion. Expression of Sec2GEF-GFP-CUE was enhanced if expressed in a subset of secretory and endocytic mutants and cause delayed Mup1 uptake from the plasma membrane. As Vps9, Sec2GEF-GFP-CUE accumulated on Class E compartments in vps4Δ strains.<br /> The authors ask here whether vesicular identity is largely predetermined by the correct localization of the specific GEFs of small GTPases and thus localization of the Rab. Although this an interesting hypothesis, the authors observed that endocytic traffic was not reversed by relocating Sec4 to these vesicles. This seems to be due to the strong affinity of the Sec2 GEF-domain for Sec4 but probably also due to the rather weak relocalization via the CUE domain. Thus, only a portion of Sec2 was displaced from its native site. Since the efficiency of this rewiring was not defined, it remains unclear whether the observed mild effects indeed speak against the assumed dominant role of the GEFs and small GTPases in shaping organelle identity or whether they are rather due to an inefficient relocalization.
Specific comments:
- The authors state decidedly that the recruitment of Vps9 occurs ubiquitin-dependent via the CUE-domain. While the CUE-domain is the only known and a likely localization determinant of Vps9, it was not a strong localization determinant. Apart from being present in some puncta, Vps9 localized strongly to the cytosol (Paulsel et al. 2013, Nagano et al. 2019). Shideler et al. also showed that ubiquitin-binding is not required for Vps9 function in vivo, which indicates that other localizing mechanisms may play a role e. g. by positive feedback of GEF-domain-Rab5 interactions which might be initiated by the other Rab5-GEF Muk1 or as suggested by transport from the Golgi (Nagano et al. 2019). These observations indicate that the CUE-domain is a rather weak recruitment domain, which was not discussed in this manuscript. The localization of the Sec2GEF-GFP-control to the polarized sites in 30% of the cells furthermore suggests that the used Sec2GEF-GFP-CUE retains some native localization via the GEF-domain. Since the relocation efficiency of Sec2GEF-GFP-CUE was not defined, the obtained phenotypic effects allow for only vague conclusions. Although the mild endo- and exocytosis defects as well as the accumulation of Sec2GEF-GFP-CUE at Class E compartments indicate that the CUE-domain indeed conferred some relocation to endosomes, this was not shown for the sec2Δ strain e. g. by looking at colocalizations with endocytic versus exocytic markers and comparing their relative abundance at the Sec2GEF-GFP-CUE-positive structures. While some of the Sec2GEF-GFP-CUE-positive structures colocalized with Mup1 in the Mup1-uptake assay, it would be important to clarify how many endosomal properties are retained and how many exocytic properties are gained by these chimeric vesicles e. g. by looking for the presence of specific phosphoinositides, or Rab5 and Rab5 effectors. A competition between endosomal and the acquired exocytic factors could also be another possible explanation for the immobility of the Sec2GEF-GFP-CUE structures and less efficient recruitment of Sec4 effectors in addition to the proposed lack of PI4P.
- While the colocalization of the Sec2GEF-GFP-CUE-signal with Sec4 indicates that this GEF-construct is generally active, it remains unclear whether the activity of the tagged constructs differ from that of the wild type Sec2 protein. This could be analyzed in vitro via a MANT-GDP GEF-activity assay (Nordmann et al., 2010). Again, it remains unclear how much of the Sec2GEF-Sec4 colocalization represents the retained native localization versus synthetic localization at chimeric endo-exocytic vesicles.
- The authors mention that tagging with GFP increases the stability of the expressed constructs. However, it remains unclear whether this is also the case for the other tags (NeonGreen, mCherry) used in the other experiments. Are the constructs expressed at similar levels?
- In Figure 5: The incomplete colocalization of Sec2GEF-GFP-CUE with Vps9 is explained by the short-timed accessibility of ubiquitin moieties. Apart from the likely retained native localization or weak CUE-domain-function, this observation could also be due to competition between Vps9 and Sec2GEF-GFP-CUE for the available ubiquitin target structures.
Minor remarks:
- Fig. 3C do not contain the arrowheads as indicated in the legend, making it harder to interpret.
- The image chosen for Sec2-GFP in Fig. 4B suggests less colocalization between Sec2-GFP and Sec8 than between Sec2GEF-GFP-CUE and Sec8. They rather look next to each other.
- Figure 5: While resolution limits are possibly reached regarding endosomes, it might be interesting to check by thin section electron microscopy whether and how class E compartment formation is affected by Sec2GEF-GFP-CUE expression.
- Discussion: "Furthermore, delivery of Mup1-GFP to the vacuole was slowed in Sec2GEF-GFP-CUE cells..." - The authors studied "the clearance of Mup1-GFP from the plasma membrane" and not vacuolar delivery. They did not show much vacuolar localization.
Literature:
Nagano, M., Toshima, J. Y., Siekhaus, D. E., & Toshima, J. (2019): Rab5-mediated endosome formation is regulated at the trans-Golgi network. Nature Communications Biology, 2 (1), 1-12.
Nordmann, M., Cabrera, M., Perz, A., Bröcker, C., Ostrowicz, C., Engelbrecht-Vandré, S., & Ungermann, C. (2010): The Mon1-Ccz1 complex is the GEF of the late endosomal Rab7 homolog Ypt7. Current Biology, 20(18), 1654-1659.
Paulsel, A. L., Merz, A. J., & Nickerson, D. P. (2013): Vps9 family protein Muk1 is the second Rab5 guanosine nucleotide exchange factor in budding yeast. Journal of Biological Chemistry, 288 (25), 18162-18171.
Shideler, T., Nickerson, D. P., Merz, A. J., & Odorizzi, G. (2015): Ubiquitin binding by the CUE domain promotes endosomal localization of the Rab5 GEF Vps9. Molecular Biology of the Cell, 26 (7), 1345-1356.
Significance
- see above
- has some deficits in interpretation as the Rab relocalization was not complete and thus conclusions are limiting
-
-
www.biorxiv.org www.biorxiv.org
-
Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
This manuscript by Gouignard et al., reports that a matrix metalloproteinase MMP28 regulates neural crest EMT and migration by transcriptional control rather than matrix remodeling. The manuscript is clearly written and provides sufficient evidence and control experiments to demonstrate that the MMP28 can translocate into nucleus of non-producing cells and that nuclear localization and catalytic activity are essential for the activity of MMP28 to regulate gene transcription. ChIP-PCR analysis also suggests that MMP28 can bind to the proximal promoters of Twist and others. However, since weak binding is also detected between MMP14 and the promoters, a more direct evidence that such binding can indeed promote Twist expression will be more appreciated.
Thank you for this comment. First, to represent the data from our ChIP assays we normalized all intensities to the GFP condition such that all levels are expressed fold change to GFP and we performed statistical comparisons. This shows that the enrichment of promoter regions by MMP28 and MMP14 are not equivalent.
Second, to substantiate our previous ChIP data, we performed a new set of ChIP experiments, by performing three independent chromatin immunoprecipitations (biological replicates), and used primers targeting three new domains in the proximal promoter of Twist and primers against two domains in the proximal promoter of E-cadherin and one domain 1kb away from transcription start of E-cadh. We found that pull down with MMP28 significantly enriches the three tested domains within the proximal promoter of Twist but not those of the E-cadherin promoter, compared to GFP pull down. These data were added to Figure 7.
However, we do not propose that MMP28 might act as a transcription factor and be able to promote Twist expression on its own. We apologize if some of the initial description of our data were too blunt and might have misled the reviewers. First, the protein sequence of MMP28, like those of all other MMPs, does not contain any typical DNA binding sites. In addition, ectopic overexpression of MMP28 is not sufficient to promote ectopic Twist expression (as shown in supplementary Figure 4) whereas, by contrast, Twist is able to promote ectopic expression of Cadherin-11 (see new Supplementary Figure 11). This indicates that MMP28 has an effect on Twist expression in the context of neural crest only and is not capable of activating Twist expression by itself.
Also, it should be added that enrichments of promoter domains by MMP28 pull-down are very modest in comparison to enrichments obtain with Twist pull-downs. Therefore, a more plausible role for MMP28 is to be part of a regulatory cascade with other factors involved in regulating the expression of the target genes important for EMT. Other MMPs such as MMP14 and MMP3 have been shown to interact with chromatin with some transcriptional downstream effects but multiple domains of these proteins seem to equally mediate such interactions. None of the data published in these studies rules out a relay via cofactors. We extensively modified the text describing our data and provided additional context.
Identifying the putative partners and their functional relationship with MMP28 is a project on its own and beyond the scope of this study.
While the nuclear translocation and transcription regulation activity of MMP28 is clearly the focus of the study, there are some minor issues that should be further clarified in the functional studies in the earlier part of the manuscript.
First, the effect of the splicing MO is somewhat unexpected. I would think that the splicing MO would lead to the retention of intron one and therefore premature termination or frameshift of the protein product, but RT-PCR or RT-qPCR suggest that there is no retention of intron 1, but a reduction in the full-length transcript, exon 1, or exon 7-8. Why is that?
Thank you for this comment. This is presumably due to nonsense mediated RNA decay. We have not explored the biochemistry of MMP28 RNA following injection with MOspl. Splicing MOs can have multiple effects. As explained on the GeneTools website splicing MOs disturb the normal processing of pre-mRNA and cells have various ways to deal with this and there are multiple possible outcomes. The PCR with E1-I1 suggests that intron 1 is not retained. Therefore, a putative concern would be that MOspl led to exon-skipping and to the generation of a truncated form of MMP28. However, we have checked that it is not the case. The fact that the PCR using E7-E8 primers indicates a reduction as well suggests an overall degradation of the mRNA for MMP28. Importantly, the effect of MOspl can be rescued using MMP28 mRNA indicating that the knockdown is specific.
Second, the effect of the splicing MO and ATG MO in NC explant spreading seems to be somewhat different, with ATG MO strongly repressed explant spreading, cell protrusion, and cell dispersion, while splicing MO does not affect cell dispersion, but affects the formation of cell protrusions. Does this reflects different severity of the phenotype or does the product of splicing MO display some activity?
Thank you for this comment. However, we think that there may be a confusion. Data on Fig2 (MOatg) and Fig3 (MOspl) both show a decrease of neural crest migration in vivo (Figure 2a-b) and of neural crest dispersion ex vivo (Fig2c, Fig3i-k). Along the course of the project we have never observed a difference in penetrance or intensity of the phenotypes between the two MOs.
Also, the switch between ATG MO and splicing MO is a bit confusing, maybe it is better to keep splicing MO only in the main text and move results involving ATG MO to supplementary studies.
The reason is purely historical. We had an effect with MOatg that can be rescued but there is no available anti-Xenopus MMP28 to assess its efficiency. So we turned to MOspl to have an internal control of efficiency by PCR. This provides an independent knockdown method reinforcing the findings. Both MOs have been controlled for specificity by rescue with MMP28 and display similar effect on NC migration/dispersion. We see no harm in keeping both in the main figures but if the reviewer feels strongly about this we could perform the suggested redistribution of data between main and supp figures.
Lastly, in Figure 3C and 3J, it says that the distance of migration or explant areas were normalized to CMO, while normalization against the contralateral uninjected side, or explant area at time 0 makes more sense.
Thank you for this comment as it will allow us to explain better these quantifications. Regarding in vivo measurements (Figure 3c), it is indeed the ratio between injected and non-injected sides that is performed in all conditions and then the ratios are normalized to CMO. We have now clarified this point on all instances throughout the figures.
Regarding ex vivo measurements (Figure 3j), NC explants are placed onto fibronectin and left to adhere for 1 hour before time-lapse imaging starts. NC cells extracted from MMP28 morphant embryos are not as efficient at adhering and spreading as control NC cells. Therefore, normalizing to t0 would erase that initial difference between control and MMP28 conditions. By normalizing to CMO at t_final we can visualize the initial defect of adhesion and spreading as well as the overall defects since CMO at t_final represents the 100% dispersion possible over the time course of the movie.
Referee Cross-commenting
I agree with comments from both Reviewers 2 and 3, especially that whether MMP28 regulates placode development (through Six1 expression) should be addressed.
Reviewer #1 (Significance):
This work provides novel insights of how a metalloprotease that is normally considered to function extracellularly can transfer into the nucleus of neighboring cells and regulate transcription. This would be of interest to researchers studying EMT, cell migration, and the functions of extracellular proteins in general. My expertise is in neural crest EMT and migration, and cytoskeletal regulation of cell behavioral changes. I do not have enough background on biochemical analysis.
Reviewer #2 (Evidence, reproducibility and clarity):
Summary:
In this study, Gouignard et al. beautifully use the Xenopus neural crest as a model system to examine the role of the matrix metalloproteinase MMP28 during EMT. The authors show that mmp28 is expressed by the placodes adjacent to the neural crest. Using in vivo and in vitro perturbation experiments, they show that the catalytic function of MMP28 is necessary for the expression of several neural crest markers, as well as neural crest migration and adhesion. Next, the authors use grafting, confocal imaging, and biochemistry to convincingly demonstrate that MMP28 is translocated into the nucleus of neural crest cells from the adjacent placodes. Finally, nuclear localization of MMP28-GFP is necessary to rescue twist and sox10 expression in MMP28 morphants, and ChIP-PCR experiments suggest direct interactions between MMPs and the proximal promoters of several neural crest genes. These results have significant implications on the field of EMT and highlight an underappreciated role for MMPs as direct regulators of gene expression.
Major comments:
Overall, the experiments presented in this study are thoroughly controlled and the results are clearly quantitated and rigorously analyzed. Most claims are well supported by multiple lines of experimental evidence; however, there are a few experiments or observations that this reviewer thinks should be reconsidered for more clarity and accuracy.
- Supplementary Figure 1 shows the effect of MMP28-MOspl on additional ectodermal markers and shows that there is a significant loss of six1 expression from the placodal domain following MMP28 knockdown. The authors note this as a "slight reduction" on line 95, but since this shows a larger reduction in gene expression than some of the neural crest markers (snai2, sox8, foxd3), this reviewer thinks these results warrant a more significant discussion in this study.
Thank you for this comment. We apologize for the poor choice of word regarding the description of the effect on Six1 expression. We corrected the associated paragraph.
Although we do observe a reduction of Six1 expression upon MMP28 knockdown, this cannot explain the observed downregulation of some neural crest genes in our MMP28 experiments. There are noticeable differences between the effects of Six1 loss of function that have been reported in the literature and the MMP28 knockdown phenotypes we describe. As suggested by the reviewer, we added a paragraph in the discussion.
Does MMP28 localize to the nucleus of placodal cells as it does with neural crest? If so, is it through interaction with the six1 proximal promoter? If MMP28 does not localize to the nucleus, that would suggest MMP28 function with a different mechanism between epithelial cells distinct from role in EMT. These questions could be addressed by analysis of the placode cells in the images in Figure 5 and use of primers against the six1 proximal promoter on any remaining samples from the ChIP experiment.
Thank you for this comment. To address whether nuclear entry is specific to the neural crest-placodes interaction, we performed new grafts:
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1/ we replaced neural crest cells from embryos expressing MMP28-GFP by placodal cells injected with Rhodamine-dextran. This generates grafted embryos with control placodes next to placodes overexpressing MMP28-GFP. There, we can analyze entry of MMP28-GFP in placodal cells that do not overexpress it. We detected MMP28 in the cytoplasm and in the nucleus of these placodal cells. However, the rate of nuclear entry was lower than in NC cells.
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2/ To assess the importance of the cell type producing MMP28, we grafted NC cells injected with Rhodamine-dextran next to caudal ectoderm expressing MMP28-GFP. MMP28 was detected in cytoplasm and the nucleus of the NC cells but with a lower efficiency than when NC are grafted next to placodes expressing MMP28-GFP.
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3/ We made animal caps sandwiches with animal caps injected with Rhodamine-dextran and animal caps expressing MMP28-GFP. In this case MMP28-GFP is detected in the cytoplasm but fails to reach the nucleus.
Collectively, these data indicate that placodes can import MMP28 produced by placodes and that NC can import MMP28 produced by other cells than placodes. However, in both cases the rate of nuclear entry was lower than in the NC-placode situation. Finally, the animal cap sandwiches indicate that entry into the cells does not predict entry into the nucleus. All these data were added to Supp Figure 7. Statistical comparisons of the proportion of cells with cytoplasmic and nuclear MMP28-GFP in all grafts were added to Figure 5.
The Six1 promoter analysis suggested is beyond the scope of this study as our focus is primarily on the role of MMP28 in neural crest development.
- In Figure 2c, the authors rescue MMP28-MOatg with injection of MMP28wt mRNA. Does the MOatg bind to the exogenous mRNA? If so, this may just reflect titration of the MOatg. If this is the case, this experiment should be repeated with MOspl instead of MOatg.
Thank you for this comment. MOatg is designed upstream of the ATG and thus the binding site is not included in the expression construct. We added this important technical information in the methods. Of note, we already have the suggested equivalent of Fig2C with the MOspl on figure 3.
- Is there a missing data point in Figure 2d corresponding to the upper bounds of the whisker in the 6 hour time point for the MMP28-MOatg dataset?
Thank you for pointing this out. The top data point was indeed missing from the graph, and we apologize for this oversight. We have now updated the figure with the correct graph.
- The authors present ChIP-PCR results in Figure 7 as the major evidence to support the mechanism of nuclear MMP28 in regulating neural crest EMT through physical interaction with target gene promoters. However, the experimental design and presentation in Figure 7 are somewhat unconventional, and as such, difficult to interpret. First, instead of displaying the band brightness across the gel, the authors should normalize their bands to their negative GFP control, thus allowing for interpretation as a "fold enrichment over GFP control". It would be most clear to present these results in the form of a plot similar to Shimizu-Hirota et al., 2012, Figure 6D. Using qPCR instead of gel-based quantitation would further increase reproducibility by removing any bias in image analysis.
Thank you for this comment. For each band the value of the adjacent local background was subtracted. We have now normalized to GFP to provide graphs showing the fold change to GFP enrichment as requested.
However, we would like to point out that we do not propose that MMP28 might act as a transcription factor and be able to promote Twist expression on its own. First, the protein sequence of MMP28 does not contain any typical DNA binding sites, as is the case for any other MMPs. In addition, ectopic overexpression of MMP28 is not sufficient to promote ectopic Twist expression (see sup figure 4) contrary to Twist that can ectopically induce Cadherin-11 for instance (see sup figure 11). Further, enrichments of promoter domains by MMP28 pull downs are very modest in comparison of the enrichments promoted by Twist pull downs.
A more plausible role for MMP28 is that it is recruited via an interaction with other factors involved in regulating the expression of the target genes related to EMT. Identifying the partners and their functional relationship with MMP28 is a project on its own, and beyond the scope of this study.
Second, a proximal promoter sequence represents only ~250 bp upstream from the transcriptional start site. What is the rationale for testing multiple loci up to 3 kb upstream?
Thank you for pointing this out. The use of the term “proximal” was indeed misleading we have now corrected this part in the text. Regulatory sequences can be located anywhere so we initially had a broader approach to test for interactions. Following on this reviewer’s comment, we removed the data points corresponding to the very distal sites. In addition, we performed three new independent ChIP-PCR assays with primers in the proximal portion of Twist and E-cadherin promoters and found enrichment in ChIP with MMP28-GFP compared to GFP for Twist but not for E-cadherin (whose expression was not affected by MMP28 knockdown). These data were added to Figure 7.
It is surprising to see that most of these proteins do not show significant enrichment to a particular locus across this ~3 kb territory, while this reviewer would expect to see enrichment close to the TSS that quickly is lost as you move further upstream. Can you explain why MMP28, MMP14, and often Twist, show similar enrichment across this long genomic region?
Thank you for this comment. Our initial choice of representation did not allow to compare profiles properly. Fold-enrichment to GFP, as suggested by this reviewer, now shows that Twist, MMP28 and MMP14 do not display the same pattern of enrichment across the various loci and that MMP28 pull downs leads to significant enrichments of some of the domains tested in Cad11 and Twist promoters.
Third, the authors should include additional genomic loci to act as negative controls. For example, E-cadherin was unaffected by MMP28-MOspl, thus there may be no physical interaction between the E-cadherin locus and MMP28. It would be ideal to display results from at least one neural crest-related and one non-neural crest-related gene. Finally, this experiment requires statistical analyses to increase confidence in these interactions.
Thank you for this comment. We tested binding to E-cadherin promoter for GFP and MMP28-GFP and found no enrichment with MMP28. We also performed statistics as requested. These data were added to Figure 7.
Minor comments:
- The authors should expand their abstract to more explicitly describe the experiments and results presented within this study.
Done
- In the introduction, line 57 is unclear. "MMP28 is the latest member..." Is this chronologically? Evolutionarily? After this, the authors' statement that the roles of MMP28 are "poorly described" (lines 59-60) seems contradicting with their next sentences citing several studies that document the roles of MMP28 in diverse systems.
Thank you for this comment. The term “poorly described” was meant with respect to other MMPs with more extensive literature. We have now rephrased this part. Regarding the “latest member” we meant the last to be identified. We have now rephrased this part.
- To increase clarity, the authors should define which cell types are labeled by in situ hybridization for sox10 and foxi4.1 in Figure 1e.
Thank you, we performed the requested clarifications and expanded the change to add the cell types labelled by the other genes used on the figure (see figure legend).
- The PCR analysis for mmp28 splicing shown in Figure 1g is very clear and well demonstrates the efficacy of the MMP28-MOspl. However, the authors should note in the figure legend what the "ODC" row represents as this is unclear.
We added the definition of ODC in the figure legends and in the methods.
- On line 118 the authors first reference "MOatg" but should explicitly define this reagent and its mechanism of action for clarity.
We performed the requested clarification.
Referee Cross-commenting
As with Reviewer #1, I was surprised that the RT-PCR analysis presented in support of the splicing MO lacked retention of intron one. I reasoned this might be due to reduced transcript abundance through a mechanism such as nonsense-mediated decay, but I agree that this data raises questions that the authors should address.
Thank you for this comment. Indeed, this is presumably due to nonsense mediated RNA decay. We have not explored the biochemistry of MMP28 RNA following injection with MOspl. Splicing MOs can have multiple effects. As explained on the GeneTools website splicing MOs disturb the normal processing of pre-mRNA and cells have various ways to deal with this and there are multiple possible outcomes. The PCR with E1-I1 suggests that intron 1 is not retained. Therefore, a putative concern would be that MOspl led to exon-skipping and to the generation of a truncated form of MMP28. However, we have checked that it is not the case. The fact that the PCR using E7-E8 primers indicates a reduction as well suggest an overall degradation of the mRNA for MMP28. Importantly, the effect of MOspl can be rescued using MMP28 mRNA indicating that the knockdown is specific.
I also agree with the other comments from Reviewers 1 and 3.
Reviewer #2 (Significance):
This study by Gouignard et al. provides compelling evidence for the role of MMP28 during neural crest EMT. As neural crest cells share similar EMT and migration mechanisms with cancer progression, they represent a powerful system in which to study these biological processes in vivo. Previous work on MMP function has focused primarily on extracellular matrix remodeling and the effect on cell migration, with less attention given to the role of MMPs during EMT. More recent reports in other systems have begun to elucidate a role for MMP translocation into the nucleus, indicating a surprising and novel mechanism for these proteins. This work would be of particular interest to audiences interested in cancer, cell, and developmental biology, as it highlights the importance of the non-canonical function of metalloproteinases during EMT and migration.
Reviewer #3 (Evidence, reproducibility and clarity):
Summary
This study by Gouignard and colleagues explores the mechanisms involving the matrix-metalloprotease MMP28 in the epithelial-to-mesenchymal transition (EMT) of neural crest cells. Interestingly and provocatively, they focus not only on the extracellular functions of this protease but also on the roles of MMP28 in the nucleus. This in non-conventional sub-cellular localization is shared with other MMPs, but its significance remains poorly understood. Here, the authors show that the nuclear function of MMP28 impacts the expression of key EMT regulators in neural crest cells in vivo.
Using Xenopus laevis as a powerful animal model to explore the early development, the authors show that mmp28 expression is found in the ectodermal placodal tissue adjacent to the neural crest prior and after EMT.<br /> In the first part of the study, the authors show that MMP28 depletion affects a subset of neural crest marker gene expression (snai2, twi, sox10) but not others (sox9, snai1), suggesting a specific role on a subset of the genes important for neural crest EMT. The MMP28 depletion phenotype is restored by coinjecting MMP28 MO and MMP28 mRNA, provided that the catalytic activity of the encoded protein is maintained. Next, epistasis (rescue) experiments show that Twist1 can compensate MMP28 depletion.<br /> The second part of the study elegantly shows that MMP28 produced by host adjacent tissues can translocate into the nucleus of neural crest cells grafted from a donor embryo (devoid of MMP28-GFP expression). It also shows that MMP28 nuclear localization as well as its catalytic activity are both required for activating the neural crest gene twist1 and sox10; and that MMP28 is found bound on the chromatin of twist1, cad11 and sox10.<br /> Altogether, these experiments strongly support a model for the nuclear role of MMP28 in the activation (or maintenance) of key genes of the EMT program in vertebrate neural crest cells.
Major comments
The key conclusions are:
Conclusion 1: MMP28, expressed and secreted by placodes, is important for complete neural crest patterning prior to EMT, including activation of twist1 and EMT effector cadherin 11 genes. MMP28 is important for neural crest EMT and migration in vivo and in explant assay in vitro.
However, this conclusion omits potential indirect effect of interfering with placode formation itself, as indicated by the strong decrease in six1 expression in morphant embryos. The effect of MMP28MO on the expression of six1 is as strong as for neural crest markers snai2, twi, for example. Line 95, "slight reduction" should be modified.
Thank you or this comment. We have now modified the associated text.
What this may mean for placodal development itself, as well as for indirect effects on neural crest cells need to be discussed.
Following this comment, we added a paragraph in the discussion about Six1.
Conclusion 2: Gain of Twist 1 (but not Cadherin 11) rescues MMP28 morphant phenotype, allowing EMT to occur and restoring several parameters of cell migration in vivo and in explant assay
Conclusion 3: When secreted from adjacent cells, MMP28 is translocated into the nucleus of neural crest cells and displays a nuclear function important for the activation of twist1 expression.
Both conclusions 2 and 3 are supported by multiple elegant and convincing experimental data. These conclusions do not depend on mmp28 exclusive expression by the placodal ectoderm, and would still be important if there was a minor expression in the neural crest cells themselves (and thus an autocrine effect).
Additional experiments to strengthen the conclusions<br /> Related to Conclusion 1:
- line 102-106: In the rescue experiment, is six1 expression rescued too?
Thank you for this comment. As detailed in the newly added discussion paragraph about the effects of Six1 loss of function that have been described in the literature, it is very unlikely that our NC phenotypes stem from the observed reduction of Six1 expression.
Nonetheless, following this comment we checked for Six1 expression in the placodal domain following MMP28 knockdown and rescue condition. In the rescue condition, only 25% of the embryos had recovered Six1 expression in placodes while 75% of the embryos recovered Sox10 expression in neural crest cells. These data further confirm that rescue of placodal genes is not a pre-requisite for the rescue of neural crest genes and were added in Supp Figure 5.
Although MMP28 is likely to have a role in placodes as well, the expansion of Sox2 and Pax3 expression domain and the loss of Eya1 expression typically associated with Six1 knockdown did not occur in MMP28 knockdown. Our story being focused on neural crest cells, we did not investigate further how the MMP28-dependent effect on Six1 might impair placode development.
- Figure 2g: qPCR analysis suggests that mmp28 is expressed in the neural crest explants themselves, levels being lowered by the MO injection. The levels of this potential expression in the neural crest itself should be compared to the levels in the placodal ectoderm. How do the authors exclude an effect of the MO within the neural crest tissue, independently of roles from the placodal tissue?
Thank you for this comment. There is a very small subpopulation of NC cells called the medial crest that expresses MMP28. They are along a thin line along the edge of the neural folds. We previously described this in Gouignard et al Phil Trans Royal Soc B 2020. It is useful for us as an internal control for MO efficiency but the expression in placodes is much stronger and involves many more cells. However, this expression called our attention at the onset of the project and we performed some experiments to assess whether some of the observed effects were due to a NC-autonomous effect, as suggested by this reviewer. To test for this we performed targeted injected of the MO such that the medial crest would receive the MO but not the placodes. Targeting the medial crest with MMP28-MO had no effect on Sox10 expression. These data were added to new supp Figure 1.
The cost and time for these additional experiments is limited (about 3 weeks), and uses reagents already available to the authors.
Data and Methods are described with details including all necessary information to replicate the study. Replication is carefully done and statistical analysis seems convincing.
Minor comments
Experimental suggestions to further strengthen the conclusions.<br /> Related to Conclusion 1: - Figure 1e, frontal histological sections would help distinguishing between placodal tissue and neural crest mesenchyme.
Thank you for this comment. We previously published a detailed expression pattern with such sections (Gouignard et al Phil Trans Royal Soc B, 2020). We rephrased the text to better refer to this previous publication.
Related to Conclusion 2: - Figure 3: in explants co-injected with twist1 mRNA, is cad11 expression restored? Could this indicate if cad11 is (or is not) part of the program controlled by Twist1 (as suggested by the last main figure)?
Thank you for this comment. We checked for Cadherin-11 expression in control MO, MMP28-MOspl and MOspl+Twist mRNA and Twist is indeed capable of inducing Cadherin-11 and even leads to ectopic activation of Cad11 on the injected side. These data were added to new Supp Figure 11.
Related to Conclusion 3: is MMP28 translocation seen in any cell context? Could the authors repeat experiments in Figure 6a with animal cap ectoderm? And with sandwich animal cap ectoderm, one expressing MMP28-GFP versions (wt, deltaSPNLS) and the other Rhodamine Dextran only? This would allow to generalize the mechanism or on the contrary to show a neural crest specificity.
Thank you for this comment. Following this suggestion and comments from the other reviewers, we performed new grafting experiments.
- 1/ we replaced neural crest cells from embryos expressing MMP28-GFP by placodal cells injected with Rhodamine-dextran. This generates grafted embryos with control placodes next to placodes overexpressing MMP28-GFP. There, we can analyze entry of MMP28-GFP in placodal cells that do not overexpress it. We detected MMP28 in the cytoplasm and in the nucleus of these placodal cells. However, the rate of nuclear entry was lower than in NC cells.
- 2/ To assess the importance of the cell type producing MMP28 we grafted NC cells injected with Rhodamine-dextran next to caudal ectoderm expressing MMP28-GFP. MMP28 was detected in cytoplasm and the nucleus of the NC cells but with a lower efficiency than when NC are grafted next to placodes expressing MMP28-GFP.
- 3/ We made animal caps sandwiches with animal caps injected with Rhodamine-dextran and animal caps expressing MMP28-GFP. In this case MMP28-GFP is detected in the cytoplasm but fails to reach the nucleus. These data indicate that placodes can import MMP28 produced by placodes and that NC can import MMP28 produced by other cells than placodes. However, in both cases the rate of nuclear entry was lower than in the NC-placode situation. Finally the animal cap sandwiches indicate that entry into the cells does not predict entry into the nucleus. All these data were added to new Supp Figure 7 and quantifications of import of MMP28-GFP in the cytoplasm and the nucleus all conditions added to Figure 5.
In supplementary figure 4a, the grey (RDx) is not visible in the zoom in images.
As the grey channel interferes with visualizing the green channel, we only show the grey channel on the first low magnification image so that the position of grafted cells can be seen. We found it better to omit it from the zoomed in images to avoid masking the GFP signal.
In figure 7a,b MMP14 is green, GFP is grey (mentioned wrongly in line 276)
Thank you for pointing this out. We have extensively modified Figure 7 and such issues are now resolved.
Bibliographical references are accurate. Clarity of the text and figures is excellent, except maybe Figure 7, where a qPCR analysis would be easier to visualize, especially with low-level or fuzzy bands on the gel.
Thank you. We have now modified Figure 7, including normalization to GFP to show fold-change enrichment and have added new data from three independent ChIP assays for proximal Twist and E-cadherin promoters that we hope further substantiate our initial observations.
Reviewer #3 (Significance):
Place of the work in the field's context:
In cancer, the MMP proteins are widely described in multiple tumor contexts and promote cell invasion. In development, several studies have focused on their functions in the extracellular space. The nuclear localization of MMP family proteins has been described previously but remained poorly understood so far. This work is thus a pioneer study aiming to understand MMP28 nuclear function.
Advance:
This study makes a significant advance in the field, by unraveling the importance of the MMP28 activity in the cell nucleus for the expression of key EMT regulators. Moreover, the study suggests that extracellular MMP28 secreted by adjacent cells or tissues can be internalized and transported to cell nucleus into cells located several cell diameters away. This study thus supports a novel facet of MMP proteins activity, complementary to their previously described role on the extracellular matrix, and further favoring cell invasion, in development and potentially in cancer too.
The target audience goes without doubt beyond developmental biologists (the primary interest) and also includes cell and cancer biologists, and any biologist interested by MMPs or cell invasion mechanisms in vivo.
My field of expertise is developmental biology focused on neural and neural crest early development, mainly using animal models in vivo and some cell culture experiments. I also focus on some aspects of cancer cell migration.
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Referee #3
Evidence, reproducibility and clarity
Summary
This study by Gouignard and colleagues explores the mechanisms involving the matrix-metalloprotease MMP28 in the epithelial-to-mesenchymal transition (EMT) of neural crest cells. Interestingly and provocatively, they focus not only on the extracellular functions of this protease but also on the roles of MMP28 in the nucleus. This in non-conventional sub-cellular localization is shared with other MMPs, but its significance remains poorly understood. Here, the authors show that the nuclear function of MMP28 impacts the expression of key EMT regulators in neural crest cells in vivo.
Using Xenopus laevis as a powerful animal model to explore the early development, the authors show that mmp28 expression is found in the ectodermal placodal tissue adjacent to the neural crest prior and after EMT.<br /> In the first part of the study, the authors show that MMP28 depletion affects a subset of neural crest marker gene expression (snai2, twi, sox10) but not others (sox9, snai1), suggesting a specific role on a subset of the genes important for neural crest EMT. The MMP28 depletion phenotype is restored by coinjecting MMP28 MO and MMP28 mRNA, provided that the catalytic activity of the encoded protein is maintained. Next, epistasis (rescue) experiments show that Twist1 can compensate MMP28 depletion.<br /> The second part of the study elegantly shows that MMP28 produced by host adjacent tissues can translocate into the nucleus of neural crest cells grafted from a donor embryo (devoid of MMP28-GFP expression). It also shows that MMP28 nuclear localization as well as its catalytic activity are both required for activating the neural crest gene twist1 and sox10; and that MMP28 is found bound on the chromatin of twist1, cad11 and sox10.<br /> Altogether, these experiments strongly support a model for the nuclear role of MMP28 in the activation (or maintenance) of key genes of the EMT program in vertebrate neural crest cells.
Major comments
The key conclusions are:
Conclusion 1: MMP28, expressed and secreted by placodes, is important for complete neural crest patterning prior to EMT, including activation of twist1 and EMT effector cadherin 11 genes. MMP28 is important for neural crest EMT and migration in vivo and in explant assay in vitro.
However, this conclusion omits potential indirect effect of interfering with placode formation itself, as indicated by the strong decrease in six1 expression in morphant embryos. The effect of MMP28MO on the expression of six1 is as strong as for neural crest markers snai2, twi, for example. Line 95, "slight reduction" should be modified. What this may mean for placodal development itself, as well as for indirect effects on neural crest cells need to be discussed.
Conclusion 2: Gain of Twist 1 (but not Cadherin 11) rescues MMP28 morphant phenotype, allowing EMT to occur and restoring several parameters of cell migration in vivo and in explant assay
Conclusion 3: When secreted from adjacent cells, MMP28 is translocated into the nucleus of neural crest cells and displays a nuclear function important for the activation of twist1 expression.
Both conclusions 2 and 3 are supported by multiple elegant and convincing experimental data. These conclusions do not depend on mmp28 exclusive expression by the placodal ectoderm, and would still be important if there was a minor expression in the neural crest cells themselves (and thus an autocrine effect).
Additional experiments to strengthen the conclusions<br /> Related to Conclusion 1:
- line 102-106: In the rescue experiment, is six1 expression rescued too?
- Figure 2g: qPCR analysis suggests that mmp28 is expressed in the neural crest explants themselves, levels being lowered by the MO injection. The levels of this potential expression in the neural crest itself should be compared to the levels in the placodal ectoderm. How do the authors exclude an effect of the MO within the neural crest tissue, independently of roles from the placodal tissue?
The cost and time for these additional experiments is limited (about 3 weeks), and uses reagents already available to the authors.
Data and Methods are described with details including all necessary information to replicate the study. Replication is carefully done and statistical analysis seems convincing.
Minor comments
Experimental suggestions to further strengthen the conclusions.<br /> Related to Conclusion 1: - Figure 1e, frontal histological sections would help distinguishing between placodal tissue and neural crest mesenchyme.<br /> Related to Conclusion 2: - Figure 3: in explants co-injected with twist1 mRNA, is cad11 expression restored? Could this indicate if cad11 is (or is not) part of the program controlled by Twist1 (as suggested by the last main figure)?<br /> Related to Conclusion 3: is MMP28 translocation seen in any cell context? Could the authors repeat experiments in Figure 6a with animal cap ectoderm? And with sandwich animal cap ectoderm, one expressing MMP28-GFP versions (wt, deltaSPNLS) and the other Rhodamine Dextran only? This would allow to generalize the mechanism or on the contrary to show a neural crest specificity.
In supplementary figure 4a, the grey (RDx) is not visible in the zoom in images.<br /> In figure 7a,b MMP14 is green, GFP is grey (mentioned wrongly in line 276)<br /> Bibliographical references are accurate. Clarity of the text and figures is excellent, except maybe Figure 7, where a qPCR analysis would be easier to visualize, especially with low-level or fuzzy bands on the gel.
Significance
Place of the work in the field's context:
In cancer, the MMP proteins are widely described in multiple tumor contexts and promote cell invasion. In development, several studies have focused on their functions in the extracellular space. The nuclear localization of MMP family proteins has been described previously but remained poorly understood so far. This work is thus a pioneer study aiming to understand MMP28 nuclear function.
Advance:
This study makes a significant advance in the field, by unraveling the importance of the MMP28 activity in the cell nucleus for the expression of key EMT regulators. Moreover, the study suggests that extracellular MMP28 secreted by adjacent cells or tissues can be internalized and transported to cell nucleus into cells located several cell diameters away. This study thus supports a novel facet of MMP proteins activity, complementary to their previously described role on the extracellular matrix, and further favoring cell invasion, in development and potentially in cancer too.
The target audience goes without doubt beyond developmental biologists (the primary interest) and also includes cell and cancer biologists, and any biologist interested by MMPs or cell invasion mechanisms in vivo.
My field of expertise is developmental biology focused on neural and neural crest early development, mainly using animal models in vivo and some cell culture experiments. I also focus on some aspects of cancer cell migration.
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Referee #2
Evidence, reproducibility and clarity
Summary:
In this study, Gouignard et al. beautifully use the Xenopus neural crest as a model system to examine the role of the matrix metalloproteinase MMP28 during EMT. The authors show that mmp28 is expressed by the placodes adjacent to the neural crest. Using in vivo and in vitro perturbation experiments, they show that the catalytic function of MMP28 is necessary for the expression of several neural crest markers, as well as neural crest migration and adhesion. Next, the authors use grafting, confocal imaging, and biochemistry to convincingly demonstrate that MMP28 is translocated into the nucleus of neural crest cells from the adjacent placodes. Finally, nuclear localization of MMP28-GFP is necessary to rescue twist and sox10 expression in MMP28 morphants, and ChIP-PCR experiments suggest direct interactions between MMPs and the proximal promoters of several neural crest genes. These results have significant implications on the field of EMT and highlight an underappreciated role for MMPs as direct regulators of gene expression.
Major comments:
Overall, the experiments presented in this study are thoroughly controlled and the results are clearly quantitated and rigorously analyzed. Most claims are well supported by multiple lines of experimental evidence; however, there are a few experiments or observations that this reviewer thinks should be reconsidered for more clarity and accuracy.
- Supplementary Figure 1 shows the effect of MMP28-MOspl on additional ectodermal markers and shows that there is a significant loss of six1 expression from the placodal domain following MMP28 knockdown. The authors note this as a "slight reduction" on line 95, but since this shows a larger reduction in gene expression than some of the neural crest markers (snai2, sox8, foxd3), this reviewer thinks these results warrant a more significant discussion in this study. Does MMP28 localize to the nucleus of placodal cells as it does with neural crest? If so, is it through interaction with the six1 proximal promoter? If MMP28 does not localize to the nucleus, that would suggest MMP28 function with a different mechanism between epithelial cells distinct from role in EMT. These questions could be addressed by analysis of the placode cells in the images in Figure 5 and use of primers against the six1 proximal promoter on any remaining samples from the ChIP experiment.
- In Figure 2c, the authors rescue MMP28-MOatg with injection of MMP28wt mRNA. Does the MOatg bind to the exogenous mRNA? If so, this may just reflect titration of the MOatg. If this is the case, this experiment should be repeated with MOspl instead of MOatg.
- Is there a missing data point in Figure 2d corresponding to the upper bounds of the whisker in the 6 hour time point for the MMP28-MOatg dataset?
- The authors present ChIP-PCR results in Figure 7 as the major evidence to support the mechanism of nuclear MMP28 in regulating neural crest EMT through physical interaction with target gene promoters. However, the experimental design and presentation in Figure 7 are somewhat unconventional, and as such, difficult to interpret. First, instead of displaying the band brightness across the gel, the authors should normalize their bands to their negative GFP control, thus allowing for interpretation as a "fold enrichment over GFP control". It would be most clear to present these results in the form of a plot similar to Shimizu-Hirota et al., 2012, Figure 6D. Using qPCR instead of gel-based quantitation would further increase reproducibility by removing any bias in image analysis. Second, a proximal promoter sequence represents only ~250 bp upstream from the transcriptional start site. What is the rationale for testing multiple loci up to 3 kb upstream? It is surprising to see that most of these proteins do not show significant enrichment to a particular locus across this ~3 kb territory, while this reviewer would expect to see enrichment close to the TSS that quickly is lost as you move further upstream. Can you explain why MMP28, MMP14, and often Twist, show similar enrichment across this long genomic region? Third, the authors should include additional genomic loci to act as negative controls. For example, E-cadherin was unaffected by MMP28-MOspl, thus there may be no physical interaction between the E-cadherin locus and MMP28. It would be ideal to display results from at least one neural crest-related and one non-neural crest-related gene. Finally, this experiment requires statistical analyses to increase confidence in these interactions.
Minor comments:
- The authors should expand their abstract to more explicitly describe the experiments and results presented within this study.
- In the introduction, line 57 is unclear. "MMP28 is the latest member..." Is this chronologically? Evolutionarily? After this, the authors' statement that the roles of MMP28 are "poorly described" (lines 59-60) seems contradicting with their next sentences citing several studies that document the roles of MMP28 in diverse systems.
- To increase clarity, the authors should define which cell types are labeled by in situ hybridization for sox10 and foxi4.1 in Figure 1e.
- The PCR analysis for mmp28 splicing shown in Figure 1g is very clear and well demonstrates the efficacy of the MMP28-MOspl. However, the authors should note in the figure legend what the "ODC" row represents as this is unclear.
- On line 118 the authors first reference "MOatg" but should explicitly define this reagent and its mechanism of action for clarity.
Referee Cross-commenting
As with Reviewer #1, I was surprised that the RT-PCR analysis presented in support of the splicing MO lacked retention of intron one. I reasoned this might be due to reduced transcript abundance through a mechanism such as nonsense-mediated decay, but I agree that this data raises questions that the authors should address.
I also agree with the other comments from Reviewers 1 and 3.
Significance
This study by Gouignard et al. provides compelling evidence for the role of MMP28 during neural crest EMT. As neural crest cells share similar EMT and migration mechanisms with cancer progression, they represent a powerful system in which to study these biological processes in vivo. Previous work on MMP function has focused primarily on extracellular matrix remodeling and the effect on cell migration, with less attention given to the role of MMPs during EMT. More recent reports in other systems have begun to elucidate a role for MMP translocation into the nucleus, indicating a surprising and novel mechanism for these proteins. This work would be of particular interest to audiences interested in cancer, cell, and developmental biology, as it highlights the importance of the non-canonical function of metalloproteinases during EMT and migration.
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Referee #1
Evidence, reproducibility and clarity
This manuscript by Gouignard et al., reports that a matrix metalloproteinase MMP28 regulates neural crest EMT and migration by transcriptional control rather than matrix remodeling. The manuscript is clearly written and provides sufficient evidence and control experiments to demonstrate that the MMP28 can translocate into nucleus of non-producing cells and that nuclear localization and catalytic activity are essential for the activity of MMP28 to regulate gene transcription. ChIP-PCR analysis also suggests that MMP28 can bind to the proximal promotors of Twist and others. However, since weak binding is also detected between MMP14 and the promoters, a more direct evidence that such binding can indeed promote Twist expression will be more appreciated.
While the nuclear translocation and transcription regulation activity of MMP28 is clearly the focus of the study, there are some minor issues that should be further clarified in the functional studies in the earlier part of the manuscript.
First, the effect of the splicing MO is somewhat unexpected. I would think that the splicing MO would lead to the retention of intron one and therefore premature termination or frameshift of the protein product, but RT-PCR or RT-qPCR suggest that there is no retention of intron 1, but a reduction in the full-length transcript, exon 1, or exon 7-8. Why is that?
Second, the effect of the splicing MO and ATG MO in NC explant spreading seems to be somewhat different, with ATG MO strongly repressed explant spreading, cell protrusion, and cell dispersion, while splicing MO does not affect cell dispersion, but affects the formation of cell protrusions. Does this reflects different severity of the phenotype or does the product of splicing MO display some activity? Also, the switch between ATG MO and splicing MO is a bit confusing, maybe it is better to keep splicing MO only in the main text and move results involving ATG MO to supplementary studies.
Lastly, in Figure 3C and 3J, it says that the distance of migration or explant areas were normalized to CMO, while normalization against the contralateral uninjected side, or explant area at time 0 makes more sense.
Referee Cross-commenting
I agree with comments from both Reviewers 2 and 3, especially that whether MMP28 regulates placode development (through Six1 expression) should be addressed.
Significance
This work provides novel insights of how a metalloprotease that is normally considered to function extracellularly can transfer into the nucleus of neighboring cells and regulate transcription. This would be of interest to researchers studying EMT, cell migration, and the functions of extracellular proteins in general. My expertise is in neural crest EMT and migration, and cytoskeletal regulation of cell behavioral changes. I do not have enough background on biochemical analysis.
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Reply to the reviewers
1. General Statements [optional]
*All three referee reports are very supportive. The referees acknowledge the insight obtained for NF2 tumor suppressor function, and they state unanimously that the appeal to the broader audience stems from the systematic deep mutational scanning approach employed. *
Indeed, the goal of the study was to utilize conformation dependent NF2 protein interaction partners as a read out in deep mutational scanning interaction perturbation, which lead to the identification of an novel region, the F3 part of the FERM domain, important for NF2 conformation. The referees recognized the advance of the study and provided constructive feedback with excellent opportunities to improve the manuscript.
*The points raised by the referees relate to the deep scanning analyses which needs additional explanations. Referee 1 has several comments with respect to experimental details, which we will address through text revisions and addition of data. Referee 2 suggests to include the Y2H in full (as supplemental part) and asks for more methodological discussion. We plan to include the data and will provide a new advantage / disadvantage discussion section for the deep scanning results. This is in line with Referee 3 who similarly says that “the deep mutational scanning interaction perturbation assay … message is somewhat lost in the main text”. *
2. Description of the planned revisions
Referee 1:
In his/her first point the referee asks about justification of the use of the kinase in the Y2H experiments. Here we will report in more detail which kinases were used, in fact it was a discovery that ABL2 in contrast to all others tested did promote the NF2-PIK3R3 interaction. However, in the manuscript we provide evidence that the kinase dependency does not necessarily relate to NF2 phosphorylation. Rather we find mutations that relieved the PIK3R3-NF2 interaction from the kinase dependency. We show that the kinase promotes the PIK3R3 dimerization. We will make this point more clear in text revisions.
We want to address the minor points 1-3 and 6-8 through revisions in the text, as we feel confident that the points can be addressed through better explanations and more detail.
*Point 4: *
We have examined expression of the YFP construct and will include the data in the revision.
*Point 5: *
We will reexamine the fluorescence images and provide better resolution pictures. Depending on the data we have, this may include new data were we record the localization of the NF2 variants again at higher resolution.
Referee 2:
Point 1: The bait construct which is missing from the panel was tested, but is autoactive and therefore the result can not be included in the figure. This will be clearly stated in the manuscript.
*Point 2: The methodological part of the paper is important, however we failed to provide a discussion on the deep scanning result and agree that a critical discussion of advantages and disadvantages is warranted. *
Minor points 1,2,4,5,6,7,9,10,12,13,14,15 can be addressed in full through text revisions.
Point 3: Data will be added to supplemental Figure S1, however as we mentioned in the main text, the Iso1N and Iso7N, when used as prey do not result any interactions.
Point 8: Taking the suggestion of the referee on board, we will provide a new Supplemental figure showing all variants that did not change the interaction patterns.
*Point 11: We will fix the inconsistencies in Figure 5. We will include Q147 in the overall structure, S265 is a surface residue providing little structural information. *
Referee 3:
We thank referees 3 for their time and effort providing an assessment as experts on the molecular and clinical aspects of NF2.
In response to the comments, we will strengthen the deep mutational scanning message through a new critical discussion part and fix the mistakes pointed at in the text.
*We agree with the referees that “The use of isoform 7 as a construct is helpful to locate protein binding regions, but its physiological relevance is unclear.” This is exactly the point, to use a non-tumor suppressive isoform as a construct contrasting the binding behavior of the canonical isoform 1. We tried to summarize the knowledge about the non-canonical isoforms in the introduction (page2 bottom to page 3 top paragraph) as well as in Supplemental Figure 1. Unfortunately literature information is sparse. *
Finally, we will check carefully (again) whether we used isoform 1 numbering throughout the manuscript.
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Referee #3
Evidence, reproducibility and clarity
Summary:
The authors developed a deep mutational scanning interaction perturbation technique, based on reverse yeast two-hybrid analysis, to identify important regions influencing conformation dependent protein function in NF2.
They test the tumor suppressive NF2 isoform 1 and a shorter non-tumor suppressive isoform 7 (lacking exons 2 and 3 and containing exon 16 instead of 17) and find three interacting proteins, KDM1A, EMILIN1 and PIK3R3 (KDM1A and EMILIN1 have been identified previously). They map binding regions of these proteins using fragments of NF2 isoforms 1 and 7 and by large-scale interaction perturbation mutation scanning.
Major comments:
The main scientific advancement in the study is the development of the deep mutational scanning interaction perturbation assay, but this message is somewhat lost in the main text of the results.
The relevance of the binding protein that did not bind isoform 1 is unclear (PIK3R3) and the relevance of characterising the binding domains for three proteins with an unknown function is not made clear. Were these the only binding partners identified in the yeast screen? The use of isoform 7 as a construct is helpful to locate protein binding regions, but its physiological relevance is unclear. Does it have known expression or a known function in human cells?
Minor comments:
Nomenclature should be updated in line with the new guidelines (i.e. NF2 vs neurofibromin)
The two major isoforms are 1 and 2, differentiated by their C-terminal region (exon 17 or Exon 16). It would be helpful to describe protein binding regions using the amino acid numbering of the full-length transcripts throughout the manuscript, rather than using isoform 7 numbering in some sections.
"Closeness", should perhaps be changed to closed-ness
The significance of the RT4-D6P2T and HEI-193 cell lines should be explained/indicated in the text.
PPI should be expanded at first use.
Results are included in the context of previous studies, but it needs to be made clearer in some places which results were found in previous studies and which were identified in the current study.
Specific recommendations
- 'NF2 (Neurofibromine 2, merlin)' -delewte 'neurofibromine' this has been deleted by HGNC
- 'Genetic mutations or deletion of NF2 cause neurofibromatosis type 2,' -Replace neurofibromatosis type 2 with NF2 related-schwannomatosis and cite Legius et al Genet Med 2022
Referees cross-commenting
I cannot see any changes to this manuscript. In particular the terms 'neurofibromine' and neurofibromatosis should be deleted
Significance
The authors developed a deep mutational scanning interaction perturbation technique, based on reverse yeast two-hybrid analysis, to identify important regions influencing conformation dependent protein function in NF2.
They test the tumor suppressive NF2 isoform 1 and a shorter non-tumor suppressive isoform 7 (lacking exons 2 and 3 and containing exon 16 instead of 17) and find three interacting proteins, KDM1A, EMILIN1 and PIK3R3 (KDM1A and EMILIN1 have been identified previously). They map binding regions of these proteins using fragments of NF2 isoforms 1 and 7 and by large-scale interaction perturbation mutation scanning.
The main scientific advancement in the study is the development of the deep mutational scanning interaction perturbation assay, but this message is somewhat lost in the main text of the results.
Dr Smith and Professor Evans are experts on the molecular and clinical aspects of NF2
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Referee #2
Evidence, reproducibility and clarity
Summary
In this manuscript the authors describe the use of a reverse Y2H-based, systematic mutational analysis method to study effects on conformation-dependent interactions of the NF2 tumor suppressor protein. Using this approach, they identified regions important for NF2 protein interaction and homomer formation and correlated some of these with cellular proliferation and matched patterns of known disease mutations. Overall, this work provides useful insight into NF2 tumor suppressor function (by identifying amino acids critical for NF2 conformational regulation) while demonstrating the power of their mutational scanning approach.
Major Comments
- Why does Figure 1b not include interaction results for the NF2-Iso1N fragment as bait? Did the authors test this?
- The authors state that the majority of retested interactions behaved like WT (i.e., could not be confirmed; page 7 last paragraph) and claim this may be due to a difference in sensitivity between the deep scanning screen and pair wise spot testing. This seems like a very vague justification for the differences between the two assays; also, it's not immediately clear to me that the high-throughput scanning assay would necessarily be more sensitive than the lower-throughput pairwise comparison assay. The authors should provide a bit more discussion on this and address the possibility of false positives in their deep mutational scanning assay.
Minor Comments
- Page 4, Line 3 from the bottom - should ready 'three isoform-specific protein interaction partners' not 'partner'.
- In Figure 1b, the interaction of NF2-Iso7-ex17 with PIK3R3 in the absence of ABL3 suggests that the observed kinase-dependence interaction of the NF2-Iso7 form may actually not be solely due to PIK3R3 homodimerization driven by phosphorylation. The authors should make note of this possibility in the text.
- On page 5 the authors mention that Iso1N and Iso7N, when used as preys, did not interact with full-length NF2. I don't see this experiment in the figures, however.
- On Page 6 (first paragraph) the authors state that the PIK3R3 interaction was 'promoted through pY-dependent PIK3R3 homodimerization'. While this is a likely and reasonable conclusion, they haven't explicitly shown this, so they should be careful about making such a strong statement. I'd recommend saying 'likely promoted' or something similar instead.
- In Figure S2, the Iso7 / EMILIN1 interaction does not appear to be giving the expected result in the rY2H (i.e., there is strong growth under both Y2H and r2H conditions). The authors should comment on/acknowledge this.
- For the deep mutagenesis screen, why wasn't an ABL2 condition used for NF2-Iso1C (see Fig. S2b)?
- For KDM1A and EMILIN1 the authors ran mutagenesis screens with both active and kinase dead ABL2, yet results were pooled. Were any differences observed in the effects of mutations on interaction between the two kinase conditions?
- Why aren't the yeast plates shown for most of the unconfirmed interactions? These could still be included in the Supplementary Material.
- On page 7, under Assessing Single Site Mutations, the authors refer to the Q147E mutation and reference Figure 3. However, Figure 3 shows only a Q147A mutation. Q147A is also referred to elsewhere. Which is the correct mutation?
- Figure S3b shows the 20 mutations presented in Figure 3. The DMS row indicates that some of these did not produce perturbations in the DMS experiments. Perhaps I'm misunderstanding here, but weren't the 20 mutations shown (and 60 total mutations) selected based on activity in the DMS assay? Or did some of the ones selected correspond to mutations which not produce an effect? Please clarify in the text.
- Why was the S265 mutation not considered in the structural analysis (other than being shown in Figure 4a, it isn't discussed). Also, Q147 (in the F2 region) is discussed and shown in Figure 4b, but not shown in the larger overall structure in Figure 4a.
- The cell proliferation results are very difficult to meaningfully interpret. While it is clear that certain mutations do affect proliferation, consistency between different types of experiments and cell lines appears to be low.
- Perhaps a bit more discussion of the possible consequences of using yeast to study human NF2 interactions and how these might affect results would be useful (i.e., due to differences in membrane composition, cellular environment, post-translational modifications etc. between yeast and mammalian cells).
- Page 13, line 10 says 'your hypothesis'. Believe should read 'the hypothesis'.
- Page 13, line 15 refers to '15' NF2 variants showing altered PPI patterns; however, 16 were described in the manuscript.
Significance
This work provides insight into how NF2 conformational changes relate to tumor suppressor function, which is particularly valuable since this area is still not well understood and published results have sometimes appeared contradictory. In addition to the insights into NF2 biology provided, the manuscript also demonstrates the value of the deep scanning mutagenesis approach. Overall, the presented research is very solid and, assuming the comments presented above (most of which are minor) are addressed I have no trouble recommending it for publication.
I believe that the NF2 biology section will be of interest to a more specialized audience, while the general demonstration of the utility of the deep scanning mutagenesis will have broader appeal.
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Referee #1
Evidence, reproducibility and clarity
The manuscript "Missense variant interaction scanning reveals a critical role of the FERM-F3 domain for tumor suppressor protein NF2 conformation and function" examines the effect of a reasonably exhaustive set of point mutations on the NF2 protein on protein-protein interactions and intra-protein interactions for two isoforms of NF2 (1 and 7), finding an interesting pattern of mutations in the region not associated with bindings nevertheless impact binding, and that this binding is sometimes dependent on the presence of kinase ABL2. Authors justify this by arguing conformation shifts in the protein, potentially regulated by phosphorylation, and with distinct conformations between isoforms 1 and 7 creating different interaction patterns, must explain the differences in binding properties. The paper specifically examines mutations to phosphomimetic (i.e., charged, so as to mimic phosphorylation) amino acid residues, with relevance for the probable biological regulation of this binding. Authors note that previous work has found inconsistent protein binding properties for phosphomimetic or phosphor-inhibiting substitutions on S518, in different conditions, which would be explained by other regulation of these conformational changes, a reasonable argument. Structural modeling of the mutants and their potential effects on a "closed" NF2 structure are intriguing and well-appreciated to support the paper's conclusions, and the paper is overall well-reasoned and convincing, and it should be published.
Concerns:
The kinase ABL2 is used to perturb NF2 phosphorylation, and this is not adequately justified. Kinases such as PAK2 (PMID: 11782491, PMID: 11719502) and PKA (PMID: 14981079) target NF2. In the methods referred to (Grossmann et al), nine tyrosine kinases were used for their screen, and while ABL2 was used in this paper and generated numerous interactions, it is not clear that ABL2 is the appropriate kinase to use here. The exhaustive use of many kinases would obviously be impractical and unreasonable for this study, but the choice of this kinase should be clearly explained.
Minor issues:
- In the intro, authors write "While the other ERM protein family members do not have activities directly linked to cancer, NF2 tumor suppressor activity was initially characterized in flies and mice". While "directly" makes the statement technically true, it could be argued that ERM protein involvement is as legitimate as the tumor suppression activity of NF2 (PMID: 11092524, PMID: 24421310), and therefore the suggested contrast is slightly misleading. This has no relevance to the broader paper or its findings.
- Figure 2b: Authors state mutational coverage is fairly even across the protein, however there appears to be a notable spike around a.a. 180? This does not match any of the site mutations later found to be particularly relevant for interactions, which cluster around 250 and 450, and is therefore not a significant issue.
- In the methods, cell concentration is at one point said to be 'concentrated to an OD600 of 40-80'. I have never seen cell concentration expressed this way. Authors no doubt grew cells to an OD between 1 and 2 and concentrated ~40-fold as is standard, and wish perhaps to avoid estimating concentrations as cell numbers, which would only be approximate and cell size-dependent? However, OD is only linear between 1 and 2 for cell concentrations. An OD above 4 simply cannot be observed, as all light would be blocked. Methodology here is sound, this is merely an unusual way of expressing things.
- Page 10: The authors point out that they cannot see any difference in the expression levels of the NF2 mutants. However there is no quantification of the immunofluorescence signal supporting this information. Maybe a western blot could suffice this argument.
- It is very difficult to see the localization of NF2 mutants with the immunofluorescence images as they are very small. May be try with a 63X objective or focusing on just one or two cells or adding insets with higher magnification would allow the reader to view the details of Nf2 localization.
- 5th line from the bottom on page 8: allowed to model -> allowed us to model
- Line 8 from the top on page 12: inY2H -> in Y2H
- Line 10 from the top on page 13: your hypothesis -> our hypothesis
Significance
Dear Editor,
The manuscript "Missense variant interaction scanning reveals a critical role of the FERM-F3 domain for tumor suppressor protein NF2 conformation and function" examines the effect of a reasonably exhaustive set of point mutations on the NF2 protein on protein-protein interactions and intra-protein interactions for two isoforms of NF2 (1 and 7), finding an interesting pattern of mutations in the region not associated with bindings nevertheless impact binding, and that this binding is sometimes dependent on the presence of kinase ABL2. Authors justify this by arguing conformation shifts in the protein, potentially regulated by phosphorylation, and with distinct conformations between isoforms 1 and 7 creating different interaction patterns, must explain the differences in binding properties. The paper specifically examines mutations to phosphomimetic (i.e., charged, so as to mimic phosphorylation) amino acid residues, with relevance for the probable biological regulation of this binding. Authors note that previous work has found inconsistent protein binding properties for phosphomimetic or phosphor-inhibiting substitutions on S518, in different conditions, which would be explained by other regulation of these conformational changes, a reasonable argument. Structural modeling of the mutants and their potential effects on a "closed" NF2 structure are intriguing and well-appreciated to support the paper's conclusions, and the paper is overall well-reasoned and convincing, and it should be published.
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Reply to the reviewers
Response to reviewers' comments
We thank the reviewers for their constructive evaluation of our manuscript. In the following point-by-point response, we explain how we will implement the suggested modifications.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary:
The formation of meiotic double-stranded DNA breaks is the starting point of meiotic recombination. DNA breaks are made by the topoisomerase-like SPO11, which interacts with a number of regulatory factors including REC114, MEI4 and IHO1. Despite the key role this process has in the continuation, and genetic variation, or eukaryotic life, there is very little known about how this process is regulated. Laroussi et al make use of biochemical, biophysical and structural biological approaches to extensively characterise the REC114-MEI4-IHO1 complex.
This is an outstanding biochemical paper. The experiments are well planned and beautifully executed. The protein purifications used are very clean, and the figures well presented. Importantly Laroussi et. al describe, and carefully characterise through point mutational analysis, the direct physical interaction between IHO1 and REC114-MEI4. This is an interaction that has, at least in yeast, previously been suggested to be driven by liquid-liquid separation. The careful and convincing work presented here represents an important paradigm-shift for the field.
I am fully supportive of publication of this excellent and important study.
We thank the reviewer for his/her positive comments, appreciation of the importance of our study and suggested modifications.
Major comments:
Point 1:
My only major concern is regarding Figure 4, and specifically the AF2 model of the coiled-coil tetramer of IHO1. Given the ease with which MSAs of coiled-coils can become "contaminated" with non-orthologous sequences, I would urge some caution with this model. This is especially since the yeast ortholog of IHO1, Mer2, has been previously reported to be an anti-parallel tetramer (albeit, not very well supported by the data). The authors have several choices here. 1) They could simply reduce the visibility of the IHO1 tetramer model, and indicate caution in the parallel tetramer model. 2) They could consider using a structure prediction algorithm that doesn't use an MSA (e.g. ESMFold). 3) They could try to obtain experimental evidence for a parallel coiled-coil tetramer, e.g. through EM, SAXS or FRET approaches. I would like to make it crystal clear, however, that I would be *very* supportive of approach 1) or 2). An experimental approach is *not* necessary.
Assuming the authors don't take a wet-lab approach, this shouldn't take more than a couple of weeks.
This is a very good suggestion. We are aware of the previously reported anti-parallel architecture of the yeast IHO1 ortholog Mer2 (Claeys Bouuaert et al., Nature 2021). It should be noted, that in the recent preprint, posted by the Claeys Bouuaert lab (BioRxiv, https://doi.org/10.1101/2022.12.16.520760), a high confidence model of yeast Mer2 (and for human) parallel tetrameric coliled-coil is presented, apparently consistent with their previous XL-MS results (Claeys Bouuaert et al., Nature 2021).
To clarify this issue we will follow the suggestions of Reviewer 1 and 2.
- As suggested also by Reviewer 2, we will produce a tethered dimer of IHO1125-260, connected by a short linker and determine its MW by SEC-MALLS (and SAXS).
- In the meantime we followed the suggestion of Reviewer 1 and modelled the IHO1130-281 by the ESMfold, which is another recent powerful AI-based program that does not use multiple sequence alignments. Remarkably, the predicted structure is very similar to the one predicted by AlphaFold, also predicting the parallel arrangement of IHO1. This model will be included as a supplementary figure.
- We will also point out in the text that these models, despite being very convincing, remain models.
Minor comments:
Point 2:
The observation that REC114 and MEI4 can also form a 4:2 complex is very interesting and potentially important. Did the authors also try to model this higher order complex in AF2?
Yes, we did this with the hope that we could identify residues whose mutation could limit the fast exchange between the 2:1 and 4:2 states. Unfortunately, no convincing additional contacts are modelled by AlphaFold. This PAE plot will be included as a supplementary figure.
Point 3:
Similarly to above, what does the prediction of the full-length REC114:MEI4 2:1 complex look like? Presumably the predicted interaction regions align well with experimental data, but it would be interesting to see (and easy to run).
The AlphaFold modelling of the FL REC114:MEI4 (2:1) complex will be included as supplementary figure. It is consistent with the model comprising only the interacting regions. No additional convincing contacts are predicted.
Point 4:
Did the authors carry out SEC-MALS experiments on any IHO1 fragment lacking the coiled-coil domain? It was previously reported for Mer2 that the C-terminal region can form dimers, for example (OPTIONAL).
We can easily do that. We have the N- and C- terminal regions lacking the coiled-coil expressed as MBP fusions and they will be analysed by SEC-MALLS.
Point 5:
Given that full-length REC114 is used for the IHO1 interaction studies, do the authors have any data as to the stoichiometry of the REC114FL-MEI41-127 complex? (OPTIONAL)
We have repeatedly analysed the REC114-MEI4-IHO1 complex sample by SEC-MALLS and native mass spectrometry, but in both cases the sample is too complex to be interpreted. This is like due to the fast exchange between REC114-MEI4 2:1 and 4:2 complexes and low binding affinity of IHO1 for REC114.
Point 6:
Did the authors try AF2 modelling of the REC114-IHO1 interaction using orthologs from other species?
Yes, but not extensively. We will repeat this modelling again.
**Referees cross commenting**
I will add cross-comments to the comments of Reviewer #2
Firstly, the comments made by Reviewer #2 are technically correct. Firstly, reviewer #2 points out that the oligomerization states that the authors report could, in part, be artifactual the based on the his-tag purification method. This is indeed correct. However, given that none of the oligomerization states reported are per se unusual, given what is already known (including pre-prints from the Keeney and Claeys Bouuaert laboratories), I think the authors could forego this step.
Secondly, the use of an experimental structural method, such as SAXS, would certainly add value to the paper. Also Reviewer #2 is correct in pointing out the availability of the ESRF beamlines to the authors. However, while SAXS is a useful method, I personally consider the use of mutants to validate the interactions, an even stronger piece of evidence that the AlphaFold2 interactions are correct. I must disagree somewhat with Reviewer #2 with their argument that SAXS would validate the fold. Certainly if one of the AF2 predicted structures is radically wrong, then SAXS would produce scattering data, and a subsequent distance distribution plot that is incompatible with the AF2 model. However, a partly correct AF2 model, of roughly the right shape, might still fit into a SAXS envelope.
Reviewer #2 shares my concern on the parallel coiled-coil of IHO1, and their suggested solution is very elegant.
In my view, due to the time constraints imposed by the partially competing work from the Keeney and Claeys Bouuaert laboratories (recently on biorxiv). I would support the authors if they chose the quickest route to publication.
Reviewer #1 (Significance (Required)):
General assessment: The strengths of the paper are as follows:
1) Quality of experiments - The proteins used have been properly purified (SEC) and properly handled. The experiments are carefully carried out and controlled.
2) Detail - The authors carry out the considerable effort of characterising protein interactions. through separation-of-function mutants. This adds to the quality of the paper, and renders the AF2 models as convincing as experimentally determined structures
3) Conceptual advances - The most important conceptual advance is the direct binding of the N-term of IHO1 to REC114. That this is the same region as used by both TOPOVIBL and ANKRD31 points to a complex regulation.
4) Integrity - the authors have taken great care not to "oversell" the results. The data are presented, and analysed, without hyperbole.
Limitations - The only limitation of the paper is the lack of in vivo experiments to test their findings. However given the time and effort required, and the pressing need to publish this exciting study, this is not a problem.
Advance: The paper provides advances from a number of directions, both conceptual and mechanistic. Mechanistically the description of the REC114-MEI14 complex is important, and in particular the observation that it can also form a higher order 4:2 structure. Likewise, while IHO1 was inferred to be a tetramer (based on work on Mer2) this was never proven formally. Most importantly, is the physical linkage between IHO1 and REC114, and that this is an interaction that is incompatible with TOPOVIBL and ANKRD31.
Audience:
Given the central role of meiotic recombination in eukaryotic life, any studies that shed additional light on the regulation of meiosis are suitable for a broad audience. However, this subject paper will be more specifically of interest to the meiosis community. The elegant methodology will also be of interest to structural biologists and protein biochemists.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
This manuscript addresses the structure of the REC114-MEI4-IHO1 complex, which controls the essential process of programmed DSB induction by SPO11/TOPOVIBL in meiosis.
The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.
We thank the reviewer for his/her positive comments on our study and the suggestions below.
I have two general suggestions:
Point 1:
Analyses have been performed on fusion proteins (His, His-MBP etc). we have previously observed that bulky tags such as MBP can interfere with oligomeric state through steric hindrance, and that His-tags can mediated formation of larger oligomers, seemingly through coordination of metals leached from IMAC purification. This latter point has also been observed by others
https://www.sciencedirect.com/science/article/pii/S1047847722000946.
Where possible, I would repeat SEC-MALS experiments using untagged proteins, or at least following incubation with EDTA to mitigate the potential for His-mediated oligomerization.
We agree with this reviewer’s comment that expression tags can have unexpected impact of the protein behaviour.
- For REC114-MEI4 complex the stoichiometry is assessed by several techniques. Figure 1f,g shows analytical ultracentrifugation, which was performed on the minimal REC114226-254-MEI41-43 complex that contains no fusion tag showing that this stoichiometry is independent of fusion tags. We will nevertheless repeat the SEC-MALLS on REC114-MEI41-127 after removing the His-tag of MEI4 as suggested.
- For the REC114 dimer, we cannot remove the His-MBP tag since this short fragment of REC114226-254 is no stable without MBP. The dimerization of Rec114 was already reported in (Claeys Bouuaert et al., Nature 2021). The dimerization is sensitive to specific point mutations within REC114. We will however, repeat the SEC-MALLS experiment following incubation with EDTA to mitigate the potential for His-mediated oligomerization.
- The presented SEC-MALLS on IHO1 fragments (Figure 4b) was done on proteins without fusion tags. Reviewer 1 and 2 also agreed that additional repeats of the experiments without fusion tags are not necessary.
The authors have relied upon mutagenesis to validate Alphafold2 models. Their results are convincing but only confirm that contacts involved in structures rather than the specific fold per se. Their finding would be greatly strengthen by collecting SEC-SAXS data and fitting models directly to the scattering data. This is extremely sensitive, so a close fit provides the best possible evidence of accuracy of the model. SAXS is affected by unstructured regions and tags, so would have to be performed using structural cores of untagged proteins rather than full-length constructs. Given the local availability of world-class SAXS beamlines at the ESRF, which is next door to the leading author's institute, it seems that the collection of SAXS data would be practical for them.
The usage of SAXS is discussed in the specific points below. We will attempt to do SEC-SAXS on the REC114-MEI4 complex. Due to instability of REC114226-254 without MBP, SAXS cannot be done. We will also do SAXS on the IHO1 tetramer.
My specific comments are below:
Point 2:
Figure 1d
The SEC-MALS shows multiple species, with 2:1 and 4:2 representing a minority of total species present. What are the larger oligomers? Could these be an artefactual consequence of the His-tags (as described above)?
This SEC-MALLS will be repeated without the His-tag on MEI4.
Point 3:
Figure 1f,g
The AUC changes over concentration and pH are intriguing - have they tried MALS in these conditions? This would be much more informative as it would reveal the range of species present. Low concentrations could be analysed by peak position even if scattering is insufficient to provide interpretable MW fits. I would advise doing this without his tag or adding EDTA (as described above).
We will perform this experiment as suggested.
Point 4:
Figure 2
I would like to see the models validated by SAXS using minimum core untagged constructs. This could be sued to test the validity of the 2:1 model directly, and to model the 4:2 complex by multiphase analysis and/or docking together of 2:1 complexes.
The hydrophobic LALALAII region of MEI4 is interesting and the mutagenesis data do agree with the model. However, it is important to point out that any decent model would place this hydrophobic helix in the core of the complex, and so would be disrupted by mutagenesis. Hence, the mutagenesis results confirm that the hydrophobic helix is critical for the interaction, but does not confirm that the specific alphafold model is more valid than any other model in which the helix is similarly in a core position.
We will attempt to perform the SEC-SAXS measurements. The challenge here will be obtaining a sample that is monodisperse in solution being required for SAXS. We showed the fast exchange between the 2:1 and 4:2 oligomeric state. The AUC data indicates that the sample has a predominantly 2:1 stoichiometry at 0.2 mg/ml, pH 4.5 and 500mM NaCl. Given the small size of the complex, the signal at 0.2 mg/ml is likely to be noisy.
Point 5:
Figure 3
This would also benefit from SAXS validation of the structural core. The mutagenesis here provides convincing evidence in favour of the structure as specific hydrophobics ether disrupt or have no effect, exactly as predicted. Hence, their data strongly support the dimer model. As this provides the framework for the 2:1 complex, these data make me far more confident of the previous 2:1 model in figure 2. I am wondering whether it would be better to present these data first such that the reader can see the 2:1 model being built upon these strong foundations?
We agree with this suggestion and will present the REC114 dimerization data before the REC114-MEI4 complex. However, REC114226-254 is not stable without the MBP tag so is not suitable for SAXS analysis.
Point 6:
Figure 4
The MALS data convincingly show formation of a tetramer. How do we know that it is parallel? The truncation supports this but coiled-coils do sometimes form alternative structures when truncated (e.g. anti-parallel can become parallel when sequence is removed), and alphafold seems to have a tendency of predicting parallel coiled-coils even when the true structure of anti-parallel (informal observation by us and others). A simple test would be to make a tethered dimer of 110-240, with a short flexible linker between two copies of the same sequence - if parallel it should form a tetramer of double the length, if anti-parallel it should form a dimer of the same length - determinable by MALS (and SAXS).
To address this point we will perform this experiment as suggested by Reviewer 2. We will produce a tethered dimer of IHO1 110-240, connected by a short linker and determine its MW by MALS (and possibly SAXS). We also performed ESMfold modelling (Reviewer 1, Point 1), resulting in the same model. As the IHO1 tetramer is likely suitable for SAXS analysis, we will also perform SAXS on it.
Point 7:
Figures 5/6
The interaction is clear albeit low affinity (but within the biologically interesting range). It would be nice to obtain MALS (using superose 6) data showing the stoichiometry of the complex - are the data too noisy to be interpretable owing to dissociation? The alpahfold model and mutagenesis data strongly support the conclusion that the IHO1 N-term binds to the PH domain, as presented.
We have repeatedly analysed the REC114-MEI4-IHO1 complex sample by SEC-MALLS (on Superose 6) and native mass spectrometry, but in both cases the sample is too complex to be interpreted. This is likely due to the fast exchange between REC114-MEI4 2:1 and 4:2 complexes and low binding affinity of IHO1 for REC114.
**Referees cross commenting**
Just to clarify a couple of points regarding consultation comments from reviewer 1:
The suggestion regarding tags was mostly directed to the cases in which MALS data are noisy, with multiple oligomeric species (such as figure 1d). In these cases, i wondered whether the large MW species may be artefactual and could be resolved by removal of the tags. In cases where oligomers agree with those reported by other labs, I agree that there's no need to explore these further.
In terms of SAXS, I agree that fitting models into envelopes will not distinguish between similar folds. However, fitting models directly to raw scattering data is extremely sensitive and I have never seen good fits with low chi2 values for incorrect models (even when very similar in overall shape to the correct structure).
Reviewer #2 (Significance (Required)):
The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Laroussi et al used Alphafold models to predict the assembly of REC114-MEI4-IHO1 complex, and verified the structure using different biochemical experiments. Both Alphafold predictions and experiment data are convincing for the overall protein complex assembly. Importantly, they identified a motif on IHO1 that share the same binding site on REC114 with TOPOVIBL and ANKRD31, suggesting that REC114 acts as a regulatory base coordinating different binding partners during meiosis progression. Overall, I believe this is a nice biochemistry paper, but lacks insights into the biology (I believe those in vivo data is beyond the scope of this paper), at least more discussions are needed in terms of these findings.
We thank the reviewer for the supportive comments on our manuscript and its evaluation. We agree with the reviewer, that including in vivo data, that might provide further biological insights, would be useful. However, there is currently no good cellular model for meiotic recombination in mouse and thus our structure-based mutations will need to be tested in transgenic mice. Such data will take a long time to obtain and would delay the publication these in-vitro results that already provide novel insight into the REC114-MEI4-IHO1 complex architecture. We will, nevertheless, as suggested, strengthen the discussion of the biological implications of our findings.
Some minor points:
Point 1:
Any data showing MEI4 forms a dimer on its own?
As mentioned in the manuscript, full-length MEI4 is difficult to produce in bacteria or insect cells. Thus, we worked with the N-terminal fragment which in absence of REC114 is nor very stable. We will perform SEC-MALLS to assess its oligomeric state. Alphafold suggests dimeric arrangement of MEI4, but only with low confidence.
Point 2:
In Fig2 and Sup Fig4, HisMBP-MEI4, you see more MBP than the fusion protein, especially more obvious in the mutants. What's your explanation?
The N-terminus of MEI4 is well produced when co-expressed with REC114. For the pull-down experiments in Figure 2 we expressed it as His-MBP fusion in absence of REC114. In this situation, there is a degradation between MBP and MEI4. We find this very often for proteins that not very stable, which is the case of MEI4 without REC114. This is the best way we could produce at least some MEI4 in absence of REC114. The MBP protein could probably be removed by other chromatography techniques, but we think that for the purpose of the pull-down its presence is not interfering with the REC114-MEI4 binding.
Point 3:
TOPOVIBL and ANKRD31, I am curious if you have looked at the conserved residues on these motifs.
We show a strong conservation of the IHO1 among vertebrates (Fig. 6c). We will further analyse the sequence conservation in more distant species.
Point 4:
Reference needed when stating that IHO1 was not interacting with REC114 in previous biochemical assay in the discussion part.
This will be corrected
Point 5:
Also, have you run AlphaFold that gives multiple models? Sometimes, with short motifs, 1 or 2 models of several models give good confidence for the interaction.
Using in-house Alphafold installation producing 25 models did not reveal better models.
Reviewer #3 (Significance (Required)):
While most of the interactions between REC114 and MEI4 or IHO1 were established with Y2H or other biochemical assays before. This paper used the AlphaFold, and finally verified the findings with biochemical experiments, which helps to establish the exact motifs/residues involved in the interaction. For example, the MEI4-REC114 interfaces are novel, more interestingly, the IHO1 shares the same interface with ANKRD31 and TOPOVIBL. Thus, this finding of REC114-MEI4-IHO1 complex assembly would be interesting to people with different working areas. I would like to see more studies on the coordination IHO1 with ANKRD31 or TOPOVIBL in the future.
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Referee #3
Evidence, reproducibility and clarity
Laroussi et al used Alphafold models to predict the assembly of REC114-MEI4-IHO1 complex, and verified the structure using different biochemical experiments. Both Alphafold predictions and experiment data are convincing for the overall protein complex assembly. Importantly, they identified a motif on IHO1 that share the same binding site on REC114 with TOPOVIBL and ANKRD31, suggesting that REC114 acts as a regulatory base coordinating different binding partners during meiosis progression. Overall, I believe this is a nice biochemistry paper, but lacks insights into the biology (I believe those in vivo data is beyond the scope of this paper), at least more discussions are needed in terms of these findings.
Some minor points:
Any data showing MEI4 forms a dimer on its own? In Fig2 and Sup Fig4, HisMBP-MEI4, you see more MBP than the fusion protein, especially more obvious in the mutants. What's your explanation? Nice finding on the IHO1 N terminus, which shares the same binding sites on REC114 with TOPOVIBL and ANKRD31, I am curious if you have looked at the conserved residues on these motifs. Reference needed when stating that IHO1 was not interacting with REC114 in previous biochemical assay in the discussion part. Also, have you run AlphaFold that gives multiple models? Sometimes, with short motifs, 1 or 2 models of several models give good confidence for the interaction.
Significance
While most of the interactions between REC114 and MEI4 or IHO1 were established with Y2H or other biochemical assays before. This paper used the AlphaFold, and finally verified the findings with biochemical experiments, which helps to establish the exact motifs/residues involved in the interaction. For example, the MEI4-REC114 interfaces are novel, more interestingly, the IHO1 shares the same interface with ANKRD31 and TOPOVIBL. Thus, this finding of REC114-MEI4-IHO1 complex assembly would be interesting to people with different working areas. I would like to see more studies on the coordination IHO1 with ANKRD31 or TOPOVIBL in the future.
-
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Referee #2
Evidence, reproducibility and clarity
This manuscript addresses the structure of the REC114-MEI4-IHO1 complex, which controls the essential process of programmed DSB induction by SPO11/TOPOVIBL in meiosis.
The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.
I have two general suggestions:
- Analyses have been performed on fusion proteins (His, His-MBP etc). we have previously observed that bulky tags such as MBP can interfere with oligomeric state through steric hindrance, and that His-tags can mediated formation of larger oligomers, seemingly through coordination of metals leached from IMAC purification. This latter point has also been observed by others https://www.sciencedirect.com/science/article/pii/S1047847722000946. Where possible, I would repeat SEC-MALS experiments using untagged proteins, or at least following incubation with EDTA to mitigate the potential for His-mediated oligomerisation.
- The authors have relied upon mutagenesis to validate Alphafold2 models. Their results are convincing but only confirm that contacts involved in structures rather than the specific fold per se. Their finding would be greatly strengthen by collecting SEC-SAXS data and fitting models directly to the scattering data. This is extremely sensitive, so a close fit provides the best possible evidence of accuracy of the model. SAXS is affected by unstructured regions and tags, so would have to be performed using structural cores of untagged proteins rather than full-length constructs. Given the local availability of world-class SAXS beamlines at the ESRF, which is next door to the leading author's institute, it seems that the collection of SAXS data would be practical for them.
My specific comments are below:
Figure 1d The SEC-MALS shows multiple species, with 2:1 and 4:2 representing a minority of total species present. What are the larger oligomers? Could these be an artefactual consequence of the His-tags (as described above)?
Figure 1f,g The AUC changes over concentration and pH are intriguing - have they tried MALS in these conditions? This would be much more informative as it would reveal the range of species present. Low concentrations could be analysed by peak position even if scattering is insufficient to provide interpretable MW fits. I would advise doing this without his tag or adding EDTA (as described above).
Figure 2 I would like to see the models validated by SAXS using minimum core untagged constructs. This could be sued to test the validity of the 2:1 model directly, and to model the 4:2 complex by multiphase analysis and/or docking together of 2:1 complexes. The hydrophobic LALALAII region of MEI4 is interesting and the mutagenesis data do agree with the model. However, it is important to point out that any decent model would place this hydrophobic helix in the core of the complex, and so would be disrupted by mutagenesis. Hence, the mutagenesis results confirm that the hydrophobic helix is critical for the interaction, but does not confirm that the specific alphafold model is more valid than any other model in which the helix is similarly in a core position.
Figure 3 This would also benefit from SAXS validation of the structural core. The mutagenesis here provides convincing evidence in favour of the structure as specific hydrophobics ether disrupt or have no effect, exactly as predicted. Hence, their data strongly support the dimer model. As this provides the framework for the 2:1 complex, these data make me far more confident of the previous 2:1 model in figure 2. I am wondering whether it would be better to present these data first such that the reader can see the 2:1 model being built upon these strong foundations?
Figure 4 The MALS data convincingly show formation of a tetramer. How do we know that it is parallel? The truncation supports this but coiled-coils do sometimes form alternative structures when truncated (e.g. anti-parallel can become parallel when sequence is removed), and alphafold seems to have a tendency of predicting parallel coiled-coils even when the true structure of anti-parallel (informal observation by us and others). A simple test would be to make a tethered dimer of 110-240, with a short flexible linker between two copies of the same sequence - if parallel it should form a tetramer of double the length, if anti-parallel it should form a dimer of the same length - determinable by MALS (and SAXS).
Figures 5/6 The interaction is clear albeit low affinity (but within the biologically interesting range). It would be nice to obtain MALS (using superose 6) data showing the stoichiometry of the complex - are the data too noisy to be interpretable owing to dissociation? The alpahfold model and mutagenesis data strongly support the conclusion that the IHO1 N-term binds to the PH domain, as presented.
Referees cross commenting
Just to clarify a couple of points regarding consultation comments from reviewer 1:
The suggestion regarding tags was mostly directed to the cases in which MALS data are noisy, with multiple oligomeric species (such as figure 1d). In these cases, i wondered whether the large MW species may be artefactual and could be resolved by removal of the tags. In cases where oligomers agree with those reported by other labs, I agree that there's no need to explore these further.
In terms of SAXS, I agree that fitting models into envelopes will not distinguish between similar folds. However, fitting models directly to raw scattering data is extremely sensitive and I have never seen good fits with low chi2 values for incorrect models (even when very similar in overall shape to the correct structure).
Significance
The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.
-
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Referee #1
Evidence, reproducibility and clarity
Summary:
The formation of meiotic double-stranded DNA breaks is the starting point of meiotic recombination. DNA breaks are made by the topoisomerase-like SPO11, which interacts with a number of regulatory factors including REC114, MEI4 and IHO1. Despite the key role this process has in the continuation, and genetic variation, or eukaryotic life, there is very little known about how this process is regulated. Laroussi et al make use of biochemical, biophysical and structural biological approaches to extensively characterise the REC114-MEI4-IHO1 complex.
This is an outstanding biochemical paper. The experiments are well planned and beautifully executed. The protein purifications used are very clean, and the figures well presented. Importantly Laroussi et. al describe, and carefully characterise through point mutational analysis, the direct physical interaction between IHO1 and REC114-MEI4. This is an interaction that has, at least in yeast, previously been suggested to be driven by liquid-liquid separation. The careful and convincing work presented here represents an important paradigm-shift for the field.
I am fully supportive of publication of this excellent and important study.
Major comments:
My only major concern is regarding Figure 4, and specifically the AF2 model of the coiled-coil tetramer of IHO1. Given the ease with which MSAs of coiled-coils can become "contaminated" with non-orthologous sequences, I would urge some caution with this model. This is especially since the yeast ortholog of IHO1, Mer2, has been previously reported to be an anti-parallel tetramer (albeit, not very well supported by the data). The authors have several choices here. 1) They could simply reduce the visibility of the IHO1 tetramer model, and indicate caution in the parallel tetramer model. 2) They could consider using a structure prediction algorithm that doesn't use an MSA (e.g. ESMFold). 3) They could try to obtain experimental evidence for a parallel coiled-coil tetramer, e.g. through EM, SAXS or FRET approaches. I would like to make it crystal clear, however, that I would be very supportive of approach 1) or 2). An experimental approach is not necessary.
Assuming the authors don't take a wet-lab approach, this shouldn't take more than a couple of weeks.
Minor comments:
- The observation that REC114 and MEI4 can also form a 4:2 complex is very interesting and potentially important. Did the authors also try to model this higher order complex in AF2?
- Similarly to above, what does the prediction of the full-length REC114:MEI4 2:1 complex look like? Presumably the predicted interaction regions align well with experimental data, but it would be interesting to see (and easy to run).
- Did the authors carry out SEC-MALS experiments on any IHO1 fragment lacking the coiled-coil domain? It was previously reported for Mer2 that the C-terminal region can form dimers, for example (OPTIONAL).
- Given that full-length REC114 is used for the IHO1 interaction studies, do the authors have any data as to the stoichiometry of the REC114FL-MEI41-127 complex? (OPTIONAL)
- Did the authors try AF2 modelling of the REC114-IHO1 interaction using orthologs from other species?
Referees cross commenting
I will add cross-comments to the comments of Reviewer #2
Firstly, the comments made by Reviewer #2 are technically correct. Firstly, reviewer #2 points out that the oligomerization states that the authors report could, in part, be artifactual the based on the his-tag purification method. This is indeed correct. However, given that none of the oligomerization states reported are per se unusual, given what is already known (including pre-prints from the Keeney and Claeys Bouuaert laboratories), I think the authors could forego this step.
Secondly, the use of an experimental structural method, such as SAXS, would certainly add value to the paper. Also Reviewer #2 is correct in pointing out the availability of the ESRF beamlines to the authors. However, while SAXS is a useful method, I personally consider the use of mutants to validate the interactions, an even stronger piece of evidence that the AlphaFold2 interactions are correct. I must disagree somewhat with Reviewer #2 with their argument that SAXS would validate the fold. Certainly if one of the AF2 predicted structures is radically wrong, then SAXS would produce scattering data, and a subsequent distance distribution plot that is incompatible with the AF2 model. However, a partly correct AF2 model, of roughly the right shape, might still fit into a SAXS envelope.
Reviewer #2 shares my concern on the parallel coiled-coil of IHO1, and their suggested solution is very elegant.
In my view, due to the time constraints imposed by the partially competing work from the the Keeney and Claeys Bouuaert laboratories (recently on biorxiv). I would support the authors if they chose the quickest route to publication.
Significance
General assessment: The strengths of the paper are as follows:
- Quality of experiments - The proteins used have been properly purified (SEC) and properly handled. The experiments are carefully carried out and controlled.
- Detail - The authors carry out the considerable effort of characterising protein interactions. through separation-of-function mutants. This adds to the quality of the paper, and renders the AF2 models as convincing as experimentally determined structures
- Conceptual advances - The most important conceptual advance is the direct binding of the N-term of IHO1 to REC114. That this is the same region as used by both TOPOVIBL and ANKRD31 points to a complex regulation.
- Integrity - the authors have taken great care not to "oversell" the results. The data are presented, and analysed, without hyperbole.
Limitations - The only limitation of the paper is the lack of in vivo experiments to test their findings. However given the time and effort required, and the pressing need to publish this exciting study, this is not a problem.
Advance: The paper provides advances from a number of directions, both conceptual and mechanistic. Mechanistically the description of the REC114-MEI14 complex is important, and in particular the observation that it can also form a higher order 4:2 structure. Likewise, while IHO1 was inferred to be a tetramer (based on work on Mer2) this was never proven formally. Most importantly, is the physical linkage between IHO1 and REC114, and that this is an interaction that is incompatible with TOPOVIBL and ANKRD31.
Audience: Given the central role of meiotic recombination in eukaryotic life, any studies that shed additional light on the regulation of meiosis are suitable for a broad audience. However, this subject paper will be more specifically of interest to the meiosis community. The elegant methodology will also be of interest to structural biologists and protein biochemists.
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Reply to the reviewers
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Reply to the reviewers
We sincerely thank the reviewers for their comprehensive and constructive feedback. Below, we submit our revision plan addressing the points raised by the reviewers.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The study analyzes the role of SLIT2 in clearance of S. aureus via neutrophils. It suggests that N-SLIT2 play a key role as an amplifier of the ROS response and release of antimicrobial peptides. The manuscript is well written and technologically sound. However, a few issues need to be addressed that preclude publication of the manuscript:
We thank the reviewer for the positive feedback.
Major comments:
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The study analyzes different parameters of neutrophil function. One major effect of neutrophil activation is NETosis. This has not been addressed in the study albeit it is deemed to act in concert with the other immune mechanisms described.
We thank the reviewer for the suggestion. S. aureus is known to promote NET formation as well as to enhance NET degradation to increase bacterial survival in vivo (Meyers, Crescente et al., 2022, Thammavongsa, Missiakas et al., 2013). Several cellular kinases (Erk, Akt, p38) have been implicated in ROS-induced NETosis, but the exact role of p38 signaling in NETosis remains less clear (Douda, Khan et al., 2015). As recommended by the reviewers, we will now investigate whether N-SLIT2 regulates S. aureus-induced NETosis in neutrophils using Sytox Green, a membrane-impermeable nucleic acid label, as previously described (Douda et al., 2015).
Furthermore, the authors discuss a role of SLIT2 in the regulation of neutrophil migration. However, the current data set does not provide sufficient evidence for this. The reviewer suggests that the authors provide migration/chemotaxis assays and/or in vivo data to prove their hypothesis or revise their argumentation.
Several groups, including ours, have previously demonstrated that SLIT2-ROBO1 signaling potently inhibits neutrophil chemotaxis in vitro and in vivo. The in vivo models, in which the negative effects of SLIT2 on neutrophil migration have been shown, include mouse models of peritonitis (Tole, Mukovozov et al., 2009), allergic airway inflammation (Ye, Geng et al., 2010), renal ischemia-reperfusion injury (Chaturvedi, Yuen et al., 2013), and cholangiocarcinoma (Zhou, Luo et al., 2022). Additionally, a recent study showed that shRNA-mediated knockdown of SLIT2 resulted in increased neutrophil infiltration into murine tumors further supporting negative regulatory effect of SLIT2 on neutrophil migration (Geraldo, Xu et al., 2021). In the revised version of the manuscript, we will now discuss these important points in the Introduction and Discussion sections.
In our current study, in an effort to selectively examine the effects of SLIT2 on neutrophil function rather than on neutrophil migration, we intentionally administered N-ROBO1 to block endogenous SLIT2 signaling at 48 and 72 hours after inducing skin and soft tissue infection (SSTI) with S. aureus. In this model, the majority of neutrophil influx occurs early on, namely within 24 hours (Prabhakara, Foreman et al., 2013). We observed that blocking endogenous SLIT2 signaling in a murine model of SSTI resulted in enhanced localized infection and injury. We will now use immunohistochemical analysis to measure tissue infiltration of neutrophils (Ly6G+F4/80-) (Chadwick, Macdonald et al., 2021). In addition, as previously described we will also use IHC to evaluate within the tissue 8-hydroxydeoxyguanosine (8-OHdG), an indicator of oxidative damage (Sima, Aboodi et al., 2016). We will compare levels of 8-OHdG to the number of neutrophils in the tissue as a gross indicator of local ROS production by infiltrating neutrophils.
The timeline of SLIT2 expression indicates that environmental conditions could influence the expression of SLIT2. Have the authors analyzed whether SLIT2 expression is affected by low pH or hypoxia? Is there any data indicating what factors regulate SLIT2 expression? In the same line, it would be interesting to know whether SLIT2 immune effects (specifically ROS and LL37 release) are similarly triggered under hypoxic conditions often found in an abscess.
We thank the reviewer for raising this important point and for the suggestions. The regulation of SLIT2 levels in tissues is an active area of research. Hypoxia has been reported to increase SLIT2 expression in placental tissue (Liao, Laurent et al., 2012) but this has not been investigated in the context of bacterial infection. In different physiologic and pathophysiologic settings, vascular endothelial cells, including dermal microvascular endothelial cells (DMEC), have been shown to be an important source of SLIT2 (Romano, Manetti et al., 2018, Tavora, Mederer et al., 2020). We will therefore investigate the effects of hypoxia and low pH, conditions founds within bacterial abscesses, on production of SLIT2 by DMEC. DMEC will be infected with S. aureus and grown in normoxic and hypoxic (2% O2) conditions for up to 72 hours, the time-point at which maximal SLIT2 levels were detected in S. aureus-induced SSTI. We will collect cells and cultured supernatant for measurement of levels of Slit2 mRNA and SLIT2 protein at different time points ranging from 0 to 72 hours after infection. We will incubate neutrophils with the conditioned medium from hypoxic DMEC to measure the effect on LL-37 secretion. Finally, we will expose neutrophils to S. Aureus (+/- N-SLIT2) in a medium with pH ranging from 5.5 to 7.4 and then measure the LL-37 secretion as the reviewer suggested (Zhou & Fey, 2020).
Lastly, it is unclear whether SLIT2 binds to a defined target on the neutrophil. This needs to be highlighted in the discussion in respect to future work and ideally resolved experimentally.
We apologize for the confusion. We and others have previously demonstrated that human and murine neutrophils express ROBO1 but not ROBO2, and that ROBO1 is the primary Roundabout receptor which binds N-SLIT2 in immune cells (Rincon, Rocha-Gregg et al., 2018, Tole et al., 2009). We have now included this information in the Introduction section (please see page- 3). In our manuscript we showed experimentally that incubation of N-SLIT2 with the soluble N-terminal fragment of ROBO1 (N-ROBO1), which contains the N-SLIT2 binding Ig1 motif (Morlot, Thielens et al., 2007), blocked the effect of N-SLIT2 on ROS production, thereby confirming that the observed actions of SLIT2 occurred through ROBO1 (Fig. 1G). In the revised version of the manuscript, we will clarify this point.
Reviewer #1 (Significance (Required)):
The manuscript provides insight into a new mechanism regulating neutrophil function in the presence of S. aureus. The study provides evidence that the N-terminus of SLIT2 is involved in these effects and highlights p38-mediated signaling events as molecular targets increasing antibacterial effects in neutrophils. However, some contradictory findings imply that timing of the response is crucial.
Nevertheless, with the molecular mechanisms not fully understood many questions remain and the study adds to the complexity of the anti-staphylococcal immune response. Therefore, the audience for this manuscript requires knowledge on S. aureus-specific host-pathogen interaction and is not suitable for a broad audience as it does not provide information on a generally new mechanism of neutrophil activation or defense.
We thank the reviewer for pointing out the complexity of host-pathogen (neutrophils and S. aureus) interactions. SLIT2 is well-known for its anti-inflammatory properties via its effects on immune cell chemotaxis in vivo (Anand, Zhao et al., 2013, Chaturvedi et al., 2013, Geraldo et al., 2021). We demonstrated that SLIT2-ROBO1 signaling inhibits macropinocytosis in macrophages, and consequently, attenuates NOD2-induced inflammasome activation in mice (Bhosle, Mukherjee et al., 2020). Based on these earlier observations, SLIT2 would be anticipated to impair the innate immune response to infection. Unexpectedly, we found that SLIT2 does not impair, but instead enhances the ability of neutrophils to kill S. aureus. Indeed, through different mechanisms SLIT2 has been shown to have widespread anti-microbial properties against not only S. aureus but instead against diverse pathogens, including Mycobacterium tuberculosis, intestinal pathogens, H5N1 influenza, and most recently, COVID-19 (Gustafson, Ngai et al., 2022, London, Zhu et al., 2010). Together, these studies highlight the importance of spatiotemporal regulation of SLIT2 levels in tissues during bacterial and viral infection and the direct effects of SLIT2 on modulating host-pathogen interactions.
Additionally, SLIT2-induced p38 MAPK activation is not limited to innate immune cells. Li et al. reported this week that SLIT2-ROBO1 signaling activates p38 in pancreatic ductal adenocarcinoma cells as well as metastatic tumors (Li, Zhang et al., 2023). In the revised manuscript, we will discuss all of the important points above.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: The manuscript deals with the role of the neurorepellent SLIT2 in killing of the bacterial pathogen Staphylococcus aureus. The authors show that neutrophils incubated with the N-terminal region of SLIT2 kill S. aureus more efficiently than neutrophils without pre-exposure to N-SLIT2. This effect was due to an increased production of reactive oxygen species by NADPH oxidase complex activation and stimulating exocytosis of antibacterial peptide containing granules. The concept was proven in an animal model of skin and soft tissue infection in mice in which neutralization of endogenous SLIT2 reduced CFU numbers in ear skin and decreased tissue destruction in response to S. aureus infection.
Major comments:
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In general the findings and key conclusions are convincingly covered by the results presented in the manuscript. The methods are adequate to allow the conclusions drawn. Data are clearly presented and easy to follow. Statistical methods are appropriate.
We thank the reviewer for the positive feedback. In the present study, we investigated the effects of SLIT2 on NADPH oxidase (NOX – p47phox) priming. Using novel methodology, neutrophil priming was recently shown to be associated with characteristic cytoskeletal changes (Bashant, Vassallo et al., 2019). We are now collaborating with Dr. Nicole Toepfner (Technische Universität Dresden, Dresden) to investigate SLIT2-induced cytoskeletal changes in neutrophils isolated from whole blood using Real-time deformability cytometry (RT-DC). We believe that these novel studies will further enhance the revised manuscript.
Minor comments:
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In the Materials and Methods section line 340 a GFP-expressing S. aureus USA300 strain is indicated. What was the exact strain designation, e.g. LAC or JE2, as USA300 is not a strain name (different strains belong to this pulsed-field electrophoresis based classification).
We thank the reviewer for this comment. The strain designation of the GFP-expressing S. aureus we used is USA300 LAC (Flannagan, Kuiack et al., 2018). In the revised version of the manuscript we will include the correct information (please see page- 10).
In the legend of figure 3 the inhibitors are mentioned for part B and E but not C and D.
We apologize for the error. Figure 3 legend has now been corrected in the revised manuscript.
Figure S4 would be nice to have in the main manuscript.
We thank the reviewer for the suggestion. In the revised manuscript we moved original Supplementary Fig. S4B to main Fig. 4B in the manuscript. The schematic from main Fig. 4B is moved to the new Supplementary Fig. 4B. The graphical summary (original Supplementary Fig. S4C) is now presented as new main Figure 5.
Reviewer #2 (Significance (Required)):
The manuscript deals with a novel mechanism of neutrophil activation by SLIT-2, a protein which was originally thought to act in the nervous system but is also expressed in many peripheral tissues. Importantly SLIT-2 may be involved in tumor suppression but also chemotaxis of immune cells. In this manuscript a novel, rather unexpected role of the N-terminal region of SLIT-2 in activation of antibacterial mechanisms of neutrophils was shown. This could be interesting for a broader readership interested in innate immune mechanisms and bacterial infections. Since little is known on the role of SLIT-2 in response to bacterial infections the paper could initiate a number of new studies in this field. This reviewer has experience with S. aureus virulence and resistance mechanisms and animal infection models.
We thank the reviewer for the very positive feedback regarding the appeal of our manuscript to a broad readership. As noted in our response to Reviewer #1 Significance, recent studies suggest that SLIT2 could not only serve as a therapeutic to combat S. aureus, but could have broad anti-microbial activity against a number of pathogens including Mycobacterium tuberculosis, intestinal pathogens, H5N1 influenza, and COVID-19 (Borbora, Bhatt et al., 2022, Gustafson et al., 2022, London et al., 2010). We believe that the ability of SLIT2 to combat diverse bacterial and viral infections will even further enhance the appeal of our manuscript to a broad audience. In the revised manuscript we will expand the discussion to include these very important points.
References:
Anand AR, Zhao H, Nagaraja T, Robinson LA, Ganju RK (2013) N-terminal Slit2 inhibits HIV-1 replication by regulating the actin cytoskeleton. Retrovirology 10: 2
Bashant KR, Vassallo A, Herold C, Berner R, Menschner L, Subburayalu J, Kaplan MJ, Summers C, Guck J, Chilvers ER, Toepfner N (2019) Real-time deformability cytometry reveals sequential contraction and expansion during neutrophil priming. J Leukoc Biol 105: 1143-1153
Bhosle VK, Mukherjee T, Huang YW, Patel S, Pang BWF, Liu GY, Glogauer M, Wu JY, Philpott DJ, Grinstein S, Robinson LA (2020) SLIT2/ROBO1-signaling inhibits macropinocytosis by opposing cortical cytoskeletal remodeling. Nat Commun 11: 4112
Borbora SM, Bhatt S, Balaji KN (2022) Mycobacterium tuberculosis infection elevates SLIT2 expression to modulate oxidative stress responses in macrophages. bioRxiv: 2022.10.13.512188
Chadwick JW, Macdonald R, Ali AA, Glogauer M, Magalhaes MA (2021) TNFalpha Signaling Is Increased in Progressing Oral Potentially Malignant Disorders and Regulates Malignant Transformation in an Oral Carcinogenesis Model. Front Oncol 11: 741013
Chaturvedi S, Yuen DA, Bajwa A, Huang YW, Sokollik C, Huang L, Lam GY, Tole S, Liu GY, Pan J, Chan L, Sokolskyy Y, Puthia M, Godaly G, John R, Wang C, Lee WL, Brumell JH, Okusa MD, Robinson LA (2013) Slit2 prevents neutrophil recruitment and renal ischemia-reperfusion injury. J Am Soc Nephrol 24: 1274-87
Douda DN, Khan MA, Grasemann H, Palaniyar N (2015) SK3 channel and mitochondrial ROS mediate NADPH oxidase-independent NETosis induced by calcium influx. Proc Natl Acad Sci U S A 112: 2817-22
Flannagan RS, Kuiack RC, McGavin MJ, Heinrichs DE (2018) Staphylococcus aureus Uses the GraXRS Regulatory System To Sense and Adapt to the Acidified Phagolysosome in Macrophages. mBio 9
Geraldo LH, Xu Y, Jacob L, Pibouin-Fragner L, Rao R, Maissa N, Verreault M, Lemaire N, Knosp C, Lesaffre C, Daubon T, Dejaegher J, Solie L, Rudewicz J, Viel T, Tavitian B, De Vleeschouwer S, Sanson M, Bikfalvi A, Idbaih A et al. (2021) SLIT2/ROBO signaling in tumor-associated microglia and macrophages drives glioblastoma immunosuppression and vascular dysmorphia. J Clin Invest 131
Gustafson D, Ngai M, Wu R, Hou H, Schoffel AC, Erice C, Mandla S, Billia F, Wilson MD, Radisic M, Fan E, Trahtemberg U, Baker A, McIntosh C, Fan CS, Dos Santos CC, Kain KC, Hanneman K, Thavendiranathan P, Fish JE et al. (2022) Cardiovascular signatures of COVID-19 predict mortality and identify barrier stabilizing therapies. EBioMedicine 78: 103982
Li Q, Zhang XX, Hu LP, Ni B, Li DX, Wang X, Jiang SH, Li H, Yang MW, Jiang YS, Xu CJ, Zhang XL, Zhang YL, Huang PQ, Yang Q, Zhou Y, Gu JR, Xiao GG, Sun YW, Li J et al. (2023) Coadaptation fostered by the SLIT2-ROBO1 axis facilitates liver metastasis of pancreatic ductal adenocarcinoma. Nat Commun 14: 861
Liao WX, Laurent LC, Agent S, Hodges J, Chen DB (2012) Human placental expression of SLIT/ROBO signaling cues: effects of preeclampsia and hypoxia. Biol Reprod 86: 111
London NR, Zhu W, Bozza FA, Smith MC, Greif DM, Sorensen LK, Chen L, Kaminoh Y, Chan AC, Passi SF, Day CW, Barnard DL, Zimmerman GA, Krasnow MA, Li DY (2010) Targeting Robo4-dependent Slit signaling to survive the cytokine storm in sepsis and influenza. Sci Transl Med 2: 23ra19
Meyers S, Crescente M, Verhamme P, Martinod K (2022) Staphylococcus aureus and Neutrophil Extracellular Traps: The Master Manipulator Meets Its Match in Immunothrombosis. Arterioscler Thromb Vasc Biol 42: 261-276
Morlot C, Thielens NM, Ravelli RB, Hemrika W, Romijn RA, Gros P, Cusack S, McCarthy AA (2007) Structural insights into the Slit-Robo complex. Proc Natl Acad Sci U S A 104: 14923-8
Prabhakara R, Foreman O, De Pascalis R, Lee GM, Plaut RD, Kim SY, Stibitz S, Elkins KL, Merkel TJ (2013) Epicutaneous model of community-acquired Staphylococcus aureus skin infections. Infect Immun 81: 1306-15
Rincon E, Rocha-Gregg BL, Collins SR (2018) A map of gene expression in neutrophil-like cell lines. BMC Genomics 19: 573
Romano E, Manetti M, Rosa I, Fioretto BS, Ibba-Manneschi L, Matucci-Cerinic M, Guiducci S (2018) Slit2/Robo4 axis may contribute to endothelial cell dysfunction and angiogenesis disturbance in systemic sclerosis. Ann Rheum Dis 77: 1665-1674
Sima C, Aboodi GM, Lakschevitz FS, Sun C, Goldberg MB, Glogauer M (2016) Nuclear Factor Erythroid 2-Related Factor 2 Down-Regulation in Oral Neutrophils Is Associated with Periodontal Oxidative Damage and Severe Chronic Periodontitis. Am J Pathol 186: 1417-26
Tavora B, Mederer T, Wessel KJ, Ruffing S, Sadjadi M, Missmahl M, Ostendorf BN, Liu X, Kim JY, Olsen O, Welm AL, Goodarzi H, Tavazoie SF (2020) Tumoural activation of TLR3-SLIT2 axis in endothelium drives metastasis. Nature 586: 299-304
Thammavongsa V, Missiakas DM, Schneewind O (2013) Staphylococcus aureus degrades neutrophil extracellular traps to promote immune cell death. Science 342: 863-6
Tole S, Mukovozov IM, Huang YW, Magalhaes MA, Yan M, Crow MR, Liu GY, Sun CX, Durocher Y, Glogauer M, Robinson LA (2009) The axonal repellent, Slit2, inhibits directional migration of circulating neutrophils. J Leukoc Biol 86: 1403-15
Ye BQ, Geng ZH, Ma L, Geng JG (2010) Slit2 regulates attractive eosinophil and repulsive neutrophil chemotaxis through differential srGAP1 expression during lung inflammation. J Immunol 185: 6294-305
Zhou C, Fey PD (2020) The acid response network of Staphylococcus aureus. Curr Opin Microbiol 55: 67-73
Zhou SL, Luo CB, Song CL, Zhou ZJ, Xin HY, Hu ZQ, Sun RQ, Fan J, Zhou J (2022) Genomic evolution and the impact of SLIT2 mutation in relapsed intrahepatic cholangiocarcinoma. Hepatology 75: 831-846
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Referee #2
Evidence, reproducibility and clarity
Summary:
The manuscript deals with the role of the neurorepellent SLIT2 in killing of the bacterial pathogen Staphylococcus aureus. The authors show that neutrophils incubated with the N-terminal region of SLIT2 kill S. aureus more efficiently than neutrophils without preexposure to N-SLIT2. This effect was due to an increased production of reactive oxygen species by NADPH oxidase complex activation and stimulating exocytosis of antibacterial peptide containing granules. The concept was proven in an animal model of skin and soft tissue infection in mice in which neutralization of endogenous SLIT2 reduced CFU numbers in ear skin and decreased tissue destruction in response to S. aureus infection.
Major comments:
In general the findings and key conclusions are convincingly covered by the results presented in the manuscript. The methods are adequate to allow the conclusions drawn. Data are clearly presented and easy to follow. Statistical methods are appropriate.
Minor comments:
In the Materials and methods section line 340 a GFP-expressing S. aureus USA300 strain is indicated. What was the exact strain designation, e.g. LAC or JE2, as USA300 is not a strain name (different strains belong to this pulsed-field electrophoresis based classification). In the legend of figure 3 the inhibitors are mentioned for part B and E but not C and D. Figure S4 would be nice to have in the main manuscript.
Significance
The manuscript deals with a novel mechanism of neutrophil activation by SLIT-2, a protein which was originally thought to act in the nervous system but is also expressed in many peripheral tissues. Importantly SLIT-2 may be involved in tumor suppression but also chemotaxis of immune cells. In this manuscript a novel, rather unexpected role of the N-terminal region of SLIT-2 in activation of antibacterial mechanisms of neutrophils was shown. This could be interesting for a broader readership interested in innate immune mechanisms and bacterial infections. Since little is known on the role of SLIT-2 in response to bacterial infections the paper could initiate a number of new studies in this field.
This reviewer has experience with S. aureus virulence and resistance mechanisms and animal infection models.
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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 study analyzes the role of SLIT2 in clearance of S. aureus via neutrophils. I suggests that N-SLIT2 play a key role as an amplifier of the ROS response and release of antimicrobial peptides. The manuscript is well written and technologically sound. However, a few issues need to be addressed that preclude publication of the manuscript:
Major comments
The study analyzes different parameters of neutrophil function. One major effect of neutrophil activation is NETosis. This has not been addressed in the study albeit it is deemed to act in concert with the other immune mechanisms described.
Furthermore, the authors discuss a role of SLIT2 in the regulation of neutrophil migration. However, the current data set does not provide sufficient evidence for this. The reviewer suggests that the auhtors provide migration/chemotaxis assays and/or in vivo data to prove their hypothesis or revise their argumentation. The timeline of SLIT2 expression indicates that environmental conditions could influence the expression of SLIT2. Have the authors analyzed whether SLIT2 expression is affected by low pH or hypoxia? Is there any data indicating what factors regulate SLIT2 expression?
In the same line, it would be interesting to know whether SLIT2 immune effects (specifically ROS and LL37 release) are similarly triggered under hypoxic conditions often found in an abscess? Lastly, it is unclear whether SLIT2 binds to a defined target on the neutrophil. This needs to be highlighted in the discussion in respect to future work and ideally resolved experimentally.
Significance
The manuscript provides inisght into a new mechanism regulating neutrophil function in the presence of S. aureus. The study provides evidence that the N-terminus of SLIT2 is involved in these effects and highlights p38-mediated signaling events as molecular targets increasing antibacterial effects in neutrophils. However, some contradictory findings imply that timing of the response is crucial. Nevertheless, with the molecular mechanisms not fully understood many questions remain and the study adds to the complexity of the antistaphyloccocal immune response. Therefore, the audience forthis manuscript requires knowledge on S. aureus-specific host-pathogen interaction and is not suitable for a broad audience as it does not provide information on a generally new mechanism of neutrophil activation or defense.
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Reply to the reviewers
We thank the reviewer for their comments. We are encouraged that the reviewers found our research “important study that addresses the interplay between two major Rho-type small GTPases involved in cell division” and “of interest to those interested in the cell biology of mitotic exit”. We agree with the comments raised by the reviewers and have provided new data as per their recommendation. We have also made changes to the text and format of the paper. We feel that with these changes the manuscript is stronger and we thank the reviewers for their suggestions. Below we provide a detailed response to the reviewers’ comments.
Reviewer #1
*This manuscript focuses on the role of Cdc42 in Rho1 activation during fission yeast cytokinesis. The primary finding is that active Cdc42 and its downstream effector Pak1 prevents accumulation of active Rho1 and the synthesis of cell wall material, at early stages of cytokinesis and despite the local recruitment of the Rho1 GEF Rgf1. The data supporting these conclusions are reasonably sound. *
*Additional experiments are presented to suggest that Cdc42 and Pak1 negatively regulate Rgf1, this conclusion is not as strongly supported (though it may be true) *
*These study relies on a newly described probe for active Rho1. However this probe is not sufficiently well validated. *
*Overall the manuscript was not assembled with sufficient care and rigor, these deficits could be readily corrected. *
The major point of the paper is that Cdc42 and Pak1 negatively regulate Rho1 activation. However, during late cytokinesis, active Cdc42 and active Rho1 co-exist at the division site. Thus, Cdc42 activation induces a delay in Rho1 activation, but how this delay is overcome is not investigated or even discussed. Indeed, while the delay is shown the transience of this inhibition is not explicitly mentioned. At a minimum, the authors should highlight this point for the readers.
We are encouraged by the fact that the reviewer found our data “reasonably sound”. We agree that this manuscript does not provide the molecular details of how Cdc42 inhibits Rho1 activation. Our genetic data suggests that this is likely mediated by multiple pathways possibly involving the regulation of the Rho regulators Rgf1, Rgf2 and Rga5. We are currently investigating the molecular details of this regulation and hope to report it in another manuscript.
Our data shows that while Cdc42 inhibits Rho1, the SIN pathway is essential for Rho1 activation regardless of the presence of Cdc42. While Cdc42 is activated at the division site as the ring completes assembly, the SIN pathway is activated immediately prior to ring constriction similar to that of Rho1 activation. It is possible that once the SIN is activated at the division site, it overcomes Cdc42-mediated Rho1 inhibition. We have highlighted this in the discussion section of this manuscript and are currently investigating the molecular details of this regulation.
*Specific points 1 - RBD probe This probe is central to this manuscript. However, there is insufficient validation of its target. Figure 1 shows the localization and its independence of Rho2. The authors should provide direct evidence that it recognizes Rho1 (for example using a repressible promotor or an anchor away approach).
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We thank the reviewers for their comments on the RBD probe. We have now provided validation for the RBD-probe. We have used rho1 temperature-sensitive and switch-off mutants to show loss of RBD-probe localization in these mutants. This data is provided I the revised manuscript in Fig1 and Supplementary fig. S1.
At various places in the manuscript the authors refer to this probe as "Rho-probe", RBD-probe, RBD, RBD-(mNG or tdTomato). On page 11 the authors state, "As per our observations, we refer to the Rho-probe signal at the division site as active Rho1 from here onwards." Yet, in the very next paragraph they refer to the localization of the "Rho probe". * This is also an issue with the figures. For example, in figures 4B,C ; 5B,C; 6B; 7B,C the figures are titled either "Rho1 activation at division site", "Rho1-probe at division site"; "Rho1-probe appearance at division site" ; "Rho1-probe in non-constricting rings". *
We agree that these multiple terms to describe the probe is confusing. We have restricted the terms to either “RBD-mNG” or “RBD-tdTomato” when reporting the data and use “Rho-probe” for descriptive purposes.
In fig 3, RBD-nNG is quantified in a graph entitled "localizaton [sic] of Rho1-GEFs at division site"
We thank our reviewers for identifying this error in our labeling of the graph in Fig. 3E. This figure now reads “Localization of Rgf1, Rgf3, active Rho1 at the division site”
In all figures but two, 5c and 7c, the authors quantify Rho1 activation by the presence or absence of the probe, rather than a quantitative measure or the extent of recruitment of the probe. This could be analyzed my quantitatively.
We appreciate this comment and provide this response in order to clarify our reasoning for presenting this data. We quantified the intensities of RBD-mNG or RBD-tdTomato where ever relevant to the question we are addressing for each experiment performed.
Where we look at Rho1 activation at the division site with respect to SPB distances, we are reporting the differences in the timing of Rho activation with respect to mitotic progression. However, in Figures 5c and 7c, and now also Fig 1 of the revised manuscript, we quantified the intensities of the probe as this indicated the changes in overall active Rho1 levels under our experimental conditions. We have added in the text for earlier experiments where we do not report intensity measurements for the active Rho probe that we do not observe any differences in the intensity levels.
*2 - Regulation of Rgf1 by Cdc42 and Pak1. The results shown in figure 8 show that "early Rho1 activation in gef1 mutants is not Rgf3-dependent". Figure 9 establishes "loss of rgf1 prevents premature Rho1 activation in gef1Δ cells restoring it to normal in late anaphase (Fig.9A, B)." This finding indicates that Rgf1, but not Rgf3, is required for Rho1 premature activation. This finding doesn't rule out the possibility that Cdc42 and Pak1 might be required to turn off RhoGAPs to allow active Rho1 to accumulate. This analysis concludes with this unclear and ungrammatical sentence, "While we were unable to assess the Rho-probe in the rgf1Δ rgf2Δ double mutants due to its lethality [sic; is the Rho probe lethal?], our observations suggest that apart from Rgf1 early Rho1 activation in gef1Δ cells is either due to activation of Rgf2 or due to inhibition of Rga5." *
We thank you for your insight and agree with these remarks. We could not investigate Rho1 activation in rgf1Δ rgf2Δ double mutants since the double mutants are inviable. We have re-worded the sentence to reflect our findings appropriately.
*The conclusion that this regulation is due to control of Rgf1 should be toned down. E.g. from the abstract: "We provide functional and genetic evidence which indicates that Pak1 regulates Rho1 activation likely via the regulation of its GEF Rgf1." *
We have now removed this statement from the abstract. We have also clarified in the discussion that the molecular details of how Cdc42 inhibits Rho1 is not known and needs to be investigated. While our data suggests that the regulator Rgf1 and Rga5 may be involved in the process the details are unclear and we are currently investigating this regulation.
*SECTION B - Significance ======================== This manuscript ties together several recent papers from the author's lab on the control of Cdc42 activation during cytokinesis and older papers on the role of Rho1 in Bgs1 activation. It provides missing information into the temporal regulation of septum assembly.
The authors make a point of the similarities of fission yeast cytokinesis to animal cell cytokinesis. Indeed the second sentence reads, "The fission yeast model system divides via an actomyosin-based contractile ring, which is assembled in the medial region of the cell, as in animal cells (Balasubramanian et al., 2004; Pollard, 2010).". However, the authors fail to point out the many differences between yeast and animal cell cytokinesis until the last paragraph of the discussion. If the authors want to include the similarities in the introduction, they should also include the differences. For example, ring assembly is independent of Rho1 activation in fission yeast, but dependent on RhoA activation in animal cells. *
We thank the reviewer for pointing out this deficiency in our writing. We have now amended the introduction to highlight the differences between Rho1 activity in fission yeast and animal cells during cytokinesis. We have added the following text to the Introduction section.
“The animal Rho1 homolog RhoA is required for ring formation and is essential for cytokinesis (Basant and Glotzer, 2018). While in yeast, Rho1 is essential for septum formation, the current literature suggests that it is dispensable for ring formation (Onishi et al., 2013; Yoshida, 2009). In fission yeast where both the actomyosin ring and the septum have important roles in the proper coordination of cytokinesis, Rho1 has no reported roles in ring formation but is essential for septation (Balasubramanian et al., 2004).”
*This work will be of interest to biologists working on yeast cell division. To a lesser extent it will be of interest to biologists interested in cytokinesis and coordination of distinct GTPase pathways.
Additional points*
1 - The text is overly wordy and needs extensive revision. Many of the experiments could be explained more clearly and with somewhat less genetic jargon. The introduction has quite a bit of extraneous information and lacks relevant facts, such as the function of Bgs1, which is central to the results.
We have now modified the text to remove unnecessary genetic jargon. We have also provided additional text to describe the role of Bgs1 in the Introduction.
2 - page 4 "GEFs promote GTP binding, thus keeping the GTPase active while the GAPs increase GTP hydrolysis, thus promoting GTPase inactivation." GEFs promote GTP binding, but they do not keep the GTPase active (an inhibitor of a RhoGAP would do that), they activate the GTPases.
We thank the reviewers for highlighting this error. We have corrected this sentence, which now reads “GEFs promote GTP exchange to activate the GTPase, while the GAPs increase GTP hydrolysis to promote GTPase inactivation.”
*3 - The current literature on animal cell cytokinesis indicates little direct role in cytokinesis, rather than the author's statement, "In larger eukaryotes, the role of Cdc42 activation has been reported mostly in meiotic division events such as polar body extrusion in oocytes, but not much is known about its role in cytokinesis in somatic cell division (Drechsel et al., 1997; Na and Zernicka-Goetz, 2006)." See for example, PMID 10898977, 10871280 which indicate Cdc42 does not play a major role during cytokinesis in at least a few systems where it has been analyzed. *
We thank our reviewer for this observation and agree that this statement can be expanded to further explain the role of Cdc42 in animal cytokinesis. The paragraph has been re-written as follows-
Pg5 - “In animal cells, the direct role of Cdc42 in cytokinesis remains indefinite. In Xenopus embryos and mouse fibroblasts for example, constitutively active Cdc42 impairs cytokinesis completion (Drechsel et al., 1997). However, in other cases such as in mouse embryonic stem cells, Cdc42 was only critical for development but not cytokinesis (Chen et al., 2000). RNA interference in animal cells demonstrate that that while RhoA is required for cytokinesis, Cdc42 is not required for this process (Jantsch-Plunger et al., 2000). Cdc42 also promotes spindle positioning and polar body extrusion in mouse oocytes, but it is not known whether its localization at these spindles affects RhoA (Na and Zernicka-Goetz, 2006). Thus, the role of Cdc42 in the cytokinetic process may be cell-type specific, and these data highlight the importance for more investigation to elucidate Cdc42 regulation in dividing cells (Jordan and Canman, 2012).”
Reviewer #2
*In many fungal cells, including fission yeast, the deposition of a new cell wall (a septum) between daughter cells is essential for cytokinesis. Cell wall synthases are trafficked to and activated at the division site, and dysregulated trafficking and/or synthase activation can lead to cytokinetic defects. In this study, the authors use fluorescent probes for Cdc42 and Rho1 activity and live-cell imaging to investigate the timing and regulation of Rho1 activity in fission yeast, and specifically, the role of Cdc42 in regulating Rho1. Summary of the proposed model: Gef1 -> active Cdc42 -> Pak1 --| Rgf1 -> active Rho1 -> septum formation
Major comments
(1) As far as I can gather from the authors' description in the manuscript and quick literature search, this will be the first publication in S. pombe utilizing the HR1-C2 domain of Pkc2p as fluorescent probe for active Rho1 (RBD-mNG). While a comparable domain of S. cerevisiae Pkc1p (not "pck2" as referenced by the authors in Page 25) has been used for similar purposes, given the importance of this probe and the precedent it sets in the S. pombe literature, it is imperative that proper tests are performed to validate that its localization reflects activity of Rho1 and nothing else (such as membrane binding of the C2 domain or transcriptional regulation of the pkc2 promoter). Such tests should also be independent of the hypotheses central to the current study (i.e., effects of Gef1, Pak1, Rgf1/2 on the timing of RBD-mNG localization). Can the authors provide data to address this point? Examples include, but not limited to, rho1 mutants, expression of constitutively active Rho1, or temporary expression of dominant-negative Rho1.*
We agree with the reviewer and now provide data to show loss of the localization of the Rho-probe RBD-mNG in rho1 mutants. Using temperature-sensitive and switch-off mutants we show that under mutant conditions the RBD-mNG localization is lost at the division site and also from the cell ends. This provides strong evidence that the probe detects active Rho1 in the cells.
*(2) Related, M&M does not provide sufficient details about the amino-acid positions corresponding to the "RBD" domain of Pkc2, thus precluding readers from reproducing the experiments. This needs to be clarified. *
We now provide in the materials and methods the details of how this probe was generated including the base pairs of the budding yeast PKC1 and the fission yeast pck2 promoter.
(3) In Figure 1B, RBD1-mNG localizes clearly to the medial region of rho2∆ cells when the Rlc1-tdTomato ring has not formed. Does this mean that Rho2 has a major role in forming the contractile ring that is independent of Rho1 activation? On this other hand, however, data in Fig. S2BC suggest that RBD-mNG does not localize to the medial region in rho2∆ cells until Rlc1-tdTomato ring forms (the timing of which seems normal). This discrepancy needs to be addressed.
In response to the issue raised here, we do not see active Rho1 at the division site of cells without rings. However, after cytokinesis, while cells are in septation, although the ring has disappeared, active Rho1 lingers at the division site. The cell shown in the panel is a septated cell after ring constriction completes. We have included DIC panels of these cells to show that active Rho1 lingers in septating cells.
*(4) Given the nature of RBD-mNG localization, it seems unavoidable to have some level of arbitrariness in measuring the onset of its localization at the division site. It would be advisable for the authors to be specific in M&M about how they defined the onset of localization, i.e., whether it was based on universal threshold in signal intensity, ratio, etc. or on manual curation (ideally double-blind).
*
We have updated the methods to describe that “onset of localization” was performed via double-blind visual observations.
Minor comments (1) Throughout the manuscript, there are quite a few places where inconsistencies in genetic nomenclature can cause confusion to readers. Below are some examples. Figs. 6B, 7B, 10B: pak1(-ts), shk1, and orb2-34 (including faint labels under category marks in 6B). Fig. 9B (gef1+ rgf1∆) vs 9C (rgf1∆). Wild-type alleles are implicit in some figures, while explicit in others.
We have corrected these inconsistencies.
*(2) The first hypothesis (Fig. 1C) is that the AMR might regulate Rho1 activation. The ring is disrupted with LatA, but Rho remains active. They cite this as evidence that the AMR does not activate Rho1, but were the cells treated before or after the rings formed? If before, then the experiment demonstrates what the authors claim, but if after, it only shows that the AMR is not essential to maintain Rho activity. *
We agree with the reviewer that this is an important distinction. We have modified this statement to “These results indicate that while at the division site the actin cytoskeleton is not required for maintaining Rho1 activation, it is necessary at the growth sites of interphase cells.”
*(3) Page 8: "Time-lapse imaging of cells simultaneously expressing CRIB-3xGFP and RBD-tdTomato [...] while Rho1 is activated ~20 minutes after SPB duplication (Fig. 2B)." This appears to refer to Fig. 2C. *
We thank the reviewers for catching this error in the text. We have now corrected it, showing timelapse as Fig. 2C, and an Image of cells simultaneously expressing CRIB and RBD as Fig. 2B.
*(4) Page 9: "[...] Rgf1 and Rgf3 localize as early as the time of ring assembly at an average SPB distance of 4-5 µm (Fig. 3D)." This sentence is confusing. How was the average calculated over the earliest ring assembly in non-time-lapse data? Fig. 3DE show distances between SPBs as short as 2.5 µm, not 4-5 µm, and average of ~8 µm for all cells at different stages of mitosis. This confusion needs to be clarified. *
We thank the reviewer for observing this mistake in our writing and interpretation. We agree that the text does not reflect the accurate interpretations of the data collected and have now fixed these errors. The current sentence reading “In an asynchronous population of cells, we find that Rgf1 and Rgf3 localize as early as the time of ring assembly at an average SPB distance of 4-5µm.” has now been replaced with the description shown below-
“Using the distance between SPBs of anaphase cells as a proxy for timing of cytokinesis, we find that in most anaphase cells, Rgf1-GFP and Rgf3-eGFP was localized at the division site at very early stages in anaphase (Fig. 3D, E). This can be observed by the short distance between the SPBs of ~2µm (Fig. 3D). We also measured the distance for which active Rho1 appeared at the division site, and find that at the distance between SPBs of ~10µm, active Rho1 was present at the division site in ~50% of the population of control cells (Fig. 3E).”
*(5) Fig. 5. Both the intensity and onset of RBD-mNG localization were affected by cdc42g12v expression. These two may form a causative relationship: reduced overall RBD signal may cause failed detection of early RBD localization. Can the authors compare cells with similar mean RBD-mNG signal intensities (Fig. 5B) and confirm that the timing of appearance at the division site is still delayed in gef1+ cdc42g12v relative to gef1+ empty? *
We thank the reviewers for pointing this out and appreciate the opportunity to further clarify our observations. While there is clear decrease in Rho-probe intensity at the division site of on cells expressing cdc42G12V, we did see some variation in the extent of the decrease likely due to the variation in the expression levels of cdc42g12V. To provide a more accurate analysis of our observation we have shown the changes in the timing and intensities of Rho-probe localization. However, due to the noisy nature of the data we cannot compare the intensities in individual cells at specific spindle pole body distance between cells. As observed cdc42G12V significantly reduces Rho1 activity globally, not just at the division site. To cherry-pick cdc42G12V cells with similar active rho1 intensity to assess time of Rho1 activation may lead to subconscious data manipulation and will not address how early Rho1 activation is regulated.
*Reviewer #3
Onwubiko et al., present a clear and well written manuscript detailing the mechanistic understanding of how Rho1 is activated in a timely manner to ensure cytokinesis occurs in a scheduled manner at the end of telophase. Using fission yeast as a model system, and with the development of a novel Rho1 biosensor, they implicate a series of GTPases, exchange factors, GTPase activating proteins and kinases acting downstream of Cdc42 in the timely activation of Rho1. Specifically, they find that Cdc42 prevents premature Rho1 activation in early anaphase in a manner requiring the kinase Pak1. They observe that the Rho1 activators Rgf1 and Rgf3 localise to the division site in early anaphase, but Rho1 doesn't get activated until late anaphase, suggesting that control mechanisms ensure that these GEFs are held inactive, or that RhoGAP activity is able to balance this activation in early anaphase. This suppression of Rho1 activity in early anaphase requires Cdc42 and Pak1 and implicate (by omission) Rgf1, rather than Rgf3, is the relevant GEF.
I liked this manuscript, it was clearly written the experimental progression was logical and the data were easy to interpret from the figures. The conclusions were precise, believable and not overstated. The manuscript provides novel observations and through good use of a series of rescues/mutants, illuminates a pathway that is held in check by Cdc42 to ensure timely Rho1 activation. The novel Rho1 probe is exciting and shows well differently regulated pools of active Rho1 at the division site and the growing tips. I thought the co-imaging/measurement of ring placement and SBP duplication allowed a really clear understanding of the kinetics during this rapid phase of the cell cycle. A critique of the study is that the the mechanism by which Cdc42 controls Pak1, and by which Pak1 controls Rgf1/Rgf2 is left unclear. I guess there could always be a molecular expansion of these points (e.g., how does Cdc42 control Pak1; how does Pak1 control Rgf1; how is Rgf activity restricted when localised), but I think that would only enhance, rather than change, the level of detail of the paper's message. I think the paper's current conclusions stand on their own, the data is clear and believable, the experiments are well performed. There are a number of observations in the paper that are left open for future studies, and I think this is a positive (e.g., any separable role of Rgf1/Rgf2 and how Rga5 integrates into this pathway. As such, I am tempted to recommend accept with only minor amendments as outlined below.
- P8 P15: should the call out be to Fig 2C, rather than 2B. *
We thank reviewer for their highlighting this error in our text. We have now fixed it.
*P14 L17: should it be 'gef1+ rgf3-', not 'gef1+, rgf3+' *
We have fixed this error and further clarified the terms for easy understanding.
Structure wise, I thought the section on Rga5 didn't really fit well on P16; it seemed sandwiched between two sections on GEFs. Is there a more appropriate place to place these data - perhaps between the paragraph breaks on P17? Related to this data, the conclusion on P16 suggests 'other' regulators of RhoGAP activity act to repress Rho1 function. Would 'additional' regulators of RhoGAP activity be more appropriate as there is some function contributed by Rga5?
We have now moved this section to the end of the section on Rho1 regulators after we discuss the Rho1 GEFs. We have also modified the text to clarify that multiple regulators are likely involved in the regulation of Cdc42-mediated Rho1 inhibition.
*In Fig 10b, you haven't defined orb2-34. Is it the rgf1-delete?
*
The mutant orb2-34 is a temperature sensitive allele of the pak1 kinase. To avoid confusion, we have replaced the allele name with pak1-ts in figure 10 and in the text.
- I find the sentence at the top of P18: 'Rho1 activation in pak1+ rgf1+....at 25oC and 35.5oc occurred at longer and similar SBP distances' quite hard to interpret. Could you perhaps expand it to make your message clearer? *
We thank the reviewer for pointing this out. These statements have now been re-written for clarity. 'Rho1 activation in pak1+ rgf1+....at 25ºC and 35.5ºC” has been changed, and now reads as follows:
“The timing of RBD-mNG localization at the division site occurs late in cytokinesis during late anaphase as depicted by longer SPB distances in pak1+ rgf1+, pak1-ts rgf1+, and pak1+ rgf1Δ cells at 25ºC (Fig.10B). As previously shown, RBD-mNG localizes to the division site in early anaphase in pak1-ts rgf1+ cells at the restrictive temperature (35.5ºC, Fig. 7A, B). In agreement with our reasoning, early RBD-mNG localization in pak1-ts mutants at 35.5ºC was rescued in the absence of rgf1 (Fig. 10A, B).”
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Referee #3
Evidence, reproducibility and clarity
Onwubiko et al., present a clear and well written manuscript detailing the mechanistic understanding of how Rho1 is activated in a timely manner to ensure cytokinesis occurs in a scheduled manner at the end of telophase. Using fission yeast as a model system, and with the development of a novel Rho1 biosensor, they implicate a series of GTPases, exchange factors, GTPase activating proteins and kinases acting downstream of Cdc42 in the timely activation of Rho1. Specifically, they find that Cdc42 prevents premature Rho1 activation in early anaphase in a manner requiring the kinase Pak1. They observe that the Rho1 activators Rgf1 and Rgf3 localise to the division site in early anaphase, but Rho1 doesn't get activated until late anaphase, suggesting that control mechanisms ensure that these GEFs are held inactive, or that RhoGAP activity is able to balance this activation in early anaphase. This suppression of Rho1 activity in early anaphase requires Cdc42 and Pak1 and implicate (by omission) Rgf1, rather than Rgf3, is the relevant GEF.
I liked this manuscript, it was clearly written the experimental progression was logical and the data were easy to interpret from the figures. The conclusions were precise, believable and not overstated. The manuscript provides novel observations and through good use of a series of rescues/mutants, illuminates a pathway that is held in check by Cdc42 to ensure timely Rho1 activation. The novel Rho1 probe is exciting and shows well differently regulated pools of active Rho1 at the division site and the growing tips. I thought the co-imaging/measurement of ring placement and SBP duplication allowed a really clear understanding of the kinetics during this rapid phase of the cell cycle. A critique of the study is that the the mechanism by which Cdc42 controls Pak1, and by which Pak1 controls Rgf1/Rgf2 is left unclear. I guess there could always be a molecular expansion of these points (e.g., how does Cdc42 control Pak1; how does Pak1 control Rgf1; how is Rgf activity restricted when localised), but I think that would only enhance, rather than change, the level of detail of the paper's message. I think the paper's current conclusions stand on their own, the data is clear and believable, the experiments are well performed. There are a number of observations in the paper that are left open for future studies, and I think this is a positive (e.g., any separable role of Rgf1/Rgf2 and how Rga5 integrates into this pathway. As such, I am tempted to recommend accept with only minor amendments as outlined below.
- P8 P15: should the call out be to Fig 2C, rather than 2B.
- P14 L17: should it be 'gef1+ rgf3-', not 'gef1+, rgf3+'
- Structure wise, I thought the section on Rga5 didn't really fit well on P16; it seemed sandwiched between two sections on GEFs. Is there a more appropriate place to place these data - perhaps between the paragraph breaks on P17? Related to this data, the conclusion on P16 suggests 'other' regulators of RhoGAP activity act to repress Rho1 function. Would 'additional' regulators of RhoGAP activity be more appropriate as there is some function contributed by Rga5?
- In Fig 10b, you haven't defined orb2-34. Is it the rgf1-delete?
- I find the sentence at the top of P18: 'Rho1 activation in pak1+ rgf1+....at 25oC and 35.5oc occurred at longer and similar SBP distances' quite hard to interpret. Could you perhaps expand it to make your message clearer?
Significance
I think the advance here is a genetic understanding of control mechanisms that order the exit from mitosis. The interplay between numerous GTPases and kinases must ensure a timely and ordered progression through M-exit, but it is often unclear how these activities are coordinated. A strength of the yeast system is that dependencies can be clearly visualised and the authors do a good job here to order the enzymatic activities needed to activate Rho1 in a timely manner for cytokinesis at the end of telophase.
I think this manuscript will be of interest to those interested in the cell biology of mitotic exit, the interplay between kinases and GTPases and those interested in the systems/netwoek biology of these processes. The description of a new Rho1 biosensor is an excellent tool for the community.
I am a cell biologist (mammalian) with interests in M-exit programmes that ensure a timely and ordered reestablishment of interphase architecture.
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Referee #2
Evidence, reproducibility and clarity
In many fungal cells, including fission yeast, the deposition of a new cell wall (a septum) between daughter cells is essential for cytokinesis. Cell wall synthases are trafficked to and activated at the division site, and dysregulated trafficking and/or synthase activation can lead to cytokinetic defects. In this study, the authors use fluorescent probes for Cdc42 and Rho1 activity and live-cell imaging to investigate the timing and regulation of Rho1 activity in fission yeast, and specifically, the role of Cdc42 in regulating Rho1. Summary of the proposed model: Gef1 -> active Cdc42 -> Pak1 --| Rgf1 -> active Rho1 -> septum formation
Major comments
- As far as I can gather from the authors' description in the manuscript and quick literature search, this will be the first publication in S. pombe utilizing the HR1-C2 domain of Pkc2p as fluorescent probe for active Rho1 (RBD-mNG). While a comparable domain of S. cerevisiae Pkc1p (not "pck2" as referenced by the authors in Page 25) has been used for similar purposes, given the importance of this probe and the precedent it sets in the S. pombe literature, it is imperative that proper tests are performed to validate that its localization reflects activity of Rho1 and nothing else (such as membrane binding of the C2 domain or transcriptional regulation of the pkc2 promoter). Such tests should also be independent of the hypotheses central to the current study (i.e., effects of Gef1, Pak1, Rgf1/2 on the timing of RBD-mNG localization). Can the authors provide data to address this point? Examples include, but not limited to, rho1 mutants, expression of constitutively active Rho1, or temporary expression of dominant-negative Rho1.
- Related, M&M does not provide sufficient details about the amino-acid positions corresponding to the "RBD" domain of Pkc2, thus precluding readers from reproducing the experiments. This needs to be clarified.
- In Figure 1B, RBD1-mNG localizes clearly to the medial region of rho2∆ cells when the Rlc1-tdTomato ring has not formed. Does this mean that Rho2 has a major role in forming the contractile ring that is independent of Rho1 activation? On this other hand, however, data in Fig. S2BC suggest that RBD-mNG does not localize to the medial region in rho2∆ cells until Rlc1-tdTomato ring forms (the timing of which seems normal). This discrepancy needs to be addressed.
- Given the nature of RBD-mNG localization, it seems unavoidable to have some level of arbitrariness in measuring the onset of its localization at the division site. It would be advisable for the authors to be specific in M&M about how they defined the onset of localization, i.e., whether it was based on universal threshold in signal intensity, ratio, etc. or on manual curation (ideally double-blind).
Minor comments
- Throughout the manuscript, there are quite a few places where inconsistencies in genetic nomenclature can cause confusion to readers. Below are some examples. Figs. 6B, 7B, 10B: pak1(-ts), shk1, and orb2-34 (including faint labels under category marks in 6B). Fig. 9B (gef1+ rgf1∆) vs 9C (rgf1∆). Wild-type alleles are implicit in some figures, while explicit in others.
- The first hypothesis (Fig. 1C) is that the AMR might regulate Rho1 activation. The ring is disrupted with LatA, but Rho remains active. They cite this as evidence that the AMR does not activate Rho1, but were the cells treated before or after the rings formed? If before, then the experiment demonstrates what the authors claim, but if after, it only shows that the AMR is not essential to maintain Rho activity.
- Page 8: "Time-lapse imaging of cells simultaneously expressing CRIB-3xGFP and RBD-tdTomato [...] while Rho1 is activated ~20 minutes after SPB duplication (Fig. 2B)." This appears to refer to Fig. 2C.
- Page 9: "[...] Rgf1 and Rgf3 localize as early as the time of ring assembly at an average SPB distance of 4-5 µm (Fig. 3D)." This sentence is confusing. How was the average calculated over the earliest ring assembly in non-time-lapse data? Fig. 3DE show distances between SPBs as short as 2.5 µm, not 4-5 µm, and average of ~8 µm for all cells at different stages of mitosis. This confusion needs to be clarified.
- Fig. 5. Both the intensity and onset of RBD-mNG localization were affected by cdc42g12v expression. These two may form a causative relationship: reduced overall RBD signal may cause failed detection of early RBD localization. Can the authors compare cells with similar mean RBD-mNG signal intensities (Fig. 5B) and confirm that the timing of appearance at the division site is still delayed in gef1+ cdc42g12v relative to gef1+ empty?
Referees cross-commenting
I find all reviewer comments fair and have nothing specific to add.
Significance
The mechanisms governing septum formation during cytokinesis represent a key regulatory step in cytokinesis. Prior work showed that the Rho GTPases Cdc42 and Rho1 together control the timing of septum formation in S. pombe, and in S. cerevisiae, similar antagonistic regulation between Cdc42 and Rho1 has been reported previously (Atkins et al., J. Cell Biol. 2013 202: 231-240; Onishi et al., J Cell Biol. 2013 202: 311-329), but the precise molecular mechanisms remained unclear.
This is an important study that addresses the interplay between two major Rho-type small GTPases involved in cell division of many eukaryotic cells, and highlights their roles outside of the regulation of contractile ring. However, there are some issues that need to be addressed prior to publication, as listed above.
Keywords for the reviewer's field of expertise: S. pombe, S. cerevisiae, cytokinesis, Rho1, Cdc42, septum, MEN/SIN, genetics, cell biology, biochemistry.
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Referee #1
Evidence, reproducibility and clarity
This manuscript focuses on the role of Cdc42 in Rho1 activation during fission yeast cytokinesis. The primary finding is that active Cdc42 and its downstream effector Pak1 prevents accumulation of active Rho1 and the synthesis of cell wall material, at early stages of cytokinesis and despite the local recruitment of the Rho1 GEF Rgf1. The data supporting these conclusions are reasonably sound.
Additional experiments are presented to suggest that Cdc42 and Pak1 negatively regulate Rgf1, this conclusion is not as strongly supported (though it may be true)
These study relies on a newly described probe for active Rho1. However this probe is not sufficiently well validated.
Overall the manuscript was not assembled with sufficient care and rigor, these deficits could be readily corrected.
The major point of the paper is that Cdc42 and Pak1 negatively regulate Rho1 activation. However, during late cytokinesis, active Cdc42 and active Rho1 co-exist at the division site. Thus, Cdc42 activation induces a delay in Rho1 activation, but how this delay is overcome is not investigated or even discussed. Indeed, while the delay is shown the transience of this inhibition is not explicitly mentioned. At a minimum, the authors should highlight this point for the readers.
Specific points
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- RBD probe This probe is central to this manuscript. However, there is insufficient validation of its target. Figure 1 shows the localization and its independence of Rho2. The authors should provide direct evidence that it recognizes Rho1 (for example using a repressible promotor or an anchor away approach).
At various places in the manuscript the authors refer to this probe as "Rho-probe", RBD-probe, RBD, RBD-(mNG or tdTomato). On page 11 the authors state, "As per our observations, we refer to the Rho-probe signal at the division site as active Rho1 from here onwards." Yet, in the very next paragraph they refer to the localization of the "Rho probe". This is also an issue with the figures. For example, in figures 4B,C ; 5B,C; 6B; 7B,C the figures are titled either "Rho1 activation at division site", "Rho1-probe at division site"; "Rho1-probe appearance at division site" ; "Rho1-probe in non-constricting rings". In fig 3, RBD-nNG is quantified in a graph entitled "localizaton [sic] of Rho1-GEFs at division site"
In all figures but two, 5c and 7c, the authors quantify Rho1 activation by the presence or absence of the probe, rather than a quantitative measure or the extent of recruitment of the probe. This could be analyzed my quantitatively. 2. - Regulation of Rgf1 by Cdc42 and Pak1. The results shown in figure 8 show that "early Rho1 activation in gef1 mutants is not Rgf3-dependent". Figure 9 establishes "loss of rgf1 prevents premature Rho1 activation in gef1Δ cells restoring it to normal in late anaphase (Fig.9A, B)." This finding indicates that Rgf1, but not Rgf3, is required for Rho1 premature activation. This finding doesn't rule out the possibility that Cdc42 and Pak1 might be required to turn off RhoGAPs to allow active Rho1 to accumulate. This analysis concludes with this unclear and ungrammatical sentence, "While we were unable to assess the Rho-probe in the rgf1Δ rgf2Δ double mutants due to its lethality [sic; is the Rho probe lethal?], our observations suggest that apart from Rgf1 early Rho1 activation in gef1Δ cells is either due to activation of Rgf2 or due to inhibition of Rga5." The conclusion that this regulation is due to control of Rgf1 should be toned down. E.g. from the abstract: "We provide functional and genetic evidence which indicates that Pak1 regulates Rho1 activation likely via the regulation of its GEF Rgf1."
Referees cross-commenting
I think reviews are appropriate and speak for themselves.
Significance
This manuscript ties together several recent papers from the author's lab on the control of Cdc42 activation during cytokinesis and older papers on the role of Rho1 in Bgs1 activation. It provides missing information into the temporal regulation of septum assembly.
The authors make a point of the similarities of fission yeast cytokinesis to animal cell cytokinesis. Indeed the second sentence reads, "The fission yeast model system divides via an actomyosin-based contractile ring, which is assembled in the medial region of the cell, as in animal cells (Balasubramanian et al., 2004; Pollard, 2010).". However, the authors fail to point out the many differences between yeast and animal cell cytokinesis until the last paragraph of the discussion. If the authors want to include the similarities in the introduction, they should also include the differences. For example, ring assembly is independent of Rho1 activation in fission yeast, but dependent on RhoA activation in animal cells.
This work will be of interest to biologists working on yeast cell division. To a lesser extent it will be of interest to biologists interested in cytokinesis and coordination of distinct GTPase pathways.
Additional points
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- The text is overly wordy and needs extensive revision. Many of the experiments could be explained more clearly and with somewhat less genetic jargon. The introduction has quite a bit of extraneous information and lacks relevant facts, such as the function of Bgs1, which is central to the results.
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- page 4 "GEFs promote GTP binding, thus keeping the GTPase active while the GAPs increase GTP hydrolysis, thus promoting GTPase inactivation." GEFs promote GTP binding, but they do not keep the GTPase active (an inhibitor of a RhoGAP would do that), they activate the GTPases.
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- The current literature on animal cell cytokinesis indicates little direct role in cytokinesis, rather than the author's statement, "In larger eukaryotes, the role of Cdc42 activation has been reported mostly in meiotic division events such as polar body extrusion in oocytes, but not much is known about its role in cytokinesis in somatic cell division (Drechsel et al., 1997; Na and Zernicka-Goetz, 2006)." See for example, PMID 10898977, 10871280 which indicate Cdc42 does not play a major role during cytokinesis in at least a few systems where it has been analyzed.
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Reply to the reviewers
We thank the reviewers for their enthusiastic support for our work and their insightful comments and suggestions which we believe strengthen the manuscript. Below we detail how we propose to respond to each of the specific points raised by each reviewer.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
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Summary:*
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In the article entitled "Unique functions of two overlapping PAX6 retinal enhancers", Uttley and coworkers characterize in detail the activity of two conserved human enhancers (i.e. NRE and HS5) previously reported to drive Pax6 expression to the neural retina. By integrating these enhancers in a PhiC31 landing site using a dual enhancer-reporter cassette, they generated a zebrafish stable line in which their activity can be followed by the expression of GFP (NRE) and mCherry (HS5). The authors show that although the enhancers have a partially overlapping activity at early stages (24hpf), later on (48 and 72hpf) they activity domains segregate: to stem cells and differentiated amacrine cells for NRE, and to proliferating progenitors and differentiated Müller glia cells for HS5. To this end they used two different approaches: a scRNA-seq analysis of sorted cells from the transgenic line and a immunofluorescent analysis employing cell specific markers. The authors conclude that their analysis allowed the identification of unique cell type-specific functions.*
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Major comments:*
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In general terms, the article is technically sound (please, see section B for an assessment of the significance of the findings). The methodology used and the data analysis are accurate. The work is well presented, the figures are clear, and the previous literature properly cited. My main concerns are the following:*
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1) A general concern on the main conclusion of the work "the identification of unique cell type-specific functions for these enhancers". This is in my opinion only partially addressed by the study, as the conclusions are limited due to the absence of genetic experiments: such as deleting the enhancers in their native genomic context (either in human organoids or the homologous sequence in animal models), or at least assessing the effect of mutating their sequence in transgenesis assays in zebrafish. I understand that these functional assays may be out of the scope of the current work, but then the text should be toned down (the word "function" is extensively used) to make clear that the authors mean just expression. I would suggest substituting the word by "activity" in many instances.*
- The absence of further genetic experiments also limits the significance of the study (see section B).*
We appreciate and agree with the reviewer’s concern and would substitute the word “function” with “activity” throughout the manuscript.
2) Whereas the work in general is technically correct (particularly transgenic lines and scRNA-seq data are well described and presented), the co-expression analyses using cell-specific markers (figure 5) need to be improved. There are several issues here. First, the magnification shown is too low to appreciate the colocalization details in the figure. The panels should be replaced by others with higher magnification/resolution (see also minor comment on color-blind compatible images) * In addition, the selection of the markers is suboptimal. Although PCNA is a good general marker of the entire CMZ, it would be advisable to repeat the experiments using more specific markers of the stem cell niche (e.g. rx1, vsx2; Raymond et al 2006; BMC dev Biol) to better define the enhancers expression domain. In addition, HuC/D labels both RGCs and amacrines, and the colocalization could also be refined using amacrine specific markers (e.g. ptf1a : Jusuf & Harris 2009, Neural Dev).*
In the revised version of the manuscript, we would:
- Provide higher magnification images as suggested by the reviewer
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Provide additional stainings and justification for our choice of markers used in these colocalizaion experiments Minor comments:
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1.- The work includes several figures (1, 2, 5, 6 and S1) showing colocalization experiments in which channels are shown in red and green. I would advise replacing the red channel with magenta (or the green with cyan) in order to make the figures accessible to readers with color-blindness. This also applies to the schematic representations in figure 6.*
We will change the channel colours throughout the manuscript as suggested by the reviewers
2.- It is unclear in the text/images whether the expression driven by the HS5 enhancer is exclusively restricted to temporal retina throughout development (By the way, this differential nasal vs temporal expression should also be included in the final scheme in Figure 6). Does this mean that the expression of Pax6 in proliferating progenitors and Müller glia cells in the nasal retina is not controlled by this enhancer? To which extent is Pax6 needed to maintain the identity of these cell types?
We will modify the figures as suggested and also include more details of expression overlap with PAX6 expression in the text of the revised manuscript.
3.- The following sentence in the Discussion "To the best of our knowledge, ours is the first report where the activities of developmental enhancers have been mapped in vivo at single-cell resolution to reveal distinct patterns of activity" should be removed/rephrased. I would argue that the activity of cis-regulatory regions associated to any developmental gene are genome-wide mapped at single cell resolution in each scATACseq experiment.
We agree that scATAC-seq gives information about potentially active enhancers but it does not define the precise cell-types unless overlapped with expression data. Our method is aimed at ‘defining’ the precise cell-types where the enhancer is active and has the potential to be used to build high resolution maps of cell-type specific enhancer usage for loci with multiple enhancers driving a single gene. We will discuss this in detail in the revised version of the manuscript.
4.- In the methods section: * (a) FACS experiments: Please provide a supplementary Figure to graphically account for all gating/sorting strategies. * (b) ScRNA-seq analysis: Please provide the values of mean reads per cell and median genes per cell as obtained from Cell Ranger. This would be informative for others performing similar experiments
This will be included in the revised version of the manuscript.
**Referees cross-commenting** * I agree with the comments by reviewer #2 on the FACsorting experiments, the description of the landing sites, and the limited significance of the results.*
Reviewer #1 (Significance (Required)):
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As described in the previous section, the technical quality of this work is high in general terms. The experiments presented are clear and the conclusions straightforward. In that sense, the study will be a useful reference for those interested in the regulatory logic of Pax6 during eye development, including mainly developmental biologists and human geneticists. This may be particularly the case if new variants can be associated with these enhancers in microphthalmic patients.*
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The significance and novelty of the findings is however limited by several factors:*
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a) First, although the level of detail described in this article was not achieved previously, the human enhancers NRE and HS5 (or their conserved homologous in other vertebrates) were previously reported to drive Pax6 expression to the neural retina in transgenesis assays.(Kammandel et al 1999; Marquardt et al 2001; McBride et al 2011; Ravi et al 2013; Kim et al 2017).*
We agree that the enhancers we describe in this study have been studied before. However, we would like to argue that ours is the first study where we define precise cell-types for the activity of these enhancers. We will revise the discussion to strengthen this argument.
b) As mentioned in the previous section, the transgenesis assays are not complemented with genetic experiments. The function of the enhancers on retina differentiation and cell fate determination could have been investigated either by deleting them (or their homologous in different species) in their native context, or by exploring their regulatory grammar introducing point mutations or micro-deletions in transgenesis assays.
We agree that the suggested experiments would be useful for unambiguously establishing the functions of these enhancers and we will discuss these prospects in the revised version of the manuscript.
c) For reasons not explained in the text, the analysis focuses only in two of the many cis-regulatory regions controlling Pax6 expression in the retina (Lima Cunha et al 2019, Genes). In the absence of a more comprehensive analysis is difficult assessing the relevance of the findings here described.
We agree that other enhancers for the PAX6 locus should be investigated using similar analysis pipeline to build a complete picture of the enhancer mediated regulation of PAX6. We will discuss this in the revised version of the manuscript.
d) Finally, from a very general methodological point of view, the approach of using scRNA-seq to investigate enhance activity at a single-cell level is valid and original. However, it is unclear to which extent will be a useful method for many studies, particularly if the activity of endogenous elements is being assessed. In such cases, available scATAC-seq data will provide genome-wide information on the activity of any cis-regulatory element with cell resolution with no need for transgenesis assays and sorting experiments. * We thank the reviewer for recognising the novelty of the approach we describe in this manuscript. We will discuss the merits and demerits of our method with scATAC-seq experiments in the revised version of the manuscript.*
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this work, Uttley et al fine characterize two previously described Pax6 retinal enhancers (NRE and HS5) by combining QSTARZ transgénesis method in zebrafish (allowing to produce site-specific integrations of a dual enhancer reporter cassette), scRNAseq and co-immunostaining with specific markers for different retinal cell populations. * The work is experimentally very well performed and well presented and only minor considerations are raised below: * - Authors observe that a large fraction Of FACs sorted cells do not display expression of mCherry or EGFP RNAm in their scRNAseq analysis and attribute this to read dropout in the scRNAseq data and/ or to false-positive FAC cell selection. However, a third possibility exists: n fact due to the high stability of the EGFP and mCherry reporters cells or their progeny could maintain relatively high levels of these reporters even after transcriptional downregulation. Accordingly, the two reporters are strongly expressed in retinal precursor at early stages (24hpf). Thus, in my opinion, it is possible that some cells expressing these reporters retained significant EGFP/mCherry protein levels at 48hpf. Could the authors comment on this? Besides, authors could provide the FACsorting data to give an idea of whether only highly EGFP/ mCherry expressing cells were selected or whether also the low or mild expressing ones were included in the scRNAseq analysis. Finally, a combination of HCR/FSH and GFP//mCherry immunostaining could be used to assess whether a discrepancy in the protein vs mRNA distribution of the reporters exists. * - The authors could provide the information on the landing site used for the QSTARZ transgene integration. While from their previous publication (Bhatia et al 2021) I assume it is the chr6 landing site, it would be worth having this information in the manuscript, as well as a genotyping validation of the correct integration.*
We will address these points and provide relevant additional data where needed in the revised version of the manuscript.
**Referees cross-commenting** * I agree with all the points raised by reviewer 1. Particularly I also find that scATACseq experiments already allow testing, to some extent, enhancer activity at cellular level.*
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Reviewer #2 (Significance (Required)):*
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From the biological point of view the work provides only an incremental advance in our understanding of the functions of the HS5 and NRE PAX6 enhancers and of PAX6 regulation in the retina. In fact, unraveling the precise contribution of these enhancers to Pax6 retinal expression and the trans-regulatory code controlling their activity would require complex genetic experiments and would fall out of the scope of this work, requiring an extensive amount of work which could not be addressed in the short term. Thus, this work should be regarded as a methodological resource, with its main strength consisting of the use scRNAseq to fine-characterize enhancer activity.*
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Referee #2
Evidence, reproducibility and clarity
In this work, Uttley et al fine characterize two previously described Pax6 retinal enhancers (NRE and HS5) by combining QSTARZ transgénesis method in zebrafish (allowing to produce site-specific integrations of a dual enhancer reporter cassette), scRNAseq and co-immunostaining with specific markers for different retinal cell populations.
The work is experimentally very well performed and well presented and only minor considerations are raised below:
- Authors observe that a large fraction Of FACs sorted cells do not display expression of mCherry or EGFP RNAm in their scRNAseq analysis and attribute this to read dropout in the scRNAseq data and/ or to false-positive FAC cell selection. However, a third possibility exists: n fact due to the high stability of the EGFP and mCherry reporters cells or their progeny could maintain relatively high levels of these reporters even after transcriptional downregulation. Accordingly, the two reporters are strongly expressed in retinal precursor at early stages (24hpf). Thus, in my opinion, it is possible that some cells expressing these reporters retained significant EGFP/mCherry protein levels at 48hpf. Could the authors comment on this? Besides, authors could provide the FACsorting data to give an idea of whether only highly EGFP/ mCherry expressing cells were selected or whether also the low or mild expressing ones were included in the scRNAseq analysis. Finally, a combination of HCR/FSH and GFP//mCherry immunostaining could be used to assess whether a discrepancy in the protein vs mRNA distribution of the reporters exists.
- The authors could provide the information on the landing site used for the QSTARZ transgene integration. While from their previous publication (Bhatia et al 2021) I assume it is the chr6 landing site, it would be worth having this information in the manuscript, as well as a genotyping validation of the correct integration.
Referees cross-commenting I agree with all the points raised by reviewer 1. Particularly I also find that scATACseq experiments already allow testing, to some extent, enhancer activity at cellular level.
Significance
From the biological point of view the work provides only an incremental advance in our understanding of the functions of the HS5 and NRE PAX6 enhancers and of PAX6 regulation in the retina. In fact, unraveling the precise contribution of these enhancers to Pax6 retinal expression and the trans-regulatory code controlling their activity would require complex genetic experiments and would fall out of the scope of this work, requiring an extensive amount of work which could not be addressed in the short term. Thus, this work should be regarded as a methodological resource, with its main strength consisting of the use scRNAseq to fine-characterize enhancer activity.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In the article entitled "Unique functions of two overlapping PAX6 retinal enhancers", Uttley and coworkers characterize in detail the activity of two conserved human enhancers (i.e. NRE and HS5) previously reported to drive Pax6 expression to the neural retina. By integrating these enhancers in a PhiC31 landing site using a dual enhancer-reporter cassette, they generated a zebrafish stable line in which their activity can be followed by the expression of GFP (NRE) and mCherry (HS5). The authors show that although the enhancers have a partially overlapping activity at early stages (24hpf), later on (48 and 72hpf) they activity domains segregate: to stem cells and differentiated amacrine cells for NRE, and to proliferating progenitors and differentiated Müller glia cells for HS5. To this end they used two different approaches: a scRNA-seq analysis of sorted cells from the transgenic line and a immunofluorescent analysis employing cell specific markers. The authors conclude that their analysis allowed the identification of unique cell type-specific functions.
Major comments:
In general terms, the article is technically sound (please, see section B for an assessment of the significance of the findings). The methodology used and the data analysis are accurate. The work is well presented, the figures are clear, and the previous literature properly cited. My main concerns are the following:
- A general concern on the main conclusion of the work "the identification of unique cell type-specific functions for these enhancers". This is in my opinion only partially addressed by the study, as the conclusions are limited due to the absence of genetic experiments: such as deleting the enhancers in their native genomic context (either in human organoids or the homologous sequence in animal models), or at least assessing the effect of mutating their sequence in transgenesis assays in zebrafish. I understand that these functional assays may be out of the scope of the current work, but then the text should be toned down (the word "function" is extensively used) to make clear that the authors mean just expression. I would suggest substituting the word by "activity" in many instances. The absence of further genetic experiments also limits the significance of the study (see section B).
- Whereas the work in general is technically correct (particularly transgenic lines and scRNA-seq data are well described and presented), the co-expression analyses using cell-specific markers (figure 5) need to be improved. There are several issues here. First, the magnification shown is too low to appreciate the colocalization details in the figure. The panels should be replaced by others with higher magnification/resolution (see also minor comment on color-blind compatible images) In addition, the selection of the markers is suboptimal. Although PCNA is a good general marker of the entire CMZ, it would be advisable to repeat the experiments using more specific markers of the stem cell niche (e.g. rx1, vsx2; Raymond et al 2006; BMC dev Biol) to better define the enhancers expression domain. In addition, HuC/D labels both RGCs and amacrines, and the colocalization could also be refined using amacrine specific markers (e.g. ptf1a : Jusuf & Harris 2009, Neural Dev).
Minor comments:
- The work includes several figures (1, 2, 5, 6 and S1) showing colocalization experiments in which channels are shown in red and green. I would advise replacing the red channel with magenta (or the green with cyan) in order to make the figures accessible to readers with color-blindness. This also applies to the schematic representations in figure 6.
- It is unclear in the text/images whether the expression driven by the HS5 enhancer is exclusively restricted to temporal retina throughout development (By the way, this differential nasal vs temporal expression should also be included in the final scheme in Figure 6). Does this mean that the expression of Pax6 in proliferating progenitors and Müller glia cells in the nasal retina is not controlled by this enhancer? To which extent is Pax6 needed to maintain the identity of these cell types?
- The following sentence in the Discussion "To the best of our knowledge, ours is the first report where the activities of developmental enhancers have been mapped in vivo at single-cell resolution to reveal distinct patterns of activity" should be removed/rephrased. I would argue that the activity of cis-regulatory regions associated to any developmental gene are genome-wide mapped at single cell resolution in each scATACseq experiment.
- In the methods section:
- (a) FACS experiments: Please provide a supplementary Figure to graphically account for all gating/sorting strategies.
- (b) ScRNA-seq analysis: Please provide the values of mean reads per cell and median genes per cell as obtained from Cell Ranger. This would be informative for others performing similar experiments
Referees cross-commenting I agree with the comments by reviewer #2 on the FACsorting experiments, the description of the landing sites, and the limited significance of the results.
Significance
As described in the previous section, the technical quality of this work is high in general terms. The experiments presented are clear and the conclusions straightforward. In that sense, the study will be a useful reference for those interested in the regulatory logic of Pax6 during eye development, including mainly developmental biologists and human geneticists. This may be particularly the case if new variants can be associated with these enhancers in microphthalmic patients.
The significance and novelty of the findings is however limited by several factors:
- a) First, although the level of detail described in this article was not achieved previously, the human enhancers NRE and HS5 (or their conserved homologous in other vertebrates) were previously reported to drive Pax6 expression to the neural retina in transgenesis assays.(Kammandel et al 1999; Marquardt et al 2001; McBride et al 2011; Ravi et al 2013; Kim et al 2017).
- b) As mentioned in the previous section, the transgenesis assays are not complemented with genetic experiments. The function of the enhancers on retina differentiation and cell fate determination could have been investigated either by deleting them (or their homologous in different species) in their native context, or by exploring their regulatory grammar introducing point mutations or micro-deletions in transgenesis assays.
- c) For reasons not explained in the text, the analysis focuses only in two of the many cis-regulatory regions controlling Pax6 expression in the retina (Lima Cunha et al 2019, Genes). In the absence of a more comprehensive analysis is difficult assessing the relevance of the findings here described.
- d) Finally, from a very general methodological point of view, the approach of using scRNA-seq to investigate enhance activity at a single-cell level is valid and original. However, it is unclear to which extent will be a useful method for many studies, particularly if the activity of endogenous elements is being assessed. In such cases, available scATAC-seq data will provide genome-wide information on the activity of any cis-regulatory element with cell resolution with no need for transgenesis assays and sorting experiments.
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Reply to the reviewers
Response to Reviewers' Comments on Fumagalli et al. "Nirmatrelvir treatment blunts the development of antiviral adaptive immune responses in SARS-CoV-2 infected mice" (Preprint RC-2022-01777).
We wish to thank the reviewers for the scholarly review of our work and the very helpful comments. Based on their constructive suggestions, we have generated substantial new experimental data that, in our opinion, positively address all the major and minor concerns raised. In particular, we have confirmed the negative impact of nirmatrelvir treatment on adaptive immune responses in setting of robust SARS-CoV-2 replication (Delta infection in K18-hACE2 transgenic mice and mouse-adapted SARS-CoV-2 infection of wild-type mice).
One main and one supplemental figure have been added in response to the reviewers' comments. One additional figure – termed Reviewer Figure 1 – has been included in this letter for the reviewers' benefit; while addressing specific comments, we believe that the data depicted in this latter figure remain tangential to the main message of our work and, as such, it should not be incorporated in the final version. To aid the reviewers in the re-evaluation of this study, all relevant passages in the revised text have been written in red. A summary of the changes made to the figures and tables is provided as an appendix at the end of this letter.
Reviewers' comments:
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In this study, Fumagalli et. al evaluated the impact of Nirmatrelvir drug treatment on the development of SARS-CoV-2-specific adaptive immune responses in a mice model. Nirmatrelvir is one of the component of Paxlovid drug that has been shown to reduce the risk of progression to severe COVID-19 and long COVID. Herein, authors show that nirmatrelvir administration early after infection blunts the development of SARS-CoV-2-specific antibody and T cell responses. Upon secondary challenge, nirmatrelvir-treated mice developed fewer memory T and B cells to the infected lungs and to mediastinal lymph nodes, respectively. Overall, the experimental methods, figures, results, statistical analysis and findings of this study are interesting and convincing.
We wish to thank the reviewer for the overall positive assessment of our work.
CROSS-CONSULATION COMMENTS I agree with the Reviewer 2 comments.
Reviewer #1 (Significance (Required)): It was known that nirmatrelvir reduces the risk of severe covid and long covid but, whether its treatment has any impact on adaptive immune response was not known/evaluated. This study has importantly addressed that impact of nirmatrelvir treatment can impair both T and B cell adaptive immune responses. It would have been impactful to understand the mechanism of T and B cell immune response impairment following nirmatrelvir treatment in mice which they have already mentioned a limitation of the study.
We agree with this reviewer that the mechanism of T and B cell impairment following nirmatrelvir treatment should be addressed in future studies.
Moreover this study provides important implications for clinical management of COVID patients and to revise the treatment strategies to avoid virological and/or symptomatic relapse after Paxlovid/nirmatrelvir treatment completion that have been reported in some individuals.
We thank the reviewer for highlighting the impact of our results.
I am not a mice model expert. Not sure whether the viral dose given to mice in this study was optimal to study the impact of the said drug.
Depending on the virus used, we infected mice with 105-106 TCID50. This is in line with most studies of SARS-CoV-2 infection in mice. It is difficult to know what the average infectious dose in humans is, but the human challenge trial in young adults shows that exposure of individuals to as low as 10 TCID50 of SARS-CoV-2 led to detectable viral RNA in the upper airways (Killingley et al, 2022).
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary:
In this manuscript, the authors show that Paxlovid, a commonly used antiviral for SARS-CoV-2 infections, blunts the adaptive immune response to the virus. Indeed, they show convincing effects on T cell and B cell responses in the K18-hACE2 mouse model infected with Omicron variant. The effect is observed when drug treatment was started at 4, 24, or 48 h post infection. Experiments are well done and the data are presented clearly.
We thank the reviewer for the overall positive assessment of our work.
However, the early timing of drug administration resulted in minimal virus replication, thus likely limiting innate immune activation and antigenic exposure. Indeed, the authors show that the drug did not decrease adaptive responses to other viral infections, indicating that the effect on adaptive immunity in SARS-CoV-2 infection can be explained by decreased viral antigen production. Whether this is the mechanism by which relapse infections occur in humans after Paxlovid treatment is unclear.
Major comments:
The authors should discuss whether the timing of drug administration in their experiments is relevant to the timing of when Paxlovid is commonly started in humans. Does Paxlovid limit the adaptive immune response when given later in infection?
We thank the reviewer for raising this valid comment. First, we would like to point out that the kinetics of viral replication upon SARS-CoV-2 exposure differ between mice and humans. When mice are exposed to a high-dose (105 TCID50) aerosolized SARS-CoV-2, they show peak viral replication in the airways at day 3 post exposure and viral RNA is undetectable in the upper and lower airways after day 7 (Reviewer Figure 1A and (Fumagalli et al, 2021)). It is difficult to extract precise data in humans, but the human challenge trial in young adults shows that exposure of individuals to an extremely low dose (10 TCID50!) of SARS-CoV-2 led to the detection of viral RNA in the upper airways for longer than 14 days (Reviewer Figure 1B and (Killingley et al, 2022)). Therefore, it is very difficult to estimate what would possibly mimic what is occurring in treated COVID-19 patients, especially in line of the current COVID-19 guidelines for ritonavir-boosted nirmatrelvir that suggests to initiate treatment as soon as possible and within 5 days of symptoms (https://www.covid19treatmentguidelines.nih.gov/therapies/antiviral-therapy/ritonavir-boosted-nirmatrelvir--paxlovid-/). The choice to start treatment 4 hours after infection was motivated by the original paper that reported in vivo antiviral activity of nirmatrelvir against SARS-CoV-2 (Owen et al, 2021). That said, we performed additional experiments whereby we treated mice with nirmatrelvir 24 or 48 hours after infection (at or near the peak of viral replication). As shown in the new Figure 3, such treatment also resulted in blunted adaptive immune responses.
Reviewer Figure 1. (A) K18-hACE2 mice were exposed to a target dose of 2 x 105 TCID50 of aerosolized SARS-CoV-2 (D614G). Quantification of SARS-CoV-2 RNA in the lung after infection. RNA values are expressed as copy numbers per ng of total RNA and the limit of detection is indicated as a dotted line. (B) Healthy adult volunteers were challenged intranasally with SARS-CoV-2. In the infected individuals (n = 18 biologically independent participants). Viral load in twice-daily nose and throat swab samples was measured by qPCR (blue) and focus-forming assay (red) (a). Results are expressed as mean ± SEM. Adapted from ref. (Killingley et al, 2022).
Omicron variant has limited replication in the K18 mouse model and does not cause disease. Thus, the authors are starting from a model with artificially limited viral antigen production. Does Paxlovid limit the adaptive immune response when given during an infection with a variant strain that replicates robustly in the K18 mice?
We thank the reviewer for raising this issue. In the revised manuscript we have now performed experiments where we infected K18-hACE2 transgenic mice with the Delta (B.1.617.2) variant, known to replicate at higher level compared to the Omicron variants (Shuai et al, 2022). Additionally, we have infected WT mice with a mouse-adapted SARS-CoV-2 (rSARS2-N501YMA30)(Wong et al, 2022) that replicates robustly and induces significant disease. These new results, now shown in the new Figure 3 and new Figure S4, confirm that nirmatrelvir treatment blunts the development of antiviral adaptive immune responses regardless of the variants/strain used for infection.
Reviewer #2 (Significance (Required)):
Significance: Nirmatrelvir/Paxlovid is used clinically for treatment of COVID-19. Relapse infections have been reported after courses of the drug. The authors show here that Paxlovid treatment during a mouse model of SARS-CoV-2 infection results in diminished induction of adaptive immunity and immune memory. This is most probably due to decreased production of viral antigenic stimuli due to inhibition of virus replication. The concept that less viral antigen will result in less induction of immunity is not surprising. Further, whether the phenomenon observed here in a mouse model with poor susceptibility to the chosen virus strain is related to relapse infections in humans was not established. Nonetheless, the audience for this work is broad and this work could be of interest due to the common use of Paxlovid and the ongoing SARS-CoV-2 infections across the world.
Although we did not investigate the mechanism underlying the reported observation in depth, we agree with this reviewer that the most likely explanation for the reduced adaptive immune responses is decreased production of viral antigens. In this regard, it is probably not terribly surprising. However, it is worth noting that successful antimicrobial treatment does not inevitably result in reduced adaptive immune responses to any pathogen. For instance, treatment of mice infected with Listeria monocytogenes with amoxicillin early after infection did not significantly impair the development of T cell responses (Corbin & Harty, 2004; Mercado et al, 2000). Furthermore, treatment with antibiotics before L. monocytogenes infection allowed the development of functional antigen-specific memory CD8+ T cells in the absence of contraction (Badovinac et al, 2004). An additional, and possibly more relevant, example was published during the revision process: monoclonal antibody therapy with bamlanivimab during acute COVID-19 did not impact the development of a robust antiviral T cell response (Ramirez et al, 2022).
As per the comment related the poor susceptibility of the mouse model to the Omicron variants of SARS-CoV-2, we believe that the new data obtained with the Delta variant and with the mouse-adapted SARS-CoV-2 (new Figure 3 and S4) convincingly show that nirmatrelvir treatment blunts antiviral adaptive immune responses to SARS-CoV-2 in mice.
List of modifications
New figures:
- Figure 3: new data as per reviewer’s suggestion.
- Figure S4: new data as per reviewer’s suggestion.
References
Badovinac VP, Porter BB & Harty JT (2004) CD8+ T cell contraction is controlled by early inflammation. Nat Immunol 5: 809–817
Corbin GA & Harty JT (2004) Duration of Infection and Antigen Display Have Minimal Influence on the Kinetics of the CD4+ T Cell Response to Listeria monocytogenes Infection. J Immunol 173: 5679–5687
Fumagalli V, Ravà M, Marotta D, Lucia PD, Laura C, Sala E, Grillo M, Bono E, Giustini L, Perucchini C, et al (2021) Administration of aerosolized SARS-CoV-2 to K18-hACE2 mice uncouples respiratory infection from fatal neuroinvasion. Sci Immunol 7: eabl9929
Killingley B, Mann AJ, Kalinova M, Boyers A, Goonawardane N, Zhou J, Lindsell K, Hare SS, Brown J, Frise R, et al (2022) Safety, tolerability and viral kinetics during SARS-CoV-2 human challenge in young adults. Nat Med 28: 1031–1041
Mercado R, Vijh S, Allen SE, Kerksiek K, Pilip IM & Pamer EG (2000) Early Programming of T Cell Populations Responding to Bacterial Infection. J Immunol 165: 6833–6839
Owen DR, Allerton CMN, Anderson AS, Aschenbrenner L, Avery M, Berritt S, Boras B, Cardin RD, Carlo A, Coffman KJ, et al (2021) An oral SARS-CoV-2 Mpro inhibitor clinical candidate for the treatment of COVID-19. Science 374: 1586–1593
Ramirez SI, Grifoni A, Weiskopf D, Parikh UM, Heaps A, Faraji F, Sieg SF, Ritz J, Moser C, Eron JJ, et al (2022) Bamlanivimab therapy for acute COVID-19 does not blunt SARS-CoV-2-specific memory T cell responses. Jci Insight 7
Shuai H, Chan JF-W, Hu B, Chai Y, Yuen TT-T, Yin F, Huang X, Yoon C, Hu J-C, Liu H, et al (2022) Attenuated replication and pathogenicity of SARS-CoV-2 B.1.1.529 Omicron. Nature 603: 693–699
Wong L-YR, Zheng J, Wilhelmsen K, Li K, Ortiz ME, Schnicker NJ, Thurman A, Pezzulo AA, Szachowicz PJ, Li P, et al (2022) Eicosanoid signaling blockade protects middle-aged mice from severe COVID-19. Nature: 1–9
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Referee #2
Evidence, reproducibility and clarity
Summary:
In this manuscript, the authors show that Paxlovid, a commonly used antiviral for SARS-CoV-2 infections, blunts the adaptive immune response to the virus. Indeed, they show convincing effects on T cell and B cell responses in the K18-hACE2 mouse model infected with Omicron variant. The effect is observed when drug treatment was started at 4, 24, or 48 h post infection. Experiments are well done and the data are presented clearly. However, the early timing of drug administration resulted in minimal virus replication, thus likely limiting innate immune activation and antigenic exposure. Indeed, the authors show that the drug did not decrease adaptive responses to other viral infections, indicating that the effect on adaptive immunity in SARS-CoV-2 infection can be explained by decreased viral antigen production. Whether this is the mechanism by which relapse infections occur in humans after Paxlovid treatment is unclear.
Major comments:
The authors should discuss whether the timing of drug administration in their experiments is relevant to the timing of when Paxlovid is commonly started in humans.
Does Paxlovid limit the adaptive immune response when given later in infection?
Omicron variant has limited replication in the K18 mouse model and does not cause disease. Thus, the authors are starting from a model with artificially limited viral antigen production. Does Paxlovid limit the adaptive immune response when given during an infection with a variant strain that replicates robustly in the K18 mice?
Significance
Nirmatrelvir/Paxlovid is used clinically for treatment of COVID-19. Relapse infections have been reported after courses of the drug. The authors show here that Paxlovid treatment during a mouse model of SARS-CoV-2 infection results in diminished induction of adaptive immunity and immune memory. This is most probably due to decreased production of viral antigenic stimuli due to inhibition of virus replication. The concept that less viral antigen will result in less induction of immunity is not surprising. Further, whether the phenomenon observed here in a mouse model with poor susceptibility to the chosen virus strain is related to relapse infections in humans was not established. Nonetheless, the audience for this work is broad and this work could be of interest due to the common use of Paxlovid and the ongoing SARS-CoV-2 infections across the world.
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Referee #1
Evidence, reproducibility and clarity
In this study, Fumagalli et. al evaluated the impact of Nirmatrelvir drug treatment on the development of SARS-CoV-2-specific adaptive immune responses in a mice model. Nirmatrelvir is one of the component of Paxlovid drug that has been shown to reduce the risk of progression to severe COVID-19 and long COVID. Herein, authors show that nirmatrelvir administration early after infection blunts the development of SARS-CoV-2-specific antibody and T cell responses. Upon secondary challenge, nirmatrelvir-treated mice developed fewer memory T and B cells to the infected lungs and to mediastinal lymph nodes, respectively. Overall, the experimental methods, figures, results, statistical analysis and findings of this study are interesting and convincing.
Referees cross-commenting
I agree with the Reviewer 2 comments.
Significance
It was known that nirmatrelvir reduces the risk of severe covid and long covid but, whether its treatment has any impact on adaptive immune response was not known/evaluated. This study has importantly addressed that impact of nirmatrelvir treatment can impair both T and B cell adaptive immune responses. It would have been impactful to understand the mechanism of T and B cell immune response impairment following nirmatrelvir treatment in mice which they have already mentioned a limitation of the study.
Moreover this study provides important implications for clinical management of COVID patients and to revise the treatment strategies to avoid virological and/or symptomatic relapse after Paxlovid/nirmatrelvir treatment completion that have been reported in some individuals.
I am not a mice model expert. Not sure whether the viral dose given to mice in this study was optimal to study the impact of the said drug.
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Reply to the reviewers
- General Statements We thank the reviewers for their thoughtful comments and suggestions, which have improved the manuscript. We are particularly gratified by their positive comments about the significance of the findings. Our point-by-point responses to the reviewer comments and suggestions are summarized below. Line numbers have been added to the revised manuscript to make it easier to locate the changes.
Point-by-point description of the revisions
Reviewer #1__ __
*1) In the study there is a lack of consideration of other targets. In and of itself this is not a problem, but once the author's identified the T130A mutation as being a key for protection it would have been good to Sanger sequence the other T. gondii myosins - a quick alignment of the TgMyo's A, C, H (class XIV), along with D and E suggests that the motif is highly conserved. This raises the currently unexplored (and exciting!) prospect of a pan-myosin inhibitor, and that there might have been mutations at an equivalent position in the other four KNX002 resistant clones - for example, MyoC has been proposed to provide some level of functional redundancy in the absence of MyoA. *
Because the goal of this work was to evaluate the druggability of TgMyoA, we specifically designed our experiments to identify resistance-conferring mutations in TgMyoA or its light chains, as described on lines 366-372. This strategy yielded the TgMyoA T130A mutation, which enabled us to rigorously determine that inhibiting TgMyoA, and TgMyoA only, was sufficient to slow the progression of disease in vivo. Because we took this targeted approach, our results did not address: (a) the basis of resistance in the 4 resistant clones that did not contain a mutation in TgMyoA or its light chains and (b) whether KNX-002 inhibits any of the other ten parasite myosins.
The most informative way to address (a) would be to do whole genome sequencing on each of the mutants, since resistance might have nothing to do with the other parasite myosins or their light chains. Any potential resistance-conferring mutations identified would need to be regenerated in a non-mutagenized background and functionally characterized, as we have done here for the T130A mutation, to be certain that this particular mutation was responsible for resistance. The most direct way to address (b) would be to individually express each of the other ten parasite myosins together with its specific associated light chains and the myosin co-chaperone protein TgUNC, purify the motor and determine the effect of the compound on motor activity (as we have done for TgMyoA; Fig. 1). These are both major undertakings that are beyond the goals and scope of the current manuscript. Critically, the absence of such data does not impact the conclusions of our phenotypic studies, which used the CRISPR-engineered T130A parasite line.
We nevertheless agree with the reviewer that these are both interesting questions that should be studied further, and we now discuss them on lines 416-422 and 451-453.
2) The fact that T130 is not thought to be the binding site of KNX002 is only introduced quite late on - this also relates to the next point - is the binding pocket conserved??? It is intriguing that the residue and proximal amino acid environment are highly conserved with vertebrates, but that KNX002 does not have an effect on their activity in their screen assay. It would be useful to know if the differences in the structures of the myosins can provide an explanation for this - along the same lines, given that the crystal structure of TgMyoA is available (PMID: 30348763), it would be useful for the authors to provide a molecular model for the binding of the inhibitor to the proposed point of engagement.
These are excellent questions that we unfortunately cannot yet answer. Docking simulations of KNX-002 to the published structure of TgMyoA in its pre-powerstroke state have thus far not yielded any promising results. The site of KNX-002 binding to P. falciparum MyoA was determined by X-ray crystallography (ref. 54); however, the PfMyoA in that study was in the post-rigor state and the coordinates of the co-crystal structure have not yet been made available in the PDB database for homology modeling.
The lack of effect of KNX-002 on the vertebrate muscle myosins may not be surprising. Although the 3D structures of myosins are rather conserved, their primary structures are quite different, which likely contributes to the different effects of KNX-002 on the different myosins. TgMyoA and PfMyoA are more similar to each other than they are to the vertebrate muscle myosins, which may enable the specific targeting of MyoA in apicomplexan parasites (lines 308-310).
*If this is an allosteric site it is possible that the mutation functions indirectly upon binding of KNX002 to the orthosteric site, but this would be useful to help the reader to understand this (and there are bioinformatic prediction tools that will score allostery - which would be interesting to include). This is explained somewhat in the discussion - but this should be introduced much earlier to clarify. What is known about allosteric regulation of Myo function? Is this a known site of regulation? *
Allosteric modulation of human cardiac myosin by small molecules such as omecamtiv is well established, and allosteric effects of the T130A mutation are certainly a possibility. As molecular motors, myosins depend on a complex and highly interconnected network of allosteric interactions to perform their function (for example, see ref. 59). This complexity, combined with the fact that the data on the PfMyoA-KNX-002 structure have not yet been released, makes it very difficult to generate any sort of model that would support meaningful conclusions. A statement to this effect has been added to the Discussion (line 375-382), and the likelihood that T130 is not part of the actual binding site for the compound is now mentioned at the very beginning of the paragraph that discusses the potential mechanism of action of the T130A mutation (lines 375-376).
*3) Introduction: 'Nearly one third of the world's population is infected with the apicomplexan parasite' - given that these data are extrapolated from serology, this should be reworded - it's fairer to say that they 'are or have been infected...' *
Done – line 65.
*4) Page 4: figure 1A - can you provide some explanation for incomplete inhibition in the screen - there seems to be a residual amount (15-20%) of activity that is not inhibited. *
The compound inhibits 80-90% of the motor’s activity at 40uM. We did not test higher concentrations in the ATPase assay; presumably we would see incrementally more inhibition as we increase compound concentration further, but the concentrations used enabled us to construct a reproducible IC50 curve without adding potentially confounding amounts of DMSO (carrier) to the assay.
*5) The authors demonstrate a general effect on growth over 7 days. It would be good to use a replication assay (e.g. parasites/vacuole over a single lytic cycle) to confirm that KNX002 does not affect cellular division. This would further strengthen the argument that the phenotypic effect is primarily via impacts on motility. *
A figure showing the lack of effect of KNX-002 on replication has now been added (new Supplemental Figure 2) and a paragraph describing these data and their implications added to the Results section (lines 137-143).
*6) Page 5: 'selected for parasites resistant to KNX-002 by growth in 40 μM KNX-002.' - could the authors add text to explain why that concentration was chosen. *
40 μM is close to the compound’s IC90 of 37.6 μM and, although we tried a number of different compound concentrations and selection schemes, 40 μM yielded parasites with the greatest shift in IC50. We now include this rationale on lines 606-607, as well as a new figure showing the shift in IC50 curves for all 5 resistant lines (Suppl. Figure 8).
*7) Page 6: 'suggesting that the effects of the T130A mutation on motor function are due to more subtle structural changes' - it's fair to say that there are not gross structural changes based on the data presented, but that does not mean it is therefore a 'more subtle structural change' - surely the mutation could prevent KNX002 binding without effecting TgMyoA structure? *
Based on the residues within P. falciparum MyoA that participate in binding to KNX-002 (ref. 54), it is unlikely that T130 of TgMyoA participates directly in compound binding. Mutation of T130 to alanine therefore seems most likely to impact compound binding through a change in protein structure, discussed more fully now on lines 375-382.
*8) Page 6: 'the proportion of filaments moving' - in the figure it's referred to as the 'fraction of filaments', which makes more sense for the data presented. Please correct to 'fraction' throughout the manuscript (discussion, page 9 - possibly other instances!). Along the same lines, in figure 6 it would be good to change the y axes on the '% moving' to be 'fraction moving' and change the numbers - this would make it easier for the reader to understand the index values presented in the lower panels - if you do the calculation with the % values presented the numbers don't make sense (as fractions they do). The axes for motility also go up to 125% - please correct - based on the data presented there is no need for this to be above 100% (or 1 - see above). *
We thank the reviewer for this suggestion; “percent moving” and “proportion moving” have been changed throughout the manuscript and figures to “fraction moving”. The y-axis labels on the motility and IC50 curves have also been modified as suggested.
*9) Page 7: 'tested whether KNX-002 (20mg/kg, administered intraperitoneally on the day of infection and two days later' - please provide some rationale for the concentration used. *
A preliminary dose tolerance study was conducted prior to the infection experiments, with doses ranging from 5-20 mg/kg. The study showed that two doses of 20 mg/kg, administered two days apart, resulted in minor hepatoxicity without signs of pain or distress. 20mg/kg was therefore considered the maximal tolerated dose. This rationale is now included on lines 715-721.
*10) Page 10: 'the T130A mutation is likely to have long range structural impact that could alter the KNX-002 binding pocket' - this is particularly interesting, and should be addressed with a model - do the authors think that the T130 region be a conserved site of allosteric regulation? This would be good to expand upon in the discussion - mutation of an allosteric site as a mechanism of resistance is unusual, and typically described as being unlikely - and used as justification for the targeted drugging of allosteric sites. *
See response to comment #2 above and the new text on lines 375-382.
Reviewer #2
*1) Considering (i) the moderate effect of KNX-002 on the acute infection process in CBA mice that received tachyzoites intraperitoneally, (ii) the fact that the drug application cannot be envisaged outside of the context of reactivation of cystogenic strains (in particular with respect to cerebral toxoplasmosis as emphasized in the introductive section), which implies the drug would have to be delivered and active in the brain parenchyma, a condition not analyzed here, it would be appropriate to modify the current title. It would be more relevant to highlight the solid body of data on the identification and functional characterization of the compound and derivatives in vitro and in the host mouse model. Apart from the title, the discussion should also recontextualize the in vivo assays and the information these assays bring on the slight delay of the "mortality" of some but not all mice. *
We agree that the major clinical application of any new anti-Toxoplasma chemotherapy would be treatment of a reactivated infection, particularly in the brain (although there could also be a role for treatment of pregnant women), and that the data we present with this compound do not speak directly to clinical efficacy in this context. That said, reactivation leads to an active infection whose pathogenesis requires TgMyoA-dependent motility, invasion and egress, like the active infections analyzed here. The KNX-002 scaffold would likely need to be modified to enable it to cross the blood-brain barrier and access parasites in the brain, but that would be a normal step in any campaign to develop new drugs for toxoplasmosis (which is well beyond the scope of this study; see response to comment #11).
Given these considerations, we gave much thought to how to accurately describe the results from the animal experiments – and we therefore appreciate the reviewer’s comment. For the title, we arrived the word “druggable”, because it has the very specific meaning described on lines 100-101: a protein whose activity is amenable to inhibition by small molecules. In our experiments with mice infected with wild-type parasites, nine of the ten compound-treated animals survived longer than the untreated controls, and 40% of the treated mice were still alive at the end of the experiment. Nevertheless, we stayed away from terms like “therapeutic” or “treatment”, for exactly the reasons the reviewer raises. We believe that the current title is an accurate summary of what we found, since we have indeed shown that MyoA is amenable to inhibition by a small molecule in a well-established animal model of infection (CBA mice infected intraperitoneally). Showing for the first time that the MyoA is druggable, in vivo, provides the rationale for identifying more potent compounds that can access the brain and serve as bona fide leads for drug development.
To the reviewer’s point, we also reviewed all sections of the text where we described the animal experiments, and in the revised manuscript we replaced all instances in the text of “ameliorate disease”, “prevent disease” and “decrease the susceptibility of mice to a lethal infection” with the more circumspect phrases “alter disease progression” or “slow disease progression” (lines 46, 56, 110, 297, 315, Figure 9 legend). We also changed the title of the Results section describing these data from “KNX-002 treatment decreases the susceptibility of mice to lethal infection with T. gondii” to “KNX-002 treatment slows disease progression in mice infected with a lethal dose of T. gondii” (line 284).
*2) Motility analysis: This comment concerns the Figure 7. It seems to the reviewers that the major hypothesis to test in data presented in panel B is that the wild type and the T130A mutant tachyzoite respond differently under similar drug conditions rather than the two populations without drug. These statistics could be added easily, hence it would validate that the proportion of motile mutant parasites is not affected by the drug when compared to vehicle. *
These statistical comparisons have now been added to revised figure 7, as suggested. Since this comparison was between different parasite lines, it required the use of unpaired t-tests (vs. the paired t-tests used for different compound treatments of the same parasite line). We have therefore revised all 3D motility figures (Figures 4 and 7, Suppl. Figures 7 and 12) and their legends to clearly indicate which samples are being compared to which and whether paired or unpaired statistical tests are being used.
However, the statistics shown panel C rather suggest that the drug does impact on the speed of the moving parasites, including when these carry the "resistance" T130 A mutation. It is not clear what we can gain in terms of messages with the motility index except to "slightly reverse" the analysis on panel B and to favor a no-effect of KNX-002 on the mutant parasite motile skills, on which the author might give more explanation. When comparing these quantitative tests with the panel presented above (panel A) it seems that the mutant parasite is still impacted by the MyoA inhibitor. Although there is no doubt for the reviewers that the T130A mutant emerging from the selected T. gondii resistant clones is a valuable probe for assessing drug selectivity: indeed the assays validate KNX-002 as a direct TgMyoA ATPase inhibitor, it might be good to rephrase some sentences and to have a harmonized definition of the parasite motility index throughout the text (Figure 7 legend, result and discussion sections).
The reviewer is correct that there is a decrease in the speed of compound-treated T130A parasites, as the p-values on Figure 7C indicate. This is why we state in the text that “the mutant parasites retain some sensitivity to the compound” (line 263). We were careful throughout the manuscript to refer to the resistance provided by the mutation as “partial”, or to describe it as a “reduced sensitivity”. Partial resistance is still sufficient to establish compound specificity, as noted by the reviewer in this comment.
We present the motility index not to try to “reverse” the effect of the compound on the mutant’s speed, but because the compound has two simultaneous effects on motility -- a decrease in the fraction moving and a decrease in speed of those that do move. Combining these two effects into one value (while still showing each component individually, as we have) enables comparison to the analogous actin filament motility index from the in vitro motility assays, and provides a more complete picture of the impact of compound treatment on parasite motility. This is a similar approach to that used in studies of e.g., phagocytosis, where the widely reported “phagocytic index” corresponds to the fraction of cells that have internalized at least one particle multiplied by the average number of beads internalized. The motility index of the mutant parasites is significantly less impacted by KNX-002 than the motility index of wild-type parasites (Figure 7D).
We have further clarified the definition and rationale for using the parasite motility index throughout, as suggested (lines 233-235, 264-267, 345-348).
*This reviewer's concern was accentuated by the comparison between the actin filament sliding index and the parasite motility index which appears as such far stretch; Aside from the "far stretched claims" easy to re-address in a revised version, the readers have appreciated the writing quality and most figure illustration. The discussion nicely synthetizes the whole dataset, including those related to the 4 T. gondii clones that resisted to KNX-002 but not through mutations targeting any of the myosinA chains. *
We have added additional text to the discussion listing possible reasons for the differential effects of the mutation on the filament and parasite motility indices (lines 403-406).
4) Ab*stract: the concept of "ameliorate disease" in this framework is odd and the objective of the work can be rephrased in a simple way (see below) *
See response to Comment #1; “ameliorate” has been replaced with “alter disease progression” (line 46).
*5) Introduction section: we think that the references on the impairment of invasiveness for the KoMyoA should be included (Bichet et al., BMC Biology 2016) as it has provided proof of an alternative and suboptimal mode of entry in many different cell types, thereby arguing that in absence of MyoA function, parasite invasiveness is not fully abolished and this without considering any MyoC-driven MyoA compensation. *
We thank the reviewer for catching this oversight; the Bichet citation has been added (line 93).
6) Introduction, third paragraph: in the sentence "Because the parasite can compensate for the loss or reduced expression of proteins important to its life cycle [29-31], small-molecule inhibitors of TgMyoA would serve as valuable complementary tools for determining how different aspects of motor function contribute to parasite motility and the role played by TgMyoA in parasite dissemination and virulence ». We definitively agree with this view but saying that, we think it would be worth evaluating (or simply discussing) the potency of the KNX-002 against MyoC, which compensatory contribution has been debated and remains questionable (at least to the reviewers) with respect to cell invasiveness restoration (related to the comment above).
We have included a discussion of a potential compensatory role for MyoC and the value of determining in future studies whether KNX-002 (or its more potent downstream analogs) inhibit any of the other parasite myosins (lines 419-423). Whether or not MyoC can functionally compensate for a lack of MyoA – we agree this is a controversial question – it is important to note (as we do on line 440-442) that “T. gondii engineered to express low levels of TgMyoA … are completely avirulent [28], arguing that sufficiently strong inhibition of TgMyoA is likely, on its own, to be therapeutically useful”.
*7) If we are correct, the screen and the characterization study have been performed with two different products (CK2140597 and KNX-002 the compound library and the re-synthetized one, respectively). Could we make sure that the two have the same potency? *
The source of compound used in each of the assays is now explicitly described on lines 481-490). Commercially obtained compound yielded an IC50 in growth assays of 16.2 and 14.9 μM (Figures 2 and 5, respectively), and compound synthesized by us yielded an IC50 value of 19.7 μM (Figure 3). The 95% confidence intervals of these three independent IC50 determinations with two different sources of compound overlap (lines 484-486).
8) We understood how the authors came to the conclusion that the KNX-002 impact on growth of the parasite and they stated "growth in culture" in the subsection title but then refers to parasite growth. Therefore, it looks a bit confusing for the reader since intracellular growth per se is probably not modified but this feature was not looked at it in this study (we would expect no impact based on published data on MyoA- genetically deficient tachyzoites, except if the drug impacts host cell metabolism for instances). Instead, it is the overall expansion of the parasite population that is analyzed here and clearly shown to be impacted. This decrease in population expansion on a cell monolayer likely results from impaired MyoA-dependent egress and invasiveness upon chemical inactivation of MyoA. Accordingly, it appears difficult to understand what is an IC50 for the "overall" growth in the context of this study. The authors should rephrase for better accuracy when necessary, including in the graph Fig2 legend axis.
While assays that measure parasite expansion in culture are by convention called “growth” assays (e.g., see Gubbels et al, High-Throughput Growth Assay for Toxoplasma gondii Using Yellow Fluorescent Protein AAC 47 (2003) 309, the paper on which our assay was based), we take the reviewer’s point that a reader may incorrectly ascribe the inhibition to some other aspect of the lytic cycle (e.g., intracellular replication), rather than a myosin-dependent motility-based process. We have therefore now: (a) more clearly defined the growth assay as one that measures parasite expansion in culture (lines 132-138); (b) described the myosin-dependent and -independent steps of the lytic cycle (lines 137-140); and (c) added a new figure (new Suppl. Figure 2, lines 140-143) showing that the compound has no effect on intracellular replication.
*9) The authors should clarify for the reader (i) why they use in some case myofibrils and other muscle F actin when measuring the Myosin ATPase activity, (ii) what does mean XX% calcium activation and (iii) why using 75% in these assays which is 3 times higher from the original assays. (iv) Why they did not include non muscle actins in their study since Myosins also extensively work on non muscle actins. *
(i) For both striated and smooth muscle myosins, the assays used here are well established and have identified compounds that have translated into animal models of disease. To assay the activity of myosins from striated muscle types, particularly to determine compound selectivity, myofibril assays are preferred as they recapitulate more of the biology as a more "native", membrane-free preparation and respond cooperatively to calcium activation. For cardiac, fast and slow skeletal muscle it is possible to derive high quality myofibril preparations that can be activated by calcium. A reference describing the value of using myofibrils in assays of striated muscle myosin ATPase activity has been added (ref. 71, line 517).
Smooth muscle, a non-striated tissue, is regulated differently and calcium exerts an effect not through binding to troponin as in the striated muscle but through g-protein signaling, with phosphorylation as an end result, making the contraction slower and also much slower to reverse - in line with the physiological role of the muscle. The only way to reliably reconstitute smooth muscle ATPase activity has been through purification and reconstitution of a more reductionist system. The SMM S1 needs to be crosslinked to the actin to achieve high enough local concentrations to generate robust ATPase activity. A reference describing the use of this assay to identify small molecule inhibitors of SMM is now included (ref. 73, line 522).
(ii, iii) Striated muscle myofibrils are responsive to calcium, as muscle contraction is mediated in vivo through calcium release from the sarcoplasmic reticulum. Titrating calcium can activate the myofibril ATPase activity up to the plateau (100%) and provide optimal signal to noise and sensitivity for the particular activity being assayed. For counterscreening to determine selectivity, we adjusted the assay conditions to a high basal ATPase activity (75% calcium) to provide high sensitivity for detecting inhibition. A sentence explaining this rationale has been added on lines 519-520.
(iv) We used skeletal muscle actin in all of our in vitro assays since we have shown skeletal muscle actin to be a good substrate for TgMyoA (ref 33, cited on line 536) and skeletal muscle actin can be purified in larger quantities than native actin from parasites or functional recombinant protein from insect cells. Others have also shown that the closely related MyoA from P. falciparum moves skeletal muscle actin at the same speeds as recombinant P. falciparum actin (Bookwalter et al [2017] JBC 292:19290).
*10) The protocol of image analysis of the 3D motility assay was increased to 80 seconds for the test of KNX-002 selectivity using wild type and mutant parasites (Fig 7) when compared to the test of KXN-002 concentration effect on wild type tachyzoites (60 sec in the result section, in Fig 4 legend and in the Methods' section). Is there any specific reason? *
The data for Figure 4 were captured earlier in the project than those of Figure 7 and Suppl. Figure 7. In the intervening time we upgraded our Nikon Elements software from v.3.20 to v.5.11 (as already described on lines 583 and 588). With the upgrade to v.5.11, we also began using Nikon’s Illumination Sequence (IS) module, a graphical user interface that provides greater time resolution through a more efficient approach to building the z-stacks and saving the data. With the addition of v.5.11 and the IS module we were able to capture twice the number of image volumes in 80 sec than we were in 60 sec using v.3.20, and that became our standard operating procedure. Other than the improved time resolution, the 60s and 80s assays give indistinguishable relative results. We have now clarified in the methods (line 588-589) that we used the IS module to acquire the data in Figure 7 and Suppl. Figure 7.
*11) In the mouse infection experimental design (Method section), it seems that they were no biological replicates in the case of the drug-treated (parasites + mice) which is not the case for the comparison of virulence between MyoA wild type and T130 mutants. If true, and considering what the authors wish to emphasize as a main message, it is fairly complicated to convincingly conclude about the KNX-002 effectiveness in vivo. Maybe the authors could explain their limitations. *
Since we did not know how the compound and parasites would interact in mice – and in keeping with animal welfare standards – we decided that rather than doing multiple replicates with smaller numbers of infected mice we would do a single experiment with a large enough number of mice per treatment condition to ensure that if any animals died unexpectedly or had to be euthanized prematurely we would still have sufficient numbers for robust statistical comparison. Single experiments with ten treated and ten untreated mice are a generally accepted approach in early studies of drug effectiveness (e.g., Ferrreira et al Parasite 2002, 9:261; Rutaganira et al, J. Med. Chem. 2017, 60: 9976; Zhang et al IJP Drugs and Drug Resistance 2019, 9:27), and power analysis shows that if mortality is 100% in untreated mice and 50% in treated mice, 10 mice per group will provide an 80% probability of detecting the difference with a p value<br /> *We are also not sure why the compound has been injected only twice, at the time of parasite injection and two days after whereas the mice succumbed after 8 to 9 days even without MyoA inhibitors. Although quite difficult to measure, do the authors have any knowledge (based on the chemistry for example) of the compound stability and lipophilicity in blood and tissues? Because the IC50 on free tachyzoites appears significantly higher (5.3 uM, Fig4) than the in vitro molecular assay, when assessed in motility tests, and is increased for intracellular growth (Fig 8), it is somehow expected that the current compound would not work that great in vivo. Did the author try to provide the inhibitor intravenously every day? *
IP injection is a standard method of administration for early drug treatment studies, and two considerations contributed to our decision to inject on days 0 and 2 post-infection: (a) the preliminary dose-tolerance studies, which were done with two IP doses of compound two days apart, showed evidence of mild toxicity so we were hesitant to inject more frequently, inject IV, or use more compound/injection; (ii) we expect the compound to work primarily on egressing and extracellular parasites, and since the parasite’s lytic cycle takes approximately 48 hours, this two-day injection schedule was chosen to maximize exposure of the extracellular parasites to freshly injected compound early in establishment of the infection. This rationale has now been added to the Methods section (lines 715-721).
In terms of the doing systematic studies of dosing, stability, PK/PD, drug partitioning etc., it is important to restate that the primary goal of this work was to test whether inhibiting TgMyoA activity in vivo alters the course of infection. The data reported in the manuscript demonstrated this to be the case. As we state on lines 454-457, “While KNX-002 provided the means to rigorously test the druggability of TgMyoA, it caused weight loss and histological evidence of liver damage in the treated infected mice. Before further animal work, it will therefore be necessary to develop more potent and less toxic analogs that retain specificity for parasite myosin.” Our colleagues at Kainomyx have in fact initiated a drug development campaign based on the KNX-002 scaffold and have already identified a derivative named KNX-115, that is 20-fold more potent against recombinant P. falciparum MyoA (described on lines 356-361). Given Kainomyx’s ongoing efforts we do not believe it makes sense to do any further animal experiments at this time with KNX-002. It will be more informative and ethical to undertake, e.g., dosing, PK and PD studies with the more potent and less toxic derivatives that emerge from the Kainomyx drug development program, once these compounds become publicly available. This does not diminish the importance of the proof-of-principle experiments reported here, which as the reviewer stated, “provide a strong rationale for developing new therapeutic strategies based on targeting MyoA”; rather, it makes it hard to justify doing additional animal studies with a compound that we know will soon be replaced with more potent and less toxic derivatives.
12) Figure 4: 2D and 3D Motility- the authors should comment on the fact that in 2D conditions with 10 uM of KNX-002, circular trajectories (one complete circle so at least 2 parasite lengths but sometimes more) largely dominate over others, whereas in absence of KNX-002 these circular trajectories are barely detectable and helical trajectories predominate. What could that mean as regard to the MyoA functional contribution to either process?
This is an interesting question that we cannot currently answer. Perhaps helical 2D gliding requires more myosin-generated force than circular 2D gliding, but this is pure speculation at this point. Whatever the explanation, the observation is striking and we believe should be reported as it shows a clear effect of the compound on motility in the widely-used 2D trail deposition assay.
*13) Figure 7: Besides the major point raised above for panel C, the information carried by the Figure could be stronger if an additional panel is introduced regarding the interesting assay on the preserved structural stability of the MyoA mutant over the WT MyoA (currently in SupFig7) *
Former Suppl. Figure 7 (now Suppl. Figure 9) addresses one particular explanation for the differential effects of the mutation in the in vitro motility assay (Figure 6) and the parasite 3D motility assay (Figure 7). The data in Suppl. Figures 14A and 14B address two other possibilities. For consistency with the other figures and clarity of the narrative, we would prefer to leave the data in Suppl. Figure 9 as a supplemental figure.
14) Material and Methods - Parasite motility assays: remove the duplicated [16] reference.
Done.
*15) The discussion starts with the ongoing debate on mechanisms underlying zoite motility; We found that the work of Pavlou et al. (ACS nano, 2020) should be part of the references listed there, as it brings evidence that a specific traction polar force is required probably in concert with microtubule storage energy at the focal point, a result that questions the prevailing model. *
This was another oversight; the citation has been added (line 307).
*16) Concerning the C3-20 and C3-21 compounds, the sentence "they have no effect on the activity of the recombinant TgMyoA (AK and GEW, unpublished data)" in the paragraph starting by "There have been only two previously..." should be refrained unless showing the results. *
We have removed reference to this unpublished work, as suggested (lines 338-340).
17) If possible, the authors should expand more on the effect of KNX-002 on Plasmodium falciparum and its homolog PfMyoA.
We have expanded our discussion of these preprint data from others on lines 356-361.
Reviewer #3
*1) The T130A IC50 was done on the mutagenized clone 5. The authors currently don't have data showing IC50 on the independently generated T130A mutant, to see if the IC50s are similar to one another, or if there were additional resistance mutations present in clone 5. *
Because we did not insert the T130A mutation into a fluorescent parasite background, we cannot directly compare its IC50 in the fluorescence-based growth assay to that of the line generated by chemical mutagenesis. Plaque assays do not require fluorescent parasites but, in our hands, these assays lack the sensitivity to reproducibly detect the expected subtle (50. While we agree that it would be interesting to know if the mutant generated by chemical mutagenesis contains any additional resistance-conferring mutations, not having this information does not alter the conclusion that the T130A mutation alone reduces the sensitivity of the motor to KNX-002 (Figures 6-9). See also response to Reviewer 1, comment 1; a discussion of the value of determining what other resistance mechanisms are available to the parasite for this class of compounds is now included on lines 416-422.
*2) For 3D motility assays, it is currently unclear from the data and text what the expected maximal inhibition of motility would be; e.g., would parasites depleted of MyoA display 0% motility. Understanding the dynamic range of this assay could help clarify whether this residual 5% motility explains why parasites treated with 20 uM KNX-002 can still form small plaques. This could be achieved by referencing previous work that assesses 3D motility after depletion of a critical motility factor. *
A small fraction of TgMyoA knockout parasites are still capable of motility in 3D (13% when normalized to wildtype for displacements > 2 μm [ref. 46]), so the dynamic range of the 3D assay for TgMyoA-deficient parasites compared to wild-type parasites is 0.13-1.0. The 13% residual motility of the TgMyoA parasites is now referred to on lines 419-420. Treatment of wild-type parasites with 20μM KNX-002 results in a fractional motility of ~0.24 compared to untreated controls (Figures 4 and 7). This less than complete inhibition compared to the knockout is not surprising, since motor activity is not completely inhibited at 20 μM compound (Figures 1 and 6) and parasite growth as assayed either by the fluorescence-based method (Figure 2A) or plaquing (Figure 8) shows greater inhibition at 40 and 80 μM compound than at 20 μM.
*3) It would be informative for the authors to discuss the rationale for the selected treatment regime. Since many drug-treatments involve daily dosing, was the two-dose regime based on poor tolerance of the compound in mice or other considerations? *
See response to reviewer 2, comment 11; the rationale for this dosing regimen has now been added to the Methods (line 715-721).
*4) Track length is not considered as a parameter in the filament sliding assays (Fig. 6) or the 3D motility assays (Fig. 7). These may be valuable parameters for the authors to examine; however, the time frames analyzed might be insufficient to capture track lengths. Could the authors include analyses of track lengths or discuss the technical limitations of their assays? *
In the in vitro motility assays, almost all of the actin filaments move for the entire 60s of video recording so trajectory length is directly proportional to speed and therefore does not provide any additional information. For the parasite 3D motility assay, we have added a new figure (Suppl. Figure 12) showing the effect of the compound on the displacement of wild-type and T130A parasites, along with new text describing these data (lines 269-273).
*5) When discussing the minor discrepancies between the results with recombinant protein and parasite motility, the authors could consider the relative concentration of motors in the pellicle; i.e. it might be necessary to inhibit a greater % of all the motors to truly block motility, perhaps consistent with the higher compound concentrations needed to affect parasite motility. *
This possible explanation has been added to the Discussion (lines 403-406).
6) The authors should include the IC50 data for all 5 KNX-002 resistant clones in the supplementary data. While the 5/26 clones showed >2.5-fold increase in IC50 for KNX-002, it's unclear how the IC50 of the single clone harboring the T130A MyoA mutation compared to the other resistant clones.
A figure has been added showing these data (new Suppl. Figure 8).
*7) For plaque assays, the authors should indicate how much DMSO was used for 0 KNX-002 conditions. It should presumably be the corresponding concentration at 80 µM drug and if not, that control should be performed to account for effects of DMSO at higher concentrations at all drug concentrations tested. *
In all experiments involving treatment with compound, the compound was serially diluted in DMSO to the appropriate range of concentrations prior to dissolving it in aqueous buffer for the experiment itself, enabling an equivalent amount of DMSO to be added to all samples in that experiment, including the DMSO only vehicle controls. This clarifying statement and the final range of DMSO concentrations in each of the different types of experiments has been added to the Methods section (lines 486-491). * *
*8) Authors should indicate the origins of their hexokinase for counter screens. *
The hexokinase used was from Millipore Sigma (#H6380); the supplier has been added on line 507.
*9) Authors should indicate µM on graphs. *
The μM label has been added to the graphs where it was missing (Figures 2 and 5, Suppl. Figures 4, 6, 8).
*10) In Figures 2A, 5A, and 5B, the use of colored lines (e.g., of different hues) could make the graphs more legible. *
We have experimented with color as a way to discriminate between the different doses on these graphs, but found the use of 8 different colors to be more distracting than helpful. The color-coding approach would be even less useful for readers who have color vision deficiency (including one of our authors). Symbol groupings have been added to the right of all growth curves to improve the legibility of the graphs.
*11) In Figure 2C, it isn't clear which cell line was treated with sodium azide to generate the positive control. *
It was the HFF cells that were treated with azide as a positive control; Figure 2C has been modified to make this clear.
*12) In the discussion, "a" is missing in the phrase "...mutation is likely to have long range structural impact..." *
Done. * *
*13) The abbreviation of species (spp.) should be followed by a period. *
Done.
Other
Further SAR analyses using an optimized actin-dependent myosin ATPase assay resulted in minor changes to Suppl. Figure 3 and Figure 3, with no significant changes to the conclusions. The text has been modified accordingly (lines 155-161, 178-180).
All other changes to the manuscript not noted above were editorial in nature, made to either improve clarity or correct minor errors in the previous version.
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Referee #3
Evidence, reproducibility and clarity
The authors identify a small-molecule inhibitor of T. gondii MyoA, the major apicomplexan myosin that is required for gliding motility and pathogenesis. Reconstitution of MyoA ATPase activity using recombinant protein enabled quantitative fluorescence measurements of actin-activated ATP usage. The authors screened a library of ~50,000 small molecules using their cell-free assay and counter screened hits by measuring their effects on hexokinase ATPase activity. The inhibitor, KNX-002, inhibited MyoA (IC50 of 2.8 µM), but had no effect on the ATPase activity of an array of vertebrate myosins. 15 analogues of KNX-002 were generated for SAR analysis, providing information on the functional groups of the molecule, despite not improving overall potency or specificity. In the context of T. gondii infection in human foreskin fibroblasts (HFFs), KNX-002 inhibited parasite growth (IC50 of 19.7 µM) while host cell viability was unaffected at the highest concentrations tested (80 µM). KNX-002 treatment (20-25 µM) reduced the percentage of motile parasites to approximately 5% compared to 30-40% in vehicle-treated parasites. The authors go on to demonstrate that MyoA is the biologically relevant target of KNX-002 during parasite infection, by generating resistant parasites by directed evolution. One of the resistant clones harbored a T130A mutation in the MyoA motor domain. While KNX-002 treatment of recombinant WT MyoA displayed dose-dependent inhibition of actin filament motility, the T130A proteoform was unaffected at all concentrations tested. T130A mutant parasites were independently generated and indeed conferred partial resistance to KNX-002 in growth and motility assays. Lastly, the therapeutic potential of KNX-002 was assessed during infection of CBA/J mice. At 10 days post-infection, mice treated with KNX-002 displayed a 40% survival rate compared to 0% in the vehicle-treated group. This was in contrast to mice challenged with T130A mutant parasites, in which KNX-002 treatment did not improve survivability. Together, these data indicate that the small molecule KNX-002 can mitigate T. gondii pathogenesis and one mechanism of action of KNX-002 is inhibition of MyoA-mediated gliding motility.
Major comments
- The T130A IC50 was done on the mutagenized clone 5. The authors currently don't have data showing IC50 on the independently generated T130A mutant, to see if the IC50s are similar to one another, or if there were additional resistance mutations present in clone 5.
- For 3D motility assays, it is currently unclear from the data and text what the expected maximal inhibition of motility would be; e.g., would parasites depleted of MyoA display 0% motility. Understanding the dynamic range of this assay could help clarify whether this residual 5% motility explains why parasites treated with 20 uM KNX-002 can still form small plaques. This could be achieved by referencing previous work that assesses 3D motility after depletion of a critical motility factor.
- It would be informative for the authors to discuss the rationale for the selected treatment regime. Since many drug-treatments involve daily dosing, was the two-dose regime based on poor tolerance of the compound in mice or other considerations?
- Track length is not considered as a parameter in the filament sliding assays (Fig. 6) or the 3D motility assays (Fig. 7). These may be valuable parameters for the authors to examine; however, the time frames analyzed might be insufficient to capture track lengths. Could the authors include analyses of track lengths or discuss the technical limitations of their assays?
- When discussing the minor discrepancies between the results with recombinant protein and parasite motility, the authors could consider the relative concentration of motors in the pellicle; i.e. it might be necessary to inhibit a greater % of all the motors to truly block motility, perhaps consistent with the higher compound concentrations needed to affect parasite motility.
Minor comments
- The authors should include the IC50 data for all 5 KNX-002 resistant clones in the supplementary data. While the 5/26 clones showed >2.5-fold increase in IC50 for KNX-002, it's unclear how the IC50 of the single clone harboring the T130A MyoA mutation compared to the other resistant clones.
- For plaque assays, the authors should indicate how much DMSO was used for 0 KNX-002 conditions. It should presumably be the corresponding concentration at 80 µM drug and if not, that control should be performed to account for effects of DMSO at higher concentrations at all drug concentrations tested.
- Authors should indicate the origins of their hexokinase for counter screens.
- Authors should indicate µM on graphs.
- In Figures 2A, 5A, and 5B, the use of colored lines (e.g., of different hues) could make the graphs more legible.
- In Figure 2C, it isn't clear which cell line was treated with sodium azide to generate the positive control.
- In the discussion, "a" is missing in the phrase "...mutation is likely to have long range structural impact..."
- The abbreviation of species (spp.) should be followed by a period.
Significance
This important work substantially advances technical and clinical aspects of studying the motility of apicomplexan pathogens by identifying a new small molecule inhibitor of gliding motility and uncovering its mode of action by inhibition of a motor protein. The evidence supporting the conclusions is convincing, with a new screening assay for myosin motor activity and advanced methods to characterize 3D motility for Toxoplasma gondii. The authors provide compelling evidence that KNX-002 inhibits MyoA, gliding motility, and MyoA-mediated virulence during mouse infection. The evidence suggests that some secondary or off-target effects remain uncharacterized within the parasite and in murine hosts. KNX-002 will enable targeted pharmacological inhibition of the motor complex, as opposed to broad inhibition of actin using cytochalasin D. While other small molecules inhibiting the motor complex have been identified-such as the myosin ATPase inhibitor 2,3-butanedione monoxime (Dobrowolski et al. 1997) and the myosin light chain 1 inhibitor TachypleginA (Heaslip et al. 2010; Leung et al. 2014)-these inhibitors have major off-target effects that render them unsuitable for therapeutic use. These findings are of interest to those studying apicomplexan pathogens, including T. gondii, Plasmodium spp., and Cryptosporidium spp. These include those interested in developing small molecule therapies and those interested in gliding motility. Our relevant expertise during this review process include: chemical genetics, cell biology of apicomplexan parasites, and signaling. We have limited expertise in the SAR strategies implemented to improve the effectiveness of KNX-002.
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Referee #2
Evidence, reproducibility and clarity
Summary
The manuscript by Kelsen et al. reports on the identification of a compound referred to as KNX-002 that inhibits the unconventional MyosinA motor ATPase activity from the intracellular parasite Toxoplasma gondii myosin A (TgMyoA), an unconventional myosin characterized by both its high divergence from those of the parasite host repertoire (i.e., about all homeotherms) and a functional contribution to crucial processes during the parasite life cycle. To identify KNX-002, the authors used assays they had previously developed to produce recombinant active TgMyoA in insect cells combined with those now designed to quantify the TgMyoA ATPase activity. With these tools in hand, the authors screened about 50.000 molecules from a library referred to as small inhibitors and further characterized the potency of the top list MyoA inhibitory compound (i.e., KNX-002) by conducting in vitro, ex vivo and in vivo studies.
The following sections of the manuscripts bring evidence that:
- the KNX-002 "re-synthetized" compound is at least 10 times more efficient at inhibiting MyoA ATPase activity when compared to muscle actin from different vertebrates in vitro (IC50 data).
- the KNX-002 can be chemically modified with chemical substitution and structural analysis. Up to 15 derivatives (all with lower potency at that stage) were structurally and functionally tested for comparison with respect to parental KNX-002.
- exposing the motile-invasive-replicative stage of T. gondii called tachyzoite to the KNX-002 compound (5 to 10 times higher doses than in vitro) impairs in a dose dependent way the tachyzoite's motility and the overall expansion of the population in host cell culture.
- mice injected intraperitoneally with type I tachyzoites and subsequently with two intraperitoneal injections of KNX-002 (at day 0 and day 2 post infection) showed slightly longer survival time when compared to those injected with parasites and then vehicle, thereby indicating a moderate effectiveness of KXN-002 in mice under the protocol used.
The authors further established the KNX-002 selectivity against TgMyoA parasites by applying chemical mutagenesis and subsequent screening for "resistance" to the KNX-002 compound. Using nucleic acid sequencing of the few genes encoding the myosin motor components (i.e., heavy and light chains), the authors eventually identified a TgMyoA mutation (T130A) which does not concern the predicted pocket to accommodate KNX-002 binding but does confer a 2.9-fold decreased sensitivity to KNX-002. Selectivity towards MyoA was also documented in vitro by analysis Actin filament sliding and ex vivo using CRISPR/Cas9 gene editing to engineer parasites expressing "exclusively" the TgMyoA on its mutated form (T130A mutant). These mutants indeed displayed fairly similar motile skills regardless of the presence of vehicle or KNX-002.
The authors conclude on the interest to consider the potential of KNX-002 (more specifically some promising derivatives) to enrich the limited current therapeutic regimens against T. gondii and other Apicomplexa (in particular Plasmodium) for which MyoA has already been argued as a relevant therapeutic target.
Major comments
The reviewers found the large set of assays appropriately designed, executed and presented to be reproduced by other scientists. The results are also mostly analyzed with enough detail and care throughout the work (except a few minor points raised below), but the reviewers also stress a few overstated conclusions easy to mitigate in particular related to the diseased model.
To the reviewer's opinion, there is no need for additional experiments but we would appreciate some rephrasing for higher accuracy and improved clarity.
Below are listed few major concerns to address.
- Considering (i) the moderate effect of KNX-002 on the acute infection process in CBA mice that received tachyzoites intraperitoneally, (ii) the fact that the drug application cannot be envisaged outside of the context of reactivation of cystogenic strains (in particular with respect to cerebral toxoplasmosis as emphasized in the introductive section), which implies the drug would have to be delivered and active in the brain parenchyma, a condition not analyzed here, it would be appropriate to modify the current title. It would be more relevant to highlight the solid body of data on the identification and functional characterization of the compound and derivatives in vitro and in the host mouse model. Apart from the title, the discussion should also recontextualize the in vivo assays and the information these assays bring on the slight delay of the "mortality" of some but not all mice.
- Motility analysis: This comment concerns the Figure 7 It seems to the reviewers that the major hypothesis to test in data presented in panel B is that the wild type and the T130A mutant tachyzoite respond differently under similar drug conditions rather than the two populations without drug. These statistics could be added easily, hence it would validate that the proportion of motile mutant parasites is not affected by the drug when compared to vehicle. However, the statistics shown panel C rather suggest that the drug does impact on the speed of the moving parasites, including when these carry the "resistance" T130 A mutation. It is not clear what we can gain in terms of messages with the motility index except to "slightly reverse" the analysis on panel B and to favor a no-effect of KNX-002 on the mutant parasite motile skills, on which the author might give more explanation. When comparing these quantitative tests with the panel presented above (panel A) it seems that the mutant parasite is still impacted by the MyoA inhibitor. Although there is no doubt for the reviewers that the T130A mutant emerging from the selected T. gondii resistant clones is a valuable probe for assessing drug selectivity : indeed the assays validate KNX-002 as a direct TgMyoA ATPase inhibitor, it might be good to rephrase some sentences and to have a harmonized definition of the parasite motility index throughout the text (Figure 7 legend, result and discussion sections). This reviewer's concern was accentuated by the comparison between the actin filament sliding index and the parasite motility index which appears as such far stretch;
Minor comments
Aside from the "far stretched claims" easy to re-address in a revised version, the readers have appreciated the writing quality and most figure illustration. The discussion nicely synthetizes the whole dataset, including those related to the 4 T. gondii clones that resisted to KNX-002 but not through mutations targeting any of the myosinA chains. Few comments are listed as:
Abstract: the concept of "ameliorate disease" in this framework is odd and the objective of the work can be rephrased in a simple way (see below)
Introduction section: we think that the references on the impairment of invasiveness for the KoMyoA should be included (Bichet et al., BMC Biology 2016) as it has provided proof of an alternative and suboptimal mode of entry in many different cell types, thereby arguing that in absence of MyoA function, parasite invasiveness is not fully abolished and this without considering any MyoC-driven MyoA compensation. Introduction, third paragraph: in the sentence "Because the parasite can compensate for the loss or reduced expression of proteins important to its life cycle [29-31], small-molecule inhibitors of TgMyoA would serve as valuable complementary tools for determining how different aspects of motor function contribute to parasite motility and the role played by TgMyoA in parasite dissemination and virulence ». We definitively agree with this view but saying that, we think it would be worth evaluating (or simply discussing) the potency of the KNX-002 against MyoC, which compensatory contribution has been debated and remains questionable (at least to the reviewers) with respect to cell invasiveness restoration (related to the comment above).<br /> Result section:
- If we are correct, the screen and the characterization study have been performed with two different products (CK2140597 and KNX-002 the compound library and the re-synthetized one, respectively). Could we make sure that the two have the same potency?
- we understood how the authors came to the conclusion that the KNX-002 impact on growth of the parasite and they stated "growth in culture" in the subsection title but then refers to parasite growth. Therefore, it looks a bit confusing for the reader since intracellular growth per se is probably not modified but this feature was not looked at it in this study (we would expect no impact based on published data on MyoA- genetically deficient tachyzoites, except if the drug impacts host cell metabolism for instances). Instead, it is the overall expansion of the parasite population that is analyzed here and clearly shown to be impacted. This decrease in population expansion on a cell monolayer likely results from impaired MyoA-dependent egress and invasiveness upon chemical inactivation of MyoA. Accordingly, it appears difficult to understand what is an IC50 for the "overall" growth in the context of this study. The authors should rephrase for better accuracy when necessary, including in the graph Fig2 legend axis.
- The authors should clarify for the reader (i) why they use in some case myofibrils and other muscle F actin when measuring the Myosin ATPase activity, (ii) what does mean XX% calcium activation and (iii) why using 75% in these assays which is 3 times higher from the original assays. Why they did not include non muscle actins in their study since Myosins also extensively work on non muscle actins.
- The protocol of image analysis of the 3D motility assay was increased to 80 seconds for the test of KNX-002 selectivity using wild type and mutant parasites (Fig7) when compared to the test of KXN-002 concentration effect on wild type tachyzoites (60 sec in the result section, in Fig 4 legend and in the Methods' section). Is there any specific reason?
- In the mouse infection experimental design (Method section), it seems that they were no biological replicates in the case of the drug-treated (parasites + mice) which is not the case for the comparison of virulence between MyoA wild type and T130 mutants. If true, and considering what the authors wish to emphasize as a main message, it is fairly complicated to convincingly conclude about the KNX-002effectiveness in vivo. Maybe the authors could explain their limitations. We are also not sure why the compound has been injected only twice, at the time of parasite injection and two days after whereas the mice succumbed after 8 to 9 days even without MyoA inhibitors. Although quite difficult to measure, do the authors have any knowledge (based on the chemistry for example) of the compound stability and lipophilicity in blood and tissues? Because the IC50 on free tachyzoites appears significantly higher (5.3 uM, Fig4) than the in vitro molecular assay, when assessed in motility tests, and is increased for intracellular growth (Fig 8), it is somehow expected that the current compound would not work that great in vivo. Did the author try to provide the inhibitor intravenously every day?
Figure 4: 2D and 3D Motility- the authors should comment on the fact that in 2D conditions with 10 uM of KNX-002, circular trajectories (one complete circle so at least 2 parasite lengths but sometimes more) largely dominate over others, whereas in absence of KNX-002 these circular trajectories are barely detectable and helical trajectories predominate. What could that mean as regard to the MyoA functional contribution to either process?
Figure 7: Besides the major point raised above for panel C, the information carried by the Figure could be stronger if an additional panel is introduced regarding the interesting assay on the preserved structural stability of the MyoA mutant over the WT MyoA (currently in SupFig7)
Material and Methods
Parasite motility assays: remove the duplicated [16] reference.
Discussion:
The discussion starts with the ongoing debate on mechanisms underlying zoite motility; We found that the work of Pavlou et al. (ACS nano, 2020) should be part of the references listed there, as it brings evidence that a specific traction polar force is required probably in concert with microtubule storage energy at the focal point, a result that questions the prevailing model.
Concerning the C3-20 and C3-21 compounds, the sentence "they have no effect on the activity of the recombinant TgMyoA (AK and GEW, unpublished data)" in the paragraph starting by "There have been only two previously..." should be refrained unless showing the results.
If possible, the authors should expand more on the effect of KNX-002 on Plasmodium falciparum and its homolog PfMyoA.
Significance
This multi-disciplinary work timely brings to the research communities (basic research and pre-clinical research) new knowledge and a new reagent quite valuable for future dissection of the T. gondii MyoA contribution across different scales of study. It also provides a strong rationale and preliminary orientations for developing a new compound targeting MyoA in the context of anti-toxoplasma or possibly anti-Apicomplexa therapeutic strategies.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In this study the authors use an in vitro screen to identify a novel inhibitor of the actin-activated ATPase activity of myosin A. The lead molecule, KNX-002, was shown to inhibit parasite growth and motility, with initial SAR studies failing to improve on the potency of the parent molecule. The author's then focus on confirming the expected mechanism of action of KNX-002 in parasites. They use a chemical mutagenesis and drug-pressure protocol to select for a drug-resistant parasite population. They identify a drug-resistant clone harbouring a missense mutation in the TgMyoA locus, converting a threonine at position 130 into an alaninie. These parasites demonstrate resistance to KNX002, and the equivalent mutation introduced de novo into the MyoA locus in otherwise wild-type parasites confirms that the T130A mutation is sufficient to provide protection from the effects of the drug. Finally, they confirm that KNX-002 can protect mice from T. gondii infection.
Overall the manuscript is very well written, with a clear and logical narrative. The data presented broadly support their conclusion, and the general quality of the figures is very high. I would recommend that the manuscript should be accepted once the following points have been addressed:
Major comments:
While the following would strengthen the manuscript, they could be addressed in the discussion or with clarification of the text:
- In the study there is a lack of consideration of other targets. In and of itself this is not a problem, but once the author's identified the T130A mutation as being a key for protection it would have been good to Sanger sequence the other T. gondii myosins - a quick alignment of the TgMyo's A, C, H (class XIV), along with D and E suggests that the motif is highly conserved. This raises the currently unexplored (and exciting!) prospect of a pan-myosin inhibitor, and that there might have been mutations at an equivalent position in the other four KNX002 resistant clones - for example, MyoC has been proposed to provide some level of functional redundancy in the absence of MyoA. The fact that T130 is not thought to the binding site of KNX002 is only introduced quite late on - this also relates to the next point - is the binding pocket conserved???
- It is intriguing that the residue and proximal amino acid environment are highly conserved with vertebrates, but that KNX002 does not have an effect on their activity in their screen assay. It would be useful to know if the differences in the structures of the myosins can provide an explanation for this - along the same lines, given that the crystal structure of TgMyoA is available (PMID: 30348763), it would be useful for the authors to provide a molecular model for the binding of the inhibitor to the proposed point of engagement. If this is an allosteric site it is possible that the mutation functions indirectly upon binding of KNX002 to the orthosteric site, but this would be useful to help the reader to understand this (and there are bioinformatic prediction tools that will score allostery - which would be interesting to include). This is explained somewhat in the discussion - but this should be introduced much earlier to clarify. What is known about allosteric regulation of Myo function? Is this a known site of regulation?
Minor comments:
- Introduction: 'Nearly one third of the world's population is infected with the apicomplexan parasite' - given that these data are extrapolated from serology, this should be reworded - it's fairer to say that they 'are or have been infected...'
- Page 4: figure 1A - can you provide some explanation for incomplete inhibition in the screen - there seems to be a residual amount (15-20%) of activity that is not inhibited.
- The authors demonstrate a general effect on growth over 7 days. It would be good to use a replication assay (e.g. parasites/vacuole over a single lytic cycle) to confirm that KNX002 does not affect cellular division. This would further strengthen the argument that the phenotypic effect is primarily via impacts on motility.
- Page 5: 'selected for parasites resistant to KNX-002 by growth in 40 μM KNX-002.' - could the authors add text to explain why that concentration was chosen.
- Page 6: 'suggesting that the effects of the T130A mutation on motor function are due to more subtle structural changes' - it's fair to say that there are not gross structural changes based on the data presented, but that does not mean it is therefore a 'more subtle structural change' - surely the mutation could prevent KNX002 binding without effecting TgMyoA structure?
- Page 6: 'the proportion of filaments moving' - in the figure it's referred to as the 'fraction of filaments', which makes more sense for the data presented. Please correct to 'fraction' throughout the manuscript (discussion, page 9 - possibly other instances!). Along the same lines, in figure 6 it would be good to change the y axes on the '% moving' to be 'fraction moving' and change the numbers - this would make it easier for the reader to understand the index values presented in the lower panels - if you do the calculation with the % values presented the numbers don't make sense (as fractions they do). The axes for motility also go up to 125% - please correct - based on the data presented there is no need for this to be above 100% (or 1 - see above).
- Page 7: 'tested whether KNX-002 (20mg/kg, administered intraperitoneally on the day of infection and two days later' - please provide some rationale for the concentration used.
- Page 10: 'the T130A mutation is likely to have long range structural impact that could alter the KNX-002 binding pocket' - this is particularly interesting, and should be addressed with a model - do the authors think that the T130 region be a conserved site of allosteric regulation? This would be good to expand upon in the discussion - mutation of an allosteric site as a mechanism of resistance is unusual, and typically described as being unlikely - and used as justification for the targeted drugging of allosteric sites.
Significance
Strengths: Discovery of new parasite-selective inhibitor of TgMyo-A motility will be a valuable tool, and potential therapeutic lead.
Weaknesses: Molecular mode of action on a modelled binding of KNX002 could have strengthened the proposed mechanism of action via a site outside of the expected KNX002 binding pocket.
Advance: the findings advance our understanding of drug-resistance mechanisms, and also validate TgMyoA as a druggable therapeutic target.
Audience: this work will appeal to molecular parasitologists, as also be of broader interest to research communities including myosin structure-function researchers, and drug discovery groups interested in drug-resistance mechanisms.
Expertise: molecular parasitology, chemical biology, proteome engineering
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Reply to the reviewers
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Reply to the Reviewers
I thank the Referees for their...
Referee #1
- The authors should provide more information when...
Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...
Response: We expanded the comparison
Minor comments:
- The text contains several...
Response: We added...
Referee #2
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Referee #2
Evidence, reproducibility and clarity
This work is is distinguished by impressive technical feats and experimental breadth, and is another excellent contribution from the Zurzolo lab. My comments are advisory regarding more explicit descriptions and qualified conclusions.
Introduction: Please define how filopodia are distinguished from TNTs - is it length only or are there other characteristics? Do filopodia and individual TNTs have the same diameter? There is presumably a functional difference as well?
Please state the number of cells in each array spot?
Paragraph 2 of Results would benefit from a general description of procedure and rationale for assessing protrusions in the artificial setups used in this study of isolated cells. It would help to explicitly state when protrusions were assessed after fixation and when the observations were made with unfixed cells. What are the issues of concern with these methods and what aspects are relevant to general cell behavior? Isn't it important to point out that the conclusions regarding Arp2/3 inhibition and TNT formation are operational for the conditions used?
Ln 148: If filopodia are distinguished/defined by their shorter relative length, the observation that "filopodia lengths showed that a majority of filopodia were far shorter" is not informative. Do cells with TNTs also have filopodia?
Does the negative effect of increasing array separation distance on frequency of TNTs suggest that the observations represent a steady state, and the possibility that the observed frequencies are measures of protrusion stability? If the experiments monitor the steady state, can the authors distinguish between stability and inherent ability to extend filopodia to longer distances? Is the conclusion (ln 151) "there seems to be an upper limit to F-actin-based elongation" justified if stability or relative rates of extension and retraction are factors? Another possibility is that the observations reflect protrusion:protrusion interactions that promote stable TNTs. There is the precedent of cytoneme:cytoneme interactions associated with stable signaling contacts (Gonzalez-Mendez et al PMID: 28825565) as well as previous work from the Zurzolo lab (Sartori-Rupp et al PMID: 30664666). A kinetic analysis in real time might be very informative.
Ln 158: "cells displaying only lamellipodia accounted for 4.1% of [cells with?] TNTs examined"
Significance
This work offers new insights into the cytoskeletal processes that generate long cell protrusions. The implications for understanding cell:cell interactions and signaling are fundamental and important.
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Referee #1
Evidence, reproducibility and clarity
I applaud the authors for the creative experimentation and intriguing findings presented in this work, but the narrative lacks a clear biological question and, as written, comes across more like a collection of thematically related results, rather than a logical point A > B > C progression of studies that significantly advances our understanding of TNT formation beyond the current published literature. In addition, there are a number of inconsistencies and ambiguities in the approach - at least as described - that make it hard to follow the logic flow of the authors. Below I list some of the major inconsistencies and questions I had after reading through the manuscript.
- From Figure 1b - the micro patterned substrates separated by different distances also appear to be printed as different diameters - is this true? I could find no mention of it in the text. My concern is that changing the contact area between the cell and substrate might impact the cell's ability to extend very long membrane protrusions towards its neighbors. Why not print patterns of exactly the same diameter separated by increasing distances?
- By using micropatterned substrates the Authors hope to force the extension of TNTs using actin driven mechanisms, while eliminating the possibility that cells are form these connections by "dislodging" from the substrate. The Authors also state that the cells do not wander into the region in between the circular patterns. However, in many images featured in multiple figures, I can find examples where cells clearly extend into the space between the circular patterns (see Fig. 2.a.i for an example). The primary concern here is that the authors did not fully eliminate the possibility that cells are making direct contact and then pulling away from each other/dislodging to form TNTs. In the supplemental material, there were movies showing TNTs that had already formed, but I was unable to find examples of TNTs in the act of forming. If the authors do have timelapse data that clearly shows this, it should be front and center in this data set.
- The authors make use of CK-666 to inhibit Arp2/3, which is thought to free up actin monomers that can be used to further elongate TNTs. Other orthogonal methods should be employed to corroborate the results from CK-666 treatment. There are other drugs that inhibit Arp2/3 (e.g. arpin, wiskostatin) and of course there is always genetic manipulation (shRNA KD).
- The authors also employ a formin agonist, IMM-01, and the results from those experiments (Fig. S4) suggest that activating formin mDia could facilitate TNT elongation, but the authors do not follow up with direct molecular manipulation to further test this idea. Are formins (specifically mDia, the target of IMM-01) needed to elongate TNTs?
- With the experiments shown in Figure 3, the authors apply optical tweezers to pull what they refer to as "nanotubes" from the cell surface under conditions where Arp2/3 is inhibited with CK-666. The panels appear to show that CK-666 allows actin to assemble out into a pulled nanotube more readily than control cells. However, the reporter for actin assembly in these experiments is F-Tractin, and it only partially fills the protrusion. I note here that F-Tractin appears more soluble under the CK-666 condition. Can the Authors rule out the possibility that there is just a larger soluble pool of F-Tractin probe under these conditions?
- Related to the previous point, it is not clear to me why the Authors need to invoke the application of external forces with an optical trap to study the enhanced elongation of TNTs under CK-666 conditions. Why don't the authors directly visualize actin accumulation and TNT elongation after treatment with this inhibitor?
- In Figure 4, the Authors move away from TNTs and instead focus on "longer protrusions" (filopodia?) to examine the effects of EPS8 and IRSp53 on growth of these structures. The general findings here are consistent with the role of these factors in protrusion growth from previous studies.
- The experiments in Figure 5 are performed with a truncated "bundling active" form of EPS8 allegedly lacking actin capping activity. The logic behind this choice is unclear. These experiments need to be repeated in parallel with full length WT EPS8 to allow for a full and clear interpretation of these results. Along these lines, could the Authors stain for endogenous Esp8/IRSp53 complex within TNT-connected cells?
- Data in Figure 5 show that the Eps8dCAP/IRSp53 complex increases the vesicle transfer within TNT-connected cells from Eps8dCAP/IRSp53 donors to EBFP-H2B acceptors indicating the functionality of TNT. Interestingly, cells with overexpression of Eps8dCAP/IRSp53 and CK-666 treatment do not increase TNT-connections. Could the authors examine the stability of TNTs under this condition? The lack of increased vesicle transfer may be due to the instability of the TNT structure rather the saturation of the system.
- Figure 5c. The data show that vesicle transfer from EpsdCAP/IRSp53 donors to EBFP-H2B acceptors increases under the overexpression of EpsdCAP/IRSp53. Are the EBFP-H2B acceptors able to form TNT? If so, could the authors show the vesicle transfer in those TNT-connected cells? The images indicate that there is no presence of TNT structures in these conditions.
Significance
This study from Henderson et al. seeks to understand the mechanisms that drive tunneling nanotube (TNT) formation. TNTs are essentially giant filopodia that extend many microns from the cell surface to contact protrusions extending from neighboring cells, to establish channels that allow for exchange of biological material. The authors use an approach that involves micro patterned substrates, various inhibitors/agonists, construct overexpression experiments, and biophysical measurements with optical tweezers. The major insights from these studies are that actin monomer availability is limiting for the formation of long TNTs, and that proteins that are well known to regulate the formation of filopodia and related linear actin structures (namely EPS8 and IRSp53) promote TNT formation. These are interesting findings that are certainly consistent with the previously published literature on actin-based protrusions, and as such they should be of interest to cell biologists.
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Reply to the reviewers
We thank both reviewers for their constructive criticism and the insightful comments on our manuscript. Reviewer 1 states that:
„The strength of this manuscript lies in its comprehensive analysis of Bim1 function, the quality of the results and that the experiments are generally well controlled and interpreted. „
And „the findings of this comprehensive analysis are of great value to the microtubule field, especially for people working in budding yeast. „
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While Reviewer 2 adds:
„The current study is indeed rich with new insights into the mechanisms by which these molecules function, and will no doubt prove valuable to a number of people in the microtubule/motor/yeast mitosis fields. As someone who is interested in and studies mitosis in budding yeast, I found the study to be interesting.
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Both reviewers conclude that:
“…there are useful data in the manuscript that make this an important contribution and that it should definitely be published”
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Both reviewers raised two major areas of concern: 1. A confusing overall structure makes the study hard to follow. 2. A clearer distinction needs to made between what has already been reported in the literature, and what are new insights provided in this study. In this regard, the appropriate citations need to be made at various positions throughout the manuscript.
In this full revision, we have addressed these major points of criticism of the reviewers as follows:
We have re-organized and re-focused the manuscript to make it more accessible and easier to follow for the reader. We have followed a suggestion from reviewer 1 and now present all experiments characterizing mitotic spindle phenotypes and how they can be suppressed consecutively in Figures 2-5 and then finish the manuscript with the characterization of the spindle orientation phenotype. This way of ordering by biological pathway allows for a better flow of the manuscript.
Throughout the text, we have added citations to better indicate the previous state of knowledge and how the presented experiments either confirm or extend the previous findings in the field. This helps to put our current study better into and overall perspective.
In addition, we have addressed the specific points raised by both reviewers in full. Please see below our point-by-point answer.
Reviewer1
There is already a huge body of published information on mitotic spindle positioning via the Kar9 and dynein pathways that grew since the late 1990s. The genetic relationships and molecular interactions between the components of these 2
pathways are well studied (many studies, including Liakopoulos et al. 2003, are not cited by the authors). The authors
should make sure to cite and compare to the relevant primary literature when they report findings that have been
described before. This will help to distinguish novel findings from validation of previous results.
We have added relevant citations throughout the manuscript, please see below.
"The strict dependence of Kar9 and Cik1-Kar3 on the presence of Bim1, as well as the different effects of bim1Δ on
nuclear and cytoplasmic Bik1, may reflect the formation of stable complexes between Bim1 and these binding partners in
cells." I believe this has already been shown (Kumar et al., 2021 and Manatschal et al., 2016). There are several other
instances as well where additional literature should be cited, for example Gardner et al., 2008 and Gardner et al. 2014.
We have now cited the Manatschal and Kumar papers in this section of the revised manuscript. We have also cited the mentioned Gardner papers later in the manuscript.
The selection of targets to study in figure 1 doesn't seem to follow the listed criteria. Many proteins included in the
study were not found by IP-MS, but some perfect targets according to the listed criteria like Duo1 were not included in the
study. In addition, there are more sophisticated ways of finding Bim1 binding motifs in the literature
(https://doi.org/10.1016/j.cub.2012.07.047). I suggest, the authors declare that they rationally chose to study 21 proteins
of interest but remove the claim that their approach was systematic.
We have changed the wording accordingly and removed the claim of systematic target selection.
Much of the microscopy data was acquired after release from alpha factor arrest. What is the reason for this
perturbation? An exponentially growing culture should mostly consist of mitotic cells anyway. Since this treatment affects
cell size and potentially protein levels/concentrations, testing its influence on spindle position as well as levels on MTs for
the most relevant proteins of interest would be important to exclude introduction of artifacts.
In principle that’s correct, but using synchronized cultures has the great advantage that mitotic timing and all the parameters associated related to it (spindle length etc.) can be quantified much better and we obtain larger N and thus get better statistics using this approach. In a typical log culture only one third of the cells are in mitosis and this entails very different states of mitosis. Observations times are limited due to fluorescent bleaching and low signal intensity. We therefore feel the benefits of alpha-factor release outweigh the problems and we compare all mutants under the same conditions.
Some of the results obtained from bim1Δ cells are a challenge to interpret due to the wide range of processes that
involve Bim1 and therefor the potential for many off-target effects- including a global change in microtubule dynamical
behavior in both the cytoplasm and the nucleus that will influence the length distributions and microtubule lifetime (and
thus number). The authors must carefully consider these caveats.
We agree in principle and have therefore not only characterized the bim1 deletion, but also more specific bim1 mutants. We also show that some aspects of the bim1 delta phenotypes, but not others, can be rescued by different strategies.
The results section on page 12 refers to phenotypes of kar9 delete cells with respect to Bim1-GFP on cytoplasmic
microtubules. In the figure 3D,F I only found data for Kar9-AID, though. The authors should refer to supplementary figure
5A or even better include quantification similar to figure 3F.
We have corrected this in the revised text. We refer to the Kar9-AID, for which we have the quantification.
The observation that cytoplasmic Bim1 localization depends on interaction with its cargo Kar9 (figure 3 + 7) fits into the
model that Kumar et al (https://doi.org/10.1016/j.str.2021.06.012) proposed in which Kar9 oligomerization is required for
its Bim1 dependent localization to microtubules. It would be valuable to point that out.
We have now included a sentence that our findings support this model and added the respective citation.
I don't fully understand the model proposed in Figure 5H and discussion page 26. Based on figure 5E, it does not look
like there is a higher concentration of Bik1 along the lattice in bim1 delete. So how would Bik1 increase Kip2 processivity
if its levels are only increased due to a MT length change? If Kip2 was not fully processive, you would rather expect to
see less of it at the tip of a longer microtubule in bim1 delete. The model suggested by Chen et al
(https://doi.org/10.7554/eLife.48627.001) suggests that Kip2 only gets loaded at the minus-end and processively walks
towards the +end without falling off. Are the authors suggesting that bim1 deletion changes this behavior?
We have rephrased this section in results and discussion and more clearly state that there is no increase in Bik1 per MT length unit in the bim1 deletion. We have amended the discussion and grant that we currently cannot explain by which molecular mechanisms Bik1 may contribute to the observed increase in Kip2 plus-end localization under conditions of a bim1 deletion.
I don't see evidence for independent pools of Bik1 in the cytoplasm and nucleus as claimed on top of page 21. Total
Bik1 levels on cytoplasmic microtubules seem to be well explained by their length. Please explain better or remove the
statement.
We have removed the respective statement from the revised manuscript.
The experiments in supplementary figure 7B are difficult to interpret. The localization on cytoplasmic microtubules is
different, but probably explained by the formation of Bim1 heterodimers. Therefore this experiment is difficult to interpret
and should be removed.
As requested, we have removed this experiment from the revised manuscript.
top of page 24: Kar9 localization in metaphase depends exclusively on SxIP, not on LxxPTPh (Manatschal 2016). The
paragraph should be removed as it is not supported by published data or sufficiently by the authors to merit the
conclusion.
We have reformulated this to avoid a misunderstanding. We merely show that in the context of the artificial GCN4 construct a fragment just including the LxxPTPh motif is sufficient for Bim1-dependent localization to microtubules in nucleus and cytoplasm. This makes no statement about localization determinants of the authentic Kar9 protein.
Top of page 26: The genetic interactions between the Kar9 pathway and the dynein pathway were already well known
before this work. Please reformulate accordingly.
We have re-written this section and introduce the two pathways with the respective citations in the very beginning of the section before describing the experiments.
page 27 second paragraph: There is no selective pressure to evolve compensation mechanisms for gene deletions. I
suggest the authors consider that Kar9 and dynein partially redundant, with Kar9 acting to position the spindle prior to
metaphase and dynein to maintain spindle position in the mother and bud compartments in late metaphase and
anaphase. The authors should consider the quantitative analysis of Kar9 and dynein dependent spindle positioning
reported in Shulist et al. 2017 and the method for analysis of spindle length and position in 3D in Meziane et al. 2021.
We have rephrased the section on the partially redundant Kar9 and Dynein pathways. See below our answer for measuring spindle length.
In addition, it is not clear to me which results suggest that the relocalization of Bik1 is required in the bim1 delete. Why
would wild type levels not be sufficient for dynein pathway function? The authors have not conclusively shown that
nuclear migration relies on upregulating the dynein pathway in bim1Δ cells. If there is no supporting data, the paragraph
should be removed.
In this revised manuscript we have phrased our observations more carefully and acknowledge the limitations regarding molecular insights. We present indications for increased levels of Dynein-Dynactin pathway components at plus-ends in the bim1 deletion cells, but it is indeed unclear, whether an increased Bik1 level in the cytoplasm is required to achieve this.
Please provide more details about intensity quantification on page 35. Were these measured on sum or max
projected stacks? What was the method of background subtraction?
Analysed images are optical axis integration scans over 3 μm taken on a Deltavision microscope. This procedure gives a sum projection. Local background was determined for every cell by drawing a line under a signal curve derived by line scan. The background line connects regions that are still within the cell but are outside of spindle (or microtubule). We added a sentence in the materials and methods section under point 2.
Are the spindle lengths in Figure 2E measured in 2D or 3D? Bim1 deletion might lead to more misalignment of the
spindles in z due to inactivation of the Kar9 pathway and thus partially explain the shorter spindles. The measurements
should therefore be performed in 3D.
As we have used optical axis integration (OAIs) on the Deltavision microscope and obtained a sum projection of this virtual stack, the spindles were measured in 2D and we don’t have the information to measure in 3D (this would require a regular stack). We show that there are different ways to restore different aspects of spindle length with alternative strategies. These are unlikely to influence just spindle orientation. In addition, we see that Bim1 deletion has an effect on the size of a nascent bipolar spindle when spindle orientation is similar to wild-type cells. We agree that z-misalignment may affect absolute values of spindle size of Bim1 deletion in late metaphase and it would be better to measure in 3D. However, we think in this case it is unlikely to affect our conclusions in this study.
The authors should try to shorten the text. There is a lot of redundancy between results and discussion sections.
We have to shortened the text to avoid redundancy (before >43000 characters, now around 41000 characters, and we have decreased the number of main figures from 9 to 8.
Data is shown that leads to conclusions that are already supported by the literature should be moved to the
supplementary material.
In the course of re-organizing the manuscript we have tried to do this.
Reviewer 2:
"Robustness of Ndc80 loading might be achieved by the coexistence of multiple kinetochore assembly pathways or
alternatively determined by intrinsic Ndc80 properties." Wouldn't Ndc80 levels be determined by Ndc80 kinetochore
loading, and not by end-binding proteins? This seems to be the more likely means to regulate Ndc80 levels.
We have removed this statement from the revised manuscript.
"Upon analyzing the associations in the cytoplasm, we found that Kar9-3xGFP foci on bud-directed cytoplasmic
microtubules were abolished in the bim1Δ strain, consistent with earlier reports." It would be helpful if the authors
commented on the how the localization of some of these proteins are affected by bim1Δ on the mother-directed plus
ends. Although I understand the need to account for one class of plus end for the sake of consistency (and the distinct
behaviors of the mother vs bud-directed plus end), the text as written leaves me wondering about the other plus end.
We have noticed that the bim1 deletion led to the loss of asymmetric distribution on cytoplasmic microtubules for a number of components. Most prominent are Bik1, Kip2 and proteins of dynein-dynactin complex. We felt that further analysing this phenotype was beyond the scope of this study.
"The CAP-Gly domain construct, expressed from a BIM1 promoter, almost exclusively localized to the spindle of yeast
cells." For clarity, the authors should explicitly state that the CAP-Gly domain in question is from Bik1. Although this can
be deduced, this was not abundantly clear.
We have clarified this in the text and in the figure.
"In addition to Ase1, we followed the kinetochore proteins Ndc80-GFP and Sgo1-GFP which specifically marks
kinetochores that lack tension." This sentence should add "the latter of which..." to clarify that SgoI, but not Ndc80
exhibits this behavior.
We have added the phrase “the latter of which” to clarify this point.
"We observed that bim1Δ cells had mispositioned kinetochores with a bright Sgo1-GFP signal that was much stronger
than in wild-type cells." I don't see the mispositioned kinetochores described here. Are the authors referring to the fact
that Sgo1 is brighter, which suggests tension-free KTs? If so, this should be clearly stated as such, since the authors are
not explicitly assessed kinetochore "positioning".
We have rephrased the sentence to clarify. We refer to a lack of bi-lobed Ndc80 signal and a bright Sgo1-GFP signal as two aspects of the phenotype.
"We speculate that Bim1-Bik1 in a complex with its cargo Cik1-Kar3 is active after bi-polar spindle formation but before
late metaphase and Ase1 can partially substitute for nuclear Bim1 functions." I struggled to grasp the reasoning for these
conclusions. I assume the former point (the timing for Bim1-Bik1-Cik-Kar3) is due to the localization dynamics of Bim1
and Bik1, while the latter (Ase1 can substitute for Bim1) is due to the synthetic interaction between Bim1 and Ase1 (I
needed to look this latter point up myself). Or is this latter point due to the brighter spindle Ase1-GFP intensity? In either
case, the authors should more clearly state their reasoning.
We have clarified this statement in the revised discussion.
The error bars in Figures 3A and 6E (shown as 95% CI) and elsewhere seem very small for the parameters that are
being plotted. Spindle length values as shown in Figure 2E cover a broad range (as would be expected for a biological
process), and it would be more accurate if the error bars in Fig 3A and 6E reflect this, even if it means they start
overlapping each other. I find the error as shown to be misleading to your readers, and unless the authors have very
good reason to use 95% CI (which is not as meaningful as standard deviation), then I would encourage them to use
standard deviation.
We prefer to use CI for the spindle length plots over time for consistency reason and to avoid overlap, which would make the graphs difficult to read. We have changed the text to provide the standard deviation instead of the standard error of the mean for spindle length and metaphase duration, see point below.
The same is true for the values stated throughout the text (e.g., for mitotic timing "47{plus minus}2 min" for metaphase
duration; for distance between SPB and bud neck {plus minus} 0.1 μm, etc). I am highly skeptical that metaphase
duration (for example) ranged from only 46-48 minutes. Please use standard deviation to describe a more accurate
description of the range of values for these parameters.
In the revised manuscript, we now give the mean values plus/minus standard deviation, instead of the standard error of the mean, as requested. In addition, the range of values is directly visible from the individual data points in the plots.
"Unexpectedly, the kar9 deletion mutant displayed a slightly accelerated metaphase progression relative to wild-type
cells (26{plus minus}1 min) (Figure 3C). This could be attributed to an increased level of Bim1 on the metaphase spindle
of kar9Δ (or Kar9-AID) cells." The authors should give us more rationale to explain the "attributing the increased levels of
Bim1" point here. Do they think that the levels of spindle-associated Bim1 impact metaphase duration somehow? If so,
how?
We have added a sentence, speculating about how this could be accomplished.
"Overall, our cell biology data suggested that major nuclear Bim1 functions are conducted in a complex with Cik1-
Kar3, while Bik1 and Kar9 have a smaller impact, probably affecting the nuclear- cytoplasmic distribution of Bim1."
Although I understand and agree with the former conclusion (that Bim1 functions are conducted via Cik1-Kar3"), the latter
was confusing to me. Did the authors mean that "Bim1 impacts Bik1 and Kar9 to a lesser extent", rather than vice versa?
The authors are discussing Bim1 functioning via Cik1, but then switch to discussing how Bik1 and Kar9 affect Bim1.
We have removed the second part of the sentence from the revised manuscript.
"Next, we compared the comparing genetic interaction profile of a bim1 deletion to that of various other factors by reanalyzing the synthetic genetic interaction data..." Remove "comparing".
Thanks for pointing out this typo, we have removed it in the revised manuscript.
As someone who is unfamiliar with the analysis shown in Figure 3H, I think it would be useful to list a Pearson
correlation value for two genes that are not functionally related. This would help define a lower limit for this analysis.
For functionally unrelated genes the Pearson correlation between genetic interaction (GI) profiles is very close to zero. The graph below depicts Pearson correlation between GI profile of Bim1 and GIs of every yeast gene (data used for graph is taken from thecellmap.org).
The axes for the plots in Figure 5E and 5I are very confusing to me. I don't understand what I'm looking at. Why does
it go from 0 to 1, and then back to 0-1 again? I don't see how this can account for MTs of different lengths. Normalizing all MT length values to 1 would do this, no?
We have clarified the labelling in the revised manuscript. The x-axis gives the relative position from either the plus-end, or the Spindle pole body (both set to position 0) in micrometres. This allowed us to compare fluorescent intensities on cytoplasmic microtubules of different lengths in wild-type and bim1 delete.
"These observations are consistent with the idea that Bik1 acts as a processivity factor for Kip2: If more Bik1 is
present on the lattice, then more Kip2 molecules are able to reach plus-ends without detachment." Perhaps I'm
misunderstanding the plot shown in Figure 5E, but it seems to indicate that the levels of lattice-bound Bik1 are the same
in BIM1 and bim1Δ cells (higher SPB-localized levels, though). There are also lower levels of Bik1 at the plus ends in
bim1Δ cells. So, if Bik1 were a processivity factor for Kip2, this would suggest that they would remain bound at plus ends
as well, which these data suggest is not the case…
We have added a section to the discussion that deals with this point and we speculate about the reasons why Kip2 is increased at plus-ends, while Bik1 is not.
"The data on the CH-Cik1 fusion is very compelling, and indeed supports their hypothesis that Bim1's main role in the
nucleus is to target Cik1 to the spindle MT plus ends. That being said, it would be a simple, but important task to ensure
that this fusion behaves as suggested (restores Cik1 plus end binding in cells). Otherwise, it can't' be ruled out that this
fusion is rescuing bim1Δ functions by some other means. However, as stated above, it's unclear how much was already
known about this fusion from the lab's previous work.
In our previous study (Kornakov et al., 2020) we have shown that the CH-Cik1Delta74 fusion indeed is sufficient to enrich Kar3 at plus ends. We expect the same to be true for this slightly different fusion construct. We have added a respective sentence to the results section.
Regarding the p1-p6 promoter data: p6 is missing from Figure S6A, in spite of it being referenced in the text and the
figure.
Thanks for pointing this out, we have corrected that in the revised manuscript and do not refer to p6 anymore.
"Exogenously expressed Ase1 displayed a similar level and kinetics of localization compared to the endogenous
protein, indicating that binding sites for microtubule crosslinkers are not a limiting factor on the budding yeast spindle."
Specifically, the authors show that binding sites for Ase1 may not be limiting (the overlapping 95% CI bars if Fig S6B
suggest this is not significant), not all crosslinkers. The authors should not use such broad language to describe results
from one experiment with one crosslinker.
We have rephrased to make clear that our statement only refers to Ase1.
"We found that all bim1 mutants were less well recruited to the metaphase spindle compared to the wild-type protein,
indicating that Bim1-interacting proteins strongly contribute to Bim1 localization." Can the authors rule out the defects in
localization of these mutants is not compromised MT binding by the Bim1 mutants? Also, regarding this statement: "To
test that the observed recruitment defects of bim1 mutants are not a result of a compromised spindle or microtubule
structure, we examined their localization in a situation when GFP-tagged mutants were covered with the unlabeled wildtype
allele. Indeed, in this situation, the Bim1 mutants displayed very similar localization profiles (Supplementary Figure
7B)." I wasn't sure what these results were similar to: the wild-type protein, or the mutant without the presence of WT
Bim1? The lack of quantitation made this difficult to determine.
At the request of reviewer 1, we have removed the analysis of Bim1-GFP mutants over an unlabelled Bim1 wild-type from the manuscript.
The zoom crops for many of the images (Fig 1F and C, 3D, 5J, etc) are not labeled. I realize the legends indicated
what was what, but it would be much easier for the reader if these panels were labeled in the figure.
We have indicated the channel by a respective frame around the zoom throughout the manuscript. We think this makes orientation easier.
"While in vitro reconstitution experiments have suggested that Bim1 is required to fully reconstitute the Kip2-
dependent loading of the Dynein-Dynactin complex to microtubule-plus ends in vitro (Roberts et al., 2014), our
experiments indicate that it may contribute relatively little to this pathway in cells." Work from other labs have also shown
Bim1 is dispensable for dynein function in cells. This should be noted by the authors, and the appropriate work cited (see
work from Lee and Pellman labs. In fact work from the Lee lab showed that Kip2 is dispensable for plus end binding of
dynein).
We have re-written this section and now also refer to the Markus 2009 paper (Wei-Lih Lee lab).
References are missing throughout the text. I have listed a few examples below:
"We have previously shown that the phenotype of Bim1-binding deficient Cik1 mutants can be rescued by fusing the
CH-domain to this Cik1 mutant (cik1-Δ74)."
We have listed the citation of our 2020 paper (Kornakov et al.)
"We constructed a series of strains expressing an extra copy of Ase1-GFP under different constitutive promoters of
increasing strength (p1 to p6)"; where did these promoters come from?
They were selected based on a systematic analysis of promoter strength in Shaw et al., 2019, DOI: 10.1016/j.cell.2019.02.023 . We have added that citation to the methods section.
"double point mutation exchanging two conserved residues in the EBH domain (bim1 Y220A E228A) is predicted to
eliminate all EBH-dependent cargo interactions, but does not affect protein dimerization."
We have cited the Honnapa 2009 paper here.
"A deletion of the terminal five amino acids is predicted to prevent binding of the CAP-Gly domain of Bik1 to Bim1. The
combination of both mutations is expected to simultaneously prevent both types of interaction."
We have cited the Stangier 2018 paper here.
"Spindle positioning in budding yeast is achieved via two pathways, one relying on the protein Kar9 which interacts
with the actin-based motor Myo2." Yin et al 2000 should be added (in addition to Hwang et al).
We have now included the Yin et al. 2000 citation.
"For nuclear migration to occur efficiently, the Dynein-Dynactin complex must be enriched at the plus-ends of
cytoplasmic microtubules..." Should cite work from the Lee lab here.
We now cite Markus and Lee, 2011 as an example.
"These long microtubules can interact with the bud cortex and initiate pulling events to move the nucleus (Omer et al.,
2018)." Many papers pre-dating the Omer study found this to the case, including work from the Cooper lab (see Adames
et al). These studies should be cited either in place of the Omer study, or in addition.
We have cited additional studies besides the Omer paper.
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Referee #2
Evidence, reproducibility and clarity
The authors of the study performed a systematic assessment of the role of Bim1 in the MT-binding activity and function of a large number of nuclear and cytoplasmic MT-associated proteins (MAPs), as well as their role during mitosis and spindle positioning. For example, they find that the reliance of MT-binding activity of several MAPs varies from complete reliance on Bim1, to almost no role (in some cases, loss of Bim1 even increases MAP-MT binding). The density and quality of the data, and the large number of players analyzed by the study, are certainly impressive, and there is no doubt a lot of valuable information contained within that will be of use to many people in the MAP/mitosis/yeast cell biology community. However, I feel the manuscript can be greatly improved following some significant revisions. In particular, although some of their findings are indeed interesting and useful, and can be used to reliably draw conclusions, it is difficult to parse out what is novel, and what is a rehashing of old data. For instance, the role of Bim1 in Bik1/Kip2 targeting was described years (Carvalho et al), and I was surprised to see that the CH-Cik1 fusion was previously described by the authors' lab a couple years ago (see note below regarding lack of appropriate citations and lack of description of previous knowledge). Also, how much did we already know about the Bim1 truncations shown in Figure 7 and S7, and how they might disrupt binding to partners? Finally, regarding this statement in the Discussion: "Our analysis indicates that Bim1 contributes to both of these processes as part of two key protein complexes (Figure 9A): Bim1-Kar9-Myo2 in the cytoplasm and Bim1- Bik1-Cik1-Kar3 in the nucleus." As far as I know, these things have been known for many years; their work might help to support these findings, but the statement as written misleads the readers in to believing the present work proves these old concepts.
One of the main issues with reading a manuscript with so much data about so many different players and pathways is that this leads to a situation in which each story is only superficially covered, with only minimal depth or detail. This made the paper somewhat difficult for me to follow (and I am a fan of budding yeast mitosis!), especially given the frequent switching from one pathway to another (e.g., the Cik1 section started on page 12 appears to be continued on page.17, only after talking about the spindle orientation story in between the two Cik1 sections). I'm not sure what to suggest, but the manuscript can be improved if the authors try to refocus some of the sections to make it easier to follow one story at a time, for a particular molecule (e.g., Cik1) or pathway (spindle orientation). In addition to explicitly describing what is already known about a particular molecule/pathway, the writing can be greatly improved by introducing their reasoning for the experiments in question. Some of the sections lack sufficient rationale for me to understand the justification for their experiments (e.g., why try to overexpress Ase1 to rescue bim1∆ phenotypes, as described on page 19?).
Although there is likely much to learn from this study, I felt that some conclusions were a little bold (see below), while alternative hypotheses were not addressed (perhaps Bim1 simply competes for MT binding with some of these factors, thus accounting for them increasing their spindle-binding behavior?). For example, the authors make a point that loss of Bim1 enhances dynein-dynactin function. However, it is important to note that mutations in tubulin (tub2-430∆) and other MAPs (Kar9 or Ase1, the latter of which the authors point out) also lead to increased dynein activity (see work by Yeh et al., 2000, and work from the Moore lab). It is unknown whether mutations to these genes affect dynein targeting in cells similar to what the authors describe here. Thus, a direct causal relationship between their bim1∆ phenotypes and enhanced dynein activity is unclear, and at best is speculative. It's also worth noting that overexpression of Bik1 has been shown to actually reduce Dhc1 localization to plus ends in cells (see Markus et al 2011), which would argues against a simple mechanism of increasing Bik1 correlating with increasing dynein localization and activity.
Below are some specific points.
- "Robustness of Ndc80 loading might be achieved by the coexistence of multiple kinetochore assembly pathways or alternatively determined by intrinsic Ndc80 properties." Wouldn't Ndc80 levels be determined by Ndc80 kinetochore loading, and not by end-binding proteins? This seems to be the more likely means to regulate Ndc80 levels.
- "Upon analyzing the associations in the cytoplasm, we found that Kar9-3xGFP foci on bud-directed cytoplasmic microtubules were abolished in the bim1Δ strain, consistent with earlier reports." It would be helpful if the authors commented on the how the localization of some of these proteins are affected by bim1∆ on the mother-directed plus ends. Although I understand the need to account for one class of plus end for the sake of consistency (and the distinct behaviors of the mother vs bud-directed plus end), the text as written leaves me wondering about the other plus end.
- "The CAP-Gly domain construct, expressed from a BIM1 promoter, almost exclusively localized to the spindle of yeast cells." For clarity, the authors should explicitly state that the CAP-Gly domain in question is from Bik1. Although this can be deduced, this was not abundantly clear.
- "In addition to Ase1, we followed the kinetochore proteins Ndc80-GFP and Sgo1-GFP which specifically marks kinetochores that lack tension." This sentence should add "the latter of which..." to clarify that SgoI, but not Ndc80 exhibits this behavior.
- "We observed that bim1Δ cells had mispositioned kinetochores with a bright Sgo1-GFP signal that was much stronger than in wild-type cells." I don't see the mispositioned kinetochores described here. Are the authors referring to the fact that Sgo1 is brighter, which suggests tension-free KTs? If so, this should be clearly stated as such, since the authors are not explicitly assessed kinetochore "positioning".
- "We speculate that Bim1-Bik1 in a complex with its cargo Cik1-Kar3 is active after bi-polar spindle formation but before late metaphase and Ase1 can partially substitute for nuclear Bim1 functions." I struggled to grasp the reasoning for these conclusions. I assume the former point (the timing for Bim1-Bik1-Cik-Kar3) is due to the localization dynamics of Bim1 and Bik1, while the latter (Ase1 can substitute for Bim1) is due to the synthetic interaction between Bim1 and Ase1 (I needed to look this latter point up myself). Or is this latter point due to the brighter spindle Ase1-GFP intensity? In either case, the authors should more clearly state their reasoning.
- The error bars in Figures 3A and 6E (shown as 95% CI) and elsewhere seem very small for the parameters that are being plotted. Spindle length values as shown in Figure 2E cover a broad range (as would be expected for a biological process), and it would be more accurate if the error bars in Fig 3A and 6E reflect this, even if it means they start overlapping each other. I find the error as shown to be misleading to your readers, and unless the authors have very good reason to use 95% CI (which is not as meaningful as standard deviation), then I would encourage them to use standard deviation.
- The same is true for the values stated throughout the text (e.g., for mitotic timing "47{plus minus}2 min" for metaphase duration; for distance between SPB and bud neck {plus minus} 0.1 µm, etc). I am highly skeptical that metaphase duration (for example) ranged from only 46-48 minutes. Please use standard deviation to describe a more accurate description of the range of values for these parameters.
- "Unexpectedly, the kar9 deletion mutant displayed a slightly accelerated metaphase progression relative to wild-type cells (26{plus minus}1 min) (Figure 3C). This could be attributed to an increased level of Bim1 on the metaphase spindle of kar9Δ (or Kar9-AID) cells." The authors should give us more rationale to explain the "attributing the increased levels of Bim1" point here. Do they think that the levels of spindle-associated Bim1 impact metaphase duration somehow? If so, how?
- "Overall, our cell biology data suggested that major nuclear Bim1 functions are conducted in a complex with Cik1- Kar3, while Bik1 and Kar9 have a smaller impact, probably affecting the nuclear- cytoplasmic distribution of Bim1." Although I understand and agree with the former conclusion (that Bim1 functions are conducted via Cik1-Kar3"), the latter was confusing to me. Did the authors mean that "Bim1 impacts Bik1 and Kar9 to a lesser extent", rather than vice versa? The authors are discussing Bim1 functioning via Cik1, but then switch to discussing how Bik1 and Kar9 affect Bim1.
- "Next, we compared the comparing genetic interaction profile of a bim1 deletion to that of various other factors by re-analyzing the synthetic genetic interaction data..." Remove "comparing".
- As someone who is unfamiliar with the analysis shown in Figure 3H, I think it would be useful to list a Pearson correlation value for two genes that are not functionally related. This would help define a lower limit for this analysis.
- The axes for the plots in Figure 5E and 5I are very confusing to me. I don't understand what I'm looking at. Why does it go from 0 to 1, and then back to 0-1 again? I don't see how this can account for MTs of different lengths. Normalizing all MT length values to 1 would do this, no?
- "These observations are consistent with the idea that Bik1 acts as a processivity factor for Kip2: If more Bik1 is present on the lattice, then more Kip2 molecules are able to reach plus-ends without detachment." Perhaps I'm misunderstanding the plot shown in Figure 5E, but it seems to indicate that the levels of lattice-bound Bik1 are the same in BIM1 and bim1∆ cells (higher SPB-localized levels, though). There are also lower levels of Bik1 at the plus ends in bim1∆ cells. So, if Bik1 were a processivity factor for Kip2, this would suggest that they would remain bound at plus ends as well, which these data suggest is not the case.
- "The data on the CH-Cik1 fusion is very compelling, and indeed supports their hypothesis that Bim1's main role in the nucleus is to target Cik1 to the spindle MT plus ends. That being said, it would be a simple, but important task to ensure that this fusion behaves as suggested (restores Cik1 plus end binding in cells). Otherwise, it can't' be ruled out that this fusion is rescuing bim1∆ functions by some other means. However, as stated above, it's unclear how much was already known about this fusion from the lab's previous work.
- Regarding the p1-p6 promoter data: p6 is missing from Figure S6A, in spite of it being referenced in the text and the figure.
- "Exogenously expressed Ase1 displayed a similar level and kinetics of localization compared to the endogenous protein, indicating that binding sites for microtubule crosslinkers are not a limiting factor on the budding yeast spindle." Specifically, the authors show that binding sites for Ase1 may not be limiting (the overlapping 95% CI bars if Fig S6B suggest this is not significant), not all crosslinkers. The authors should not use such broad language to describe results from one experiment with one crosslinker.
- "We found that all bim1 mutants were less well recruited to the metaphase spindle compared to the wild-type protein, indicating that Bim1-interacting proteins strongly contribute to Bim1 localization." Can the authors rule out the defects in localization of these mutants is not compromised MT binding by the Bim1 mutants? Also, regarding this statement: "To test that the observed recruitment defects of bim1 mutants are not a result of a compromised spindle or microtubule structure, we examined their localization in a situation when GFP-tagged mutants were covered with the unlabeled wild-type allele. Indeed, in this situation, the Bim1 mutants displayed very similar localization profiles (Supplementary Figure 7B)." I wasn't sure what these results were similar to: the wild-type protein, or the mutant without the presence of WT Bim1? The lack of quantitation made this difficult to determine.
- The zoom crops for many of the images (Fig 1F and C, 3D, 5J, etc) are not labeled. I realize the legends indicated what was what, but it would be much easier for the reader if these panels were labeled in the figure.
- "While in vitro reconstitution experiments have suggested that Bim1 is required to fully reconstitute the Kip2- dependent loading of the Dynein-Dynactin complex to microtubule-plus ends in vitro (Roberts et al., 2014), our experiments indicate that it may contribute relatively little to this pathway in cells." Work from other labs have also shown Bim1 is dispensable for dynein function in cells. This should be noted by the authors, and the appropriate work cited (see work from Lee and Pellman labs. In fact work from the Lee lab showed that Kip2 is dispensable for plus end binding of dynein).
- References are missing throughout the text. I have listed a few examples below:
- a. "We have previously shown that the phenotype of Bim1-binding deficient Cik1 mutants can be rescued by fusing the CH-domain to this Cik1 mutant (cik1-Δ74)."
- b. "We constructed a series of strains expressing an extra copy of Ase1-GFP under different constitutive promoters of increasing strength (p1 to p6)"; where did these promoters come from?
- c. "double point mutation exchanging two conserved residues in the EBH domain (bim1 Y220A E228A) is predicted to eliminate all EBH-dependent cargo interactions, but does not affect protein dimerization."
- d. "A deletion of the terminal five amino acids is predicted to prevent binding of the CAP-Gly domain of Bik1 to Bim1. The combination of both mutations is expected to simultaneously prevent both types of interaction."
- e. "Spindle positioning in budding yeast is achieved via two pathways, one relying on the protein Kar9 which interacts with the actin-based motor Myo2." Yin et al 2000 should be added (in addition to Hwang et al).
- f. "For nuclear migration to occur efficiently, the Dynein-Dynactin complex must be enriched at the plus-ends of cytoplasmic microtubules..." Should cite work from the Lee lab here.
- g. "These long microtubules can interact with the bud cortex and initiate pulling events to move the nucleus (Omer et al., 2018)." Many papers pre-dating the Omer study found this to the case, including work from the Cooper lab (see Adames et al). These studies should be cited either in place of the Omer study, or in addition.
Referees cross-commenting
It seems that one of my major concerns is reflected in Reviewer #1's review: that a lot of the findings described in the manuscript have been published elsewhere, and are not novel. In spite of this, I do think there are useful data in this manuscript that make this an important contribution, and that it should definitely be published. However, this would first require a significant re-writing with appropriate description of known vs unknown, and additional citations.
Significance
The current study aims to clarify the role of Bim1 (EB1 homolog in budding yeast) in the various pathways in which it has been implicated. To achieve this aim, the authors assess the localization of numerous other microtubule-associated proteins in cells with and without Bim1. In addition to high quality localization data (e.g., intensity values), the authors perform a number of cell biological assessments (e.g., mitotic spindle length values before, during and after anaphase), genetic assessments (synthetic interaction assays), and in vitro binding assays. The current study is indeed rich with new insights into the mechanisms by which these molecules function, and will no doubt prove valuable to a number of people in the microtubule/motor/yeast mitosis fields. As someone who is interested in and studies mitosis in budding yeast, I found the study to be interesting.
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Referee #1
Evidence, reproducibility and clarity
Kornakov and Westermann provide a comprehensive analysis of the functions of microtubule +end binding proteins (+TIPs) in budding yeast. Bim1 is the EB1 ortholog of budding yeast and serves as a scaffold for other +TIPs. As Bim1 is not essential for cell viability, the authors could use a deletion of Bim1 to evaluate the global loss of function of +TIP proteins on cellular processes involving microtubules in the nucleus and the cytoplasm. During mitosis Bim1 functions almost exclusively in two previously characterized complexes with different functions: 1. The Kar9-Bim1-Bik1 complex which mediates spindle positioning at the bud neck in metaphase and 2. The Kar3-Cik1-Bik1-Bim1 complex which functions in spindle assembly and spindle elongation. Much is already known about Bim1's function in spindle positioning e.g. =TIPs on cytoplasmic microtubules, but the authors provide new insights into Kar9-Bim1 co-dependence in localization to cytoplasmic microtubules and how in turn affects localization of Bik1 and Kip2, both of which act in the dynein dependent spindle positioning pathway. The role of Bim1 in spindle assembly has also been characterized previously. The authors show how Bim1 is required to recruit the kinesin-14 Cik1/Kar3 to mitotic spindles, which interactions are involved, and that spindle elongation is delayed in its absence. Unfortunately, there is considerable overlap between their results and the published literature, and the impact of their finding is therefore reduced. The strength of this manuscript lies in its comprehensive analysis of Bim1 function , the quality of the results and that the experiments are generally well controlled and interpreted.
Major points:
- There is already a huge body of published information on mitotic spindle positioning via the Kar9 and dynein pathways that grew since the late 1990s. The genetic relationships and molecular interactions between the components of these 2 pathways are well studied (many studies, including Liakopoulos et al. 2003, are not cited by the authors). The authors should make sure to cite and compare to the relevant primary literature when they report findings that have been described before. This will help to distinguish novel findings from validation of previous results.
- "The strict dependence of Kar9 and Cik1-Kar3 on the presence of Bim1, as well as the different effects of bim1Δ on nuclear and cytoplasmic Bik1, may reflect the formation of stable complexes between Bim1 and these binding partners in cells." I believe this has already been shown (Kumar et al., 2021 and Manatschal et al., 2016). There are several other instances as well where additional literature should be cited, for example Gardner et al., 2008 and Gardner et al. 2014.
- The selection of targets to study in figure 1 doesn't seem to follow the listed criteria. Many proteins included in the study were not found by IP-MS, but some perfect targets according to the listed criteria like Duo1 were not included in the study. In addition, there are more sophisticated ways of finding Bim1 binding motifs in the literature (https://doi.org/10.1016/j.cub.2012.07.047). I suggest, the authors declare that they rationally chose to study 21 proteins of interest but remove the claim that their approach was systematic.
- Much of the microscopy data was acquired after release from alpha factor arrest. What is the reason for this perturbation? An exponentially growing culture should mostly consist of mitotic cells anyway. Since this treatment affects cell size and potentially protein levels/concentrations, testing its influence on spindle position as well as levels on MTs for the most relevant proteins of interest would be important to exclude introduction of artifacts.
- Some of the results obtained from bim1Δ cells are a challenge to interpret due to the wide range of processes that involve Bim1 and therefor the potential for many off-target effects- including a global change in microtubule dynamical behavior in both the cytoplasm and the nucleus that will influence the length distributions and microtubule lifetime (and thus number). The authors must carefully consider these caveats.
Minor points:
- The results section on page 12 refers to phenotypes of kar9 delete cells with respect to Bim1-GFP on cytoplasmic microtubules. In the figure 3D,F I only found data for Kar9-AID, though. The authors should refer to supplementary figure 5A or even better include quantification similar to figure 3F.
- The observation that cytoplasmic Bim1 localization depends on interaction with its cargo Kar9 (figure 3 + 7) fits into the model that Kumar et al (https://doi.org/10.1016/j.str.2021.06.012) proposed in which Kar9 oligomerization is required for its Bim1 dependent localization to microtubules. It would be valuable to point that out.
- I don't fully understand the model proposed in Figure 5H and discussion page 26. Based on figure 5E, it does not look like there is a higher concentration of Bik1 along the lattice in bim1 delete. So how would Bik1 increase Kip2 processivity if its levels are only increased due to a MT length change? If Kip2 was not fully processive, you would rather expect to see less of it at the tip of a longer microtubule in bim1 delete. The model suggested by Chen et al (https://doi.org/10.7554/eLife.48627.001) suggests that Kip2 only gets loaded at the minus-end and processively walks towards the +end without falling off. Are the authors suggesting that bim1 deletion changes this behavior?
- I don't see evidence for independent pools of Bik1 in the cytoplasm and nucleus as claimed on top of page 21. Total Bik1 levels on cytoplasmic microtubules seem to be well explained by their length. Please explain better or remove the statement.
- The experiments in supplementary figure 7B are difficult to interpret. The localization on cytoplasmic microtubules is different, but probably explained by the formation of Bim1 heterodimers. Therefore this experiment is difficult to interpret and should be removed.
- top of page 24: Kar9 localization in metaphase depends exclusively on SxIP, not on LxxPTPh (Manatschal 2016). The paragraph should be removed as it is not supported by published data or sufficiently by the authors to merit the conclusion.
- Top of page 26: The genetic interactions between the Kar9 pathway and the dynein pathway were already well known before this work. Please reformulate accordingly.
- page 27 second paragraph: There is no selective pressure to evolve compensation mechanisms for gene deletions. I suggest the authors consider that Kar9 and dynein partially redundant, with Kar9 acting to position the spindle prior to metaphase and dynein to maintain spindle position in the mother and bud compartments in late metaphase and anaphase. The authors should consider the quantitative analysis of Kar9 and dynein dependent spindle positioning reported in Shulist et al. 2017 and the method for analysis of spindle length and position in 3D in Meziane et al. 2021.
- In addition, it is not clear to me which results suggest that the relocalization of Bik1 is required in the bim1 delete. Why would wild type levels not be sufficient for dynein pathway function? The authors have not conclusively shown that nuclear migration relies on upregulating the dynein pathway in bim1Δ cells. If there is no supporting data, the paragraph should be removed.
- Please provide more details about intensity quantification on page 35. Were these measured on sum or max projected stacks? What was the method of background subtraction?
- Are the spindle lengths in Figure 2E measured in 2D or 3D? Bim1 deletion might lead to more misalignment of the spindles in z due to inactivation of the Kar9 pathway and thus partially explain the shorter spindles. The measurements should therefore be performed in 3D.
- The authors should try to shorten the text. There is a lot of redundancy between results and discussion sections.
- Data is shown that leads to conclusions that are already supported by the literature should be moved to the supplementary material.
Referees cross-commenting
I am in agreement with reviewer 2
Significance
The role of Bim1 in the Kar9 spindle positioning pathway and in recruiting Kar3/Cik1 to spindles have been extensively characterized in previous publications, however this manuscript adds mechanistic insight into what interactions are essential for localization, what happens to other proteins that have not previously been studied in the context of Bim1 and what are the exact consequences of Bim1 loss with some explanation for the outcomes. Some data presented here was expected from previous work, but never experimentally confirmed and these findings should be the focus of the manuscript. While the manuscript does not provide a huge conceptual advancement, the findings of this comprehensive analysis are of great value to the microtubule field, especially for people working in budding yeast.
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Reply to the reviewers
We would like to thank the reviewers for their thorough and positive assessment of our work. We also thank them for their careful review of our manuscript. Our responses to their specific comments are provided in the lines below.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary:
The manuscript entitled „Metastatic potential in clonal melanoma cells is driven by a rare, early-invading subpopulation" by Kaur and colleagues provides a phenotypical analysis of the invasive potential of established melanoma cell lines on single cell level. The aim of the study was to answer the question if even homologous tumor cells bear the intrinsic potential to give rise to cells with high invasive (and therefore potentially metastatic) capacity in absence of selection pressure from the tumor microenvironment.
The authors used clones from two different melanoma cell lines (to prevent the accumulation of random (epi)genetic changes during cultivation) and performed invasion assays with Matrigel-coated transwell inlays to differentiate between cells that were able to invade early (up to 8 h, approx. 1% of the total cell population) or late (8-24 h; approx. 3% of the total cell population) after plating. Comparative RNA sequencing of early invaders and non-invaders populations revealed a high expression of SEMA3C in early invaders, which was then established as marker in the used cell lines. Interestingly, in vivo models using NSG mice injected with a mixture of early and late invading melanoma cells revealed that both contributed similarly to the primary tumor, while metastatic cells in the lung consisted almost exclusively of early invaders. Subsequent ATAC sequencing revealed an increase of binding sites for the transcription factor NKX2.2 in the early invaders. Functional analyses revealed that a knockout of NKX2.2. led to an increase in both invasion and proliferation. Finally, the authors showed with different sorted early and late invaders as well as SEMA3Chigh and SEMA3Clow expressers that pro-invasive features go along with reduced proliferation potential in accordance to previously published data. However, they decrease with time, thus demonstrating a reversion of the phenotype and high plasticity.
Major comments:
In general, the paper contains novel and interesting data, is concisely written and supported by replicates. The key conclusion, the presence of a small proportion of highly invasive cells in a seemingly homologous cell population and their striking requirement for lung metastasis, is very convincing. In vitro, SEMA3C was confirmed as a marker for the early invaders in two independent cell lines. However, a few questions remain open, as detailed below:
We thank the reviewer for their positive assessment of our work. We also thank them for their careful review of our manuscript. Our responses to their specific comments are provided in the lines below.
1) The relevance of NKX2.2 in the early invaders is currently unclear to me.
The ATAC sequencing data revealed a high enrichment of accessible NKX2.2 binding sites in early invaders, and data were tested by comparative RNA sequencing of control cells and cells with NKX2.2 ko (Figure 2). The Figure legend of Figure 2 says: "NKX2.2 is a transcription factor that promotes the invasive subpopulation", but the data don`t support this (ko leads to reduced invasion). Accordingly, the authors also state in the Results part "... the direction of the effect is the opposite of what one might have expected".
To set the role of NKX2.2 into context, it would be useful to confirm the actual involvement of NFX2.2 in the invasive phenotype and clarify if NFX2.2. might probably even suppress some pro-invasive genes. I would advise to investigate the protein levels and/or protein localization of NFX2.2 and probably perform ChIp experiments on selected pro-invasive genes that play a role in the early invaders.
The reviewer has raised some excellent points about our studies of NKX2.2 and its role in invasion. Indeed, we were also surprised by the fact that NKX2.2 had the opposite effect as expected (its peaks are enriched for accessibility in the early invaders in FS4, but knockout leads to increased invasion). We elected to include the results because it was a hypothesis we tested, so in the interest of full disclosure of results, we chose to leave the result in.
The reviewer has also made some nice suggestions about how to further explore the role of NKX2.2 in regulation (e.g. ChIP-seq). Owing to the complexity of validating and performing this assay, we felt these experiments were beyond the scope of the current manuscript; we hope to explore these possibilities more fully in the future.
Another excellent suggestion the reviewer made was to look at the regulatory capacity of NKX2.2 to directly demonstrate the link between NKX2.2 regulation and expression differences between early- and late-invading cells. In order to establish this connection, we used a gene set from molecular signatures database (MSigDB: https://www.gsea-msigdb.org/gsea/msigdb/human/geneset/NKX2_2_TARGET_GENES.html) consisting of genes with an NKX2.2 binding site within their promoter (TSS -1000 bp to TSS +100 bp) identified by the gene transcription regulation database (GTRD–paper here: https://pubmed.ncbi.nlm.nih.gov/33231677/). We used the Fisher’s exact test to see if the overlap between these genes regulated by NKX2.2 and genes that are differentially expressed between early-invading cells versus their respective parental population in both cell lines had more overlap than one would expect by chance. Indeed, the p-values using this approach were 3.937e-16 and 0.037 for the FS4 and 1205Lu cell lines, respectively. These results, combined with the motif analysis with our ATAC-seq data, demonstrated that the activity of NKX2.2 is relevant in the early-invading state. We thank the reviewer for the suggestion and feel this additional analysis has improved our conclusions about NKX2.2.
Also, we further checked whether NKX2.2 levels correlated in early versus late invading cells across a panel of cell lines (Fig. 2C). We found that in 4/6 of these lines, NKX2.2 expression was higher in the early invaders. These results further support the case that NKX2.2 is an important positive regulator of invasion in multiple contexts.
“In order to establish the generality of our results, we measured NKX2.2 expression levels across multiple cell lines by single molecule mRNA FISH. We found that the early invaders had higher levels of NKX2.2 expression in four out of the 6 lines tested (Fig. 2C), demonstrating the generality of our results and strengthening the case that NKX2.2 is a potential regulator of early invasiveness. The role of NKX2.2 as a regulator of early invasiveness was further established through comparative analysis between genes with NKX2.2 promoter region binding sites (-1000 bp to +100 bp relative to the transcription start site (TSS) as annotated by the Gene Transcription Regulation Database (GTRD)) and genes differentially expressed in early-invading and parental cells. Analysis using Fisher's exact test revealed a significant overlap between GTRD annotated genes regulated by NKX2.2 and genes expressed in FS4 (****p=3.937e-16) and 1205Lu (*p=0.037) early-invading cells. These results, in complement with our results from ATAC-sequencing motif analysis, further supported the relevance of NKX2.2 regulation in the early-invading state.”
2) The sequencing data are currently accessible via a Dropbox link. They should be deposited instead in a data repository.
We thank the reviewer for noting this problem. We have uploaded all data to the SRA/GEO at the following links:
https://urldefense.com/v3/https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE224772;!!IBzWLUs!SEr5DTViPf08-IBQnv0ml-CoLX3cbaiNlCz-DJbpIKm7UcVXlL9-OD9reVQJs5pm_gzeqJYC_dM-MV8DonwX4c4$
https://urldefense.com/v3/https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE224769;!!IBzWLUs!SEr5DTViPf08-IBQnv0ml-CoLX3cbaiNlCz-DJbpIKm7UcVXlL9-OD9reVQJs5pm_gzeqJYC_dM-MV8DtY6ZB3A$
https://urldefense.com/v3/https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE224771;!!IBzWLUs!SEr5DTViPf08-IBQnv0ml-CoLX3cbaiNlCz-DJbpIKm7UcVXlL9-OD9reVQJs5pm_gzeqJYC_dM-MV8Dq_3ghAU$
Minor comments:
1) The cell line used for Supplementary Figure 4 should be named in the figure legend.
We thank the reviewer for the suggestion. We have included the name of the cell line in the figure legend for Supplementary Figure 4. The text reads as follows:
“A. FS4 melanoma cells were sorted based on SEMA3C expression. Cells were live-imaged for ~10 days every hour and single cells were tracked manually for cell position, cell division and lineage. Lineages were traced manually from single cells. Cell speed was calculated for each cell using the average distance traveled over time.”
2) In Figures 4H-M and Supplementary Figure 4D-I, the authors describe data performed in "sister" and "cousin" cells. It would be useful to provide a definition for both in the main text or figure legend.
This is a very good point. We have provided the following definitions in the main text, and have changed the wording from “sister” to “sibling” to avoid gendered terminology:
“(sibling cells are defined as those that share a common parent cell, and cousin cells are defined as those that share a common grandparent.)”
3) Discussion: "This lack of permanence may reflect the fact that the invasive cells are not subjected to stress-in our case, cells merely pass through a transwell, which may be the reason for the "burning in" of the phenotype in the case of resistance."
This sentence is misleading - please clarify.
We apologize for the confusion caused by this sentence. We have now changed it to the following:
“It is interesting that the early-invading cells eventually revert to the population average even after going through the transwell. Such a result contrasts with our previous work (Shaffer et al., 2017b), in which a rare subpopulation became permanently therapy resistant and did not revert even after several weeks off-treatment. One possibility is that the stress of undergoing therapy treatment induces a transcriptional rewiring, and this rewiring is not induced by the migration through transwells. Further studies will be required to test these hypotheses.”
Furthermore, there are some errors in the reference to the Figures throughout the paper. These which should be corrected:
We thank the reviewer for their detailed reading and finding these issues. We have now fixed them all in our revised manuscript.
4) Results, section "NKX2.2 is a transcription factor that promotes the invasive subpopulation".
Here the authors write: "...we performed RNA sequencing on the NKX2.2 knockout cells and compared the effects on gene expression to the gene expression differences between early vs. non- invaders across the two cell lines." This sentence should contain the reference to Supplementary Figure 3B-D (which is otherwise not referred to).
We thank the reviewer for their detailed reading and noticing this issue. We have now referenced Supplementary Figure 3B-D in the text cited above.
5) Results: "Overexpression of SEMA3C in FS4 cells revealed no changes in invasiveness, suggesting that SEMA3C is a marker with no functional relevance to invasiveness per se; Fig. 1D, Fig. 2A-B)"
The correct reference should be: Suppl. Fig. 1D, Fig. 2A-B. Also, in the current manuscript version the authors jump from Figures 1 to Figure 2 A,B, before coming back to Figure 1. To avoid this, I would advise to shift the current Figure 2A, B to Figure 1 or the supplementary information.
We thank the reviewer for pointing out this error in the reference to these figures. Figure 2A-B is now referenced as “Supp. Fig. 1 E-F”. The figure legend has also been updated.
6) Results: "We then sampled lungs from mice at various times post-injection to look for metastatic cells (Fig.1F, Suppl. Fig. 2B,C)."
As Supplementary Figure 2B, C does not show metastasis, but rather primary tumor growth, I would advise the following wording: "We then sampled lungs from mice at various times post-injection to look for metastatic cells (Fig.1F) and overall tumor growth (Suppl. Fig. 2B,C)."
We thank the reviewer for their advice to reword the sentence cited above. We have now edited the text to read as suggested by the reviewer. In addition, Supp. Fig. 2B,C is not referenced as Supp. Fig. 2C,D.
"We then sampled lungs from mice at various times post-injection to look for metastatic cells (Fig.1F) and overall tumor growth (Supp. Fig. 2C,D)."
7) Results: "Interestingly, NKX2.2 knockout cells showed markedly increased invasion and proliferation (Fig. 2A,B), suggesting a change in regulation of both processes. "
The correct reference is Fig. 2C, D.
The reviewer is right that we only have results in one cell line, and fully agree that the results in FS4 are only correlative. We have now weakened the language in the abstract and the results to emphasize that this result held in 1205Lu cells only.
- Given the robust literature regarding phenotypic switching in melanoma, the NKX2.2 knockout increasing both invasiveness and proliferation (figures 2C, 2D) suggests it may not be involved in phenotype switching. Perhaps NKX2.2 is a negative regulator of cell activity/metabolism. We thank the reviewer for highlighting the possible connections with metabolism. To explore this possibility , we performed metabolic assays on NKX2.2 knockout and AAVS control cells and observed no significant changes in Extracellular acidification rate (B). We did observe some differences in oxygen consumption rate in the cells (A), but the differences do not seem to be large enough or systematic enough to be meaningful given the variation within the controls. We have now included these results in Supp. Fig. 3E-F.
Note, the data previously referenced as Figure 2C,D is now in Figure 2A,B.
“NKX2.2 is a transcriptional repressor and activator essential for the differentiation of pancreatic endocrine cells (Habener et al., 2005). In mice, deletion of NKX2.2 prevents the specification of pancreatic islet cells resulting in the replacement of insulin-expressing β cells and glucagon-expressing α cells with ghrelin-expressing cells; This lack of specification resulted in mortality of newborn mice due to hyperglycemia (Sussel et al. 1998; Prado et al. 2004). Given the link of NKX2.2 with glucose metabolism, we wondered whether NKX2.2 had an effect on metabolic activity prompting us to test the NKX2.2 knockout lines for metabolic differences in the oxygen consumption rate (OCR; an indicator of oxidative phosphorylation) and the extracellular acidification rate (ECAR; an indicator of glycolysis) of the cells. Seahorse assay analysis revealed no systematic differences in metabolic activity (Supp. Fig. 3E,F).”
We thank the reviewer for the correction. The reference has now been corrected in the main text.
Reviewer #1 (Significance (Required)):
Nature and significance of the advance/ literature context:
In their manuscript, the authors provide interesting biological data about the presence of intrinsically and reversibly pro-invasive / pro-metastatic melanoma cells in a seemingly homogenous subpopulation. With SEMA3C, they also provide a marker for early invading cells, which might be useful in future studies to identify therapeutic vulnerabilities for this subgroup. This study sheds further light on the functional effects of phenotypic plasticity, which was previously described particularly in the context of therapy resistance, as mentioned by the authors.
We thank the reviewer for their kind assessment of the impact of our work.
Audience:
The study is interesting for scientists from the melanoma field as well as the cancer metastasis field in general.
Own expertise:
Melanoma, phenotypic switch, metabolism, signal transduction, stress response
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Metastatic potential in clonal melanoma cells is driven by a rare, early-invading subpopulation
Kaur et al.
In this manuscript the authors highlight a small subpopulation of "early-invading" melanoma cells and functionally characterize the nuances of these early cells compared to their slowly invading counterparts. A cell surface marker, SEMA3C and the transcription factor NKX2.2 were associated with differences in the invasive rates. Importantly, the group demonstrates that existence of the invasive subpopulation is not reliant on genetic changes, and thus exhibits plasticity. While the underlying concept surrounding this paper (phenotypic plasticity) is not novel, highlighting a surface marker and transcription factor that may, at least in part, be associated with phenotype plasticity is interesting. However, the current study seems underdeveloped. Specific points of concern are listed:
Major
- Only two cell lines are used throughout this study. We thank the reviewer for pointing out the need for more cell lines. We have now added two new cell lines to our study, WM793 and WM1799, both of which recapitulate the fundamental phenomenology in question. Although we did not show it in our initial submission, we had originally queried a panel of melanoma cell lines in order to determine their suitability for our study (from which we settled on 1205Lu and FS4). This panel has multiple melanoma cell lines obtained from a variety of melanoma tumor samples from Radial Growth Phase (RGP), Vertical Growth Phase (VGP), and metastatic tissues. We now have included these data in our revised manuscript, since they further support our point.
“We tested a panel of different melanoma cell lines from Radial Growth Phase (RGP), Vertical Growth Phase (VGP), and metastatic tumor types for the existence of fast invading subpopulations. We used four patient-derived melanoma cell lines, FS4, 1205Lu, WM1799, WM793, all of which have BRAF mutations (V600K for FS4, V600E for 1205Lu, WM1799, and WM793) and are known to be highly invasive in vitro and in vivo (27). Out of the 11 melanoma cell lines tested, the FS4 (not shown) and 1205lu cell lines displayed the highest levels of fast invading subpopulations (Supp. Fig. 1A).”
First, we showed that they all have an invasive subpopulation, with 1205Lu and FS4 (not shown) having the most invasive cells. Second, validating a central claim of the manuscript, we showed that many of these cell lines, including WM1799 and WM793, showed much higher levels of both SEMA3C (4/6) and NKX2.2 (4/6) expression in the early invading population as compared to the late invading population.
Together, these data make a strong case that our findings generalize across multiple cell lines, including RGP and VGP models. We have incorporated new text that reads as follows:
“In order to establish the generality of our results, we measured expression of the surface marker SEMA3C across the early and late invading subpopulations of a panel of melanoma cell lines. We found that SEMA3C levels were higher in the early invading subpopulation in 4 of the 6 lines tested (Supp. Fig. 1H). Thus, these results held across a variety of cell lines and, thus, were not a unique feature of a particular patient sample.”
- The in vivo metastasis assay in figure 1 is difficult to interpret and presents a number of concerns. 1) Only ~50% of early invading cells were labeled with GFP, this confounds many aspects of the experiment. The authors comment that in the primary tumor, as expected "...a roughly equal mix of human melanoma cells that were GFP positive and negative." If there was an expectation of equal proliferative rates in the primary tumor of early and late invading cells, given that only 1/2 of the early cells were GFP+, wouldn't we expect only 25% of the human cells to be GFP+?
The reviewer has raised a very important quantitative question about our experiments, which we have now addressed with a more thorough set of analyses. Initially, we quantified GFP positivity post -transduction by looking at fluorescent protein levels, for which the threshold was fairly arbitrary, and potentially could have miscounted many GFP positive cells as GFP negative due to low but non-zero levels of expression. We hence recalculated our positivity rate based on single molecule RNA FISH for GFP and mCherry, given that the technique is sensitive down to even veryl ow levels of expression.
As can be seen in Supp. Fig. 2B, the vast majority of transduced cells did indeed get the transgene and had some level of expression of GFP/mCherry. At a threshold of 5/10 molecules (GFP/mCherry, respectively), we obtained 88% and 96.15% positivity rates for GFP and mCherry, respectively. At these rates of positivity, we would expect much closer to 50% of the cells being GFP positive in the tumors, as observed. We thank the reviewer for noticing this discrepancy, and feel that our new analysis clears up the confusion and strengthens our results. These results are described in the main text as follows:
“We labeled the cells with sufficient virus so that 88% of the early invaders were labeled with GFP and 96.15% of the late invaders were labeled with mCherry (Supp. Fig. 2B). We then sampled lungs from mice at various times post-injection to look for metastatic cells (Fig.1F) and overall tumor growth (Supp. Fig. 2C,D).”
2) The authors note technical difficulties in detecting mCherry in sections. It seems as though this forced them to use a RNA FISH probe to identify human vs. mouse and by extension/negative selection the human FISH positive, GPF negative cell represented a mCherry stained late-invading cell. This is not ideal and seems over complicated. If the population of interest was engineered to express mCherry, why not directly probe for mCherry?
The reviewer has raised an important point about our experimental design. Indeed, we attempted multiple times and in multiple ways to detect mCherry protein directly. We tried multiple times with multiple antibodies, but the signal was simply not detectable. Hence, we arrived at the experimental design we outlined. We felt that a fully transparent disclosure of the issues was preferable, even if it did make the design sound overly complex. We will note that our primary result—that the vast majority of the metastatic cells are GFP positive and hence derived from fast invaders—is robust to any detection issues for mCherry.
3) Given the poor initial labeling/transduction of the early invaders, how can the authors be confident that all human cells without GFP signal are late invaders?
The reviewer raises a great point that is addressed by our GFP and mCherry RNA FISH analysis above, showing that the transduction efficiency was actually quite a bit higher than initially thought due to low but non-zero GFP signal being counted as GFP negative. With the much higher transduction efficiencies we have now validated, we believe that the vast majority of human cells with no GFP signal should be late invaders.
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The authors may have missed an opportunity to study FS4 clone F6 and 1205 clone E11. What is the SEMA3C and NKX2.2 status of these clones? Are they able to revert expressions? The reviewer has pointed out an interesting opportunity for further exploration. Unfortunately, because they were identified as part of an initial screening study, those particular clones were not kept for subsequent analysis. However, in our revised manuscript, we have now worked up multiple additional cell lines (WM1799 and WM793), both of which had high expression levels of both SEMA3C (Supp. Fig. 1H, shown above) and NKX2.2 (Fig. 2C) in the early invading subpopulation. Currently, we do not have data on reversion experiments for these two cell lines, but we would expect them to behave similarly to the other cell lines we examined in this study.
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The lack of statistical analysis/comparisons throughout the paper needs to be addressed. We thank the reviewer for pointing out these deficiencies. We have now added statistical comparisons throughout.
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In figures 1E and 3B, why do the parental (homogenous) cells demonstrate less invasiveness than the selected for the SEMA3C low or "late-invaders" respectively? This is an important point that the reviewer has raised. The finding did occur in every replicate, so we assume it is biologically and not statistical. We have now included the following language in the discussion noting the issue and some possible explanations.
“It is worth noting that, while the SEMA3C-high (early-invading) subpopulation drove the highly invasive phenotype, the SEMA3C-low (late-invading) subpopulation also displayed a somewhat more invasive phenotype than the parental population. It is unclear what the underlying cause of this difference in invasive behavior is between the SEMA3C-low and parental populations. One possibility is that paracrine signaling between cells in the parental population confers them with less invasive potential than when the cells are isolated into early- and late-invading subpopulations. Another possibility is that technical factors associated with the sorting of SEMA3C-low cells from the parental population alter their invasive properties, thus making them distinct from the parental population.”
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Conclusions that NKX2.2 knockout increases invasiveness and proliferation are based on 1 cell line. The comparisons done with FS4 early and late invading cells in Figure 1F may be supportive but is correlative in nature. The reviewer is right that we only have results in one cell line, and fully agree that the results in FS4 are only correlative. We have now weakened the language in the abstract and the results to emphasize that this result held in 1205Lu cells only.
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Given the robust literature regarding phenotypic switching in melanoma, the NKX2.2 knockout increasing both invasiveness and proliferation (figures 2C, 2D) suggests it may not be involved in phenotype switching. Perhaps NKX2.2 is a negative regulator of cell activity/metabolism. We thank the reviewer for highlighting the possible connections with metabolism. To explore this possibility , we performed metabolic assays on NKX2.2 knockout and AAVS control cells and observed no significant changes in Extracellular acidification rate (B). We did observe some differences in oxygen consumption rate in the cells (A), but the differences do not seem to be large enough or systematic enough to be meaningful given the variation within the controls. We have now included these results in Supp. Fig. 3E-F.
Note, the data previously referenced as Figure 2C,D is now in Figure 2A,B.
“NKX2.2 is a transcriptional repressor and activator essential for the differentiation of pancreatic endocrine cells (Habener et al., 2005). In mice, deletion of NKX2.2 prevents the specification of pancreatic islet cells resulting in the replacement of insulin-expressing β cells and glucagon-expressing α cells with ghrelin-expressing cells; This lack of specification resulted in mortality of newborn mice due to hyperglycemia (Sussel et al. 1998; Prado et al. 2004). Given the link of NKX2.2 with glucose metabolism, we wondered whether NKX2.2 had an effect on metabolic activity prompting us to test the NKX2.2 knockout lines for metabolic differences in the oxygen consumption rate (OCR; an indicator of oxidative phosphorylation) and the extracellular acidification rate (ECAR; an indicator of glycolysis) of the cells. Seahorse assay analysis revealed no systematic differences in metabolic activity (Supp. Fig. 3E,F).”
- Given that sorted SEMA3C high levels did not revert to parental FS4 levels, yet the invasive phenotype reverted to parental-like behavior undermines the usefulness of SEMA3C as a marker of invasiveness. The reviewer has brought up an important point. We were able to show that 1205Lu cells had SEMA3C levels revert to those of the parental. The reviewer is right that FS4 did not, which may be because it takes longer for FS4 to revert. It is true that the phenotypic behavior did revert. We have seen similar things in our therapy resistance work (Shaffer et al. 2017, etc.). One possible reason is that the phenotype is governed by multiple factors, and so the phenotype can revert before the expression of SEMA3C. We still think that SEMA3C is a good marker, just perhaps context dependent. We have added text to the discussion to make these important points.
“We note that SEMA3C levels in FS4-SEMA3C-high cells did not revert to the parental levels within two weeks. This incomplete reversion may be because SEMA3C takes longer to revert than the tested time period. Interestingly, the invasive phenotype did revert in this time period, suggesting that there may be multiple factors associated with the phenotype beyond SEMA3C. It may thus be that SEMA3C is a marker of the early-invading population, but only in certain contexts.”
Minor
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How does SEMA3C and/or NKX2.2 expression (here 1.5% of FS4 cells were noted as "SEMA3C high") of metastatic cell lines (FS4 and 1205) compare to RGP and VGP cell lines? The reviewer has asked a great question about radial and vertical growth phase cells. We have tested several other cell lines to determine cell lines that were suitable for transwell assays. We have now included two figures (Supp. Fig. 1H and Fig. 2C) showing the SEMA3C and NKX2.2 status of each of these cell lines (parental cells) and their different subpopulations (early invaders and late invaders)—see also Reviewer #2, Major point 1. We found that the same pattern of SEMA3C-high cells held for both RGP and VGP cell lines.
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There were a number of instances throughout the manuscript that were not clear, colloquial, or simply unnecessary - i.e. description of transwell assay. The reviewer has raised a good point about our language. We have gone through and tried to improve the clarity and precision. As for descriptions of the various assays, we have found that some readers of our papers are unfamiliar with these assays, so we elected to keep those descriptions in. We hope the reviewer does not object too strenuously.
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The authors only analyze/mention lung metastases. Were metastases observed at other sites? The reviewer has posed a very good question about whether metastasis occurred at other locations. We stained additional tissues (liver and kidney) that were collected from the same mice and stained as per our lung invasion assays. As shown in our new Supplemental Fig. 2E, we found a similar pattern with the vast majority of metastatic cells being GFP positive; i.e., early-invaders, just as was the case for lung. We thank the reviewer for this helpful suggestion.
“In the lung, however, we saw predominantly GFP-positive cells, showing that the vast majority of cells that migrated from the primary tumor site were initially early invading cells (Fig. 1I,J). The number of GFP cells in the lung was variable, but generally increased with time. The liver and kidney also showed an enrichment of GFP-positive cells (early invaders), suggesting that the metastatic potential of these cells is not limited to any one particular metastatic location (Supp. Fig. 2E). Thus, we established that the highly invasive subpopulation was able to drive metastasis in vivo.”
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What is PE indicating in Figure 1D? Apologies, PE refers to the channel we used for the sorting on the FACS machine and stands for “Phycoerythrin”. To avoid any confusion, we have omitted the “PE” text on the y-axis of Fig. 1D.
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The number of invaded cells seems to vary quite a bit between experiments - Parental 1205 cells in Fig 2C = ~200, yet 1205 clone F6 and the non-clonal 1205 cell line demonstrate ~10,000. Similar differences observed with Fs4 cells - Parental Fig 1E vs. Empty control Figure 2A. The reviewer has a good eye—indeed, there is a wide variability in the amount of invading cells. We have now remarked on this variability in the results section:
“We note that the number of invading cells varied significantly between experiments. This variability is due to the fact that we employed transwell dishes with different growth areas, ranging from 0.33 cm2 to 4.67 cm2, leading us to collect different cell numbers for individual experiments. The cell density per cm2, however, was kept constant between experiments.”
Note that Figure 2C and Figure 2A are now referenced as Figure 2A and Supplemental Figure 1F, respectively .
Reviewer #2 (Significance (Required)):
This work contributes to the growing fields of phenotypic plasticity and intratumoral heterogeneity. The authors claim to have identified a surface marker SEMA3C and a transcription factor NKX2.2 that may play a role in driving invasive proclivity. Importantly, the group demonstrates that changes in these proteins are not genetic, and therefore represent "intrinsic differences" that are a property of the tumor. Furthermore, the authors indicate how the present observations of early invading cells parallels drug resistance phenomena as their previous works highlights intrinsically resistant subpopulations (Shaffer et al., Nature 2017, Torre et al., Nature Genetics 2021 and others.). Taken together, the current and previous work underscores the importance of cell to cell non-genetic variability in disease progression and response to therapy.
We thank the reviewer for their kind comments on the significance of our manuscript.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In this study, Kaur et al. intended to use similar strategy that the same group had developed (https://www.nature.com/articles/nature22794) to identify the subpopulation in melanoma responsible for metastasis. In brief, the melanoma cell population was subjected to the selection of a specific phenotype (transwell migration dubbed as "invasiveness" behavior). By comparing the early and late invaders, a cell maker was identified to allow distinguishing the high-invasive subpopulation. A series of experiments were devised to validate the metastatic function of the high-invasive cells and delineate the signaling that drove this phenotype. The authors concluded that this rare subpopulation was originated from transcriptional fluctuation, and invasiveness is a trade-off of cell growth. Therefore, as the cells growing, overtime the phenotype was reverted to low invasiveness.
Consistency is the most important factor for evaluating observation over temporal and spatial range. Therefore, several controls need to be clarified before further investigation in mechanisms:
1) If the rare invader cells are arising from gene expression fluctuation, the SEMA3C-low population of parental line should generate SEMA3C-high invader subpopulation over time. This should be addressed.
The reviewer has made an excellent point. Indeed, it is the case that the SEMA3C-low population starts to regenerate the high invader subpopulation over time. We have re-graphed Figure 3D to demonstrate this fact more clearly (See Supplemental Fig. 5A,B), showing that the SEMA3C low population regenerates many more SEMA-3C high cells after 14 days.
2) Both early and late invader cells exhibited higher invasiveness than the parental line (Fig. 3B). Therefore, the in vivo metastatic potential of the three lines should be compared to validate the role of the invader cells in the metastatic function.
We thank the reviewer for their comment about testing all three populations in the in vivo context. It is an excellent suggestion, but in order to fully control the experiment, we would need to add all three populations in three separate colors. Given the difficulties we had with getting even the two colors to work together, we think it is beyond the scope of our current efforts to attempt this complex experiment. We have added the following caveat to the text:
“For unknown reasons, the parental population consistently showed lower invasiveness than the early- and late-invading subpopulations. Given that we did not test the parental population for invasiveness in vivo, future studies may address the sources and mechanisms by which the parental population differs and how those differences manifest in vivo.”
3) To evaluate the possible intervention of cellular function by fluorescent proteins (https://doi.org/10.1016/j.ccell.2022.01.015), admix of GFP- and mCherry-labeled populations of early invader cells should be used as a control in Fig. 1F. Noticeably, the labeling ratio of the two populations was not even in Fig. 1F.
The reviewer has brought up an important point about the potential differences brought about by the fluorescent proteins themselves. At this point, it is difficult to redo these complex in vivo experiments, but we can appeal to the fact that the admixture is maintained throughout time as the primary tumor site still has a roughly equal ratio of GFP and mCherry cells in it (Fig. 1I and Supp. Fig. 2E).
4) When the invader cells were expanded and passed, their invasiveness will revert to the level similar to parental line in 14 days (Fig. 3B). The isolated cells were expanded for further testing and manipulation in Fig. 1C and 1F, respectively. How long did was the period for cell expansion in these experiments?
We thank the reviewer for bringing up an important question about the details of cell expansion. For the RNA-seq, the cells were directly processed upon going through the transwell, so there was no expansion period. We have made sure to outline this more carefully in our methods section (see below).
“RNA sequencing and analysis:
RNA collection and library prep: Each treatment/sample was tested in 3 separate biological replicates. Upon passing through the transwell, cells were immediately collected and processed for RNA sequencing. Total RNA isolation was performed using the phenol-chloroform extraction followed by RNA cleanup using RNAeasy Micro (Qiagen 74004) kit. For transwell assays, library preparation was performed using Nebnext single-cell/low input RNA library prep kit (E6420L, NEB). For NKX2.2 CRISPR experiments, library preparation was done using NEBNext Poly(A) mRNA Magnetic Isolation Module (NEB E7490L) integrated with NEBNext Ultra II RNA Library Prep Kit for Illumina (NEB E7770L).
Mouse tumor implantation and growth:
All mouse experiments were conducted in collaboration with Dr. Meenhard Herlyn at The Wistar Institute, Philadelphia, PA. NSG mice (NOD.Cg-Prkdcscid Il2rgtm1Wjl/SzJ) were bred in-house at The Wistar Institute Animal Facility. All experiments were performed under approval from the Wistar Institute Care and Use Committee (protocol 201174). As in the case of RNA sequencing experiments, cells were not expanded prior to injection into the mouse, but were collected and implanted right after passing through the transwell. 50,000 melanoma cells were suspended in DMEM with 10% FBS and injected subcutaneously in the left flank of the mouse.”
5) If invasiveness and growth are trade-off, why did the mCherry-labeled cells not dominate the population of primary tumors in Fig. 1J?
Note that Figure 1J is now referenced as Figure 1I. The reviewer brings up a good point. For potential explanations, first, the difference in growth rate is not large, so we would not necessarily expect mCherry cells to dominate on this timescale. Also, we believe that in vivo, the tradeoff may be mitigated by other factors and cell-cell interactions that are not present in vitro. We have added a note on this point to the results.
“(Note that these numbers were similar despite the slightly increased growth rate of the late-invading subpopulation; we assume this is due to the relatively small difference and cell-cell interactions that could prevent one population from dominating the other.)”
6) In Fig. 1G, why RNA FISH was not used to detect mCherry-labeled cells?
Another excellent point. RNA FISH in tissue sections can often be rather challenging due to various reasons including RNA degradation, and mCherry RNA signal was hard to definitively show in these sections. Hence, we opted for MALAT1, which is very heavily expressed and hence provided a strong and reliable signal.
“For technical reasons, the mCherry cells were not detectable due to the fluorescence of the mCherry protein not being visible in the mouse sections. Nevertheless, we were able to detect late invaders in the population by using a human-specific MALAT1 RNA FISH probe that binds only to human MALAT1 RNA and not mouse MALAT1 RNA (28).”
7) In vivo cycling (harvesting the cells from metastatic site and implanting them to the primary site in mouse models) has been employed to select metastatic sublines from a parental line. Could in vivo cycling make the early invader phenotype fixed?
The reviewer has raised a very interesting point about cycling and selection. Indeed, the 1205Lu cells were derived from repeated cycling of invasive lung cells. That is probably the reason that these cells were useful for our assay, because the percentage of early-invading cells was higher. Nevertheless, the cells still have a significant proportion of late invaders, suggesting that the phenotype has not yet been fixed in the population. Perhaps with further cycling, such a fixation could be achieved. We have now noted this possibility in our discussion.
“It is also possible that repeated cycles of selection, even of non-genetic phenotypes, could lead to an increased fraction of invasive cells. Indeed, 1205Lu cells were derived by exactly such repeated cycles, which presumably are the reason they have a higher percentage of invasive cells; however, despite these repeated rounds of selection, most cells are still not highly invasive, suggesting that it is difficult for this property to fully fix in the population.”
**Referees cross-commenting**
Both reviewers' questions are important for adequate controls.
Reviewer #3 (Significance (Required)):
There are several studies trying to identify subpopulation responsible for the metastasis of melanoma and other types of cancer, and a few mechanisms have been revealed. However, the significance depends on if the results can be validated on clinical data. It is lacking in this study.
We thank the reviewer for their statement of interest in the problem. We agree that it is helpful to link these results to clinical data. We did perform TCGA analyses of several different genes, including SEMA3C, that emerged from our data, and there were no systematic relationships to phenotype. Of course, the relationship to clinical data is complex and many important factors are not obvious from the TCGA data, so we do not think that necessarily diminishes our results. Rather, we think our results raise a conceptual point that there can be rare cells with non-genetic differences that can drive metastasis. Further work will be required to translate these results to the clinic.
We have added the following to the main text:
“We found that the SEMA3C-high cells were far more invasive, intrinsically, than SEMA3C-low cells and the population overall, thus demonstrating that cells vary intrinsically in their invasiveness, and the very invasive subpopulation is marked by the expression of SEMA3C (Fig. 1E). Note, overexpression of SEMA3C in FS4 single cell clones revealed no changes in invasiveness, suggesting that SEMA3C is a marker with no functional relevance to invasiveness per se (Fig. 1D; Supp. Fig. 1E-G). We verified the expression levels of the genes identified in our RNA sequencing study in the The Cancer Genome Atlas (TCGA) data. We combined the list of differentially expressed genes in early invaders with the gene set enrichment analysis (GSEA) “Hallmarks of cancer epithelial-mesenchymal transition” and compared expression in primary vs. metastatic TCGA samples, finding no appreciable difference (Fig. 5A-B). These data suggest that these markers do not have obvious clinical correlates. Moreover, Kaplan Meier analysis comparing the survival time (days to death) between patient cohorts with either high or low SEMA3C expression levels revealed that SEMA3C does not predict survival time post-diagnosis, as both survival curves (p=0.898) follow comparable trends between the two cohorts (Fig. 5C). However, conceptually, our results raise the possibility that a rare, non-genetically defined subpopulation of cells may drive metastasis due to its increased degree of invasiveness, which further data collection efforts in patient samples may help validate.”
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Referee #3
Evidence, reproducibility and clarity
In this study, Kaur et al. intended to use similar strategy that the same group had developed (https://www.nature.com/articles/nature22794) to identify the subpopulation in melanoma responsible for metastasis. In brief, the melanoma cell population was subjected to the selection of a specific phenotype (transwell migration dubbed as "invasiveness" behavior). By comparing the early and late invaders, a cell maker was identified to allow distinguishing the high-invasive subpopulation. A series of experiments were devised to validate the metastatic function of the high-invasive cells and delineate the signaling that drove this phenotype. The authors concluded that this rare subpopulation was originated from transcriptional fluctuation, and invasiveness is a trade-off of cell growth. Therefore, as the cells growing, overtime the phenotype was reverted to low invasiveness.
Consistency is the most important factor for evaluating observation over temporal and spatial range. Therefore, several controls need to be clarified before further investigation in mechanisms:
- If the rare invader cells are arising from gene expression fluctuation, the SEMA3C-low population of parental line should generate SEMA3C-high invader subpopulation over time. This should be addressed.
- Both early and late invader cells exhibited higher invasiveness than the parental line (Fig. 3B). Therefore, the in vivo metastatic potential of the three lines should be compared to validate the role of the invader cells in the metastatic function.
- To evaluate the possible intervention of cellular function by fluorescent proteins (https://doi.org/10.1016/j.ccell.2022.01.015), admix of GFP- and mCherry-labeled populations of early invader cells should be used as a control in Fig. 1F. Noticably, the labeling ratio of the two population was not even in Fig. 1F.
- When the invader cells were expanded and passed, their invasiveness will revert to the level similar to parental line in 14 days (Fig. 3B). The isolated cells were expanded for further testing and manipulation in Fig. 1C and 1F, respectively. How long did was the period for cell expansion in these experiments?
- If invasiveness and growth are trade-off, why did the mCherry-labeled cells not dominate the population of primary tumors in Fig. 1J?
- In Fig. 1G, why RNA FISH was not used to detect mCherry-labeled cells?
- In vivo cycling (harvesting the cells from metastatic site and implanting them to the primary site in mouse models) has been employed to select metastatic sublines from a parental line. Could in vivo cycling make the early invader phenotype fixed?
Referees cross-commenting
Both reviewers' questions are important for adequate controls.
Significance
There are several studies trying to identify subpopulation responsible for the metastasis of melanoma and other types of cancer, and a few mechanisms have been revealed. However, the significance depends on if the results can be validated on clinical data. It is lacking in this study.
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Referee #2
Evidence, reproducibility and clarity
RC-2022-01474 Metastatic potential in clonal melanoma cells is driven by a rare, early-invading subpopulation Kaur et al.
In this manuscript the authors highlight a small subpopulation of "early-invading" melanoma cells and functionally characterize the nuances of these early cells compared to their slowly invading counterparts. A cell surface marker, SEMA3C and the transcription factor NKX2.2 were associated with differences in the invasive rates. Importantly, the group demonstrates that existence of the invasive subpopulation is not reliant on genetic changes, and thus exhibits plasticity. While the underlying concept surrounding this paper (phenotypic plasticity) is not novel, highlighting a surface marker and transcription factor that may, at least in part, be associated with phenotype plasticity is interesting. However, the current study seems underdeveloped. Specific points of concern are listed:
Major
- Only two cell lines are used throughout this study.
- The in vivo metastasis assay in figure 1 is difficult to interpret and presents a number of concerns.
- 1.) Only ~50% of early invading cells were labeled with GFP, this confounds many aspects of the experiment. The authors comment that in the primary tumor, as expected "...a roughly equal mix of human melanoma cells that were GFP positive and negative." If there was an expectation of equal proliferative rates in the primary tumor of early and late invading cells, given that only 1/2 of the early cells were GFP+, wouldn't we expect only 25% of the human cells to be GFP+?
- 2.) The authors note technical difficulties in detecting mCherry in sections. It seems as though this forced them to use a RNA FISH probe to identify human vs. mouse and by extension/negative selection the human FISH positive, GPF negative cell represented a mCherry stained late-invading cell. This is not ideal and seems over complicated. If the population of interest was engineered to express mCherry, why not directly probe for mCherry?
- 3.) Given the poor initial labeling/transduction of the early invaders, how can the authors be confident that all human cells without GFP signal are late invaders?
- The authors may have missed an opportunity to study FS4 clone F6 and 1205 clone E11. What is the SEMA3C and NKX2.2 status of these clones? Are they able to revert expressions?
- The lack of statistical analysis/comparisons throughout the paper needs to be addressed.
- In figures 1E and 3B, why do the parental (homogenous) cells demonstrate less invasiveness than the selected for the SEMA3C low or "late-invaders" respectively?
- Conclusions that NKX2.2 knockout increases invasiveness and proliferation are based on 1 cell line. The comparisons done with FS4 early and late invading cells in Figure 1F may be supportive but is correlative in nature.
- Given the robust literature regarding phenotypic switching in melanoma, the NKX2.2 knockout increasing both invasiveness and proliferation (figures 2C, 2D) suggests it may not be involved in phenotype switching. Perhaps NKX2.2 is a negative regulator of cell activity/metabolism.
- Given that sorted SEMA3C high levels did not revert to parental FS4 levels, yet the invasive phenotype reverted to parental-like behavior undermines the usefulness of SEMA3C as a marker of invasiveness.
Minor
- How does SEMA3C and/or NKX2.2 expression (here 1.5% of FS4 cells were noted as "SEMA3C high") of metastatic cell lines (FS4 and 1205) compare to RGP and VGP cell lines?
- There were a number of instances throughout the manuscript that were not clear, colloquial, or simply unnecessary - i.e. description of transwell assay.
- The authors only analyze/mention lung metastases. Were metastases observed at other sites?
- What is PE indicating in Figure 1D?
- The number of invaded cells seems to vary quite a bit between experiments - Parental 1205 cells in Fig 2C = ~200, yet 1205 clone F6 and the non-clonal 1205 cell line demonstrate ~10,000. Similar differences observed with Fs4 cells - Parental Fig 1E vs. Empty control Figure 2A.
Significance
This work contributes to the growing fields of phenotypic plasticity and intratumoral heterogeneity. The authors claim to have identified a surface marker SEMA3C and a transcription factor NKX2.2 that may play a role in driving invasive proclivity. Importantly, the group demonstrates that changes in these proteins is not genetic, and therefore represents "intrinsic differences" that is a property of the tumor. Furthermore, the authors indicate how the present observations of early invading cells parallels drug resistance phenomena as their previous works highlights intrinsically resistant subpopulations (Shaffer et al., Nature 2017, Torre et al., Nature Genetics 2021 and others.). Taken together, the current and previous work underscores the importance of cell to cell non-genetic variability in disease progression and response to therapy.
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Referee #1
Evidence, reproducibility and clarity
Summary:
The manuscript entitled „Metastatic potential in clonal melanoma cells is driven by a rare, early-invading subpopulation" by Kaur and colleagues provides a phenotypical analysis of the invasive potential of established melanoma cell lines on single cell level. The aim of the study was to answer the question if even homologous tumor cells bear the intrinsic potential to give rise to cells with high invasive (and therefore potentially metastatic) capacity in absence of selection pressure from the tumor microenvironment. The authors used clones from two different melanoma cell lines (to prevent the accumulation of random (epi)genetic changes during cultivation) and performed invasion assays with Matrigel-coated transwell inlays to differentiate between cells that were able to invade early (up to 8 h, approx. 1% of the total cell population) or late (8-24 h; approx. 3% of the total cell population) after plating. Comparative RNA sequencing of early invaders and non-invaders populations revealed a high expression of SEMA3C in early invaders, which was then established as marker in the used cell lines. Interestingly, in vivo models using NSG mice injected with a mixture of early and late invading melanoma cells revealed that both contributed similarly to the primary tumor, while metastatic cells in the lung consisted almost exclusively of early invaders. Subsequent ATAC sequencing revealed an increase of binding sites for the transcription factor NKX2.2 in the early invaders. Functional analyses revealed that a knockout of NKX2.2. led to an increase in both invasion and proliferation. Finally, the authors showed with different sorted early and late invaders as well as SEMA3Chigh and SEMA3Clow expressers that pro-invasive features go along with reduced proliferation potential in accordance to previously published data. However, they decrease with time, thus demonstrating a reversion of the phenotype and high plasticity.
Major comments:
In general, the paper contains novel and interesting data, is concisely written and supported by replicates. The key conclusion, the presence of a small proportion of highly invasive cells in a seemingly homologous cell population and their striking requirement for lung metastasis, is very convincing. In vitro, SEMA3C was confirmed as marker for the early invaders in two independent cell lines. However, a few questions remain open, as detailed below:
- The relevance of NKX2.2 in the early invaders is currently unclear to me. The ATAC sequencing data revealed a high enrichment of accessible NKX2.2 binding sites in early invaders, and data were tested by comparative RNA sequencing of control cells and cells with NKX2.2 ko (Figure 2). The Figure legend of Figure 2 says: "NKX2.2 is a transcription factor that promotes the invasive subpopulation", but the data don`t support this (ko leads to reduced invasion). Accordingly, the authors also state in the Results part "... the direction of the effect is the opposite of what one might have expected". To set the role of NKX2.2 into context, it would be useful to confirm the actual involvement of NFX2.2 in the invasive phenotype and clarify if NFX2.2. might probably even suppress some pro-invasive genes. I would advise to investigate the protein levels and/or protein localization of NFX2.2 and probably perform ChIp experiments on selected pro-invasive genes that play a role in the early invaders.
- The sequencing data are currently accessible via a Dropbox link. They should be deposited instead in a data repository.
Minor comments:
- The cell line used for Supplementary Figure 4 should be named in the figure legend.
- In Figures 4H-M and Supplementary Figure 4D-I, the authors describe data performed in "sister" and "cousin" cells. It would be useful to provide a definition for both in the main text or figure legend.
- Discussion: "This lack of permanence may reflect the fact that the invasive cells are not subjected to stress-in our case, cells merely pass through a transwell, which may be the reason for the "burning in" of the phenotype in the case of resistance." This sentence is misleading - please clarify.
Furthermore, there are some errors in the reference to the Figures throughout the paper. These which should be corrected: 4. Results, section "NKX2.2 is a transcription factor that promotes the invasive subpopulation". Here the authors write: "...we performed RNA sequencing on the NKX2.2 knockout cells and compared the effects on gene expression to the gene expression differences between early vs. non- invaders across the two cell lines." This sentence should contain the reference to Supplementary Figure 3B-D (which is otherwise not referred to). 5. Results: "Overexpression of SEMA3C in FS4 cells revealed no changes in invasiveness, suggesting that SEMA3C is a marker with no functional relevance to invasiveness per se; Fig. 1D, Fig. 2A-B)" The correct reference should be: Suppl. Fig. 1D, Fig. 2A-B. Also, in the current manuscript version the authors jump from Figures 1 to Figure 2 A,B, before coming back to Figure 1. To avoid this, I would advise to shift the current Figure 2A, B to Figure 1 or the supplementary information. 6. Results: "We then sampled lungs from mice at various times post-injection to look for metastatic cells (Fig.1F, Suppl. Fig. 2B,C)." As Supplementary Figure 2B, C does not show metastasis, but rather primary tumor growth, I would advise the following wording: "We then sampled lungs from mice at various times post-injection to look for metastatic cells (Fig.1F) and overall tumor growth (Suppl. Fig. 2B,C)." 7. Results: "Interestingly, NKX2.2 knockout cells showed markedly increased invasion and proliferation (Fig. 2A,B), suggesting a change in regulation of both processes. " The correct reference is Fig. 2C, D.
Significance
Nature and significance of the advance/ literature context:
In their manuscript, the authors provide interesting biological data about the presence of intrinsically and reversibly pro-invasive / pro-metastatic melanoma cells in a seemingly homogenous subpopulation. With SEMA3C, they also provide a marker for early invading cells, which might be useful in future studies to identify therapeutic vulnerabilities for this subgroup. This study sheds further light on the functional effects of phenotypic plasticity, which was previously described particularly in the context of therapy resistance, as mentioned by the authors.
Audience:
The study is interesting for scientists from the melanoma field as well as the cancer metastasis field in general.
Own expertise:
Melanoma, phenotypic switch, metabolism, signal transduction, stress response
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Reply to the reviewers
RC-2022-01661
Response to reviewers:
Review Commons questions and Reviewers’ comments verbatim in plain text.
Authors’ responses in bold text. Line numbers refers to numbers in the marked-up manuscript. In text citations in this document – see bibliography at bottom of this document.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary: Cells within multicellular organisms are mutually dependent on each other - cells of one type or in one location provide signals that can regulate the health and differentiation of the target cells that receive those signals. Such signalling can operate bi-directionally, emphasizing the co-dependence of cells upon each other. The ovarian follicle provides an excellent model system to study intercellular signaling and its consequences, in this case between the oocyte and the somatic granulosa cells that surround it. Oocytes secrete members of the TGFbeta growth factor family that are required for normal differentiation of the granulosa cells, which in turn is necessary for normal development of the oocyte. Here the autohors show that adding TGFB-type growth factors (cumulin or BMP15) to the cuture medium during in vitro maturation increases the fraction of oocytes that can reach the blastocyst stage (improved developmental competence) and alters the pattern of protein landscape in both the (cumulus) granulosa cells and the oocyte. Changes in the mitochondria and parameters relevant to energy metabolism are also altered. They conclude that these changes underpin the acquisition of developmental competence by the oocytes.
Major issues: The authors are world leaders in this field and therefore exceptionally well-qualified to carry out the proposed work. There are a number of issues, however, that limit the confidence with which conclusions may be drawn.
First, the experimental strategy makes drawing inferences about the role of cumulin and BMP15 challenging. Maturing oocytes express GDF9 and BMP15 (the components of cumulin). Thus, the experiments are not comparing presence vs absence of cumulin and BMP15, but rather comparing oocytes and cumulus cells exposed to supra-physiological levels of these factors to controls that are exposed to physiological levels. In other words, the experimental setup detects changes that occur in response to higher than normal levels of the factors. Ideally, one would have complementary experiments where GDF9 and BMP15 were deleted from the system, to illustrate the effects of their absence. This would be a massive additional undertaking, however. Yet, without such experiments, relying on the results of the overexpression approach to understand the functions of cumulin and BMP15 at physiological levels is risky. RESPONSE #1 We appreciate these insightful perspectives. We apologise for not making it clear that the model used is not in fact an overexpression model. This is because, by removing the cumulus-oocyte complex from the follicle and studying it in vitro (oocyte IVM), secretion of these growth factors by the oocyte is notably compromised, so the controls are not exposed to normal physiological levels as suggested by the reviewer. This loss of normal secretion ex vivo is evidenced by: 1) in Mester B. et al _[1]_; Figure 2, we showed the mouse oocytes matured in vitro (i.e. as per the current study) are essentially devoid of the mature domain BMP15 protein, which will therefore be likewise for cumulin as cumulin contains one subunit of BMP15, and 2) mammalian cumulus-oocyte complexes explanted and cultured in vitro by IVM benefit (in terms of developmental competence) from the addition of exogenous oocyte-secreted factors such as BMP15, GDF9 and cumulin, demonstrating that they are rate-limiting under IVM conditions. We were the first to demonstrate this in 2006 _[2]_ which has been subsequently verified in many papers, including in the current paper for cumulin. The exact extent to which the controls are deficient in BMP15 and cumulin is unclear, as there are not yet reliable mouse ELISAs for these, but the model is an add-back model rather than an overexpression model. We have now added text at lines 150-152 and in the Fig 1 legend, to make this point clearer.
Re using complimentary deletion, knock-out or antagonist-type experiments: we agree this would be ideal. However, this is likely impossible as cumulin is a non-covalent heterodimer of BMP15 and GDF9 (as first named and characterised by us: Mottershead DG et al ____[3]____). Hence, to knockout cumulin one needs to knockout either or both of BMP15 and GDF9, making it impossible to discriminate the actions of the heterodimer from the homodimers. In support of this, reviewer #3 made exactly this point, and stated “Such functional analysis cannot be done using gene knockout mouse lines…… only functional work as the one presented in this manuscript can find the mechanisms of action of these hormones”. This issue is further complicated by the fact that BMP15 and GDF9 are thought to exist as homodimers, as well as monomers, including in equilibrium in heterodimeric form as cumulin (also noted by Reviewer #3). Furthermore, there is no cumulin-specific antagonist, e.g. a cumulin-specific neutralizing antibody. Small molecule signaling inhibitors (e.g. Smad2/3 or Smad1/5/8 antagonists) certainly block cumulin actions, but therefore simultaneously also block GDF9 or BMP15 actions. Collectively, these unique (with the TGFβ superfamily) structural peculiarities of cumulin make it complex to interrogate its mechanisms of action, to the extent that others have largely focused on BMP15 or GDF9 homodimer actions only, when in reality, cumulin is likely the key natural protagonist responsible for oocyte paracrine signalling. We have added a paragraph to this effect to the discussion, at lines 417-423, including acknowledging the experimental limitations of the study dictated by having to deal with a noncovalent heterodimer.
Second, the granulosa cells and oocytes interact throughout the prolonged period of growth, and this is the time when the beneficial effects of the granulosa cells on the oocyte have been most clearly documented. Yet the experiments focus on the much shorter period of meiotic maturation. This is when oocyte-granulosa cell interaction is being down-regulated, even if not entirely disrupted. RESPONSE #2: Indeed, oocyte-granulosa interaction is absolutely essential during oocyte growth, development and meiotic maturation, for healthy oocyte function, including the orchestrated down-regulation of oocyte-granulosa interactions during the latter phase. As pioneered by John Eppig and others, including ourselves ____[4]____ (ref has 673 citations), the master conductor of this dynamic oocyte-granulosa interaction during oocyte meiotic maturation are the oocyte-secreted factors. Hence, these factors are critical at this stage, and we maintain that this is a very important phase of oocyte development to study.
Third, the data reported illustrate associations or correlations, but no experiments test the function of the changes in the proteome or of the changes in the morphology of the mitochondria or ER. Which if any of these is linked to the improved development of the oocytes after fertilization is unknown. Moreover, no experiments address how the growth factors cause the observed changes, which occur over a period of a few hours. RESPONSE #3 This is true. The study is already very large and has many functional experiments (e.g. oocyte respiration, oocyte MS, etc), that follow-up the findings from the proteomic analysis. Hence, the study has taken a global cellular metabolism approach, e.g. we show that cumulin downregulates oxidative phosphorylation globally, c.f. pathways within OXPHOS. We found an abundance of individual proteins altered in this period (see figure 4) and to follow up on the actions and consequences of individual proteins would: 1) at best show small incremental effects, as metabolism of such a cellular syncytium is vastly complex and inter-connected, 2) further increase the size of what is already a large study, and 3) detract from the more important wholistic effects on cumulus-oocyte complex metabolism, which must act as whole, interacting entity, to support the complexities of supporting early life post-fertilization.
__Taken together, these issues unfortunately limit the potential impact of the work. But the amount of work required to address them would be substantial and not really feasible for this manuscript. The best route may be to present the work as an overexpression study that has identified associations, with a discussion that acknowledges the limitations of this approach. __RESPONSE #4 This is not an over-expression study – see RESPONSE #1 above. We have added text in the discussion at lines 417-423, that acknowledges the limitations of the study by the impossibility to conduct a killer knockout experiment of cumulin.
Minor issues: The text of the manuscript should be revised in a number of places. 32: We characterized the molecular mechanisms by which two model OSFs, cumulin and BMP15, regulate oocyte maturation and cumulus-oocyte cooperativity. --Mechanistic studies were not performed. RESPONSE #5 The scope of this work was to; (a) identify global changes to protein expression, and (b) to use this data to implement follow-up experiments on some of the lead indicators, such as metabolism (respiration, small molecule metabolic markers) and cellular morphology. This work provides the groundwork, insight and rationale for future additional studies of specific mechanisms of COC interactions. As discussed at RESPONSE# 1, these studies are as close as anyone can probably get currently to mechanistic studies of a NOVEL noncovalent heterodimer, when the noncovalent homodimers are also in play, as also noted by reviewer #3 who specifically references mechanisms: “…… only functional work as the one presented in this manuscript can find the mechanisms of action of these hormones”.
In some instances, in the interests of brevity, we made remarks based on our data, but without specifying details in the text. To redress this, we have now added specific details which illustrate and justify our statements based on the data collected (see RESPONSES #6, #7, #9 below). For greater clarity, we have also restructured our supplementary data set to cover the analysis progression from full raw proteomic data to differentially expressed proteins, to use of differentially expressed proteins in network analysis. The supplementary data set now includes the full proteomics lists for both cells and treatments (Supplementary Tables S1, S2, S3, S4), protein sequences confidently identified by both proteomic software platforms (Supplementary Tables S5, S6), differentially expressed proteomics lists for both cells and treatments (Supplementary Tables S7, S8, S9, S10), differentially expressed protein list used for the network analysis (supplementary Table S11). The Table S11 lists are intended to facilitate use by readers to perform their own analyses, if they so wish, since they can simply copy and paste the list to the on-line STRING platform. Finally, the reanalysed network analysis output, based on the differentially expressed proteins shown in supplementary Table S11, are shown in supplementary Tables S12 and S13.
__40: Collectively, these data demonstrate that OSFs remodel cumulus cell metabolism during oocyte maturation in preparation for ensuing fertilization and embryonic development. --No mechanistic studies demonstrate this. __RESPONSE #6 There is no mention of mechanism in this sentence at line 40 and we have provided exhaustive evidence that cumulus cell metabolism is remodelled as stated (Figures 4B and 4C). For example, of the 59 upregulated proteins in the cumulus cells of cumulin treated COC (Figure 4C and supplementary Table S11), 38 (i.e. 64%) are involved in primary metabolic processes (supplementary Table S12), including amino acid metabolism (GOT2, SHMT1, CTH, MAT2B), lipid and steroid metabolism (CERS5, DHCR7, HSD17b4), aldehydes metabolism (RDH11), nucleotides biosynthesis (RRM1, GMPR2), glycans biosynthesis and protein glycosylation (UGDH, GFPT2, GALNT2), respiratory chain (mt-ND1). The cellular macromolecule metabolic process is also a significantly enriched network, involving 26 out of the 59 upregulated proteins (i.e. 44%, Figure 4C and supplementary Table S11) and includes processes such as protein complex assembly (TM9sF4, DHX30, AP2M1), RNA metabolism and mRNA processing (DDX17, DDX5, DDX39bPRPF19, PRPF6, HNRNPF, CPSF6). To help clarify the specificity of our findings, we have added this text to the revised manuscript (lines 465-474).
__46: Oocyte-secreted factors downregulate protein catabolic processes, and upregulate DNA binding, translation, and ribosome assembly in oocytes. --No direct evidence is provided. __RESPONSE #7 The proteomic data provides direct evidence that these processes are involved. Sentence modified at lines 47-48 to be more specific re processes. Additional text has been included (revised manuscript lines 434-443) to provide specific details of the differentially expressed proteins involved in each of these processes.
48: Oocyte-secreted factors alter mitochondrial number... --Need to establish that the MitoTracker is a suitable tool to measure the number of mitochondria. RESPONSE #8____ We recognise that total mitochondrial uptake of the MitoTracker Orange dye could be a reflection of either mitochondrial function (polarity) and/or mitochondrial number, given the manufacturer’s (Thermo Fischer) statement that “MitoTracker™ Orange CMTMRos is an orange-fluorescent dye that stains mitochondria in live cells and its accumulation is dependent upon membrane potential”, as we specified in several places in the original manuscript (Lines 354-355, 366-367 and 235 of the marked up manuscript version) . However, we agree that in several places in the manuscript we also indicated that MitoTracker was being used as a measure of mitochondrial number. To avoid this ambiguity, we have made some clarifications in the text (revised manuscript lines 235, 351-352, 377, 481-482, and in Figure 5B legend). Given the extensive and diverse metabolic changes indicated by the proteomic data, our aim was to explore the potential role of mitochondria in response to cumulin and BMP15 treatment of COCs, which we did by use of EM morphology studies (figure 5A), mitochondrial respiration (figures 6B and 6C), quantification of energy metabolites, such as ATP, NAD and related compounds, by mass spectrometry (figure 6D), metabolites identified in multispectral unmixing studies (figure 7) and mitochondrial function using MitoTracker (figure 5B). Collectively this data suggested a modest downturn of energy metabolism, particularly in cumulin treated COCs. This downturn did not cause a change in net energy charge in COCs (figure 6D) despite a reduction in redox ratio in both cells (figure 7A and 7B) and respiration in COCs (Figure 6B and 6C), and could reflect adaptive changes in response to cumulin and BMP15, reflecting metabolic plasticity/Warburg effect, as explained in the discussion (revised manuscript lines 453-551).
79: ...for maintaining genomic stability and integrity of the oocyte... 83: ...minimizing secondary production of potentially DNA damaging free radicals. --Please provide supporting references from the literature. RESPONSE #9 References have been added (lines 82 and 85 of the revised manuscript)
373: This study provides a detailed exploration of the mechanisms by which oocyte-secreted factors... --No mechanistic studies were performed. RESPONSE #10 We respectfully disagree. One of many mechanisms we have studied here is OXPHOS. We have shown this is how OSFs change metabolism – that is a mechanism. As discussed at RESPONSE #1, these studies are as close as anyone can probably get currently to mechanistic studies of a noncovalent heterodimer, when the noncovalent homodimers are also in play, as also noted by reviewer #3 who specifically references mechanisms: “…… only functional work as the one presented in this manuscript can find the mechanisms of action of these hormones”. Please also refer to the comments in RESPONSE #5.
383: Collectively, these data demonstrate that oocyte paracrine signaling remodels COC metabolism in preparation for ensuing fertilization and embryonic development. --Studies do not show that the differences observed between control and treatment groups are related to fertilizability or embryonic development. RESPONSE #11 The data in Fig 2C, 2D show exactly that; that the difference between control and treatment (cumulin) is an increase in embryonic development. It does not show fertilizability, so we removed that at lines 41 and 415.
396: suggesting that cumulin affects meiosis in the oocyte and may increase meiotic fidelity... --This statement is highly speculative. RESPONSE #12 We accept this critique - reference to meiosis and meiotic fidelity removed, line 435 (revised manuscript).
409: ...lacks the machinery for amino acid uptake... --Is the oocyte unable to take up any amino acids or only certain amino acids? RESPONSE #13 Thank you for noting this as this sentence is too absolute. Oocytes have a very poor capacity to take up most or even all AAs, which are instead supplied to the oocyte via cumulus cells. Sentence modified at lines 455-456 to be less absolute.
In general, the manuscript is written clearly. However, in several places, technical terms or jargon will make tough going for readers who are not already familiar with the techniques being used. These should be explained using language that will be understood by journal readers who are unfamiliar with the details of the techniques. Examples include:
51: define metabolic workload using scientific terms.
RESPONSE #14____ “metabolic workload” rephrased to “metabolic processes”. Lines 52-53.
67: metabolically 'inept' requires more precision. RESPONSE #15 “metabolically inept” rephrased to “metabolically dependent on surrounding granulosa cells” ____[5]____. Line 69
262: explain 'multispectral analysis' RESPONSE #16 A citation has been added, which explains the technique (ref ____[6]____ at the end of this response letter, which is the same paper as citation [34] in the revised manuscript; lines 111 and 217; revised manuscript). A detailed explanation of this technique has also been added in the supplementary information, under the section “Multispectral microscopy”.
268: how is 'limited' overlap defined. RESPONSE #17 The phrase “distinct profiles, with limited overlap between…” has been rephrased to “distinct profiles, between…” (line 279 of the revised manuscript), as the main point is that the patterns/profiles across treatments are different, and we did not quantify the extent of overlap.
318: define higher workload RESPONSE #18 the phrase “…implying a higher workload for both organelles” has been replaced with a more specific explanation; “We suggest that such changes in morphology may be related to the remarkable increase in a diversity of metabolic processes which we observed (Figure 4C and supplementary Table S12), since ER morphology and architecture is known to be highly dynamic in response to environmental and developmental factors which affect cells” ____[7]____ (Lines 342-345).
324: provide documentation or citations to support the assertion that the intensity of MitoTracker staining is an accurate proxy for the number of mitochondria.
RESPONSE #19____ Please refer to explanation under RESPONSE #8
358: Multispectral discrimination modelling utilised cellular image features from the autofluorescent profiles of oocytes and cumulus cells. --Please clarify this merthodology and provide support for its utility.
RESPONSE #20____ The supplementary information section (Multispectral microscopy, lines 239-258) has been expanded and clarifications provided as to the wavelengths of the channels, the features used and the unsupervised nature of algorithms.
360: intersection of union of 5-22%
RESPONSE #21____ This is a measure of the extent of overlap of data distribution for each class (treatment), i.e. of how different they are. The ellipse (Fig 3D) represents one standard deviation around the central mean value for that data set. The overlap of these ellipses is quantified by their intersection over union (IoU) value, which is the ratio of the area of the two-ellipse intersections, divided by the area of their union (the shape created by their overlap being treated as creating one continuous object). IoU values range from 0 to 100% for fully separated and fully overlapping, respectively. Hence, a 5% IoU represents a low level of overlap of data distribution between treatments. Brief explanatory text has now been added at line 387-388.
Comments on Figures. Fig. 3A, B. The total number of proteins and the number of differentially expressed proteins among the treatment groups don't match between A and B. For example, A (Mascot-Sheffield) indicates that 17 proteins were differentially expressed between untreated and cumulin-treated oocytes. B shows (138 + 74) expressed un the untreated but not cumulin-treated and (156 + 87) expressed in the cumulin-treated but not untreated. Please account for this difference. RESPONSE #22 The panels in Fig 3A and Fig 3B each contain different representations of the information contained within the proteomics dataset, and explain different aspects of the data. The Venn diagram panels in Figure 3B display the level of overlap of specific proteins identified in each cell, treatment and software subgroup. The degree of overlap in each cluster is high (i.e., 76 – 78% for Mascot/scaffold and 95 - 97 % for PD2.4) as would be expected within the same cell type and analysis approach, where the main variable is cell treatment. We agree that the total numbers in the Venn diagrams did not exactly match the total numbers in Figure 3A, which likely resulted from using slightly different parameters during data processing. We have now used exactly the same data set in panels A and B (the full PD2.4 and Mascot/scaffold datasets are shown in the supplementary proteomics summary Excel spreadsheet), so that total numbers are now identical, and will hopefully avoid any confusion in comparing across panels. However, the main conclusion to be drawn from Fig 3B remains unchanged, in that it shows that by far the majority of identified proteins overlap between treatments (control, BMP, cumulin), regardless of cell type or data analysis approach. However, it should be noted that Figure 3B has no information about protein fold change/differential expression, and only represents numbers of proteins confidently identified, and the level of overlap of identified proteins between treatments. Only panel 3A shows differential protein expression relative to the respective control groups.
Fig. 3D. What do the circles represent and how were their parameters (size, position) established? RESPONSE #23 The separation of data distributions for each class is shown by an ellipse for each cluster, which encompasses one standard deviation around the central mean values. This text has now been added to the Fig 3 legend.
Reviewer #1 (Significance (Required)): These studies identify changes in cumulus cells and oocytes that occur in response to addition of cumulin or BMP15 to the culture medium during in vitro maturation. While the data are new, the significance of the advance is limited by (i) the fact that the control group were exposed to physiological levels of GDF9 and BMP15, so this is essentially an over-epxression study and (ii) no mechanistic studies experimentally tested how the observed changes (eg, in quantity of a specific protein) affect the developmental potential of the oocytes or cumulus cells. RESPONSE #24 We thank the reviewer for their perspectives however we respectfully disagree on all accounts. We have rebutted these 2 concerns: point (i) at RESPONSE #1, and point (ii) at RESPONSE #5 above.
Reviewer expertise: growth and meiotic maturation of the mammalian oocyte
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: The report by Richani et al, presents a research carried out in mice, in which they treated cumulus-oocyte complexes with either BMP15 and cumulin. Upon treatment they evaluated a series of biologically relevant parameters in oocytes and cumulus cells. Their findings indicate that the treatment with these molecules alter the molecular composition of oocytes and cumulus cells (proteome and metabolome), mitochondrial morphology in cumulus cells and overall oxygen consumption in COCs.
Major comments: - Are the key conclusions convincing? - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? * part of the discussion related to metabolic pathways being up regulated due to the treatments need to the revised because For instance, It is hard for me to grasp how a pathway with 2 proteins achieved FDR significance below 0.01, as I see in figure 4c
RESPONSE #25____ Network enrichment was performed using the open access software STRING ( ____https://string-db.org/ [8]____), and we have now provided additional information on how we utilised STRING in the supplementary information section, under “Gene Ontology Network Enrichment Analysis” (lines 176-217). STRING utilises information available in the Gene Ontology (GO) database ( ____http://geneontology.org/docs/ontology-documentation/____ ) to determine; (a) how many of the differentially expressed proteins identified in the proteomics experimental data fall into specific networks, (b) how much enrichment this represents relative to a random network of the same size, and (c) whether the enrichment is statistically significant based on the FDR statistic. The size of each GO network within the background set (whole genome or other) will therefore be a major determinant of whether the number of proteins identified in the proteomics experiment represents significant enrichment of a particular network. A few proteins identified within a small background network will represent greater enrichment (and lower FDR score) than the same number of proteins in a much larger network. In fact the “count in network” is often approximately the inverse of the enrichment strength (see supplementary Table S12, within the supplementary dataset Excel spreadsheet). Note that only significantly differentially expressed proteins were used for the network analysis presented in this paper, so even in the case where just 2 proteins are significantly enriched in a network (e.g., “Farnesyl diphosphate metabolic process” identified in the GO biological process section of BMP15 treated cumulus cells) they represent two upregulated proteins in a small network, so the functional/biological significance of this is likely quite high.
In revision of the manuscript we noticed that we had likely originally used the full lists of differentially expressed proteins for network analysis, rather than separating up and downregulated proteins as intended. Furthermore an updated version of STRING is now available, with improvements in the method of correction for multiple testing within the FDR output (STRING version 11.5, current since August 12, 2021). We have therefore revised the STRING network analyses, and have provided a list of the STRING input proteins (supplementary Table S11), STRINGv11.5 gene ontology (GO) functional enrichments for up and downregulated proteins in BMP and cumulin treated cumulus cells and oocytes respectively (supplementary Tables S12 and S13), and replaced the very large Figure 4C and D heatmaps (submitted version) with a summary (new Figure 4C; revised version). The updated heat maps can still be viewed in supplementary Tables S12 and S13 (the heatmaps now being the updated ones, deriving from our review response).
* In the discussion the authors use the term "oocyte secreted factors" a lot (one example lanes 490, 515, 516, 517), but they should specify BMP15 and cumulin, because these were their treatments. *Including in the title, you did not evaluate all oocyte paracrine factors, just BMP15 and cumulin RESPONSE #26 “Oocyte secreted factors (OSFs)” replaced with BMP15 and cumulin throughout the manuscript where we refer specifically to our treatments, results or discussion of results, except where we refer to “these OSFs” (eg line 34), and not where we refer to the principal of OSF signalling more generically. Re the latter, hence we wish to retain the title as is, as BMP15 and cumulin are prototypical oocyte secreted factors, as the title refers to the principal more generally.
- 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. NA
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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. NA
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Are the data and the methods presented in such a way that they can be reproduced? *no, in some instances, the methods are not described, see my comment below about enrichment analysis. RESPONSE #27 Addressed next below
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Are the experiments adequately replicated and statistical analysis adequate? *I was not able to access enrichment analysis.
RESPONSE #28____ The method of Network Enrichment is now described in more detail in the supplementary methods section. See previous explanation under RESPONSE #25 above.
*lines 241-242: "MitoTracker staining and data from metabolite analysis by mass spectrometry were analysed by one-way ANOVA with Tukey's (parametric data) or Kruskal-Wallis (non- parametric data) post-hoc tests. " Specify which test was used for which data RESPONSE #29 Post-hoc test for MitroTracker data was Tukey’s, as already stated in Figure 5 legend. Post-hoc test for metabolite analyses was Kruskal-Wallis – text now added to Figure 6 legend.
Minor comments: - Specific experimental issues that are easily addressable. NA
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Are prior studies referenced appropriately? Yes
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Are the text and figures clear and accurate? *lines 178-180: "expressed proteins list was further analyzed using STRING software to explore clustering and enrichment of specific molecular functions, and biological pathways. Detailed methodology and rationale for this approach is provided in the supplementary methods." I did not read text in the supplementary materials indicating how enrichment analysis was carried out.
RESPONSE #30____ Our apologies for this oversight. We have now provided additional information on how we utilised STRING in the supplementary information, in a new section titled “Gene Ontology Network Enrichment Analysis” (lines 176-217).
* What was the concentration of treatment for the samples used for proteome and mascot/scaffold experiments?
RESPONSE #31____ The two bioinformatic analyses were conducted on common biological samples, so naturally the treatment concentrations were also the same. Text modified at line 175 to make this clearer.
* lanes 263 and 264: "Cell types and treatment conditions can be clearly distinguished based on these orthogonal global approaches." I did not see what is the basis for this statement
RESPONSE #32____ The sentences immediately following this (i.e. lines 274-281) elaborated the basis for this statement, particularly where it is explicitly stated “____Proteomic heat maps (Fig. 3C) and multispectral analysis plots (Fig. 3D) both show distinct profiles, between controls, BMP15 and cumulin treated COCs, in both cell types.____”, at lines 277-281.
The data for the two global approaches are shown in Figure 3C (heat maps generated by PD2.4 comparing differences in protein abundance across treatments, shown separately for cumulus cells and oocytes), and Figure 3D (linear discriminant analysis comparing differences in multispectral imaging data across treatments, shown separately for cumulus cells and oocytes). Both of these global analyses show clear differences in distribution pattern between controls (untreated) and treated samples (BMP15 and cumulin), in both oocytes and cumulus cells. The approaches are (a) global, since each relates to analysis of the complete cell extracts (as opposed to targeting a specific component/analyte), and (b) orthogonal because different and unrelated measurement techniques are used i.e., proteomics (mass spectrometry) and multispectral imaging (spectroscopy).____ *I did not understand the discrepancy between the numbers observed in Figure 3A and Figure 3B.
RESPONSE #33____ Refer to RESPONSE #22 above. We have checked the data, and revised the Venn diagrams (Figure 3B) with data analysed using identical parameters, for both Figures 3A and 3B, to avoid confusion over protein numbers. We also noticed and corrected a discrepancy with regard to the number of differentially expressed oocyte proteins under the merged data column of Figure 3A.____ *I could not make sense of the shades of green or red that were used in 4C and 4D. Is the reader only supposed to make those comparisons within column? RESPONSE #34 Note: Figures 4C and 4D are now Supplementary Tables S12 and S13. The red shades represent network enrichment analysis of upregulated proteins, while the green shades represent network enrichment analysis of downregulated proteins. The colour gradients in each case follow the numerical values for “count in network”, enrichment strength, and lower FDR, with greater colour intensity for higher numbers (and lower FDR). However, we agree that the original four panels (A, B, C and D) comprising figure 4, made for a very large and potentially overwhelming figure. To simplify the data presentation we have reprocessed the data in STRING (see details under RESPONSE #25 above) and have moved the now considerably shorter network lists (originally displayed as Figures 4C and 4D) to supplementary Tables S12 and S13, and the new Figure 4C provides a network enrichment summary instead. This is likely easier to comprehend, with the marked contrast in networks identified between oocytes and cumulus cells easier to see. The numbers of up and downregulated proteins on which the network analysis is based are also shown in Figure 4C, while the specific proteins used and networks identified are shown in supplementary tables S11, S12 and S13 (original colour coding retained, and also explained within each table). - Do you have suggestions that would help the authors improve the presentation of their data and conclusions? *Figure 4 is really hard to process. At least in my pdf it spanned 4 pages.
RESPONSE #35____ Indeed Figure 4 was large and has now been shortened. We made considerable effort to attempt to present in Fig 4 the vast amount of proteomic data in a summarized, hopefully comprehensible fashion. We have now moved Figs 4C and 4D to the supplementary, and replaced it with the simplified new Fig 4C (tabular format). Pease also see comments under RESPONSES#25 and #34 re this. *I did not understand why put networks that are not significant as up-regulated or down-regulated. Besides, as mentioned above, I do not know how significance was assessed.. RESPONSE #36 Network analysis was performed using only those proteins which were significantly differentially expressed and had a consistent direction of fold change in both mascot/scaffold spectral counting and PD2.4 peak intensity proteomics quantitative approaches. Proteins with no significant expression change (i.e., the majority of proteins, which represented proteins with __Reviewer #2 (Significance (Required)):
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Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. - Place the work in the context of the existing literature (provide references, where appropriate). *This paper is significant because it provided a variety of measurements following the treatment of cumulus cells with BMP15 and cumulin. The authors show that these two oocyte factors can impact the molecular structure, physiology and structure of organelles in cumulus cells. The work is well contextualized with the current literature. RESPONSE #37 We thank the reviewer for these positive remarks.
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State what audience might be interested in and influenced by the reported findings. *Researchers in the field of developmental biology would be most interested in this report.
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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 do not have expertise in hyperspectral analysis. I have been working with cumulus-oocyte complexes for over a decade, mixing technologies in cell biology, microscopy, high-throughput genome, and proteome analysis. We do all our bioinformatics work in-house.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The work is interesting. Cumulin is a heterodimer hormone formed of GDF9 and BMP15. It is the main oocyte secreted factor. Being an heterodimer, gene knockout provides very little information about its mechanism of action. The team has a unique form of cumulin that is stable. This is why I think this work is important. However, I found two technical issues: one regarding mitochondrial count using MitoTracker and the other about comparing gene lists between the two cell types when protein input submitted to mass spectrometry differ between the two cell types. It is expected to find more with more input material. The text would need to be adjusted accordingly. Also, there is a lot of free statements and a lack of precision that is annoying. In my opinion, there are many overstatements that are not supported by the data because the work was not designed to test what is stated. The Discussion is very circular as the same statements come back on the next pages. RESPONSE #38 See specific responses below
Detailed review:
The manuscript entitled "Oocyte and cumulus cell cooperativity and metabolic plasticity under the direction of oocyte paracrine factors" reports an in depth analysis of the exposure of cumulus oocyte complexes to either BMP15 or cumulin, the GDF9-BMP15 heterodimer. Impact assessment was done by determining developmental competence of the exposed oocytes, comparative profiling of the proteomes and spectral emissions as well as testing a potential impact at the ultrastructure level by electron microscopy imagery. Mitochondrial respiration as well as abundance of related metabolites was contrasted between the two treatments.
Overall, the work is interesting. It is very difficult to study hormonal heterodimers because they originate from two different genes and they can naturally be found in a monomeric as well as a dimeric state. Such functional analysis cannot be done using gene knockout mouse lines. Genetic disruption provided the background that GDF9 and BMP15 are key oocyte secreted factors however only functional work as the one presented in this manuscript can find the mechanisms of action of these hormones. RESPONSE #39 We thank the reviewer for these positive comments, especially in relation to the difficulty of getting to the mechanism of actions of a non-covalent heterodimer, and hence the importance of functional experiments in providing mechanistic insights.
Comments:
I really appreciated the reference to auto-symbiosis. We often see the reference to a cellular syncytium but this one is interesting. RESPONSE #40 Thank you.
Although I appreciated the work, two important technical issues (between cell types comparisons and mitochondrial count) have been raised and there is a bit of unnecessary overselling throughout the manuscript. Sticking to the results would keep the value of the work high and wouldn't give that impression of overstatement. RESPONSE #41 Technical issues – see responses below, as well as responses to other reviewers. We have provided additional methodological information for greater clarity, and added specific observations from our data, to support all statements, to avoid the impression of unsubstantiated overstatements.
Technical issues:
While the gene/protein enrichment analysis can be influenced by the input material submitted to mass spectrometry, the gene network analysis is influenced by the number of gene/proteins available for the enrichment analysis. It is thus difficult to compare both cell types. RESPONSE #42 We agree that shorter protein lists might be expected to result in fewer networks. However, it is interesting to consider the possible reasons for the shorter list:
(1) In our case the amount of protein extracted from oocytes (2-3____m____g) was much less than from cumulus cells (15-17____m____g) as explained in the “Mass Spectrometry for proteomic analysis” section in the Supplementary Information. This is because COCs have many more cumulus cells than oocytes by number as well as total mass. Consequently it was possible to load a larger ____m____g amount of total peptides from cumulus cells onto the nanoLCMSMS system, but it should be noted that on-column loading is not only determined by the total amount of material injected, but also by the limits in capacity of the C18 peptide capture cartridge upstream from the column (which is 1 – 1.5 ug estimated from the binding capacity of C18 with a bed volume of 0.35____m____L, since the trap cartridges have dimensions of 300____m____m ID and 5mm length; ____http://tools.thermofisher.com/content/sfs/manuals/Man-M5001-LC-Nano-Capillary-Micro-Columns-ManM5001-EN.pdf____ and ____https://www.optimizetech.com/opti-pak-trap-columns/____ ). Consequently, the different initial loading of oocyte vs cumulus cell proteins/peptides are likely to have made little if any contribution to proteome coverage, since 2-17____m____g all exceed the trap cartridge binding capacity, and consequently 1 - 1.5____m____g was captured and transferred to the nano-column, while the excess was transferred to waste. Based on the capacity limits of the capture cartridge, there was likely enough peptides/proteins in both oocyte and cumulus cell extracts to reach the saturation point, and therefore much more consistent on-column loadings than the initial ____m____g loadings would imply. We have added some additional information re this to the method section (see the section “Mass Spectrometry for proteomic analysis” in the Supplementary Information).
(2) The expressed proteomes of different cell types may be expected to differ not only in specific proteins expressed but also in the number of different proteins. In a recent study by Marei et al ____[9]____, equal amounts of total protein (9.5ug) from bovine oocytes and matching cumulus cells were prepared for their proteomics comparisons, and interestingly these authors also report about half as many proteins identified in oocytes as compared with cumulus cells, despite equal amounts of total protein used; “A total of 1703 and 1185 proteins were identified in CCs and oocytes, respectively, 679 of which were common.” Furthermore, a transcriptomic study of bovine oocytes and cumulus cells by Moorey et al ____[10]____, showed 69 and 128 differentially expressed genes (DEGs) in oocytes and cumulus cells respectively (comparing small vs large cells in each case), pointing to about double the differential gene expression in cumulus cells than oocytes, again implying a larger cumulus cell vs oocyte transcriptome. Our data support these observations, which collectively suggest a real difference in proteome size between oocytes and cumulus cells. If the difference in proteome size is real, then differences in network enrichment are also likely to have biological relevance, despite differences in size of the differentially expressed proteins lists.
(3) Even if initial protein loading was a contributing factor to the size of the oocyte vs cumulus cell proteomes, it is of note that we observed approximately 2 fold fewer total proteins identified in oocytes as in cumulus cells (Figure 3A, 3B and new Figure 4C), yet the difference between number of identified networks is multiple-fold (a cumulative total of 2 networks identified in BMP15 and cumulin treated oocytes vs 143 networks identified in BMP15 and cumulin treated cumulus cells – see new Figure 4C). Furthermore, there does not seem to be a strictly linear relationship between the number of proteins submitted for network analysis and the numbers of networks identified. For example, 34 upregulated proteins in cumulin treated oocytes identified a single enriched network, while a similar number of 38 upregulated proteins in BMP15 treated cumulus cells, identified a total of 42 networks (new Figure 4C), and similarly cumulin treated cumulus cells had 59 upregulated proteins and 58 downregulated proteins, which resulted in 57 and 23 enriched networks respectively.
Also, when performing GO terms analysis, the level of "branching" can explain the results. In other words, GO terms are organized in a tree like structure where general elements (e.g. nucleus) are delineated in finer elements (e.g. nuclear function) leading to finer ones (e.g. DNA binding)... to finer ones (e.g. DNA repair)... etc. The number of genes/proteins available in the initial list directly dictates to which level of precision the analysis can reach. In the present work, the number of identified network may simply reflect the number of elements available in the initial lists. With more info on the cumulus cells side, it is logical to be able to reach finer branches that contain only a few genes. I have looked in the supplemental data files but could not find more info about the background used. Was it all known proteins? Was it all identified proteins where the differentially expressed proteins are compared to the detected proteins? Using the list of detected proteins as background for the analysis could help. Proteome Discoverer generated much less differentially expressed proteins between treatments than Mascot/Scaffold (2-17 vs. 74-390). Maybe use the Mascot/Scaffold data using the same number of top genes (e.g. 87) between both cell types. Then it would be much more comparable. RESPONSE #43 Please also refer to the explanations under RESPONSE #34 and #42 above. We have added an additional explanation of how we performed the enrichment analysis, in the supplementary information section under the heading “Gene Ontology Network Enrichment Analysis”. In the data presented here we used the whole mouse genome as our background set. The number of total proteins identified by Mascot/Scaffold and ProteomeDiscoverer were similar, but actually considerably more differentially expressed proteins were identified using ProteomeDiscoverer (Fig 3A), as expected using peak intensity vs spectral counting ____[11]____. The spectral counting approaches usually identify fewer differentially expressed proteins, but also with a lower quantitative false positive rate, while peak intensity approaches tend to identify more differentially expressed proteins, but with a higher quantitative false positive rate ____[11]____. Our reasoning was therefore to combine proteins which vary in common across both platforms, to maximise the differentially expressed proteins list while simultaneously minimising the quantitative false positive rate. We thank the reviewer for the suggestion of using our full protein list as the background set. Initially we revised our network enrichment analysis (see comments under RESPONSE #25) still using the mouse whole genome, resulting in fewer overall networks, but improved contrast between oocytes and cumulus cells (see summary in new Figure 4C, and network analysis details in supplementary Tables S12 and S13). We then repeated the network analyses using our full protein list (4450 proteins identified in both oocytes and cumulus cells; see background list in Supplementary Table S11) as the background set. With this we similarly found no enriched GO networks for BMP15 and cumulin treated oocytes, and only 6 and 1 enriched network in BMP15 and cumulin treated cumulus cells. We suggest that detecting network enrichment against a cell specific background list may not give us the same level of “contrast” as can be achieved when comparing against the whole mouse genome.
Line 226 and 324-328 and line 350: I have never seen the use of MitoTracker Orange to count mitochondria. According to the manufacturer: "MitoTracker Orange CMTMRos is an orange-fluorescent dye that stains mitochondria in live cells and its accumulation is dependent upon membrane potential. The dye is well-retained after aldehyde fixation." It is indicative of mitochondrial potential but it is not a method to count the number of mitochondria within a cell. I do not agree that more fluorescence means more mitochondria. RESPONSE #44 We agree and in places we used ambiguous language re mitochondrial function vs mitochondrial number. We have now clarified and corrected this - please refer to detailed comments and manuscript changes under RESPONSE #8.
I understand that the MitoTracker data is counterintuitive to the oxygen consumption rate and stable levels of energetic metabolites. However, as the authors mention, mitochondria are known to be capable of switching from aerobic to anaerobic energy production. In some cases, heterogeneity in the mitochondrial population (such as the one in the oocyte) could mean that a mosaic respiratory potential exists where some mitochondria are more aerobic than others... To change the number of mitochondria, either fission or mitophagy must occur. Although mitochondrial DNA replication is done in approximatively 2 h and fission/division can occur over 1 h, and protein ubiquitination is done over 12 h-18 h during mitophagy, TEM micrographs (figure 5) do not show elongated mitochondria in the process of division. To detect active mitophagy, protein markers and association with lysosome would be needed. A shift in mitochondrial number may not be the suitable interpretation of the data. RESPONSE #45 Please refer to comments under RESPONSE #8
For the spectral data analysis (Figure 3D), how did the three replicates perform? The figure does not show the replication variance relative to the treatment variance. RESPONSE #46 A version of Figure 3D but with the replicates colour-coded has been added to Supplementary Material (Supplementary Figure 2) and the manuscript text has been revised with the information that data from the three replicates are shown, added to the caption to Figure 3D.
Wording/interpretation issues
Lines 114-116: "This intercellular cooperativity facilitates oocyte maturation while simultaneously protecting germ-line genomic integrity, in a manner which could not be achieved by a single cell." This is an overstatement because genomic integrity was not assessed. Why consider that the nuclear function found in the proteome contrast is necessarily associated with genomic integrity. Miosis requires in dept chromatin handling. What evidence provided from the results is associated with cellular numbers. The presence of cumulus cells is known to support meiosis but it doesn't mean that some of the cellular processes have been imparted to the surrounding somatic cells. The work done for this manuscript does not test any of this claim. RESPONSE #47 We accept this point and agree that, especially the claim re germ-line genomic integrity, is an overstatement. This has been removed. We maintain however that there is ample evidence in our results that there is clear inter-cellular metabolic cooperativity between oocyte and cumulus cells and that this ultimately leads to an oocyte with improved developmental competence. The sentence has been modified to reflect this, line 117-118.
On numerous occasions, the statements are imprecise. For example: Line 274: "More than double the number..." Since doubling a minute value does not mean the same thing as doubling a large value, values, measurements with units and ideally with SEM should be added. RESPONSE #48 Has been rephrased (see line 284 of the revised manuscript)
Line 287: "... and almost a third more significant networks..." Please add values. RESPONSE #49 Section has been deleted (line 291-300 of the revised manuscript)
On the same statement, since sample input material to the mass spectrometry is vastly different between cumulus cells and oocytes, is it truly comparable? Could these differences between the two cell types be associated with the amounts of proteins in the extracted samples? Typically, more variable results are obtained with the low input. It sometimes lead to apparently more difference between treatments simply because of low count numbers. On line 292, authors mentioned that protein loading was considered. How was that done? Low input cannot be compensated or normalized. The following statement on line 293 indicate that more proteins were identified in cumulus cells. This is probably due to more input material submitted to mass spectrometry. It is not necessarily a difference in protein diversity between cumulus cells and oocytes. RESPONSE #50 Please refer to detailed explanations under RESPONSES #42 and #43
Line 293: "... resulted in the identification of about double the number..." Please add values. RESPONSE #51 Values added at lines 305-306, and additional detail has been added to this section of the manuscript (lines 305-317 revised manuscript). Line 294: "However, there were 4-5 times as many differentially expressed proteins..." Please add values. RESPONSE #52 Values added and additional detail added to this section (new lines 309-312 of the revised manuscript).
Line 298: "...difference was quite marked..." More factual info should be added. RESPONSE #53 Values added and additional detail has been provided (lines 314-317 of the revised manuscript), as follows; “____Cumulin appeared to have a greater impact on proteomic differential expression in both cell types than BMP15 did, with 59 vs 38 and 34 vs 27 upregulated proteins in cumulin vs BMP15 treated cumulus cells and oocytes respectively, and similarly 14 vs 6 downregulated proteins in cumulin vs BMP15 treated cumulus cells and oocytes respectively (Figure 4C)”.
Line 305: Again, the whole comparison between cell types could be argued from the standpoint of input material subjected to the analysis. Given the point is to state that cumulin has a profound impact on cumulus cells, maybe it is not necessary to compare with the oocyte data. It is logical that an oocyte secreted factor targets the neighbouring cells. The point can be made without raising the question about the potential issue of input material. RESPONSE #54 We agree with the reviewers point that it is logical that OSFs should target cumulus cells, with lesser impact on the oocyte. Nonetheless the treatments were performed on COCs, and even though the OSFs are targeting the cumulus cells, however ultimately the cumulus cells response is expected to impact oocytes. Therefore, it is relevant to look at proteomic changes to both cell types and also the related network analysis. We have however rephrased this section, to be more specific as to which data we are reporting, and have included additional citations (lines 325-334 of the revised manuscript).
__Line 317-317: "... exhibited more rounded and swollen mitochondria..." How was that determined? In the periphery of the oolemma, mitochondria aggregates in clusters which can be quite different from one another. Maybe proportions of different shapes of mitochondria could be provided if enough mitochondria are counted from the EM micrographs. __RESPONSE #55 These are subjective observations of the typical morphological features seen in response to the different treatments. This is the typical application of TEM. Quantitative features of mitochondria are better assessed using confocal than TEM, which is the complimentary approach we took using MitroTracker in the companion figure 5B, the text for which immediately follows the TEM results. We altered the text at the sentence in question to note that these are subjective observations (line 340).
Line 169: What do you mean by "The results were merged based on consistency..."? This seems to be a trivial way to analyse the data. RESPONSE #56 The majority of published papers reporting data dependent analysis (DDA) proteomics results utilise just a single quantitative method (i.e., either spectral counting or peak intensity). This certainly simplifies reporting, and avoids confronting uncomfortable discrepancies between different analytical approaches. However, we reasoned that robust expression change data would maintain consistency, despite the orthogonal quantitative methods. We consider it a notable strength of the approach used here that we have utilised a differentially expressed proteins list which includes only those proteins with consistent direction of fold-change in both the spectral counting and peak intensity workflows. Please also refer to comments under RESPONSE #43, re spectral counting vs peak intensity quantitative methods in data dependent analysis (DDA) proteomics.
Line 170: "A further requirement was that at least one, if not both methods..." Again, when did you decide to use one method or to use both? Why not use the common ground from both methods? RESPONSE #57 Refer also to RESPONSE #43. In fact the main question being asked in many/most proteomics experiments is whether there is a real expression change between treatment groups. Therefore fold-change is the most pertinent common ground across disparate quantitative methodology, and indeed commonality of fold-change was the basis for merging the datasets. Since integrating peak areas is a very different approach to counting the number of spectra, then this difference in approach can make a big difference to the p-values, and is the reason why spectral counting is less sensitive to detect differential expression. For similar reasons the fold-change ratio may differ somewhat between these quantitative methodologies. However direction of fold-change is a minimum requirement for demonstrating consistent trends, hence we used this as the common ground for merging the datasets.
Line 384: Is the paracrine signaling remodeling COC metabolism or is it enhancing the rate at which it is done? I believe this switch in metabolism occurs in untreated COCs. RESPONSE #58 We see the reviewers point in this subtle difference in wording. We agree that there is a switch in metabolism in untreated COCs during maturation – our point is that that process of changing metabolism is further remodelled by oocyte paracrine signals, to the overall betterment of the oocyte in terms of competence. We have edited this sentence to make this point clearer (line 413-415). Our data on energy charge, respiration, energy metabolite levels (Figure 6), redox potential (Figure 7) and mitotracker intensity (Figure 5) are all presented in comparison with “untreated” cells, and our conclusion that there is remodelling of metabolism is therefore relative to “untreated” COCs.
__ __The Discussion is somewhat circular. Section will need to be adjusted if the Mitotracker-based mitochondrial count and between cell types gene/protein lists comparisons are removed.
Accounts for mitochondrial counts: (lines 387-393) (lines 424-427) (line 463).
RESPONSE #59 All reference to Mitotracker in the context of mitochondrial counts only have been altered to Mitotracker being an indicator of mitochondrial function/polarity and/or counts. Accounts for comparisons of gene lists length between cell types: Lines 389-391 and 475-477 and 496-499). RESPONSE #60 Please see comments under RESPONSE # 53 and the new Figure 4C.
Line 395: "... a substantial number of oocyte upregulated proteins... Please provide number. RESPONSE #61 Additional specific proteins have been listed to support our claims of effects on specific processes (see lines 435-443 of the revised manuscript). Also see comments under RESPONSE # 7.
Line 397: The data was not designed to test the potential of cumulin to preserve meiotic fidelity. This is an overstatement since DNA binding is part of the normal course of even during meiosis. Again, cumulin could accelerate the kinetic of meiosis. RESPONSE #62 Reference to meiosis and meiotic fidelity removed, line 435.
__ __Line 402-405: the work was not designed to determine if cumulin would shift work allocation between the oocyte and the cumulus cells. Showing that cumulin drives meosis is interesting by itself.
__RESPONSE #63____ Not clear that any change is requested or needed. This sentence is interpreting the significance of the results, as required in a Discussion.
__Line 453-455: the link with the epigenome is an overstatement. RNA and DNA processing pathways are general cellular processes.
RESPONSE #64____ The link to the epigenome was a reference to some published work. However it was linked to observations in the current data, and additional information has now been added to the updated manuscript to explain this further, as follows (currently lines 509-516);
"These included significantly enriched networks of RNA binding, helicase activity, ribonucleoprotein complex biogenesis, and mRNA processing (supplementary Tables S11 and S12; upregulated proteins RNF20, SHMT1, DHX30, DDX17, DDX5, PRPF19, RPS4X, NOP58, DDX39b, HNRNPF, RPS271, NOP56, PRPF6, POLR2b, CPSF6, OOEP), as well as upregulation of key epigenetic regulators (HDAC2 and UHRF1; see supplementary Table S11), histone modifying protein MTA2, and significant network enrichment of the spliceosomal complex (supplementary Table S12; proteins DDX5, PRPF19, HNRNPF, PRPF6, POLR2B), which has been linked to epigenetic regulation ____[12]____.
Minor details Line 36: I suggest to be more precise on the "nuclear" function that is affected in the oocyte. Given that oocytes are transcriptionaly quiescent at this stage, some might argue that it is a vague statement.
RESPONSE #65____ Information relating to specific oocyte upregulated proteins and their cellular roles has been added to the updated manuscript (currently lines 434-443).
DNA binding and ribosomal constituents (Fig. 4A, 4C),
In vitro should be in italic because it is Latin. RESPONSE #6____6 corrected throughout
__Lines 125-126: are the batch numbers relevant to anything? __RESPONSE #6____7 We would assume so – for the historical record. These are in-house produced proteins, cumulin is complex to produce and only a few labs worldwide have made it.
__Line 168: Mascor = Mascot __RESPONSE #6____8 Corrected
__Line 168: a reference for the software? __RESPONSE #6____9 URL and published references added (lines 172-175 revised manuscript)
Line 178: need a reference for the software? RESPONSE #70 URL and published references added (line 185)
__Line 187: Need a complete source for "Procure, 812" __RESPONSE #71 Added
Line 188: Need a complete source for "Diatome" RESPONSE #72 Added
Line 197: Need a complete source for "Cell-Tak" RESPONSE #73 Added
Line 232: though = through RESPONSE #74 Corrected
Line 243: define OCR RESPONSE #75 Added
Line 268: If I am not mistaking, it is not a multispectral analysis. The multispectral values were analysed through a principal component analysis. RESPONSE #7____6 Data was analysed through linear discriminative analysis (LDA). This information has been added in Line 278.
Line 363: What is the "behaviour" of an oocyte and cumulus cells? RESPONSE #77 replaced with “function”
Line 512-513: Maybe add more on the fact that most clinics use ovulated eggs and do not perform IVM. However, IVM is needed is specific contexts such as PCOS. RESPONSE #78 Edited accordingly; lines 575-577.
Reviewer #3 (Significance (Required)):
Cumulin is the most potent oocyte secreted factor. Its mecanism of action is still unknown.
I have been working on the mammalian oocyte for the past 25 years.
References
- Mester, B., et al., Oocyte expression, secretion and somatic cell interaction of mouse bone morphogenetic protein 15 during the peri-ovulatory period. Reprod Fertil Dev, 2015. 27(5): p. 801-11.
- Hussein, T.S., J.G. Thompson, and R.B. Gilchrist, Oocyte-secreted factors enhance oocyte developmental competence. Dev Biol, 2006. 296(2): p. 514-21.
- Mottershead, D.G., et al., Cumulin, an Oocyte-secreted Heterodimer of the Transforming Growth Factor-beta Family, Is a Potent Activator of Granulosa Cells and Improves Oocyte Quality. J Biol Chem, 2015. 290(39): p. 24007-20.
- Gilchrist, R.B., M. Lane, and J.G. Thompson, Oocyte-secreted factors: regulators of cumulus cell function and oocyte quality. Hum Reprod Update, 2008. 14(2): p. 159-77.
- Sugiura, K., F.L. Pendola, and J.J. Eppig, Oocyte control of metabolic cooperativity between oocytes and companion granulosa cells: energy metabolism. Dev Biol, 2005. 279(1): p. 20-30.
- Campbell, J.M., et al., Multispectral autofluorescence characteristics of reproductive aging in old and young mouse oocytes. Biogerontology, 2022. 23(2): p. 237-249.
- Schwarz, D.S. and M.D. Blower, The endoplasmic reticulum: structure, function and response to cellular signaling. Cell Mol Life Sci, 2016. 73(1): p. 79-94.
- Szklarczyk, D., et al., STRING v11: protein-protein association networks with increased coverage, supporting functional discovery in genome-wide experimental datasets. Nucleic Acids Res, 2019. 47(D1): p. D607-D613.
- Marei, W.F.A., et al., Proteomic changes in oocytes after in vitro maturation in lipotoxic conditions are different from those in cumulus cells. Sci Rep, 2019. 9(1): p. 3673.
- Moorey, S.E., et al., Differential Transcript Profiles in Cumulus-Oocyte Complexes Originating from Pre-Ovulatory Follicles of Varied Physiological Maturity in Beef Cows. Genes (Basel), 2021. 12(6).
- Ramus, C., et al., Benchmarking quantitative label-free LC-MS data processing workflows using a complex spiked proteomic standard dataset. J Proteomics, 2016. 132: p. 51-62.
- Luco, R.F., et al., Epigenetics in alternative pre-mRNA splicing. Cell, 2011. 144(1): p. 16-26.
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Referee #3
Evidence, reproducibility and clarity
The work is interesting. Cumulin is a heterodimer hormone formed of GDF9 and BMP15. It is the main oocyte secreted factor. Being an heterodimer, gene knockout provides very little information about its mechanism of action. The team has a unique form of cumulin that is stable. This is why I think this work is important. However, I found two technical issues: one regarding mitochondrial count using MitoTracker and the other about comparing gene lists between the two cell types when protein input submitted to mass spectrometry differ between the two cell types. It is expected to find more with more input material. The text would need to be adjusted accordingly. Also, there is a lot of free statements and a lack of precision that is annoying. In my opinion, there are many overstatements that are not supported by the data because the work was not designed to test what is stated. The Discussion is very circular as the same statements come back on the next pages.
Detailed review:
The manuscript entitled "Oocyte and cumulus cell cooperativity and metabolic plasticity under the direction of oocyte paracrine factors" reports an in depth analysis of the exposure of cumulus oocyte complexes to either BMP15 or cumulin, the GDF9-BMP15 heterodimer. Impact assessment was done by determining developmental competence of the exposed oocytes, comparative profiling of the proteomes and spectral emissions as well as testing a potential impact at the ultrastructure level by electron microscopy imagery. Mitochondrial respiration as well as abundance of related metabolites was contrasted between the two treatments.
Overall, the work is interesting. It is very difficult to study hormonal heterodimers because they originate from two different genes and they can naturally be found in a monomeric as well as a dimeric state. Such functional analysis cannot be done using gene knockout mouse lines. Genetic disruption provided the background that GDF9 and BMP15 are key oocyte secreted factors however only functional work as the one presented in this manuscript can find the mechanisms of action of these hormones.
Comments:
I really appreciated the reference to auto-symbiosis. We often see the reference to a cellular syncytium but this one is interesting.
Although I appreciated the work, two important technical issues (between cell types comparisons and mitochondrial count) have been raised and there is a bit of unnecessary overselling throughout the manuscript. Sticking to the results would keep the value of the work high and wouldn't give that impression of overstatement.
Technical issues:
While the gene/protein enrichment analysis can be influenced by the input material submitted to mass spectrometry, the gene network analysis is influenced by the number of gene/proteins available for the enrichment analysis. It is thus difficult to compare both cell types.
Also, when performing GO terms analysis, the level of "branching" can explain the results. In other words, GO terms are organized in a tree like structure where general elements (e.g. nucleus) are delineated in finer elements (e.g. nuclear function) leading to finer ones (e.g. DNA binding)... to finer ones (e.g. DNA repair)... etc. The number of genes/proteins available in the initial list directly dictates to which level of precision the analysis can reach. In the present work, the number of identified network may simply reflect the number of elements available in the initial lists. With more info on the cumulus cells side, it is logical to be able to reach finer branches that contain only a few genes. I have looked in the supplemental data files but could not find more info about the background used. Was it all known proteins? Was it all identified proteins where the differentially expressed proteins are compared to the detected proteins? Using the list of detected proteins as background for the analysis could help. Proteome Discoverer generated much less differentially expressed proteins between treatments than Mascot/Scaffold (2-17 vs. 74-390). Maybe use the Mascot/Scaffold data using the same number of top genes (e.g. 87) between both cell types. Then it would be much more comparable.
Line 226 and 324-328 and line 350: I have never seen the use of MitoTracker Orange to count mitochondria. According to the manufacturer: "MitoTracker{trade mark, serif} Orange CMTMRos is an orange-fluorescent dye that stains mitochondria in live cells and its accumulation is dependent upon membrane potential. The dye is well-retained after aldehyde fixation." It is indicative of mitochondrial potential but it is not a method to count the number of mitochondria within a cell. I do not agree that more fluorescence means more mitochondria.
I understand that the MitoTracker data is counterintuitive to the oxygen consumption rate and stable levels of energetic metabolites. However, as the authors mention, mitochondria are known to be capable of switching from aerobic to anaerobic energy production. In some cases, heterogeneity in the mitochondrial population (such as the one in the oocyte) could mean that a mosaic respiratory potential exists where some mitochondria are more aerobic than others... To change the number of mitochondria, either fission or mitophagy must occur. Although mitochondrial DNA replication is done in approximatively 2 h and fission/division can occur over 1 h, and protein ubiquitination is done over 12 h-18 h during mitophagy, TEM micrographs (figure 5) do not show elongated mitochondria in the process of division. To detect active mitophagy, protein markers and association with lysosome would be needed. A shift in mitochondrial number may not be the suitable interpretation of the data.
For the spectral data analysis (Figure 3D), how did the three replicates perform? The figure does not show the replication variance relative to the treatment variance.
Wording/interpretation issues
Lines 114-116: "This intercellular cooperativity facilitates oocyte maturation while simultaneously protecting germ-line genomic integrity, in a manner which could not be achieved by a single cell." This is an overstatement because genomic integrity was not assessed. Why consider that the nuclear function found in the proteome contrast is necessarily associated with genomic integrity. Miosis requires in dept chromatin handling. What evidence provided from the results is associated with cellular numbers. The presence of cumulus cells is known to support meiosis but it doesn't mean that some of the cellular processes have been imparted to the surrounding somatic cells. The work done for this manuscript does not test any of this claim.
On numerous occasions, the statements are imprecise. For example: Line 274: "More than double the number..." Since doubling a minute value does not mean the same thing as doubling a large value, values, measurements with units and ideally with SEM should be added.
Line 287: "... and almost a third more significant networks..." Please add values.
On the same statement, since sample input material to the mass spectrometry is vastly different between cumulus cells and oocytes, is it truly comparable? Could these differences between the two cell types be associated with the amounts of proteins in the extracted samples? Typically, more variable results are obtained with the low input. It sometimes lead to apparently more difference between treatments simply because of low count numbers. On line 292, authors mentioned that protein loading was considered. How was that done? Low input cannot be compensated or normalized. The following statement on line 293 indicate that more proteins were identified in cumulus cells. This is probably due to more input material submitted to mass spectrometry. It is not necessarily a difference in protein diversity between cumulus cells and oocytes.
Line 293: "... resulted in the identification of about double the number..." Please add values.
Line 294: "However, there were 4-5 times as many differentially expressed proteins..." Please add values.
Line 298: "...difference was quite marked..." More factual info should be added.
Line 305: Again, the whole comparison between cell types could be argued from the standpoint of input material subjected to the analysis. Given the point is to state that cumulin has a profound impact on cumulus cells, maybe it is not necessary to compare with the oocyte data. It is logical that an oocyte secreted factor targets the neighbouring cells. The point can be made without raising the question about the potential issue of input material.
Line 317-317: "... exhibited more rounded and swollen mitochondria..." How was that determined? In the periphery of the oolemma, mitochondria aggregates in clusters which can be quite different from one another. Maybe proportions of different shapes of mitochondria could be provided if enough mitochondria are counted from the EM micrographs.
Line 169: What do you mean by "The results were merged based on consistency..."? This seems to be a trivial way to analyse the data.
Line 170: "A further requirement was that at least one, if not both methods..." Again, when did you decide to use one method or to use both? Why not use the common ground from both methods?
Line 384: Is the paracrine signaling remodeling COC metabolism or is it enhancing the rate at which it is done? I believe this switch in metabolism occurs in untreated COCs.
The Discussion is somewhat circular. Section will need to be adjusted if the Mitotracker-based mitochondrial count and between cell types gene/protein lists comparisons are removed.
Accounts for mitochondrial counts: (lines 387-393) (lines 424-427) (line 463).
Accounts for comparisons of gene lists length between cell types: Lines 389-391 and 475-477 and 496-499).
Line 395: "... a substantial number of oocyte upregulated proteins... Please provide number.
Line 397: The data was not designed to test the potential of cumulin to preserve meiotic fidelity. This is an overstatement since DNA binding is part of the normal course of even during meiosis. Again, cumulin could accelerate the kinetic of meiosis.
Line 402-405: the work was not designed to determine if cumulin would shift work allocation between the oocyte and the cumulus cells. Showing that cumulin drives meosis is interesting by itself.
Line 453-455: the link with the epigenome is an overstatement. RNA and DNA processing pathways are general cellular processes.
Minor details
Line 36: I suggest to be more precise on the "nuclear" function that is affected in the oocyte. Given that oocytes are transcriptionaly quiescent at this stage, some might argue that it is a vague statement.
In vitro should be in italic because it is Latin.
Lines 125-126: are the batch numbers relevant to anything?
Line 168: Mascor = Mascot
Line 168: a reference for the software?
Line 178: need a reference for the software?
Line 187: Need a complete source for "Procure, 812"
Line 188: Need a complete source for "Diatome"
Line 197: Need a complete source for "Cell-Tak"
Line 232: though = through
Line 243: define OCR
Line 268: If I am not mistaking, it is not a multispectral analysis. The multispectral values were analysed through a principal component analysis.
Line 363: What is the "behaviour" of an oocyte and cumulus cells?
Line 512-513: Maybe add more on the fact that most clinics use ovulated eggs and do not perform IVM. However, IVM is needed is specific contexts such as PCOS.
Significance
Cumulin is the most potent oocyte secreted factor. Its mecanism of action is still unknown.
I have been working on the mammalian oocyte for the past 25 years.
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Referee #2
Evidence, reproducibility and clarity
Summary:
The report by Richani et al, presents a research carried out in mice, in which they treated cumulus-oocyte complexes with either BMP15 and cumulin. Upon treatment they evaluated a series of biologically relevant parameters in oocytes and cumulus cells. Their findings indicate that the treatment with these molecules alter the molecular composition of oocytes and cumulus cells (proteome and metabolome), mitochondrial morphology in cumulus cells and overall oxygen consumption in COCs.
Major comments:
- Are the key conclusions convincing?
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
- part of the discussion related to metabolic pathways being up regulated due to the treatments need to the revised because For instance, It is hard for me to grasp how a pathway with 2 proteins achieved FDR significance below 0.01, as I see in figure 4c
- In the discussion the authors use the term "oocyte secreted factors" a lot (one example lanes 490, 515, 516, 517), but they should specify BMP15 and cumulin, because these were their treatments.
- Including in the title, you did not evaluate all oocyte paracrine factors, just BMP15 and cumulin
- 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.
NA - 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.
NA - Are the data and the methods presented in such a way that they can be reproduced? - no, in some instances, the methods are not described, see my comment below about enrichment analysis. - Are the experiments adequately replicated and statistical analysis adequate? - I was not able to access enrichment analysis. - lines 241-242: "MitoTracker staining and data from metabolite analysis by mass spectrometry were analysed by one-way ANOVA with Tukey's (parametric data) or Kruskal-Wallis (non- parametric data) post-hoc tests. " Specify which test was used for which data
Minor comments:
- Specific experimental issues that are easily addressable.
NA - Are prior studies referenced appropriately?
Yes - Are the text and figures clear and accurate? - lines 178-180: "expressed proteins list was further analyzed using STRING software to explore clustering and enrichment of specific molecular functions, and biological pathways. Detailed methodology and rationale for this approach is provided in the supplementary methods." I did not read text in the supplementary materials indicating how enrichment analysis was carried out. - What was the concentration of treatment for the samples used for proteome and mascot/scaffold experiments? - lanes 263 and 264: "Cell types and treatment conditions can be clearly distinguished based on these orthogonal global approaches." I did not see what is the basis for this statement - I did not understand the discrepancy between the numbers observed in Figure 3A and Figure 3B. - I could not make sense of the shades of green or red that were used in 4C and 4D. Is the reader only supposed to make those comparisons within column? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions? - Figure 4 is really hard to process. At least in my pdf it spanned 4 pages. - I did not understand why put networks that are not significant as up-regulated or down-regulated. Besides, as mentioned above, I do not know how significance was assessed..
Significance
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. - Place the work in the context of the existing literature (provide references, where appropriate).
This paper is significant because it provided a variety of measurements following the treatment of cumulus cells with BMP15 and cumulin. The authors show that these two oocyte factors can impact the molecular structure, physiology and structure of organelles in cumulus cells. The work is well contextualized with the current literature. - State what audience might be interested in and influenced by the reported findings.
Researchers in the field of developmental biology would be most interested in this report. - 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 do not have expertise in hyperspectral analysis. I have been working with cumulus-oocyte complexes for over a decade, mixing technologies in cell biology, microscopy, high-throughput genome, and proteome analysis. We do all our bioinformatics work in-house.
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Referee #1
Evidence, reproducibility and clarity
Summary:
Cells within multicellular organisms are mutually dependent on each other - cells of one type or in one location provide signals that can regulate the health and differentiation of the target cells that receive those signals. Such signalling can operate bi-directionally, emphasizing the co-dependence of cells upon each other. The ovarian follicle provides an excellent model system to study intercellular signaling and its consequences, in this case between the oocyte and the somatic granulosa cells that surround it. Oocytes secrete members of the TGFbeta growth factor family that are required for normal differentiation of the granulosa cells, which in turn is necessary for normal development of the oocyte. Here the autohors show that adding TGFB-type growth factors (cumulin or BMP15) to the cuture medium during in vitro maturation increases the fraction of oocytes that can reach the blastocyst stage (improved developmental competence) and alters the pattern of protein landscape in both the (cumulus) granulosa cells and the oocyte. Changes in the mitochondria and parameters relevant to energy metabolism are also altered. They conclude that these changes underpin the acquisition of developmental competence by the oocytes.
Major issues:
The authors are world leaders in this field and therefore exceptionally well-qualified to carry out the proposed work. There are a number of issues, however, that limit the confidence with which conclusions may be drawn.
First, the experimental strategy makes drawing inferences about the role of cumulin and BMP15 challenging. Maturing oocytes express GDF9 and BMP15 (the components of cumulin). Thus, the experiments are not comparing presence vs absence of cumulin and BMP15, but rather comparing oocytes and cumulus cells exposed to supra-physiological levels of these factors to controls that are exposed to physiological levels. In other words, the experimental setup detects changes that occur in response to higher than normal levels of the factors. Ideally, one would have complementary experiments where GDF9 and BMP15 were deleted from the system, to illustrate the effects of their absence. This would be a massive additional undertaking, however. Yet, without such experiments, relying on the results of the overexpression approach to understand the functions of cumulin and BMP15 at physiological levels is risky.
Second, the granulosa cells and oocytes interact throughout the prolonged period of growth, and this is the time when the beneficial effects of the granulosa cells on the oocyte have been most clearly documented. Yet the experiments focus on the much shorter period of meiotic maturation. This is when oocyte-granulosa cell interaction is being down-regulated, even if not entirely disrupted.
Third, the data reported illustrate associations or correlations, but no experiments test the function of the changes in the proteome or of the changes in the morphology of the mitochondria or ER. Which if any of these is linked to the improved development of the oocytes after fertilization is unknown. Moreover, no experiments address how the growth factors cause the observed changes, which occur over a period of a few hours.
Taken together, these issues unfortunately limit the potential impact of the work. But the amount of work required to address them would be substantial and not really feasible for this manuscript. The best route may be to present the work as an overexpression study that has identified associations, with a discussion that acknowledges the limitations of this approach.
Minor issues:
The text of the manuscript should be revised in a number of places. 32: We characterized the molecular mechanisms by which two model OSFs, cumulin and BMP15, regulate oocyte maturation and cumulus-oocyte cooperativity.
--Mechanistic studies were not performed.
40: Collectively, these data demonstrate that OSFs remodel cumulus cell metabolism during oocyte maturation in preparation for ensuing fertilization and embryonic development.
--No mechanistic studies demonstrate this.
46: Oocyte-secreted factors downregulate protein catabolic processes, and upregulate DNA binding, translation, and ribosome assembly in oocytes.
--No direct evidence is provided.
48: Oocyte-secreted factors alter mitochondrial number...
--Need to establish that the MitoTracker is a suitable tool to measure the number of mitochondria.
79: ...for maintaining genomic stability and integrity of the oocyte...
83: ...minimizing secondary production of potentially DNA damaging free radicals.
--Please provide supporting references from the literature.
373: This study provides a detailed exploration of the mechanisms by which oocyte-secreted factors...
--No mechanistic studies were performed.
383: Collectively, these data demonstrate that oocyte paracrine signaling remodels COC metabolism in preparation for ensuing fertilization and embryonic development.
--Studies do not show that the differences observed between control and treatment groups are related to fertilizability or embryonic development.
396: suggesting that cumulin affects meiosis in the oocyte and may increase meiotic fidelity...
--This statement is highly speculative.
409: ...lacks the machinery for amino acid uptake...
--Is the oocyte unable to take up any amino acids or only certain amino acids?
In general, the manuscript is written clearly. However, in several places, technical terms or jargon will make tough going for readers who are not already familiar with the techniques being used. These should be explained using language that will be understood by journal readers who are unfamiliar with the details of the techniques.
Examples include:
51: define metabolic workload using scientific terms.
67: metabolically 'inept' requires more precision.
262: explain 'multispectral analysis'
268: how is 'limited' overlap defined.
318: define higher workload
324: provide documentation or citations to support the assertion that the intensity of MitoTracker staining is an accurate proxy for the number of mitochondria.
358: Multispectral discrimination modelling utilised cellular image features from the autofluorescent profiles of oocytes and cumulus cells.
--Please clarify this merthodology and provide support for its utility.
360: intersection of union of 5-22%
Comments on Figures.
Fig. 3A, B. The total number of proteins and the number of differentially expressed proteins among the treatment groups don't match between A and B. For example, A (Mascot-Sheffield) indicates that 17 proteins were differentially expressed between untreated and cumulin-treated oocytes. B shows (138 + 74) expressed un the untreated but not cumulin-treated and (156 + 87) expressed in the cumulin-treated but not untreated. Please account for this difference.
Fig. 3D. What do the circles represent and how were their parameters (size, position) established?
Significance
These studies identify changes in cumulus cells and oocytes that occur in response to addition of cumulin or BMP15 to the culture medium during in vitro maturation. While the data are new, the significance of the advance is limited by (i) the fact that the control group were exposed to physiological levels of GDF9 and BMP15, so this is essentially an over-epxression study and (ii) no mechanistic studies experimentally tested how the observed changes (eg, in quantity of a specific protein) affect the developmental potential of the oocytes or cumulus cells.
Reviewer expertise: growth and meiotic maturation of the mammalian oocyte
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
This manuscript reports an investigation into the metabolic alterations induced by Zika virus (ZIKV) infection in human neuronal progenitor cells. The authors differentiated human iPSCs to derive neuronal progenitor cells (NPCs) at different days of incubation to represent the different stages of foetal CNS development. They found differences in the levels of ZIKV NS1 proteins as well as marginal differences in ZIKV titres in infected early and late hi-NPCs. Correspondingly, they also showed differences in glucose consumption, lipid metabolism and mitochondrial stress in ZIKV-infected early and late hi-NPCs. They concluded that differences in energy metabolism in neuronal progenitors both before and upon infection may contribute to the brain damage observed in congenital Zika syndrome.
The evidence supporting a role for dysregulated metabolism in mediating the pathogenesis of congenital Zika syndrome is gaining traction and findings from this study could add to this body of knowledge. However, in its present form, this study has several gaps that limit the extent to which it informs on the clinical pathogenesis of congenital Zika syndrome.
Major concerns: 1. The most important concern in this study is the strain of ZIKV used in all of the studies. ZIKV MP1751 was isolated from a mosquito and belongs to the African lineage of ZIKV. Unlike the Asian lineage ZIKV isolated from Latin America and French Polynesia, gestational infection with ZIKV of the African lineage has not been clinically associated with increased risk of foetal abnormality. It is thus uncertain how the changes observed in this study relates to the observed neonatal pathology. Perhaps a way to address this issue is to argue that a difference in these lineages it the ability of the virus to evade systemic and endothelial innate immune responses to cross the placental and blood brain barriers (several papers on attenuated ZIKV have shown this data). Once these barriers are breached, strain differences should not materially affect the similar pathogenic processes in neuronal cells, as also been shown by others using the MR766 strain of ZIKV. Such a discussion would be helpful to contextualise the clinical relevance of this study.
The authors agree with the reviewer and have now included a discussion paragraph to address this relevant point. In addition, the authors acquired a strain from the Asian lineage (PRVACB59) and performed a single round side-by-side infection in three patient-derived lines with the two different strains of ZIKV. From the infected samples, the authors measured glucose consumption, lactate release and viral output to demonstrate, within the same research, that in in vitro assays, whereas number of ZIKV particles available to infect pools of brain progenitors is not mediated by tissue tropism/advantage. This data has been included in the extended figure 5.
While the metabolic changes upon ZIKV infection are all interesting, how these changes affect CNS development is unclear. Figure 2F shows marginal impact on productive ZIKV infection and comparable extent of cell death in early and late hi-NPCs. What specific CNS pathology is dependent on the reported metabolic changes?
The authors acknowledge that a correlation of findings from in vitro research and Zika congenital syndrome would be e.g., observing greater differences in cell survival and/or viral replication kinetics. After revisions of the current data, the authors have reanalysed the datasets corresponding to glucose and lactate metabolism, cell survival and viral output and corrected the results and discussion, accordingly. This correction was done due by calculating cell survival/death using lactate dehydrogenase (LDH) readouts. Thus, the data from CCK-8 was replaced due to the conversion of tetrazolium-based salts are metabolically depending on NAD+ and mitochondrial function– which may well have skewed the results as Zika virus potentially alters mitochondrial homeostasis. The preliminary graphs presented in the previous version of this manuscript are presented in the extended data figure 8 for comparison purposes. Datasets corrected for LDH mirror the in-vitro observations in which Zika-infected early hi-NPCs exhibit greater cell death than late hi-NPCs – this may potentially translate to the fetal pathogenesis observed over different trimesters. The corrected data also shows a significantly greater ZIKV release from late hi-NPCs at 48 and 56 h.p.i. suggesting a window of efficient replication in these cells. Lastly, the authors have expanded the conclusion paragraph highlighting intrauterine pathogenesis correlated with impaired brain metabolism to link how metabolic changes induced by ZIKV may correlate with pathophysiological phenotypes aggravated during early trimesters.
Figure 2D: The most remarkable virological difference observed is the significant difference in cytoplasmic NS1 levels between early and late hi-NPCs at 56 hpi. Although the data in Fig 2D in general could have been compromised by the quality of the anti-NS1 mAb (the anti-E assay in Fig 2E used polyclonal antibody), it would have been useful to test for NS1 expression using western blot on a denaturing gel (and appropriate anti-NS1 antibody). The mAb used in this study binds a conformational epitope on NS1. The difference in data in Figure 2D and 2E could thus have been misfolding of NS1. Misfolded NS1 could contribute to ER stress that could be important for dysregulated CNS development. A more detailed investigation of the finding in Figure 2D could be highly informative.
The authors appreciate the comments and hypothesis that NS1 detection may have been compromised due to potential misfolding. This hypothesis was tested by the authors showing no detection of NS1 by denaturing western blot with the referred antibody. However, before using a different NS1 antibody to investigate this potentially relevant phenomenon, the authors attempted to detect NS1 by flow cytometry using fewer markers than in the previous experiments. The authors decided to take this approach due to, although to low levels, NS1 was detected by imaging flow cytometry at early timepoints. When using a combination of markers that did not compromise the signal of NS1 by light compensations and low signal secondary fluorophore, the authors successfully detected NS1 and to similar levels of the Envelope protein. Thus, the authors discarded the possibility that the lowered levels presented in the previous version were due to misfolded NS1. The graphs within Figure 2 have now been corrected with this newly generated dataset.
Figure 3A and related text: The fold-change in GLUT1, HK-1 and GAPDH expression are shown in log10 scale. In this scale, 1 would indicate 10-fold increase in expression. The data in Figure 3A are entirely inconsistent with the description in the related text. Which is correct?
The authors thank the reviewer and would like to highlight that both the Figure 3A and its description were correct in the previous version of this manuscript. The description of the data, however, may have been misleading and unclear thus, the authors have amended the text for clarity. Figure 3 displays the fold-change of key glycolytic genes in early and late Zika infected hi-NPCs, each normalised to their respective controls. The in-text description, besides highlighting this important feature of the ZIKV infection in hi-NPCs, it highlight a more important finding correlated to the significances computed when compare the ratio of fold change between infected early and late hi-NPCs.
Minor concerns:
- Figure 5: The effects of ZIKV infection on the mitochondria of hi-NPCs are interesting and the comparison between ZIKV-infected and uninfected cells in the same culture is a strength of this study. It would be helpful to readers if the authors could include a discussion on the kinetics of ZIKV infection; diminished differences at 48 and 72 hours could be due to the mixture of cells infected at inoculation and hence observed at 24 hours and newly infected cells that were negative for ZIKV E protein at 24 hours. Emphasis should thus be on the 24 h data in Figures 5 C-E.
The authors thank the reviewer for highlighting the relevance of our experimental approach. The authors also thank for the interpretation of the data focused at early timepoints during the infection kinetics of ZIKV when the metabolic alterations are likely to be exclusive from cells infected at inoculation. The discussion of the data in this new revision of the manuscript emphasises the results based on the kinetics of infection and also clarify and strengthen the findings on Env+ and Env- cells within the pool of infected cells.
- Hi-NPCs likely have a diploid genome and thus a finite lifespan. Using the term "cell line" to describe these cells is technically incorrect. Please consider using other terms, such as cell strain.
The authors appreciate the comment and have amended the text accordingly. The authors decided to use the terminology patient line.
Discussion section, 3rd paragraph, lines 6-7. The authors suggest thermal decay as an explanation for their observation yet Figure 2B argues against this explanation. Moreover, Kostyuchenko et al (Nature 2016; 533:425-8) have also shown that ZIKV is relatively thermostable. This explanation offered by the authors lack supporting evidence.
The authors thank the reviewer for the observation. Regarding the discussion on thermal decay, the authors aimed to highlight that circulating virions without available hosts to continue replication (due to cell death) may suffer from thermal decay as the difference in collection timepoints exceeds the tested 3 h reported in this research (Fig 2B). The results from Kostyuchenko et al (Nature 2016; 533:425-8) show thermal stability of ZIKV at different ranges of temperature yet, similar to Fig 2B, only under 2 h. Unpublished data from our group using an FFU assay shows that infectivity of ZIKV virions decrease after 10 h at 37C, knowledge that was used for the discussion. Moreover, the authors have strengthened the discussion by including in the discussion the native immunity of hi-NPCs at different stages of differentiation.
Discussion section, 3rd paragraph, line 16 and Supplementary Figure 2. I believe the authors are referring to Supplementary Figure 3 and not 2. The indentations observed could be due to ZIKV replication although the data, as presented is not convincing. Co-staining for ZIKV E protein would be useful.
The authors have corrected the issue and confirm that the reference to potential replication sites of ZIKV was made to the Extended Figure 3 rather than 2. To strengthen these findings, the authors have now acquired nuclear data by confocal imaging of infected late hi-NPCs co-stained for ZIKV E protein and DAPI. Representative images are included in the Extended Figure 6.
CROSS-CONSULTATION COMMENTS
- I fully agree with both Reviewers #2 and #3 on the quality of the immunofluorescence images and that these images alone are not sufficiently convincing to support the inferences the authors are making.
The authors would like to clarify that the confocal imaging displayed in the current manuscript was not used for the interpretation of the data but rather validation of the immunostaining used in fluorescence flow cytometry. The nuclear screening comprised the only result generated from microscopy analysis. The bulk of data presented on this manuscript was generated by imaging flow cytometry (Imagestream) due to the higher degree of unbiased screening and the larger sample size. The authors acknowledge that Imagestream produces low quality immunofluorescence imaging compared to confocal imaging but believe this is justified by the greater data and unbiased analysis offered by imaging flow cytometry. The power of analysis displayed in this research is unlikely to be achieved by confocal microscopy in which no more than 1.000 cells are screened whilst the authors screened 10.000 cells from each patient line to generate each dataset. Lastly, the authors acknowledge the lack of robustness in the images from nuclei and ZIKV replication thus, for late hi-NPCs in which the perinuclear replication sites where evident, data was acquired by confocal imaging; samples co-stained for ZIKV E protein and nuclei DAPI (Extended Figure 6).
- I also appreciate the first major comment from Reviewer #3. That is important insight and the authors should test their assumption that they have monocultures of human progenitor cells.
The authors have paraphrased the document for better clarity and accuracy as consider the text was confusing causing misinterpretation of the data. This research is intended to show the impact of ZIKV in two pools of cortical progenitor cells (less and more differentiated/mature) clustered by their distinct metabolic profiles rather than single cell types present at different stages of brain development. Both early and late hi-NPCs comprise pools of cells generated during hiPSC differentiation of cortical progenitors. The authors showed in Fig.1 that both pools have brain identity and express several brain markers to similar levels. When gating these cells by populations present in the developing brain small differences were observed exclusively in one out of three subgroups. Nevertheless, the main distinction of these two populations was due to significant differences in their metabolic profile. Thus, the results obtained in this research are likely to obey to the metabolic maturation of early and late hi-NPCs rather than the percentages of different brain cell types present within these pools.
Reviewer #1 (Significance (Required)):
The focus on the metabolism and mitochondrial stress in ZIKV infected neuronal progenitors is interesting and could fill an important gap in knowledge on Zika pathogenesis. The study uses human iPSC derived NPCs instead of animal cells, which is also more clinically relevant than animal models. The findings would thus be of interest to all who are interested in Zika pathogenesis as well as therapeutic/vaccine development. If the above concerns could be addressed, the findings in this study could form the missing links in our current understanding of congenital Zika syndrome.
Expertise: Flavivirology and immunology. Flavivirus-host interactions.
The authors thank the reviewer for the comments provided to improve several aspects of the current research. The authors also thank the reviewer for the positive feedback and for highlighting the relevance of our research.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In the manuscript entitled "Zika virus-induces metabolic alterations in fetal neuronal progenitors that could influence in neurodevelopment during early pregnancy", Javier G.-J. and colleagues investigated the role of cellular metabolism during ZIKA virus infection in hiPSC-derived neural progenitor cells (NPC) at different stage of differentiation. Indeed, the authors use a modified protocol of 2D cultures to obtain early-hiNPC and by continuing the cultures for two additional passages, they obtain late-hiNPCs. These two cell populations are characterized by cell morphology and marker expression. Then they test their susceptibility to ZIKV infection and show that late-hiNPCs are more efficient than early- hiNPCs to support viral replication. Moreover, authors demonstrate that the two cell populations are characterized by different cellular metabolism as glucose consumption is higher in early-hiNPCs than in late-hiNPCs although the overall glycolytic capacity is not different between the two subtypes. However, during ZIKV productive infection, late-hNPCs increased the glucose consumption (Fig. 3). The authors examined the mitochondrial alterations during infection showing different kinetics in early vs. late hiNPCs. Then, they show alterations of expression in genes of the lipid metabolism and content of lipid droplets that follow different kinetics of expression during infection in early vs. late hiNPCs. Overall, no significant differences were observed in the lipid droplet homeostasis between the two subtypes. This is a potentially interesting manuscript as they analyze the susceptibility of subtypes of neural progenitors to ZIKV infection and their metabolic alterations before and during infection. However, there are some concerns listed below.
Major issues:
- It is well established that the NPC maturation during neurodevelopment is complex and cells at different stage of maturation play an important role. The authors propose a model that may recapitulate distinct populations of neural progenitors present during neurodevelopment. They use a modified protocol that it is well described. However, the characterization of these NPC subtypes needs to be improved. The pictures selected to be shown in Fig 1B and C do not highlight the morphology of these cells as described in the text.
The authors thank the reviewer for the comment and have improved the description of the morphology of the cells constituting the two pools of cells at different stages of differentiation. In addition, the authors have included a new figure (Extended Fig. 1) with different magnifications of the acquired brightfield images for better representation of the morphological differences observed between early and late hi-NPCS.
Late-hiNPC are more efficient than early-hiNPC in supporting ZIKV replication, however the differences are present exclusively at 56 h post-infection and they are modest (ca. 2-fold). Nevertheless, ZIKV cytopathic effects are similar between the two subtypes at 72 h post-infection. Authors should try to lower the MOI and extend the timing of analysis to up 10 days post-infection. They used MOI of 1, but it would be informative to know whether the different efficiency of viral replication is dependent on the MOI. Furthermore, are the differences between early and late-hiNPCs dependent on expression of entry receptor, or a different interferon response to virus infection or state of cell proliferation?
The authors thank the reviewer for the insights provided on this matter and appreciate the overall positive response towards the research. After several revisions, the authors have corrected the data using a normalisation method that is expected to rely less on cellular metabolism which may well be disturbed during ZIKV infection. Although still modest, differences in virion release between early and late hi-NPCs are observed at 48 and 56 h.p.i. This data matches the increased accumulation of transcripts. Moreover, in the new version of this manuscript, the cytopathic effects are distinct between hi-NPCs. Regarding the reviewer’ comment on MOI. The authors selected the MOI of 1 due to metabolic dysregulations due to viral infection require a good proportion of cells infected with the inoculum. To support this, the authors highlight the comments from reviewer 1 whom encouraged that the main interpretation should be done at the 24 h timepoint as the population is reflecting alterations due to the initial round of infection rather than differences potentially being masked by cells at different stages of ZIKV replication. In addition, MOI of 1 has been reported elsewhere for ZIKV and other flaviviruses. Although it sounds interesting to the authors the lower MOI exposure for longer period of times, this approach is not feasible to conduct in our models as early hi-NPCs have a length of 3-4 days in culture due to exacerbated cell proliferation. After this time, cells need to be passaged. Similar technical complications will be faced if extending the infection times in late hi-NPCs as these cells require passaging/freezing after day 5. Lastly, the authors consider studying the expression of entry receptors in early and late hi-NPCs to be important in explaining potential differences in viral kinetics yet, the lack of differences in virion release at early timepoints of infection suggest the entry and length of the ZIKV replication cycle is conserved between early and late hi-NPCs. Thus, differences during the ZIKV kinetics potentially due to other mechanisms. For this reason, the authors have included a discussion paragraph in which they highlight potential differences may be due to the development of the native immunity of hi-NPCs during differentiation. It is still controversial whether IFN responses are significant in hi-NPCs, with research suggesting that greater IFN responses are observed upon maturation of NPCs.
The authors state that that this is the first report showing differential changes in nuclear morphology between neural progenitor cells. They show a main finding that is the perinuclear centers only visible in late but not in early-hiNPC in a supplemental figure. These results are not convincing, and an effort should be made in order to support these claims.
The authors have now addressed this issue by using confocal microscopy and co-stained DAPI (nuclei) and ZIKV envelope protein to better show the perinuclear centres in late hi-NPCs (Extended Fig. 6). Confocal images of early hi-NPCs with non-perinuclear replication centres than late hi-NPCs was not possible to acquire as early hi-NPCs did not adhere to glass coverslips for more than 24 h.
Gene expression should be supported by data of protein expression (western blot) of some of the enzymes reported in Fig. 5.
The authors have detected some of the proteins (western blot) involved in lipid metabolism in both early and late hi-NPCs. The authors screened for FASN, PDK2 and ACACA to validate the findings at the mRNA level. The authors selected 56 h.p.i. as a timepoint to measure proteins mainly due to high ZIKV infection levels but not abundant cell death that facilitates obtaining sufficient material for WB. The image of the WB is included in the Extended Fig. 4 of the new version of this manuscript.
Minor issues: 1. Since this work is based on in vitro data, I would suggest using the term infection rather than challenge when referring to infection experiments.
The authors have edited the document and replaced the terminology for what was suggested by the reviewer.
Improve quality of the graphs. Enlarge symbols as in Fig. 6. Try to use linear scales as the differences are not dramatic and a linear scale would highlight them better.
The authors thank the reviewer for the observation on the graphs. The authors have enlarged the symbols where possible – in some cases this could not be conducted as otherwise the error bars were not visible for example when displaying the viral output. The authors appreciate the comment on plotting the data on a linear scale to reflect subtle differences to a larger magnitude yet, this may well fit into misleading the interpretation of some results due to the nature of the analysis (e.g., fold-change); where possible, these changes have been applied.
CROSS-CONSULTATION COMMENTS
I agree with all comments of Rev#1 and 3. Some/many of the claims are made without the supporting evidence.
Reviewer #2 (Significance (Required)):
Many papers have reported the efficient ZIKV infection of neural progenitor cells that have been derived from the reprogramming of human pluripotent stem cells (PSC). Most of this literature has not been cited. In fact, ZIKV virus infects human PSC-derived brain neural progenitors causing heightened cell toxicity, dysregulation of cell-cycle and reduced cell growth as reported in many papers. In this manuscript, the advancement consists in having used NPC subtypes that are at different stage of differentiation and having studied their susceptibility to ZIKV infection. Then, the author analyze the fluctations of the glucose and lipid metabolism during infection.
The audiance that is interested in this manuscript are virologists and , in particular, experts in arboviruses that are for the most part neurotropic viruses. In addition, this is a topic for experts of neurodevelopment.
My expertise is virology. Key words: Zika virus, neural progenitors, antivirals.
The authors thank the reviewer for the productive constructivism provided to this research. We would like to highlight that most of the literature in Zika infection and hi-NPCs was not included as this does not directly focuses on metabolism. However, as the document has been amended, some of this literature has now been included to contextualise the current knowledge of ZIKV infectivity in relevant in vitro systems.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary The authors present the analysis of the cellular metabolism in Zika virus-infected human neural cell cultures differentiated from fibroblast-derived hiPSCs. Neural cell cultures from days 12-15 after hiPSC induction to neuronal lineages were designated as 'early neuronal progenitors' (early hi-NPCs), while cultures from days 18-21 post induction were designated as 'late neuronal progenitors' (late hi-NPCs). The outcomes of ZIKV infection in both types of neural cell cultures were analyzed. The authors first characterized several viral parameters of infection including accumulation of viral RNA and proteins and ZIKV replication, as well as nuclear morphology of infected cells. The major body of evidence in the presented study encompasses the comparative analysis of several parameters of glucose and lipid metabolism as well as mitochondrial function and cellular lipid accumulation and storage. The authors postulate that ZIKV replicates differentially in early and late hi-NPCs, inducing some common metabolic responses like upregulated glycolytic capacity, as well as responses unique to either early or late differentiation stage of the neural cultures like the lipid metabolism, lipid droplet homeostasis or mitochondrial function. The authors propose that the differential metabolic responses to ZIKV infection in early and late neural progenitors might help to explain the differences in the fetal brain damage in early or late pregnancy.
Major comments 1. The authors refer to the induced neural cell cultures as monocultures of human neural progenitors. This assumption is incorrect and it undermines the proper interpretation of the presented data. The neural lineage induction of iPSC produces neural cell cultures, which depending on the differentiation stage consist of neural stem cells of neuroepithelial-like morphology (Nestin and Sox-2 positive) which differentiate further to more elongated early progenitors with radial glial cell morphology (Nestin, sox2 and PAX-6 positive). Radial glial cells differentiate further into several neural lineages including oligodendrocyte precursors, astrocytes (S100B - positive) and intermediate progenitors (TBR2 - positive). The intermediate progenitors then divide to produce one progenitor and one post mitotic immature neuron (still TBR-positive and also beta II tubulin, Tuj1/TuB3-positive). The neurons then mature further and become NeuN and MAP2-positive. All the above mentioned differentiation markers were used by the authors to characterize the early and late cell cultures. According to the data presented in Fig 1E, both cultures were positive for all the markers indicating that they are not monocultures. The immunofluorescence data provided in Extended Fig.1 in support of the analysis presented in Fig. 1E clearly shows that both cultures stain similarly for Tuj1 (also known as TuB3), a marker of post-mitotic neurons, which are clearly present in both cultures. Abundant MAP2 positive cells (marker of mature neurons) in "early hi-NPCs" presented in extended figure 1B is quite surprising and confusing and is not presented for 1A panel - "late hi-NPCs", which suggests that perhaps figure 1A and 1B were mislabeled. The immunostaining for PAX6 presented in the same figure 1B presents strong cytoplasmic staining while PAX6 is expected to be detected in the cell nucleus, suggesting that the red staining comes most probably from the overexposed background. On a closer look the PAX6 staining presented on panel 1A shows weak and underexposed but most probably positive nuclear staining. Of note, the authors argue that the only significant difference in the staining for differentiation markers was observed for PAX6 (early neural progenitor marker) which was higher in late cultures than the early ones. In the same figure all the pictures in red are generally underexposed except from PAX6, while the DAPI staining is overexposed. This makes the interpretation of the data difficult especially when looking at the merged images. Despite the overall confusion with this part of results it is clear that the early and late cultures consist of different cell types including early and intermediate progenitors as well as astrocytes (S100B - positive), probably glial cells (not tested for) and post-mitotic neurons. The relative ratio of these populations might be different in the two cultures, however the cultures are not monocultures of early or late neural progenitors. They might contain different ratios of both and thus respond differently to the infection. Therefore, the metabolic and virological analysis performed globally on these cell cultures might just as well reflect the cell type ratio related effects rather than the differential responses of the early or late progenitors. This has never been addressed or explained by the authors.
The authors thank the reviewer for the comment and observation regarding the nomenclature used in the preliminary version of this document. The authors used the terminology “subtypes” not to refer as a monoculture of a particular cell type within the developing brain but to the group of cells that share a metabolic profile. This was due to the abundance of markers to characterize cellular lineages within each population reflected to be similar at the two stages of differentiation. The authors showed cell type differences only in the ratio of glial Pax6 +ve cells (Fig. 1D) whilst greater significant differences were observed in the metabolism between both cultures. Thus, differences to viral responses are most likely to obey to the maturation stage (longer times under culture) rather than different ratio of brain cells. Nevertheless, the authors acknowledge the confusion that the terminology “neuronal subtypes” could have caused and have changed it to “cortical progenitors at different stages of differentiation” or “hi-NPCs”. The authors would like to address the reviewer’ comment on the data presented in Extended Fig. 2 (MAP2 staining in early hi-NPCs). This is not a mislabel between the figure but rather a demonstration that the staining was observed in early hi-NPCs. This staining was not performed in late hi-NPCs thus not showed. Moreover, the data used to quantify the presence of brain markers in early and late hi-NPCs was generated by flow cytometry and not by confocal imaging (ICC). The ICC included in the Extended Fig. 2 was used to demonstrate the antibody staining and to discard potential unspecific antibody binding that may generate false positive detection by flow cytometry. The authors agree with the reviewer that the staining for Pax6 was not clear in the previous version of this manuscript and have redone the figure.
The data presented is often based on the analysis of the immunofluorescence images, however the quality of the images presented (resolution, magnification, over or under saturation) is often insufficient to support the findings and claims. The most striking example are images supporting the analysis of nuclear morphology in ZIKV-infected cells presented in the Extended figure 2.
The authors thank the reviewer and would like to clarify that, although displaying some confocal images within the figure, the graphs were generated from data collected by imaging flow cytometry (Imagestream). In response to the comments from reviewer 1 and 2, the authors explained the advantages and disadvantages of using Imagestream over confocal imaging. The main rationale behind this is the greater sample size and unbiased acquisition of data yet compromising the immunostaining resolution. Regarding the displayed confocal images within the text, the authors have redone the figures and/or acquired new images to correct the issues of oversaturation/overexposure. The authors acknowledge that the data interpretation from the nuclear imaging needs to be done with caution due to its low quality yet, as early hi-NPCs do not adhere to glass as efficiently as late, any confocal acquisition will be limited to plastic-based materials ending in lower resolution. Thus, thanking the reviewers for the observation, the authors have now conducted confocal microscopy co-stained for ZIKV envelope protein and nuclei (DAPI) in late hi-NPCs to better display the nuclear morphology upon infection and the replication centres.
Some of the claims are made without the supporting evidence. For example in the discussion the authors claim that "Our main finding was that viral perinuclear replication centers (26) (white arrows, Supplementary Figure 2) were only visible in late hi-NPCs and not in early hi-NPCs". This conclusion is made based presumably on Extended Figure 3 (Figure 2 does not have arrows) based on the nuclear morphology of infected cells without staining for any of the viral proteins localizing to the replication centers. Despite low image quality similar crescent-shaped nuclei to the ones indicated by the arrows in "late hi-NPCs" and many more of them are visible in "early hi-NPCs" (Extended Fig.2), however the authors seem ignore them.
The authors thank the reviewer for the comment and notify that the respective amendments have been done. The data presented in the new version of this manuscript related to the nuclear morphology is from a new dataset of co-stained ZIKV envelope and DAPI (Extended Fig. 6).
Based on the arguments presented above the conclusions are not convincing, lacking the supporting evidence or ignoring some of the essential facts of the chosen experimental system.
The authors thank the reviewer for the criticism on the research and notify that several changes throughout the document have been made to support the claims and conclusions of this manuscript.
The study in presented form, where all the analysis is performed in globally is not informative and would require the characterization of the metabolic and virological responses in different cell populations as characterized by the expression of neural differentiation markers. Alternatively, the population sizes of different types of cells should be determined and accounted for when analyzing the experimental data. It should be determined which types of cells are targeted by the Zika virus and replicate the virus. It could be done by, for example, co-staining for viral and neural differentiation markers. This would however require the entirely different experimental approach from the one presented in this manuscript.
The authors thank the reviewer for the comments and inputs provided to our research. We would like to highlight that, although it would be highly relevant to distinguish ZIKV infection and metabolic dysregulations in different cell populations; all the published literature in neuronal progenitors and ZIKV infection do not contain insights on the infection per cell populations. This may be due to the difficulties in isolating/sorting populations of immature cells within the pool of in vitro cortical differentiation whilst achieving significant cell survival. The authors would like to address this comment by highlighting that the population sizes of different types of cells within the pools of early and late hi-NPCs was accounted as a starting point of this research (Fig 1D). This characterization was done using a commercially available kit aimed for the sorting of human neural stem cells. These results showed small differences in the ratio of cell types present in early and late hi-NPC cultures. ZIKV has been reported to target all brain cells with lower impact on mature neurons, which arguably will be present in either of the cortical progenitor pools used for this research. Thus, the authors focused on interpreting the results as an impact of ZIKV infection in the overall metabolism of each pool of hi-NPCs used in this study. Metabolism that is likely influenced by most of the cell types present within each hi-NPC pool.
Some methods are not explained clearly. For the metabolic analysis like Oleic acid oxidation and others, it is not clear at which step of the protocol ZIKV infection was performed. In "Extracellular lactate measurement" freshly made running buffer is mentioned but no composition of the buffer is provided.
The authors thank the observation of the reviewer and have now amended the method section to clearly state several methods that could have been difficult to understand in the previous version of this manuscript.
Minor comments 1. Figure 2G shows the survival of ZIKV-infected hi-NPC subtypes. Clearly for "late hi-NPCs" there is 50% cell death at 56 hours post infection and about 70% death at 72 hours. Subsequent analysis of many metabolic parameters is measured at 56 and sometimes even at 72 hours when the significant differences in responses are observed for example Fig. 3 B and C. The role of cell death in the critical analysis of these parameters is not provided.
The authors appreciate the reviewers’ comment and would like to emphasise that all the analysis at every timepoint during ZIKV infection was normalised to the cell number present at the time. The use of different timepoints for different measurements (e.g., 56 and 72 h.p.i.) were selected by the authors to adjust the used methodology. In short, 56 h.p.i. was used as the last timepoint to study mitochondrial and lipid dysregulations by imagestream as we observed the highest viral output with sufficient cell survival in early hi-NPCs; 72 h.p.i. will not give sufficient cell number for counting 10.000 cells by Imagestream. However, 72 h.p.i. was used to assess the genetic expression of metabolically relevant genes as the material obtained was sufficient and will signify the interpretation of the latest point during the ZIKV kinetics in our models.
There are multiple spelling mistakes throughout. The professional terminology of the virology part of the study is often missing. Example the levels of ZIKV RNA measured in the infected cells are designated as "transcriptional levels of ZIKV" which seems incorrect as the level of the genomes is the effect of viral replication and not transcription.
The authors thank the reviewer for the observation made and have corrected the terminology throughout the document. The spelling has been checked.
CROSS-CONSULTATION COMMENTS
Agree with Rev #1 comment on Fig 2D and the levels of NS1. It is striking that the levels of expression drop below the level detected at 48h while the ZIKV E protein continues to accumulate (Fig. 2E) at the same time. Both proteins are translated from the same polyprotein and are processed similarly. It is also confusing that at 48h only about 5% live cells express NS1 while at the same time 15% of live cells express E protein. In my experience both proteins are expressed in all infected cells. The reason why 10% of infected and still alive cells would express only E and not NS1 is difficult to conceive.
The authors have addressed this issue and highlighted that the limitations of the Imagestream technique may have caused this oddity due to loss of signal detection by compensation. The experiments conducted to correct this manuscript include a new detection by flow cytometry using a smaller panel of markers and labelled-secondary antibodies that will provide greater signal. This approach has demonstrated that detection levels of NS1 mirror those of Envelope.
I stand with the Rev #1 in asking what specific CNS pathology is dependent on the reported metabolic changes? There is no attempt to link the findings to ZIKV-induced CNS pathologies.
The authors have included discussion paragraphs to link the observed phenotypes during ZIKV infection to relevant CNS pathologies.
In relation to major comment 2 from the Rev #2, I disagree that Late-hiNPC are more efficient than early-hiNPC in supporting ZIKV replication. 2-fold difference in a viral plaquing assay falls within the error of the assay which is usually quite substantial for the plaquing assay. Lack of error bars for late hi-NPCs 56 h raise my suspicion as to how real is this effect in viral replication.
The authors would like to clarify that the error bars were present in the graph but the size of the symbol difficulted the visualisation. After correcting all the datasets to a less dependent metabolic assay (LDH based survival), the differences in virion release are observed at 48 and 56 h.p.i., like that of ZIKV replication measured by qPCR. The authors also clarify that, although a 2-fold difference may fall within the technical error of plaque assay, minor differences observed in our research are potentially greater if displayed in a different form as our analysis comprises three independent ZIKV infection conducted in three patients’ lines and further normalisation to cell number.
I stand behind Rev #2 major comment 2 there there is no evidence to support the claims about the nuclear morphology or the replication centers
This issue has now been addressed (Extended Fig. 6).
Reviewer #3 (Significance (Required)):
Despite global research efforts the course of Zika virus infection of the fetal brain during pregnancy is not clear. Among many knowledge gaps, the molecular determinants of differential outcomes of Zika virus infection during early or late pregnancy are unknown. The study aims to address this highly significant issue by focusing on the metabolic responses of cells to infection. In the presented form the study however, fails to deliver significant progress in our understanding of Zika virus infection of developing fetal brain. The experimental design and the quality of presented data does not allow to make unbiased conclusions and to support the claims. My expertise is in iPSC-derived neural cell cultures, molecular virology, in particular that of Flaviviruses like Zika virus and hepatitis c virus and confocal microscopy. I am not familiar with metabolic techniques and I find the description of methods for this part of the study insufficient to fully understand the experimental approach.
The authors thank the reviewer for the valuable inputs provided to the research. We would like to highlight that, whereas possible, new sets of experiments have been conducted to better support some of the conclusions and claims. Lastly, the authors would like to mention that the method section has been corrected for a better understanding of the metabolic assays and data normalisation. Within the text, paragraphs have been added to clarify the nature of the results and data acquisition.
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Referee #3
Evidence, reproducibility and clarity
Summary
The authors present the analysis of the cellular metabolism in Zika virus-infected human neural cell cultures differentiated from fibroblast-derived hiPSCs. Neural cell cultures from days 12-15 after hiPSC induction to neuronal lineages were designated as 'early neuronal progenitors' (early hi-NPCs), while cultures from days 18-21 post induction were designated as 'late neuronal progenitors' (late hi-NPCs). The outcomes of ZIKV infection in both types of neural cell cultures were analyzed. The authors first characterized several viral parameters of infection including accumulation of viral RNA and proteins and ZIKV replication, as well as nuclear morphology of infected cells. The major body of evidence in the presented study encompasses the comparative analysis of several parameters of glucose and lipid metabolism as well as mitochondrial function and cellular lipid accumulation and storage. The authors postulate that ZIKV replicates differentially in early and late hi-NPCs, inducing some common metabolic responses like upregulated glycolytic capacity, as well as responses unique to either early or late differentiation stage of the neural cultures like the lipid metabolism, lipid droplet homeostasis or mitochondrial function. The authors propose that the differential metabolic responses to ZIKV infection in early and late neural progenitors might help to explain the differences in the fetal brain damage in early or late pregnancy.
Major comments
- The authors refer to the induced neural cell cultures as monocultures of human neural progenitors. This assumption is incorrect and it undermines the proper interpretation of the presented data. The neural lineage induction of iPSC produces neural cell cultures, which depending on the differentiation stage consist of neural stem cells of neuroepithelial-like morphology (Nestin and Sox-2 positive) which differentiate further to more elongated early progenitors with radial glial cell morphology (Nestin, sox2 and PAX-6 positive). Radial glial cells differentiate further into several neural lineages including oligodendrocyte precursors, astrocytes (S100B - positive) and intermediate progenitors (TBR2 - positive). The intermediate progenitors then divide to produce one progenitor and one post mitotic immature neuron (still TBR-positive and also beta II tubulin, Tuj1/TuB3-positive). The neurons then mature further and become NeuN and MAP2-positive. All the above mentioned differentiation markers were used by the authors to characterize the early and late cell cultures. According to the data presented in Fig 1E, both cultures were positive for all the markers indicating that they are not monocultures. The immunofluorescence data provided in Extended Fig.1 in support of the analysis presented in Fig. 1E clearly shows that both cultures stain similarly for Tuj1 (also known as TuB3), a marker of post-mitotic neurons, which are clearly present in both cultures. Abundant MAP2 positive cells (marker of mature neurons) in "early hi-NPCs" presented in extended figure 1B is quite surprising and confusing and is not presented for 1A panel - "late hi-NPCs", which suggests that perhaps figure 1A and 1B were mislabeled. The immunostaining for PAX6 presented in the same figure 1B presents strong cytoplasmic staining while PAX6 is expected to be detected in the cell nucleus, suggesting that the red staining comes most probably from the overexposed background. On a closer look the PAX6 staining presented on panel 1A shows weak and underexposed but most probably positive nuclear staining. Of note, the authors argue that the only significant difference in the staining for differentiation markers was observed for PAX6 (early neural progenitor marker) which was higher in late cultures than the early ones. In the same figure all the pictures in red are generally underexposed except from PAX6, while the DAPI staining is overexposed. This makes the interpretation of the data difficult especially when looking at the merged images. Despite the overall confusion with this part of results it is clear that the early and late cultures consist of different cell types including early and intermediate progenitors as well as astrocytes (S100B - positive), probably glial cells (not tested for) and post-mitotic neurons. The relative ratio of these populations might be different in the two cultures, however the cultures are not monocultures of early or late neural progenitors. They might contain different ratios of both and thus respond differently to the infection. Therefore, the metabolic and virological analysis performed globally on these cell cultures might just as well reflect the cell type ratio related effects rather than the differential responses of the early or late progenitors. This has never been addressed or explained by the authors.
- The data presented is often based on the analysis of the immunofluorescence images, however the quality of the images presented (resolution, magnification, over or under saturation) is often insufficient to support the findings and claims. The most striking example are images supporting the analysis of nuclear morphology in ZIKV-infected cells presented in the Extended figure 2.
- Some of the claims are made without the supporting evidence. For example in the discussion the authors claim that "Our main finding was that viral perinuclear replication centers (26) (white arrows, Supplementary Figure 2) were only visible in late hi-NPCs and not in early hi-NPCs". This conclusion is made based presumably on Extended Figure 3 (Figure 2 does not have arrows) based on the nuclear morphology of infected cells without staining for any of the viral proteins localizing to the replication centers. Despite low image quality similar crescent-shaped nuclei to the ones indicated by the arrows in "late hi-NPCs" and many more of them are visible in "early hi-NPCs" (Extended Fig.2), however the authors seem ignore them.
- Based on the arguments presented above the conclusions are not convincing, lacking the supporting evidence or ignoring some of the essential facts of the chosen experimental system.
- The study in presented form, where all the analysis is performed in globally is not informative and would require the characterization of the metabolic and virological responses in different cell populations as characterized by the expression of neural differentiation markers. Alternatively, the population sizes of different types of cells should be determined and accounted for when analyzing the experimental data. It should be determined which types of cells are targeted by the Zika virus and replicate the virus. It could be done by, for example, co-staining for viral and neural differentiation markers. This would however require the entirely different experimental approach from the one presented in this manuscript.
- Some methods are not explained clearly. For the metabolic analysis like Oleic acid oxidation and others, it is not clear at which step of the protocol ZIKV infection was performed. In "Extracellular lactate measurement" freshly made running buffer is mentioned but no composition of the buffer is provided.
Minor comments
- Figure 2G shows the survival of ZIKV-infected hi-NPC subtypes. Clearly for "late hi-NPCs" there is 50% cell death at 56 hours post infection and about 70% death at 72 hours. Subsequent analysis of many metabolic parameters is measured at 56 and sometimes even at 72 hours when the significant differences in responses are observed for example Fig. 3 B and C. The role of cell death in the critical analysis of these parameters is not provided.
- There are multiple spelling mistakes throughout. The professional terminology of the virology part of the study is often missing. Example the levels of ZIKV RNA measured in the infected cells are designated as "transcriptional levels of ZIKV" which seems incorrect as the level of the genomes is the effect of viral replication and not transcription.
Referees cross-commenting
Agree with Rev #1 comment on Fig 2D and the levels of NS1. It is striking that the levels of expression drop below the level detected at 48h while the ZIKV E protein continues to accumulate (Fig. 2E) at the same time. Both proteins are translated from the same polyprotein and are processed similarly. It is also confusing that at 48h only about 5% live cells express NS1 while at the same time 15% of live cells express E protein. In my experience both proteins are expressed in all infected cells. The reason why 10% of infected and still alive cells would express only E and not NS1 is difficult to conceive.
I stand with the Rev #1 in asking what specific CNS pathology is dependent on the reported metabolic changes? There is no attempt to link the findings to ZIKV-induced CNS pathologies.
In relation to major comment 2 from the Rev #2, I disagree that Late-hiNPC are more efficient than early-hiNPC in supporting ZIKV replication. 2-fold difference in a viral plaquing assay falls within the error of the assay which is usually quite substantial for the plaquing assay. Lack of error bars for late hi-NPCs 56 h raise my suspicion as to how real is this effect in viral replication.
I stand behind Rev #2 major comment 2 there there is no evidence to support the claims about the nuclear morphology or the replication centers
Significance
Despite global research efforts the course of Zika virus infection of the fetal brain during pregnancy is not clear. Among many knowledge gaps, the molecular determinants of differential outcomes of Zika virus infection during early or late pregnancy are unknown. The study aims to address this highly significant issue by focusing on the metabolic responses of cells to infection. In the presented form the study however, fails to deliver significant progress in our understanding of Zika virus infection of developing fetal brain. The experimental design and the quality of presented data does not allow to make unbiased conclusions and to support the claims.
My expertise is in iPSC-derived neural cell cultures, molecular virology, in particular that of Flaviviruses like Zika virus and hepatitis c virus and confocal microscopy. I am not familiar with metabolic techniques and I find the description of methods for this part of the study insufficient to fully understand the experimental approach.
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