- May 2023
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Referee #3
Evidence, reproducibility and clarity
The manuscript "Single molecule visualization of native centromeric nucleosome formation reveals coordinated deposition by kinetochore proteins and centromere DNA sequence" by Popchock and colleagues describes a new high-throughput single-molecule technique that combines both in vitro and in vivo sample sources. Budding yeast centromeres are genetically defined centromeres, which makes them ideal for studying short DNA segments at the single-molecule level. By flowing in whole cell lysates, Cse4 nucleosomes can form under near physiological conditions. Two analytical experiments were performed: endpoint and time-lapse. In the former case, nucleosomes were allowed to form within 90 minutes and the latter case, nucleosome formation was tracked for up to 45 minutes. In addition, well described genetic mutants were used to assess the stability of Cse4 nucleosomes, as well as different DNA sequences (this we particularly liked- well done). Overall, this is a very interesting technique with potential to be useful for studying any DNA-based effect, ranging from DNA repair to kinetochore assembly. This is strong and impactful work, and the potential this kind of microscopy has for solving kinetic problems in the field. We think it's worthy of publication after revising technical and experimental concerns that would elevate the ms significantly.
Major comments:
Statistics are highly recommended for all the data in the ms.
- At what rate is data collected in the TIRFM setup. For clarity for the reader, it is important to provide imaging details for time-lapse. What is the impact of photobleaching on the stability of the fluorophore signal? Please clarify.
- The power of single-molecule technique is precisely that such data can be made quantitative. Indeed, the Kaplan-Meyer graphs do show nice quantitative results. Unfortunately, in the text few quantitative measurements are reported. In fact, the Kaplan-Meyer graphs can be interpreted in a quantitative manner such as probability of residency time. Although in most cases the statistical significance between two conditions can be expected, this is not formally calculated and shown. What is the 50% survival time of Cse4 alone or with Ndc10, for instance? This manuscript would greatly benefit from a quantitative approach to the data, including a summary table of the results of the various conditions tested. Please add this important table.
- This reviewer would expect that the endpoint (90 min) would roughly reflect the occupancy results from time-lapse (45 min) experiments. Based on the data presented in Figures 1, 2, S1-3, this does not appear to be the case. 50% of Cse4-GFP and 70% Ndc10-mCherry colocalized with CEN3 DNA in the endpoint experiment, whereas in Fig 2C, ~30 and ~52 traces were positive for Cse4-GFP and Ndc10-mCherry, resp. with the former having drastically lower residency survival compared to Ndc10-mCherry. If indeed, 50% of Cse4-GFP makes it to the endpoint, about 50% of all traces should reach the end of the 45 minutes time-lapse window. Only about 1/3 of all positive Cse4-GFP traces can be seen at the end of the 45 min window. Could this be due to technical issues of photostability of GFP? Why does the colocalization of Cse4 signal with the DNA signal disappear so readily? Are Cse4 so unstable? Is the same true for canonical H3 nucleosomes? This unlikely true for nucleosomes in cells. Along the same lines, in Suppl Fig 3 there is a disconnect between residency survival and endpoint colocalization on either CEN3, CEN7, or CEN9. What could be the underlying mechanism between the discordance of endpoint results and time-lapse results? Could this be the result of experimental differences?
- What fraction of particles show colocalization between Cse4-GFP and Ndc10-mCherry? What fraction of occupancy time show colocalization between Cse4-GFP and Ndc10-mCherry? Altogether, understanding the limitation and benefits of endpoint analysis and time-lapse analysis in this particular experimental set-up is important to be able to interpret the results. Please clarify these points.
- Page 9, third sentence of third paragraph it is stated that the "results suggests that Scm3 helps promote more stable binding of Cse4 ...". This is indeed one possible explanation of the results, and this possibility is tested by overexpressing Psh1 or Scm3 by endpoint colocalization analysis. 1) Taking the concerns regarding the endpoint vs time-lapse results into account, wouldn't it be more accurate to compare either time-lapse results against each other or endpoint results? 2) Alternatively, more stable Cse4 particles are able to recruit Scm3, simply because of the increased binding opportunity of a more stable particle. In this scenario, just the residency time of Cse4 alone is the predicting factor in likelihood to associate with Scm3. To test the latter possibility, Cse4 stability would need to be altered. Please consider this experiment- should be relatively easy with the right mutant of either CSE4 or CDEII (see Luger or Wu papers).
- In Figure 1C and Supplemental Figure 5B, there appears to be foci that CEN3-ATTO-647 positive, but Cse4-GFP negative and visa verse. It seems logical that there are DNA molecules that didn't reconstitute Cse4 nucleosomes. But how can there be Cse4-GFP positive foci without a positive DNA signal? Is it possible that unlabeled DNA make it onto the flow chamber? If so, can these unlabeled DNA be visualized by Sytox Orange for instance to confirm that no spurious Cse4 deposition occurred? Please clarify.
- On page 10, at the end of the first paragraph, growth phenotype of pGAL-SCM3 and pGAL-PSH1 mutants were tested. On GAL plates, pGAL-PSH1 shows reduced growth, but not pGAL-SCM3. Wouldn't a more accurate conclusion be that Psh1 is limiting stable centromeric nucleosome formation, instead of Scm3?
- In the section where DNA was tethered at either one or both ends, an important control is missing. How does such a set-up impact nucleosome formation in general. Can H3 nucleosomes form on random DNA that is either tethered at one or both ends? Does this potentially affect the unwrapping potential/topology of AT-tract DNA? Please comment.
Minor comments
- Censored data points are not explained in the text.
- Number of particles tested should be reported in the main and supplemental figures, not just the legends for those readers who first skim the manuscript before deciding to read it.
- Typo on page 5, first line: "nucleosom" should be "nucleosome".
- Typo on page 9, second line: sentence is missing something "... is required for Scm3-dependent ..."
- It is unclear how the difference in Supplemental figure 5D was calculated.
- Figure 4C: why are there more Ndc10-mCherry foci observed in double tethered constructs vs single tethered constructs?
- For the display of individual traces as shown in Fig 2B, 3A, 4E, and 5E, it might be more informative if the z-normalized signal and the binary read-out are shown in separate windows to better appreciate how the z-normalized signal was interpretated.
- Page 17, fifth line of the second paragraph, it is stated that a conserved feature of centromeres is their AT-richness. This is most certainly true for the majority of species studied thus far, but bovine centromeres for instance are about 54% GC rich. Indeed, Melters et al 2013 Genome Biol showed that in certain clades centromeres can be comprised of GC-rich sequences. It might be worthwhile to nuance this statement.
- Page 17, last paragraph. Work by Karolin Luger and Carl Wu is cited in relationship to AT-rich DNA being unfavorable for canonical nucleosome deposition. A citation is missing here: Stormberg & Lyubchenko 2022 IJMS 23(19): 11385. Also, the first person to show that AT-tracts affect nucleosome positioning are Andrew Travers and Drew. This landmark work should be cited.
- Page 18, 9th line from the top, it is stated that yeast centromeres are sensitive to negative genetic drift. This reviewer is of the understanding that genetic drift is a statistical fluctuation of allele frequency, which can result in either gain or loss of specific alleles. Population size is a major factor in the potential power of genetic drift. The smaller a population, the greater the effect. Budding yeast is found large numbers, which would mean that drift only has limited predicted impact. Maybe the authors meant to use the term purifying selection?
Significance
This study developed an in vitro imaging technique that allows native proteins from whole cell lysates to associate with a specific DNA sequence that is fixed to a surface. By labeling proteins with specific fluorophore-tags colocalization provides insightful proximity data. By creating mutants, the assembly or disassembly of protein complexes on native or mutated DNAs can therefore be tracked in real time. In a way, this is a huge leap forward from gel shift EMSA assays that have traditionally been used to do comparative kinetics in biochemistry.
This makes this technique ideal for studying DNA binding complexes, and potentially, even RNA-binding complexes. This study shows both the importance of using genetic mutants, as well as testing the effects of the fixed DNA sequence. As many individual fixed DNA molecules can be tracked at one, it allows for high-throughput analysis, similar to powerful DNA curtain work from Eric Greene's lab. Overall, this is a promising new single-molecule technique that combines in vitro and ex vivo sample sources, and will likely appeal to a broad range of molecular and biophysics scientists.
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Referee #2
Evidence, reproducibility and clarity
Centromeres drive chromosome inheritance from one cell generation to the next, so understanding their nature is of utmost importance in biology. The assembly of centromeric chromatin is of outstanding interest since defects in this step impair faithful genetic inheritance. Popchock et al investigate the molecular mechanisms of Cse4(CENPA) deposition and stabilization on a native budding yeast centromeric DNA. Using TIRMF (Total Internal Reflection Fluorescent Microscopy) enabled single molecule visualization of de novo Cse4(CENPA) nucleosome formation from a yeast cellular extract. The centromeric DNA used in this study was derived from PCR amplification of plasmids containing the native yeast point centromere from chromosome 3 (CEN3 DNA) sequences containing the CDEI, CDEII, CDEII, flanking pericentromeric DNA and linker DNA totaling ~750bp. In the PCR preparation, the CEN3 DNA contains a 5'-fluorescent dye and a biotinylated 3'-end, and was tethered to a functionalized (streptavidin) slide for TIRFM. The yeast extract was extracted from cells arrested in mitosis. This system is a novel application of a single molecule to study Cse4(CENPA) formation on centromeric DNA.
Using this system, the authors observed coordinated Cse4(CENPA) deposition on the CEN3 DNA, reporting inherent, transient colocalization of Cse4(CENPA) with CEN3 DNA. Stable Cse4(CENPA) colocalization on the CEN3 DNA is correlated with the Cse4(CENPA) chaperone Smc3(HJURP), and an ability for nucleosome formation on the CEN3 DNA. Further stabilization of Cse4(CENPA) was shown to depend on the DNA binding CCAN protein chl4(CENPN) and okp1(CENPQ) which dimerizes with the DNA/CENPA binding Ame1(CENPU).
Using this single molecule system they also demonstrated a role for the A/T run (>4) content in the CDEII as specifically important for Cse4(CENPA) deposition on CEN3 DNA. Cse4(CENPA) colocalization was preferred on the native CDEII sequence, relative to mutant CDEII sequences with similar A/T content but variable homopolymeric runs.
Major comments:
- Figure S1A-D seem like some of the most compelling data in the paper to bolster the rigor of their experimental setup. There appears to be plenty of space to include these data in the main figure set in Figure 1 after panel D. The authors would be well served to consider moving S1A-D somewhere in the main figure set.
- The authors conclude that Ndc10 recruits HJURP(Smc3) to the yeast point centromeres. If this is the case, can the TIRFM assay measure ternary residence lifetimes complexes between Ndc10/HJURP(Smc3)/CenDNA?
- Throughout the manuscript short- and long- term residence lifespans are mentioned, referencing the figures containing lines with lengths depicting residence times. This is a qualitative reference to short and long residences. Can the authors provide a graph for short-term (<120 s) and long-term (> 300 s) residence life-spans for, CENPA alone, CENPA/Ndc10, and CENPA/HJURP on CEN3 DNA? Or some figure similar to Figure 3C, but reporting the proportion of short-term vs long-term residence?
- The choice of CCAN components for analysis in Fig. 5 is interesting, but many readers may be curious why Mif2 wasn't selected for disruption, since it has such a cozy placement with CENP-A and CEN DNA. Can choice to not include Mif2 mutants/degrons be mentioned/justified in the text (unless, even better yet, they choose to address Mif2 role directly in new experimentation)?
Minor comments:
- Are these whole cell extracts (WCE) DNA-free? I'm curious if there is any competition from endogenous DNA from the yeast cellular extract.
- In relation to Mif2 and comment #4 above, do the authors make any connection to their results with synthetic nucleosome sequences not being conducive to yeast centromere formation with the prior observation (Allu et al 2019) using recombinant components that the human version of Mif2 more easily saturates its binding sites on CENP-A nucleosomes when they are assembled with natural centromere DNA rather than the Widom 601 sequence?
- Providing a gel (or other measure) of the DNA templates (750, 250, and 80 bp) used in TIRFM assay would be nice to show to confirm the designed size of the pre-tethered DNA.
- Some of the references to figures/figure panels in the main text do not match the figures. (discussion, pg 16, paragraph 1 & 2;pg 18, paragraph 1).
Significance
This work demonstrates the dynamics of Cse4(CENPA) coordination with Smc3(HJURP) to form nucleosomes on point centromeric DNA, and the necessity for homopolymeric A/T runs. It is a truly impressive piece of work that makes sense of findings from prior genetics experiments. Then it extends the understanding and clarifies the role of both centromere proteins and DNA sequence. The quantitative and powerful single molecule-based experimentation, the high importance of the subject matter, and its connection to studies using yeast genetics, will make this work, upon modest improvements (see section A of this review), of outstanding interest to an extremely broad audience of biologist.
My relevant expertise keywords: centromeres, nucleosomes, biochemical reconstitution, chromosome engineering
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Referee #1
Evidence, reproducibility and clarity
Summary
This work presents a novel experimental setup to explore native centromeric nucleosome formation at a single molecule level with a high degree of temporal resolution. It combines TIRF microscopy with an immobilized fluorescent yeast CEN3 DNA sequence. Binding of centromere proteins was probed by using whole-cell lysates produced from various mutant yeast strains expressing fluorescently tagged centromere proteins. This system was used to investigate the recruitment of Cse4 (yeast CENP-A), the histone H3 variant which defines centromeres, to the native yeast CDE3 sequence. Consistent with previous studies, the authors identified a requirement for Ndc10, which binds the CDE3 sequence with high efficiency, in Cse4 recruitment. Colocalization of Ndc10 with Cse4 significantly increases the stability of the Cse4-CDE3 interaction, and Ndc10 binding predominantly precedes Cse4 recruitment. Secondly, they investigated the impact of Scm3 (yeast equivalent of HJURP) on Cse4 stability and found that Scm3 is not required for transient short-term associations between the DNA and Cse4 but is needed for longer more stable interactions between Cse4 & the CDE3 sequence. Overexpression of Scm3 & its negative regulator Psh1 also showed that Scm3 availability is the rate-limiting factor in stable Cse4 associations with DNA. However, these interactions were abolished when the CDE3 DNA sequence was topologically restricted by tethering both ends to the streptavidin-coated coverslip suggesting that the formation of a nucleosome is essential for stable binding of Cse4 to CEN3. The sequence-specific DNA binding kinetochore proteins ChI4 & Okp1 were also found to improve the lifetime of Cse4-CDE3 interactions suggesting a stabilizing interaction. Finally, the impact of A/T runs on nucleosome formation was examined using a library of scrambled CDEII sequences, with approximately native levels As & Ts but shorter runs of the 2 nucleotides. Previous studies found a correlation between the length of AT runs and the incidence of chromosome missegregation. They now extend this correlation to a decreased ability of DNA to stably recruit Cse4. Finally, experiments with other sequences including the Wisdom601 sequence suggest that A/T runs along with CBF3 binding inhibit the recruitment of histone H3 to the CDEII sequence which is overcome by the interactions between Cse4 and Scm3.
Assessment
This is an insightful, well-executed study of a high technical standard. While several observations confirm or further validate previous findings in vivo (such as the requirement for Ndc10 and Scm3 for Cse4 assembly), this work adds a better understanding of the dynamics of Cse4 requirement and the role of Scm3 in assembly and the role of CCAN components in stabilizing Cse4. Figures are well laid out and methods are clearly described. In general, the claims are supported by the data. The development of their single-molecule setup to assay Cse4 nucleosome assembly is a promising tool for future work and for this reason work reporting. In short, I believe this paper contains exciting developments in the understanding of the specific mechanism and temporal dynamics of the formation of a Cse4 nucleosome on its native DNA and the interactions which underpin its stability in vitro and in vivo.
Major comments
I have several comments and suggestions for further analysis of the data. I also have suggestions for additional experiments, but I would stress that none of these are essential for publication.
Figure 2E. This shows the residence time of Cse4 without Ndc10 association. How does this compare to the residence time on mutant CEN3 (Supplemental Figure 1). It looks like Cse4 still binds to CEN3 with some specificity even in the absence of Ndc10. Does this suggest that Cse4 has some intrinsic ability to recognize CEN3? Alternatively, Ndc10 is still required for Cse4 binding but is below detection in the Cse4-alone residence lifetimes. Ideally, the authors would compare this with Cse4 binding in an Ndc10 mutant.
Figure 3 explores the very interesting relationship between Scm3 dynamics and Cse4 binding but I feel that the data is not fully flushed out. A key finding is that Cse4 can potentially bind to CEN DNA prior to engaging with Scm3 to be incorporated. This predicts that Cse4 should bind first and then colocalize with Scm3. Can this be detected in the timing of the traces? How often does Scm3 bind to already prebound Cse4 and does this correlate with Cse4 residing longer?
A related and perhaps even more interesting point is whether Scm3 is involved in "loading" of Cse4. If so, then one would expect that once Cse4 is assembled into nucleosomes it should be stable, even if Scm3 leaves. Can the authors extract this from the data? Alternatively, it is possible that Scm3 remains associated to Cse4 to maintain the nucleosome which would imply a more extended role for Scm3 apart from assembly alone. It would be interesting if information on this can be extracted from the data.
Even in the presence of Scm3 and CCAN components, Cse4 appears to have a limited lifetime in the in vitro assay compared to in vivo stability. The authors should speculate on whether activities exist in their extract that actively disassembles nucleosomes. Perhaps ATP could be depleted to inactivate remodellers?
For Figure 6, it is not clear why AT-track mutants of CDEII are labeled as genetically stable and genetically unstable. This is confusing as the "genetically stable" show a more than 10-fold increase in chromosome loss rates. Perhaps these can be renamed into "unstable" and "very unstable" or "weak" and "strong" mutants, just to make clear that these classes are both poorer than wild type.
Finally, it would be wonderful to include data to assess whether a full Cse4 nucleosome is assembled or a partial nucleosome e.g. just Cse4/H4 tetrasomes. This could be done by tracking the accumulation of H2A or H2B at the CEN3. This would give further insight into what step Scm3 catalyses.
Minor comments:
Typo on page 5, line 1 "nucleosom" missing an e.
Kaplan-Meyer should be spelled Kaplan-Meier
The term "censored" is mentioned across many figures but comes up just ones in the methods where it is not clearly explained. Perhaps this could be clarified in the legend.
The abstract states that Cse4 can arrive at the centromere without its chaperone. More likely, Cse4 is in complex with other chaperones that may allow it to bind. Perhaps the abstract can be modified to read "Cse4 can arrive at the centromere without its dedicated centromere-specific chaperone Scm3..."
Related to this point, the discussion states the possibility that Cse4 can initially bind to CEN3 via other more general chaperones. However, it should be acknowledged that transient Cse4 binding in their assay may simply occur through mass action due to high concentrations of CEN3 DNA. In vivo, this transient binding may not be that relevant.
Significance
This paper offers new insight into the assembly of yeast centromeres with a focus on the role of the Chaperone Scm3 in the assembly of the centromere-specific histone Cse4. This is still a poorly understood process and the authors offer an elegant in vitro system to study this and have presented new insights. For this reason, this is study is of interest to a broad readership in the area of mitosis and chromosome structure. The advance is strong at the technical level but also new insight is provided particularly in the role of Scm3 and the nature of centromeric DNA in centromeric chromatin assembly. Overall a strong, high-quality paper.
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Referee #3
Evidence, reproducibility and clarity
Summary
In this manuscript, Wang and colleagues demonstrate that a single systemic injection of a high dose of Akkermansia muciniphila (A.m.) lysate drives a rapid pancytopenia followed by prolonged anaemia and hepatosplenomegaly with late-onset extramedullary hematopoiesis (EMH). The latter, as well as the splenomegaly, were likely mediated through activation of pattern recognition receptors and IL-1R signalling pathways. This was demonstrated through the partial and full phenotype reversal in Tlr2;4-/- and MyD88;Trif-/- mice, respectively. Moreover, the phenotype was partially reversed following IL-1R antagonism. After performing multiplex protein assays and flow cytometry, the authors conclude that EMH, in this model, is mediated by IL-1a produced within the spleen by local monocytes and DC.
Overall, the manuscript by Wang et al. is quite well presented, the experiments are mostly well controlled, the methods are well reported, and the data fit a clearly defined story with clinical relevance. Nevertheless, there are several major concerns that if addressed would greatly increase the strength of the authors conclusions.
Major comments
- The "two wave" hypothesis of hematopoiesis - first in the bone marrow (BM) and then in the spleen - is interesting. However, although an early wave of BM hematopoiesis would make sense, under these circumstances, I don't think the data are strong enough to support this hypothesis as they stand. For example, although the frequency of LSK cells increase, the numbers of most LSK subsets decrease. Given the decrease in the absolute number of BM cells 1d after A.m. injection, isn't it possible that the LSK cells are only proportionally increased relative to the remaining Lin- cells? What happens to the absolute number of LSK cells following A.m. injection?
Also, describing "two distinct waves of HSPC increase in the A.m.-injected spleen" (Fig 2 & S2 titles) and describing a "first wave" of HSPC expansion in the BM (lines 396, 399, 402 etc.) is misleading for the following reasons: (i) the data strongly support a single wave of increasing HSPC in the spleen, peaking at d14, and (ii) there is no evidence HSPC are increased in the BM until d56, although there does appear to be an early increase in MPP. The language should be changed accordingly. 2. The flow cytometry panel is not comprehensive enough to fully characterize the mature hematopoietic cell populations to the levels that are claimed here. For example, it is a stretch to assume that all B220- CD3- CD11c- cells are DC (splenic NK cells, eosinophils, monocytes and red pulp macrophages, for example, can express CD11c, particularly following inflammatory insult), or that CD11b+ F4/80+ SSC-hi cells are eosinophils, especially when eosinophils should be F4/80-lo are not known to express Ly6C in the spleen (For reference, see Immgen). These gating issues may explain the conspicuous absence of macrophages (should be F4/80+CD11b+Ly6C- and would also have a higher SSC than monocytes) in the plots. The B cell gate will also contain PDC, which express B220 (but can be easily excluded using Ly6C and CD11c). With respect to assessing the mature leukocyte populations in the spleen, relabelling the gates (CD11c+ cells instead of DC, F4/80+ myeloid cells instead of eosinophils) would suffice, however, these issues become a problem when trying to identify which cell populations express IL-1a.
Due to the limited antibody panel used here, there is not enough evidence to suggest that DC and monocytes are producing IL-1a. Moreover, the histograms showing the changes in expression of IL-1a on the "DC" and "Mo" are not very convincing. How does the IL-1a staining look on a dot plot? Is there good separation between positive and negative? These plots need to be included. What happens if you gate on the IL-1a+ cells first, then phenotype them?
Macrophages and splenic stromal cells are also likely candidates for IL-1a production. To assess which cell types are the true source of IL-1a, the authors need to repeat these experiments (namely, injecting A.m. and assessing IL-1a expression by leukocytes (and ideally also mesenchymal cells)) at d1 and d14, using a more comprehensive panel. Consider adding MHCII, CD64, Siglec F and CD24 to help differentiate between DC, MF, eosinophils and monocytes. CD45+ vs CD45- could be used as a minimum to assess the expression of IL-1a on leukocytes vs. stroma.
OPTIONAL: The mechanism could be better defined using bone marrow chimeras to assess the different contribution of TLR2/4 signalling and IL-1R signalling on the hematopoietic vs. mesenchymal cell compartments. 3. From these experiments, it is difficult to fully rule out a contribution from the adaptive immune system to the splenomegaly phenotype due to the marked difference in the size of BALB/c and MSTRG spleens at steady state. The authors should show the differences in spleen weight and total cell number as a % increase from control. The no of HSPC should also be normalized per gram of tissue weight or represented as a fold change compared to the relevant control groups. 4. When using fluorescent imaging to compare the abundance of HSPC and other cell populations in the spleen, the authors should provide absolute quantification from multiple FOV and multiple mice. 5. Finally, although the experiments are adequately replicated, the stats are not always appropriate. For example, a t-test shouldn't be used when there are >2 groups, or for a time course. This needs to be amended.
Minor comments
- Line 82-83: I'm fairly certain monocytes and inflammatory Ly6Chi cells are the same thing.
- Line 83-84: "IL-1a is crucial for sustaining inflammatory responses, recruiting myeloid cells to infected tissue and inducing hematopoietic stem and progenitor cell (HSPC) mobilization and expansion both in vitro and in vivo" - I don't believe IL-1a has been shown to be crucial for either, even if it has been shown to play a role. If I am mistaken, please reference with a manuscript showing relevant phenotypes using KO mice.
- Line 214: "Thus, we decided to use 200ug of lysate for the rest of all experiments." - is this what was usen for Figures 1A-C? This is not mentioned anywhere.
- Line 227: "containing both non-hematopoietic cells and immature HSPCs" Please reference Fig. 1H here. Otherwise, it is unclear how you identified the "HSPC and other cell types" in Fig. 1G.
- Figure S2A is described in text before Supp 1I-O and Fig S1H is not referenced in text at all.
- It would be interesting to include what happens to hepatomegaly in MSTRG, Tlr2;4-/- and MyD88;Trif-/- mice.
- Please define WBM. Presumably whole bone marrow?
- Notably, CCL2 is increased in spleen lysate, BM lysate and serum. Given is role in myeloid cell mobilization from the BM, I would expect its role in the phenotype described here to at least be discussed.
- HSPC LT gate includes MPP1, and should be labelled as such.
Significance
General assessment: The manuscript provided by Wang et al. describes, for the first time, a prolonged anaemia and hepatosplenomegaly with late-onset extramedullary hematopoiesis following a single systemic injection of A.m. lysate. The EMH phenotype appears robust and the data implicating TLR-signalling and IL-1a production are compelling. The work has clinical relevance as it increases our understanding of the factors driving EMH.
There are two key limitations that let this study down. Firstly, the lack of depth in the flow cytometry panel used for immunophenotyping means it is not at all clear which cell types are producing IL-1a. Secondly, the authors use an enormous dose of bacterial lysate that is well above physiological levels, even following a loss of barrier integrity (e.g., in patients with IBD). This makes me question the biological relevance of the study, particularly with respect to Akkermansia translocation.
Advance: With some improvement, this study will advance the field, in general. Previous work has looked at EMH following LPS injection, or live E. coli infection, however; the authors are able to demonstrate a distinct Akkermansia-specific effect that differs to that of LPS, membrane components of a different gram-negative bacteria, B. theta. The advancements implicate IL-1a in the modulation of EMH, for the first time, providing some mechanistic insight into this phenomenon.
Audience: This work will likely be of interest to basic researchers interested in EMH. It may also be of interest to clinical researchers of pathologies where EMH is a known complication, such as rheumatoid arthritis and cancer. The impact of the work will depend on whether or not EMH contributes to pathogenesis, or is an epiphenomenon. To my knowledge, this has not been fully established, although this is not my area of research.
I am a basic researcher with expertise in immunology focused on host-microbe interactions, both within the intestine and at distal tissues. I have knowledge of BM hematopoiesis and the microbial factors that influence if although my knowledge on extramedullary hematopoiesis is limited.
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Referee #2
Evidence, reproducibility and clarity
In this study, Wang et al reported single injection of Akkermansia muciniphila (A.m.) induces two waves of extramedullary hematopoiesis (EMH), and demonstrated the mechanism of "second wave" was contributed by IL-1α secretion in spleen DCs and Ly6C+ monocytes. It is an important work on understanding infection-induced EMH. However, several major concerns about claims in this manuscript need to be addressed.
- The authors demonstrated that A.m.-induced EMH were alleviated by knockout of Tlr2;4 or Myd88-Trif, or even IL-1R inhibition. EMH in the spleen is a mechanism by which the hematopoietic system responds to stresses. Therefore, whether inhibition of EMH by these ways can affect normal hematopoiesis in mice? Do mice have pancytopenia? Will the function of HSC in bone marrow be affected?
- In Fig.S1E, why did the WBC and PLT recover quickly after the first day, while the RBC took 14 days to recover? Are WBC and RBC regulated by two waves of EMH, respectively?
- The authors should show absolute numbers of each cell type, not just the percentage of immunophenotypically defined cells. For example, in Fig.1G, I, 2B.
- In transplantation assays, whole BM cells or splenocytes was use. However, the proportion of HSCs in BM and spleen were all changed post A.m injection, which could affect the outcome of chimerism rate after transplantation. Transplantations should be done on by transplanting sorted fresh immunophenotypic HSCs.
- The concentration of IFN-γ in both spleen and serum were increased continuously from D1 to 14. Would IFN-γ cause the second wave of EMH? Relevant assays for exclusion are necessary.
Significance
It is an important work on understanding infection-induced EMH.
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Referee #1
Evidence, reproducibility and clarity
Wang et al. examined the mechanisms of splenic extramedullary hematopoiesis upon systemic injection of Akkermansia muciniphila in mice. They showed that components of this mucin-degrading bacterium mobilize bone marrow hematopoietic cells and induce splenomegaly by MYD88/TRIF-dependent innate immune signaling pathways. Activation of TLRs and release of interleukin 1-alpha from splenic cells were then responsible for the expansion and differentiation of functional hematopoietic progenitors in the spleen. Genetic deletion of TLR2 and 4 restrained splenomegaly, while, pharmacological inhibition of IL1 receptor abrogated splenomegaly and extramedullary hematopoiesis suggesting their cooperation in the observed phenotype. It has been widely accepted that splenomegaly arises as a consequence of inflammation and that TLRs are major drivers of this process in the context of bacterial or viral infections. Here, the novelty relies on the potential circuit with the IL1alpha-IL1R axis as an additional driver of splenic extramedullary hematopoiesis. Although the results summarized above indicate that both TLRs and IL1 individually participate to some extent in splenomegaly after Akkermansia muciniphila administration, they fail to demonstrate that they concertedly do so in the spleen. In fact, the blockade of IL1R has a more profound impact.
Significance
My concerns are the following: - The authors mentioned that a specific lipid from Akkermansia muciniphila is able to trigger a non-canonical TLR2-TLR1 heterodimer to release inflammatory cytokines and regulate human immune response. Why TLR1 was not considered in the experimental strategy? - IL1alpha is up-regulated in several splenic cells (in particular in macrophages, Fig. S4F). To demonstrate a critical involvement of dendritic cells or monocytes, depletion studies or conditional mice models should be evaluated. What about megakaryocytes? Why were excluded from the analyses? - Interleukin 1alpha KO mice model should be also evaluated. - The paper is very dense and not easy to read and follow. English editing is required.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The manuscript presents a detailed numerical model of blood flow in a region of the zebrafish vasculature.
The results section is quite intense and detailed. it is difficult to understand what the authors are after. I think a rewrite would beneficial. The authors present simulations for a wild type and a couple of phenotypes. For each of these they speculate on the possible adaptation mechanism leading to the discussed phenotype, as preservation of constant wall shear stress. However, the comparison between experiments and numerical simulations is really elusive as the conclusions on those mechanisms. Overall we suggest a rewrite with clearer organisation in a way that the reader is not overflown with useless details.
We thank the reviewer for the advice on the general writing standard and data organization. We have reanalyzed experiment data and interpreted the findings more conservatively for application into the simulation models. As a result, some conclusions to the results sections have changed. Accordingly, we have done a major revision of the entire Results, Discussion and Models and Methods sections in the paper to articulate these reinterpretations while removing superfluous details that may obfuscate the data.
It is not always clear what info of the experiments are used in the simulations on top of the anatomy. Our understanding is that the pressure boundary conditions are set to match the red blood cel velocity observed in experiments. Is this always the case for the three phenotypes and which vessels ?
We thank the reviewer for the question. Only WT and Marcksl1 KO have been matched for peak velocities in the CA, CV and ISVs between experiments and simulations. WT results were compared to both the experimental reference of 27 embryos in Table 3 and also to the current experiment pool of WT (5 embryos) in Table 6. Marcksl1 KO simulation models 1, 2 and 3 were compared against the average level seen in the low and moderate perfusion Marcksl1 KO phenotypes (8 embryos) from the experiment (Table 5 and Table 6). Additionally, we also have represented the similar level of RBC hematocrit in the CA for WT model to WT experiment data from the reference cited in Table 3.
In addition to the velocity comparisons, we now use the experimentally observed trend of decreased flow rate in the CA of Marcksl1 KO experiment data to assess the model boundary conditions amongst Marcksl1 KO models 1, 2 and 3 that best reflect the experimental observations:
Page 11, lines 1 to 20
The Marcksl1 OE cannot be matched because we do not have the experiment data for that, the same goes for PlxnD1 where we have no experiment flow data. These two networks represent more conceptual discussions, particularly in PlxnD1 case where we have explicitly stated in the new discussion section:
Page 15, lines 24 to 34
There are about 7 inlets and outlets where to impose pressure boundary conditions. Can the author comment on the uniqueness of this problem?
Can different combination of pressure boundary condition leading to the same result ? In how many points/vessels is the measured velocity matched ?
We thank the reviewer on this insightful concern. Indeed, the uniqueness of flow and pressure field can be a problem without careful consideration. We have tried to address this to some extent, because CA, CV are connected by the ISV and DLAV network, to match flow velocity in all regions, the pressure distribution ought to be unique to the particular setting we employed.
As shown in table 3, average systolic peak flow velocities in the entire CA and CV encompassing the 5 ISV segment domain is matched between the simulation and the population-averaged experimental data from the experimental reference (27 fish sampled in the cited reference) for the same regions in WT network. Average systolic peak flow velocities for the 10 ISVs in the simulation were matched against WT experiment population-averaged systolic peak flow velocities in arterial and venous ISVs in the same caudal region.
Additionally, we also compared the flow velocities to the experiment conducted within this study (5 WT, and embryos). This comparison data is shown in Table 6. Admittedly the discrepancy was large for CV and ISVs regions likely due to a smaller data set sampled in this study and biological variations that happen from one experiment to another. We have acknowledged this deficiency in the revised discussion section:
Page 15, lines 3 to 9
The argument that similar beating frequency in the WT and GATA1 MO suggest pressure does not change is not clear. If the heart was a volumetric pump it would impose the same flow rate, not the same pressure. It would be more useful to measure the cardiac output in terms of flow rate in the Dorsal Aorta. Previous measurements by Vermot suggested the latter would not change much in gata1 MO. It could be that the cardiac output is the same but the vasculature network is different in a way that the shear stress remain the same. It does not look like this was checked by the authors.
We thank the reviewer for this insight. In accordance with the reviewer’s suspicion, we have estimated the flow rates in the CA of gata1 MO injected embryos and found the level to be similar to WT. This supports the reviewer’s opinion that the heart rate similarity indicates cardiac output similarity and not arterial pressure similarity as we previously put forward. Furthermore, we have checked that the gata1 morphants do in fact present reduced ISV diameters. In light of this reinterpretation, we performed an additional zero hematocrit model (model 3 in section 2.1). We have consequently rewritten the entire section on how RBC hematocrit modulates hemodynamics in a microvascular network:
Page 6, line 18 to page 8 line 10.
Additionaly, it would be useful to provide an effective viscosity for the different vessels, and an effective hydraulic impedance relating DP and Q to interpret the results.
We have followed the reviewer’s advice and have analyzed for vessel hydraulic impedance and effective viscosity in all the network models presented. This is included in the main figures and discussion. The vessel impedances are discussed for the various models in these following parts of the manuscript:
Page 9, lines 20 to 29
Page 11, lines 28 to 30
Page 12, line 1 to page 13 line 10
Is the hydraulic impedance of the vessels kept constant in the smooth-geometry model? This needs clarification
The SGM diameters have been determined based on geometric averages and not impedance equivalency. The reason why we did this is because the impedance will not be known until the CFD is performed for the WT network. This is because without a pressure distribution (which cannot be determined experimentally) we cannot calculate vessel impedance since only flow can be measured and both flow and pressure are requirements to impedance calculation. Our intention with the SGM is to highlight how geometric averaging of morphological characteristics lead to incorrect flow and stress predictions. However, we understand the reviewer’s sensibility and have revised the entire section of the SGM results. We have now discussed three SGM models with varying degrees of geometry simplification. The SGM1 in the revised manuscript matches WT network impedance in the ISVs by including both axial variation in lumen diameter of the WT network and the elliptical fit representation of cross-sectional skewness seen in WT ISV lumens. SGM 2 has representation of axial variation but not luminal skewness and SGM3 has only geometric average similarity to WT ISVs. The new findings and discussion can be found in the revised manuscript here:
Page 8, line 19 to page 9 line 36.
As mentioned by the authors they propose a very complex and time expensive simulation. However the results they report are kind of intuitive. Given the availability of the experimental results, would it be useful to use a simpler red blood cell model in the future, to make their simulation more practical? Or clarify when such demanding simulations can add something new?
We agree that the intuition feedback depends on the expertise of the investigator. The boundary condition selection is intuitive from the experimental findings and key data like pressures in the network cannot be measured. Furthermore, population-averaged flow data does not always match the flow-to-geometry situations that vary from sample to sample, thus demonstrated by the high margin of prediction discrepancy for flow velocities in table 6. We have discussed these challenges and our recommendations for improvement in the Discussion section:
Page 15, lines 3 to 9
Page 15, lines 35 to 40
Page 16, lines 12 to 15
On the topic of RBC model simplification, we agree with the reviewer that our work suggests the methodology would benefit from a further coarse-graining approach to the RBC phase. Accordingly, we discussed the possibility of using a low-dimensional RBC model already published in literature:
Page 14, lines 13 to 17
The authors should check their references as this is not the first time work has been done on the topic. Would be good to have a check in the work of Freund JB and colleagues, as well as Dickinson and colleagues and Franco and colleagues to discuss how the work compares. There may be interesting work in modelling cardiac flow forces in the embryo too.
Thank you for referring us to other publications that are related to our study. To our knowledge and after performing publication search on these authors, we find that although Dickinson and colleagues performed experiments to examine the effects of perturbed blood flow on vessel remodelling (Udan et al., 2013), they did not perform any numerical modelling to calculate hemodynamic forces such as WSS and luminal pressure. Instead, changes in vessel morphogenetic process were only correlated with blood flow velocity. In our study, we attempt to quantitatively correlate WSS and pressure distributions within a vascular network. Franco and colleagues (Bernabeu et al., 2014) developed PoINet to model haemodynamic forces in mouse retina model of angiogenesis. From what we understand, PoINet is different from our 3D CFD model by 1) not having red blood cells incorporated in their model and as such, the blood viscosity prediction is modelled using shear-rate dependent formulation and not through red blood cell hematocrit, 2) cross sections of blood vessels are assumed to be circular and therefore have no irregularity and 3) live imaging of blood flow is difficult in mouse retina therefore preventing accurate boundary conditions for the model.
We have included the reference to work of Franco and colleagues:
Page 14, line 28 to line 31
Page 9, lines 12 to 14
Freund JB indeed has had extensive work on RBC and cellular flow in microvessels. We have included a reference of his work in:
Page 14, lines 22 to 25.
Reviewer #1 (Significance (Required)):
The authors discuss the applicability of a detailed numerical model of blood flow in a region of the zebrafish vasculature.
We are not expert in the lattice boltzmann method used here, but the results are what it would be expected from a physical stand point, and together with the information from the method section, we do not have major concerns about the numerics.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: The authors report corroborating numerical-experimental studies on the relationship between morphological alterations (e.g. vessel lumen dilation/constriction, network mispatterning) and hemodynamical changes (e.g. variation in flow rate, pressure, wall shear stress) in the vascular network of zebrafish trunk circulation. Various physiological or pathological adaptation scenarios were proposed and tested, with a range of simulation and experiment models. Where I found it a solid piece of work supported by abundant data, certain aspects need to be clarified/enhanced to improve the scientific rigor and potential impact of the manuscript. Below are my detailed comments in the hope of helping the authors improve the manuscript's quality.
Major comments:
- Cellular blood flow in vascular networks has been extensively studied in recent years by existing computational models (some of which were published open-source) with similar methods and features to the one proposed by the present work. Can the authors be more explicit about the original contributions of the current model, and provide evidence accordingly (e.g. Github repository or code resources)
The RBC model is essentially the model developed by Fedosov and colleagues (Fedosov, et al., 2010). Likewise, the LBM solver for fluid flow calculation is not. Following the reviewer’s advice, we have removed the details of these non-novel aspects of the methodology and placed them in sections E and F of supplementary material instead. The new Models and methods now show condensed descriptions of the three numerical solvers used and the addition of a grid independence matrix discussion section:
Page 17, line 8 to page 20, line 33.
Crucial details for the simulation setup and model configuration are missing. What were the exact boundary conditions (e.g. inlet and outlet pressures) and initial conditions (e.g. feeding hematocrit of RBCs), and how the numerical-experimental validation process of "to match the velocities of various segments of the network by iteratively altering the pressure inputs ..." as stated on page 13 (lines 1-2) was performed for simulations in this work?
We apologize for the vagueness of our description on how numerical to experimental validations were performed. As replied to reviewer 1 for a similar clarification, we have indicated in Table 3 how average systolic peak flow velocities in the entire CA and CV encompassing the 5 ISV segment domain were matched between the simulation and the population-averaged experimental data for the same regions in WT network. Average systolic peak flow velocities for the 10 ISVs in the simulation were matched against WT experiment population-averaged systolic peak flow velocities in arterial and venous ISVs in the same caudal region.
With regards to what iterative alterations of pressure inputs mean, we monitored the average systolic peak velocities and hematocrit levels in CA, CV and ISVs in intervals of 5 cardiac cycle intervals before manually correcting the pressure input levels to better match average systolic peak velocities in these vessels from the experiment averages. Since we are using population averaged flow data, we do not expect their levels to match the levels in a particular fish-specific geometry, the degree of discrepancy between experiment averages and the model predictions of systolic velocities can be large (Table 6). Admittedly, this is one of the weaknesses of our approach and this limitation is stated in the Discussion section:.
Page 15, lines 3 to 9
As RBC flow typically requires roughly 5 cardiac cycles of flow to reach flow development this process of iterative correction typically takes place over 10 to 20 cardiac cycles. We understand that validation may be a subject of keen interest to readers, hence we have now briefly described the solution initialization and flow development protocol in our modeling approach here:
Page 6, lines 5 to 8
What lattice resolution was used for the flow solver and was the RBC membrane mesh chosen accordingly? Were there any sensitivity analysis (regarding pressure input) or grid-independence study (regarding lattice resolution)
We originally decided on the grid (∆X) and time (∆T) discretization resolutions (0.5 µm and 0.5 µs) based on the acceptable computing turnaround time for each model within our scale of resources. We have now included a section on the grid independence matrix in Models and Methods:
Page 19, line 20 to page 20, line 33
Details of the statistical tests (type of tests used, assessment of data normality, sample size etc.) should be given in the figure caption where applicable (e.g. Fig. 3C, Figs. 7-9).
We apologize for the lack of clarity. All statistical tests used have now been mentioned at least once in each section of results and also in Figure captions wherever significance bars are displayed.
The regression models should also be used with caution, e.g. in Fig. 4B, why should data from two different fish types, namely Gata1 MO and WT, be grouped to fit a linear regression model?
We understand the reviewer’s concern that two population data sets should not be carelessly pooled together for regression analysis without adequate justification. In this case we are utilizing gata1 morpholino injection as a means to alter hematocrit level. There is no reported side-effect as to the best of our knowledge, only hematocrit and possibly hemodynamics and morphological response related to hematocrit level should be affected. Moreover, we have mislabelled the companion set to the gata1 morpholino as WT, the data is in fact data from control morphants and not WT. This change has been applied to Fig. 3 graphs and Table 4 and results section:
Page 7, lines 3 to 16
Finally, as we want to generate a continuum range of varying hematocrit for embryos of the same developmental age. In this regard, we think that within the scope of our intentions and well-accepted usage of gata1 morpholino as a hematocrit reduction protocol it is reasonable to pool the two data sets together for regression analysis.
4.I found the data presented in Fig. 7 insufficient to confidently exclude the numerical models 2, 3 but favor model 1 as the adaptation scenario for the Marcksl1KO case. The first question is, how are the threshold RBC perfusion levels determined to categorize the experimented Marcksl1KO fishes into four groups, i.e. "high", "moderate", "low", "zero"? The authors also need to justify why the "high", "moderate", "low" groups can be mapped to the three modelling scenarios (namely models 1, 2, 3) is it just because "a qualitative match with the experimental trend of ascending CA blood velocity" (Fig. 7F)?
We thank the reviewer for his interpretation of our results. Firstly, we apologize for generating the confusion but we are not trying to map simulation models 1, 2 and 3 to high moderate and low groups respectively in Fig. 7. The high, moderate and low categorizations of experimental Marcksl1 KO phenotypes are based on RBC flux levels observed experimentally. We are trying to ascertain which Marcksl KO phenotype the models 1, 2 and 3 fit, if they do fit the experiment trend at all.
Second, in Fig. 7C, it is shown that no significant difference exists between the "high" group and the WT in their average ISV diameter, then what is defining that group as Marcksl1KO type ?
We apologize for the confusion generated. High flow phenotype is similar to WT flow, the diameter is also similar to WT. In Marcksl1 KO mutants we don’t always see clear phenotyping and often a range is presented from mutant to mutant. Hence the high group is essentially morphometrically and hemodynamically similar to WT, the only reason we know it is a mutant because we have genotyped the zebrafish (marcksl1a-/-;marcksl1b1-/-).
Third, a central assumption here is using heart rate as a measure of the pressure drop in different fish individuals (Fig. 7D). Can't two fishes with similar heart rate have distinct pressure drops in the trunk due to difference in network architecture and topology, vice versa?
We agree with the reviewer’s opinion and now feel that our initial proposition was naïve. After addressing the interpretation of heart rate similarity in the gata1 morphants with more convincing CA flow rate estimations, we now believe that heart rates might not be useful indicators of flow or pressure levels in the network. Instead, cardiac output in the form of CA flow rate as reviewer 1 has suggested might be a better indicator. As the reanalysis has dismantled the earlier interpretation, and found that based on the flow rate estimation for the CA, Marcksl1 KO networks have reduced blood flow rates in the CA.
Page 11, lines 9 to 20
This finding has been incorporated into the consideration of flow adaptation scenarios predicted by the simulation models accordingly in the revised manuscript:
Page 12, line 1 to page 13, line 10
Fourth, the authors should explain why a power-law fit (note that it is not "exponential" as stated on page 10, line 3) should be adopted for the regression analysis in Figs. 7E-v,vi (a useful reference may be Joseph et al. eLife 2019: 10.7554/eLife.45077).
We thank the reviewer for the useful reference and the careless mislabeling of regression curve used. This figure has been redone and a linear regression is instead used that does not attempt to imply any physical law for a power or exponential fitting.
Change made: Fig. 7C
Minor comments:
- The state of art of cell-resolved blood flow models employed to simulate microcirculatory hemodynamics is not accurately described in the introduction (page 4). More recent works should be cited and critically reviewed to present a fair view on the novelty of the computational model developed herein.
We apologize that the models were mentioned in a passing manner. However ,the need for brevity in introduction somewhat limits their expansion. We have instead gave more direct discussion on similar studies and their relevance to our present work in the Discussion section:
Page 14, lines 13 to 31
It is unclear what "realistic representation of local topologies in the network" (page 7, lines 28-31) means as a claim of novelty. If it means vessel "diameter variation", this geometric feature has been modeled by the works the author referenced (namely Roustaei et al. 2022, Zhou et al. 2021). If it means something else, for example, unsmooth or non-circular vessel surface (or "irregularity of the local endothelium surface" as mentioned on page 5, line 2), then strangely the effects of such features are actually not described in the manuscript.
We apologize for not meeting the expectation of novelty as claimed. We see value in the SGM study matrix have now generated data on three SGM scenarios. The SGM1 in the revised manuscript matches WT network impedance in the ISVs by including both axial variation in lumen diameter of the WT network and the elliptical fit representation of cross-sectional skewness seen in WT ISV lumens. SGM 2 has representation of axial variation but not luminal skewness and SGM3 has only geometric average similarity to WT ISVs. Essentially the comparison between SGM1 and SGM2 highlights the role of luminal cross-sectional shape skewness while SGM2 to SGM3 highlights the role of axial variation in luminal diameter. With this new SGM data set, we think we can better qualify the aspiration of demonstrating how vessel shape “irregularities” can alter network hemodynamics. The new findings and discussion can be found in the revised manuscript here:
Page 8, line 19 to page 9 line 36.
Why should Fig. 8 contain data from Marcksl1KO model 2? The scenario underlying model 2 was rejected earlier in the manuscript (see point 6 above), and the Marcksl1KO model 2 data are not mentioned in the text when describing the results of Fig. 8, either.
We have reanalyzed the experiment trend and rewritten the outcome of this results section. In summary, both models 1 and model 2 meet the trend of flow rate reduction (with respect to WT levels) in the CA observed in the experiment. Hence, model 2 inclusion is relevant to the WSS analysis. The changes pertaining to this can be found here:
Page 11, line 9 to page 13 line 10.
It is a dense article with loads of data, which is an advantage but only if appropriately streamlined. More subheadings should be considered, especially for section 2.3 (for which the current subsections appear mistaken, 2.3.1 followed by 2.4.2) The manuscript could also benefit from restructuring through optimal combination of simulation visualizations and quantitative analyses. For example, in Fig. 6, not all simulation snapshots are needed here (it is difficult to visually compare the changes between different cases), whereas some quantification in the form of histograms or boxplots will be handy for the readers to note the variation of WSS magnitudes and ranges.
Thank you for the advice, we removed the unnecessary graphical plots and refer to simulation videos in supplementary data instead for such cases. The bad indexing of results subsections has been fixed, while new subsections have been made for better directional narrative to the paper. These changes are colored in red throughout the revised results section:
Page 4, line 37 to page 13 line 39
Related to point 8, the authors could also consider integrating or synthesizing the analyses for individual aISVs and vISVs presented in various figures. Current descriptions for the ISV data appear scattered with frequent exceptions to the summarized trends or relationships. Some minor formatting issues should also be addressed, e.g. the confusing color codes in Figs. 9D-i, E-i.
Thank you for the advice, we have now pooled aISVs together into one group and vISVs into another, instead of discussing data trends on each of the 10 ISVs.
The mispattening case presented in the end of the results section (section "2.4.2") is interesting but appears loosely connected to the preceding contents. Also, it seems not even mentioned in the discussion section.
We agree that the mispatterning case has been only tangentially relevant to the rest of the manuscript. We have linked the topic thematically by network alterations transforming network flows. It is also now included in the discussion section here:
Page 15, lines 30 to 34
Finally, apart from the effect of topological features on local blood flow, the authors should consider the global flow redistribution arising from the network structure (useful refs. Include Chang et al. PLOS Computational Biology 2017: 10.1371/journal.pcbi.1005892; Meigel et al. Physical Review Letters 2019: 10.1103/PhysRevLett.123.228103; Schmid et al. eLife 2021: 10.7554/eLife.60208).
Thank you for the additional references. These are solid pieces of work that have been added to the discussion here:
Page 16, lines 3 to 10
**Referees cross-commenting**
This review report resonates with mine from an experimental perspective and I agree with all points made regarding issues of the current manuscript that the authors need to address with a revised version.
Reviewer #2 (Significance (Required)):
Significance: The particular merit of the work lies in its comprehensiveness of design and abundance of data, which will be of great interest to both the computational and experimental communities in this research field. However, some crucial details (especially with respect to the modelling aspects) are missing, thus hampering the scientific rigor and potential impact of the work. Furthermore, certain justifying statements appear speculative and inconclusive to explain the obtained data, especially regarding the effect of boundary conditions and systemic parameters. The citation of references (some not cited, some cited already but not properly discussed) also needs to be enhanced with engaging discussions to better bridge the findings of the current work (e.g. RBC partitioning in vascular network, effect of WSS on vasculature morphogenesis) with recent works on this research topic.
References
Fedosov DA, Caswell B, Karniadakis GE. 2010. A Multiscale Red Blood Cell Model with Accurate Mechanics, Rheology, and Dynamics. Biophys J 98:2215–2225. doi:10.1016/j.bpj.2010.02.002
Freund JB, Goetz JG, Hill KL, Vermot J. 2012. Fluid flows and forces in development: functions, features and biophysical principles. Dev Camb Engl 139:1229–45. doi:10.1242/dev.073593
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Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
Summary: The authors report corroborating numerical-experimental studies on the relationship between morphological alterations (e.g. vessel lumen dilation/constriction, network mispatterning) and hemodynamical changes (e.g. variation in flow rate, pressure, wall shear stress) in the vascular network of zebrafish trunk circulation. Various physiological or pathological adaptation scenarios were proposed and tested, with a range of simulation and experiment models. Where I found it a solid piece of work supported by abundant data, certain aspects need to be clarified/enhanced to improve the scientific rigor and potential impact of the manuscript. Below are my detailed comments in the hope of helping the authors improve the manuscript's quality.
Major comments:
- Cellular blood flow in vascular networks has been extensively studied in recent years by existing computational models (some of which were published open-source) with similar methods and features to the one proposed by the present work. Can the authors be more explicit about the original contributions of the current model, and provide evidence accordingly (e.g. Github repository or code resources)?
- Crucial details for the simulation setup and model configuration are missing. What were the exact boundary conditions (e.g. inlet and outlet pressures) and initial conditions (e.g. feeding hematocrit of RBCs), and how the numerical-experimental validation process of "to match the velocities of various segments of the network by iteratively altering the pressure inputs ..." as stated on page 13 (lines 1-2) was performed for simulations in this work? What lattice resolution was used for the flow solver and was the RBC membrane mesh chosen accordingly? Were there any sensitivity analysis (regarding pressure input) or grid-independence study (regarding lattice resolution)?
- Details of the statistical tests (type of tests used, assessment of data normality, sample size etc.) should be given in the figure caption where applicable (e.g. Fig. 3C, Figs. 7-9). The regression models should also be used with caution, e.g. in Fig. 4B, why should data from two different fish types, namely Gata1 MO and WT, be grouped to fit a linear regression model? 4.I found the data presented in Fig. 7 insufficient to confidently exclude the numerical models 2, 3 but favor model 1 as the adaptation scenario for the Marcksl1KO case. The first question is, how are the threshold RBC perfusion levels determined to categorize the experimented Marcksl1KO fishes into four groups, i.e. "high", "moderate", "low", "zero"? The authors also need to justify why the "high", "moderate", "low" groups can be mapped to the three modelling scenarios (namely models 1, 2, 3); is it just because "a qualitative match with the experimental trend of ascending CA blood velocity" (Fig. 7F)? Second, in Fig. 7C, it is shown that no significant difference exists between the "high" group and the WT in their average ISV diameter, then what is defining that group as Marcksl1KO type? Third, a central assumption here is using heart rate as a measure of the pressure drop in different fish individuals (Fig. 7D). Can't two fishes with similar heart rate have distinct pressure drops in the trunk due to difference in network architecture and topology, vice versa? Fourth, the authors should explain why a power-law fit (note that it is not "exponential" as stated on page 10, line 3) should be adopted for the regression analysis in Figs. 7E-v,vi (a useful reference may be Joseph et al. eLife 2019: 10.7554/eLife.45077).
Minor comments:
- The state of art of cell-resolved blood flow models employed to simulate microcirculatory hemodynamics is not accurately described in the introduction (page 4). More recent works should be cited and critically reviewed to present a fair view on the novelty of the computational model developed herein.
- It is unclear what "realistic representation of local topologies in the network" (page 7, lines 28-31) means as a claim of novelty. If it means vessel "diameter variation", this geometric feature has been modeled by the works the author referenced (namely Roustaei et al. 2022, Zhou et al. 2021). If it means something else, for example, unsmooth or non-circular vessel surface (or "irregularity of the local endothelium surface" as mentioned on page 5, line 2), then strangely the effects of such features are actually not described in the manuscript.
- Why should Fig. 8 contain data from Marcksl1KO model 2? The scenario underlying model 2 was rejected earlier in the manuscript (see point 6 above), and the Marcksl1KO model 2 data are not mentioned in the text when describing the results of Fig. 8, either.
- It is a dense article with loads of data, which is an advantage but only if appropriately streamlined. More subheadings should be considered, especially for section 2.3 (for which the current subsections appear mistaken, 2.3.1 followed by 2.4.2). The manuscript could also benefit from restructuring through optimal combination of simulation visualizations and quantitative analyses. For example, in Fig. 6, not all simulation snapshots are needed here (it is difficult to visually compare the changes between different cases), whereas some quantification in the form of histograms or boxplots will be handy for the readers to note the variation of WSS magnitudes and ranges.
- Related to point 8, the authors could also consider integrating or synthesizing the analyses for individual aISVs and vISVs presented in various figures. Current descriptions for the ISV data appear scattered with frequent exceptions to the summarized trends or relationships. Some minor formatting issues should also be addressed, e.g. the confusing color codes in Figs. 9D-i, E-i.
- The mispattening case presented in the end of the results section (section "2.4.2") is interesting but appears loosely connected to the preceding contents. Also, it seems not even mentioned in the discussion section.
- Finally, apart from the effect of topological features on local blood flow, the authors should consider the global flow redistribution arising from the network structure (useful refs. Include Chang et al. PLOS Computational Biology 2017: 10.1371/journal.pcbi.1005892; Meigel et al. Physical Review Letters 2019: 10.1103/PhysRevLett.123.228103; Schmid et al. eLife 2021: 10.7554/eLife.60208).
Referees cross-commenting
This review report resonates with mine from an experimental perspective and I agree with all points made regarding issues of the current manuscript that the authors need to address with a revised version.
Significance
The particular merit of the work lies in its comprehensiveness of design and abundance of data, which will be of great interest to both the computational and experimental communities in this research field. However, some crucial details (especially with respect to the modelling aspects) are missing, thus hampering the scientific rigor and potential impact of the work. Furthermore, certain justifying statements appear speculative and inconclusive to explain the obtained data, especially regarding the effect of boundary conditions and systemic parameters. The citation of references (some not cited, some cited already but not properly discussed) also needs to be enhanced with engaging discussions to better bridge the findings of the current work (e.g. RBC partitioning in vascular network, effect of WSS on vasculature morphogenesis) with recent works on this research topic.
-
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 presents a detailed numerical model of blood flow in a region of the zebrafish vasculature.
The results section is quite intense and detailed. it is difficult to understand what the authors are after. I think a rewrite would beneficial. The authors present simulations for a wild type and a couple of phenotypes. For each of these they speculate on the possible adaptation mechanism leading to the discussed phenotype, as preservation of constant wall shear stress. However, the comparison between experiments and numerical simulations is really elusive as the conclusions on those mechanisms. Overall we suggest a rewrite with clearer organisation in a way that the reader is not overflown with useless details.
It is not always clear what info of the experiments are used in the simulations on top of the anatomy. Our understanding is that the pressure boundary conditions are set to match the red blood cel velocity observed in experiments. Is this always the case for the three phenotypes and which vessels ? There are about 7 inlets and outlets where to impose pressure boundary conditions. Can the author comment on the uniqueness of this problem? Can different combination of pressure boundary condition leading to the same result ? In how many points/vessels is the measured velocity matched ?
The argument that similar beating frequency in the WT and GATA1 MO suggest pressure does not change is not clear. If the heart was a volumetric pump it would impose the same flow rate, not the same pressure. It would be more useful to measure the cardiac output in terms of flow rate in the Dorsal Aorta. Previous measurements by Vermot suggested the latter would not change much in gata1 MO. It could be that the cardiac output is the same but the vasculature network is different in a way that the shear stress remain the same. It does not look like this was checked by the authors.
Additionaly, it would be useful to provide an effective viscosity for the different vessels, and an effective hydraulic impedance relating DP and Q to interpret the results.
Is the hydraulic impedance of the vessels kept constant in the smooth-geometry model? This needs clarification
As mentioned by the authors they propose a very complex and time expensive simulation. However the results they report are kind of intuitive. Given the availability of the experimental results, would it be useful to use a simpler red blood cell model in the future, to make their simulation more practical? Or clarify when such demanding simulations can add something new?
The authors should check their references as this is not the first time work has been done on the topic. Would be good to have a check in the work of Freund JB and colleagues, as well as Dickinson and colleagues and Franco and colleagues to discuss how the work compares. There may be interesting work in modelling cardiac flow forces in the embryo too.
Significance
The authors discuss the applicability of a detailed numerical model of blood flow in a region of the zebrafish vasculature.
We are not expert in the lattice boltzmann method used here, but the results are what it would be expected from a physical stand point, and together with the information from the method section, we do not have major concerns about the numerics.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The current study uses 3D organotypic rafts to culture primary keratinocytes from Foreskin, Tonsil and Cervix. Further the authors looked at the transcriptomic profiles of each tissue types to study similarities and differences depending on the tissue of origin as well as show the similarity in the tissue specific gene signatures and the ex-vivo samples (data from GTEx). As mentioned by authors Skin and Cervix keratinocytes have been previously cultured on collagen rafts however extending it to Tonsil provides resource and possibility of growing more tissue specific epithelial cells in 3D.
Major comments 1. As the papers focus is to culture epithelial/ epidermal cells on 3D rafts, methods section needs more details about the raft composition, preparation, fibroblast embedding what was the plate size used for raft preparation and culturing of cells on those rafts. What culture media was used for epithelial raft cultures?
We have a detailed published protocol that highlight these details. However, we will expand on some of these details in the manuscript
Results: Figure 1, authors show IF staining's for COL17A1 as marker for basal cells and cornulin for differentiated layers. However, it is important to show how many cells in the basal layer are proliferative? (or how many layers of proliferative cells are present in different epithelia analysed here?) after 14 days majority of cells might already start losing their stemness potential (maybe staining for at least ki67 if staining for basal stem cell marker not possible? Along with loricrin or Involucrin might be good idea).
We will stain for ki67 as suggested. However, based on published data using these raft cultures, we do not expect that many cells will be positive.
This is also important as from supp fig 3 you can see F1 has higher expression of Loricrin, filaggrin etc as compared to all other samples indicating higher diff in this sample. Also, if authors can comment on what was the passage of cells used? And have they observed any difference in the re-epithelization in early passage versus late passage of keratinocytes?
We will expand on this is the updated manuscript. Importantly, we grow these cells in a rho-kinase inhibitor that ‘conditionally’ immortalizes these cells as described (DOI: 10.1172/JCI42297).
It is interesting to see Tonsillar 3D epithelia recapitulate the crypt and surface epithelia and authors also show this with gene expression profile, if possible (Optional), can authors show staining for crypt specific and surface specific markers.
We agree that this is an important control. This will be included.
For all the Supplementary tables where only Ensembl ids are represented, please add gene Id column alongside (it is easier to get biological context from gene id for the reader rather than looking up Ensembl ids). Rename the file names to include the Supplementary file 1, 2, 3?
Since there is 1-to-1 conversion for Ensembl to Gene Id, we elected to not include these. The online app does try tp accommodate this as much as possible. We propose to include two versions of each table. 1 with Ensemble ids only and one with both IDs.
Its excellent to see that in vitro tissue signature matched the in vivo tissue samples (Figure 8) but it will be interesting to show the gene expression differences if found any between the in vitro and in vivo samples that will give insight on the changes as result of in vitro system.
Since the in vivo data will be a mixture of epithelial cells and stroma, these comparisons are not straightforward. However, we are currently examining the use of existing scRNA-Seq data to begin addressing these concerns. This data will be included in the next revision.
Minor comments
- Abstract: Give sample number (n?) and brief results about the genes that had tissue specific expression pattens.
- Gene names needs to be in Italics throughout.
- Introduction: page 5 line 9, authors claim that they based on comparisons they can "identify potential therapeutic targets for various disease" I think this statement either needs experimental evidence or statement / claim needs to be modified.
- Data submission to GEO???
- Typo (page 15, line 16 should be "HFK-down", same on page 23 "ectocervix", "endocervix", "uterus", so on, please correct, comma needs to be placed after "
- Page 24 last line is the heatmap referred here Fig 9B?
- Fig. 1 legends please indicate what F1, F2, F3, C1--- T1--- represent. Fig 1C Please add axis range/ values for protein atlas data as well.
- Can authors comment in discussion how was current 3D cervix cells on raft method different from Meyers, C., 1996 3D system?
All these ‘minor’ comments will be addressed.
Reviewer #1 (Significance (Required)):
This article does extend and validate the 3D raft culture method to different epithelial tissues in addition to Skin and cervix. This will be useful for the researchers using co culture systems and interested in understanding epithelial cell and immune cell interactions or host pathogen interacts etc
Describe your expertise: establishing and maintaining primary skin and oral keratinocyte cultures on feeders and 3D cultures on DEDs, Organoid cultures from oral keratinocytes, Oral cancer biology, Histopathology, transcriptomics study, Immuno-oncology.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary Jackson et al.'s manuscript describes an experiment that directly compares 3D organotypic assays created with primary human epithelial cells from foreskin, cervix and tonsil using histological and bulk RNA sequencing approaches. The authors convincingly show the retention of site-specific histological and transcriptomic differences between the stratified epithelial tissues in culture. Differentially expressed genes are identified and pathway analyses suggest genes that might be involved in the different differentiation processes between these tissue sites and differential regulation of ECM and immune pathways. Differentially expressed genes are used to develop a classifier for tissue identification, which is tested using GTEx data.
Major Comments • The interferon stimulated genes of B cells and macrophages (from Mostafavi et al., 2016) are likely to be very different from those in epithelial cells, so the analysis presented in Figure 9 seems like a stretch to me.
We will include caveats to this interpretation. We are planning stimulation experiments of each tissue to compare IFN responses. However, depending on the outcomes, these may end up being outside of the scope of the current manuscript.
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OPTIONAL: Further data comparing the nature and magnitude of the interferon responses of the three epithelia would improve interest in the manuscript but are not necessary for publication of the current dataset.
See above
Minor Comments • Details of n numbers and what each point represents should be added to Figure 1C. Are these points measurements from 25 um intervals of just one raft per donor? What are 'fields of view' here? Are measurements from one section or from multiple sections per raft? • Page 12 - provide a figure/panel citation for the "micrograph derived from a tonsillectomy" that is suggested for comparison. • In Figure 1 - Figure Supplement 1, how representative of the whole raft are these images? Does the extent of stratification change near to the edge of the collagen gel, for example? How well matched for location within a raft are the images shown? • Page 24 - clarify uses of the phrase "down-regulated in tonsils". Presumably this section refers to tonsil epithelium in 3D organotypic rafts.
Typos • Page 3 - "the cervix is lined with stratified squamous epithelia", should be epithelium. • "J.G. Rheinwald" in in text references. • Page 6 - 'or' not 'and' in first sentence of primary cell culture section.
All these ‘minor’ comments and typos will be addressed.
Reviewer #2 (Significance (Required)):
This highly descriptive study provides a detailed analysis of a bulk RNA sequencing experiment comparing foreskin, cervix and tonsil 3D organotypic rafts. Retained histological and transcriptional differences between epithelial tissues of different origins in organotypic assays are well documented in the literature (e.g., parmoplantar vs non-parmoplantar skin, PMID: 36732947; airway tract, PMID: 32526206) so the observed differences between these three very distinct anatomical tissues are unsurprising overall. The data have been made available via SRA and a shiny web app and are likely to be of interest and use to other researchers working on these tissues in culture. The experiment was performed in matched cell culture conditions so replicates are well-controlled, if limited in number (n=3).
We appreciate this feedback. We agree this is a descriptive study. Nonetheless, we believe there is value in formally demonstrating differences and similarities between these tissues. The provided references will be included to expand our discussion.
I am an epithelial cell biologist specializing in human cell culture models. I do not have sufficient computational background to comment in detail on the RNA sequencing methods or analysis within the manuscript.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
This is very carefully analysed and written study describing the transcriptional differences between in vitro models of epithelia derived from cervix, foreskin and tonsil tissues. Importantly, they compare the findings to in vivo samples using publicly available data. The findings are significant and will be of interest to the scientific community. I cannot fault the analysis pathways or the conclusions, and the manuscript is a pleasure to read. I recommend it is accepted for publication as is.
Reviewer #3 (Significance (Required)):
This is an important study that is highly significant for researchers interested in epithelia tissue and infection. The data are clearly presented and the analysis is thorough. The authors state that they will make the data publicly available. This will be an important resource for the community.
We appreciate the kind words
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Referee #3
Evidence, reproducibility and clarity
This is very carefully analysed and written study describing the transcriptional differences between in vitro models of epithelia derived from cervix, foreskin and tonsil tissues. Importantly, they compare the findings to in vivo samples using publicly available data. The findings are significant and will be of interest to the scientific community. I cannot fault the analysis pathways or the conclusions, and the manuscript is a pleasure to read. I recommend it is accepted for publication as is.
Significance
This is an important study that is highly significant for researchers interested in epithelia tissue and infection. The data are clearly presented and the analysis is thorough. The authors state that they will make the data publicly available. This will be an important resource for the community.
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Referee #2
Evidence, reproducibility and clarity
Summary
Jackson et al.'s manuscript describes an experiment that directly compares 3D organotypic assays created with primary human epithelial cells from foreskin, cervix and tonsil using histological and bulk RNA sequencing approaches. The authors convincingly show the retention of site-specific histological and transcriptomic differences between the stratified epithelial tissues in culture. Differentially expressed genes are identified and pathway analyses suggest genes that might be involved in the different differentiation processes between these tissue sites and differential regulation of ECM and immune pathways. Differentially expressed genes are used to develop a classifier for tissue identification, which is tested using GTEx data.
Major Comments
- The interferon stimulated genes of B cells and macrophages (from Mostafavi et al., 2016) are likely to be very different from those in epithelial cells, so the analysis presented in Figure 9 seems like a stretch to me.
- OPTIONAL: Further data comparing the nature and magnitude of the interferon responses of the three epithelia would improve interest in the manuscript but are not necessary for publication of the current dataset.
Minor Comments
- Details of n numbers and what each point represents should be added to Figure 1C. Are these points measurements from 25 um intervals of just one raft per donor? What are 'fields of view' here? Are measurements from one section or from multiple sections per raft?
- Page 12 - provide a figure/panel citation for the "micrograph derived from a tonsillectomy" that is suggested for comparison.
- In Figure 1 - Figure Supplement 1, how representative of the whole raft are these images? Does the extent of stratification change near to the edge of the collagen gel, for example? How well matched for location within a raft are the images shown?
- Page 24 - clarify uses of the phrase "down-regulated in tonsils". Presumably this section refers to tonsil epithelium in 3D organotypic rafts.
Typos
- Page 3 - "the cervix is lined with stratified squamous epithelia", should be epithelium.
- "J.G. Rheinwald" in in text references.
- Page 6 - 'or' not 'and' in first sentence of primary cell culture section.
Significance
This highly descriptive study provides a detailed analysis of a bulk RNA sequencing experiment comparing foreskin, cervix and tonsil 3D organotypic rafts. Retained histological and transcriptional differences between epithelial tissues of different origins in organotypic assays are well documented in the literature (e.g., parmoplantar vs non-parmoplantar skin, PMID: 36732947; airway tract, PMID: 32526206) so the observed differences between these three very distinct anatomical tissues are unsurprising overall. The data have been made available via SRA and a shiny web app and are likely to be of interest and use to other researchers working on these tissues in culture. The experiment was performed in matched cell culture conditions so replicates are well-controlled, if limited in number (n=3).
I am an epithelial cell biologist specializing in human cell culture models. I do not have sufficient computational background to comment in detail on the RNA sequencing methods or analysis within the manuscript.
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Referee #1
Evidence, reproducibility and clarity
The current study uses 3D organotypic rafts to culture primary keratinocytes from Foreskin, Tonsil and Cervix. Further the authors looked at the transcriptomic profiles of each tissue types to study similarities and differences depending on the tissue of origin as well as show the similarity in the tissue specific gene signatures and the ex-vivo samples (data from GTEx). As mentioned by authors Skin and Cervix keratinocytes have been previously cultured on collagen rafts however extending it to Tonsil provides resource and possibility of growing more tissue specific epithelial cells in 3D.
Major comments
- As the papers focus is to culture epithelial/ epidermal cells on 3D rafts, methods section needs more details about the raft composition, preparation, fibroblast embedding what was the plate size used for raft preparation and culturing of cells on those rafts. What culture media was used for epithelial raft cultures?
- Results: Figure 1, authors show IF staining's for COL17A1 as marker for basal cells and cornulin for differentiated layers. However, it is important to show how many cells in the basal layer are proliferative? (or how many layers of proliferative cells are present in different epithelia analysed here?) after 14 days majority of cells might already start losing their stemness potential (maybe staining for at least ki67 if staining for basal stem cell marker not possible? Along with loricrin or Involucrin might be good idea). This is also important as from supp fig 3 you can see F1 has higher expression of Loricrin, filaggrin etc as compared to all other samples indicating higher diff in this sample. Also, if authors can comment on what was the passage of cells used? And have they observed any difference in the re-epithelization in early passage versus late passage of keratinocytes?
- It is interesting to see Tonsillar 3D epithelia recapitulate the crypt and surface epithelia and authors also show this with gene expression profile, if possible (Optional), can authors show staining for crypt specific and surface specific markers.
- For all the Supplementary tables where only Ensembl ids are represented, please add gene Id column alongside (it is easier to get biological context from gene id for the reader rather than looking up Ensembl ids). Rename the file names to include the Supplementary file 1, 2, 3?
- Its excellent to see that in vitro tissue signature matched the in vivo tissue samples (Figure 8) but it will be interesting to show the gene expression differences if found any between the in vitro and in vivo samples that will give insight on the changes as result of in vitro system.
Minor comments
- Abstract: Give sample number (n?) and brief results about the genes that had tissue specific expression pattens.
- Gene names needs to be in Italics throughout.
- Introduction: page 5 line 9, authors claim that they based on comparisons they can "identify potential therapeutic targets for various disease" I think this statement either needs experimental evidence or statement / claim needs to be modified.
- Data submission to GEO???
- Typo (page 15, line 16 should be "HFK-down", same on page 23 "ectocervix", "endocervix", "uterus", so on, please correct, comma needs to be placed after "
- Page 24 last line is the heatmap referred here Fig 9B?
- Fig. 1 legends please indicate what F1, F2, F3, C1--- T1--- represent. Fig 1C Please add axis range/ values for protein atlas data as well.
- Can authors comment in discussion how was current 3D cervix cells on raft method different from Meyers, C., 1996 3D system?
Significance
This article does extend and validate the 3D raft culture method to different epithelial tissues in addition to Skin and cervix. This will be useful for the researchers using co culture systems and interested in understanding epithelial cell and immune cell interactions or host pathogen interacts etc
Describe your expertise: establishing and maintaining primary skin and oral keratinocyte cultures on feeders and 3D cultures on DEDs, Organoid cultures from oral keratinocytes, Oral cancer biology, Histopathology, transcriptomics study, Immuno-oncology.
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Reply to the reviewers
We thank the three reviewers for their thorough evaluation of our work and for their positive and constructive feedback. Below we provide an initial response to these comments, including descriptions of several changes incorporated in our preliminary revision. Please note that introductory and significance comments are not repeated here:
Reviewer 1
In my opinion, the main strength of this work is in the development and use of the original assay for adapter identification. As I already indicated, this is a biologically very important problem for cytoplasmic dynein. Another important strength of the paper is the extension of the work to Drosophila. Demonstration of the fact that Heatr5B is an essential gene, and that the product of this gene is involved in dynein-dependent trafficking in fly embryos makes the results significantly more important.I do not think there are many problems with the results in this manuscript. Generally speaking, the data on biochemical interactions are not as strong as I would like them to be. This is explained mainly by the fact that the authors do not have an expressed recombinant Heatr5B that they can use in biochemical experiments, and they limit their biochemistry by pulling down the protein from cell extracts.
Whilst we are very grateful to the reviewer for their thorough evaluation of our work, we do not understand this particular comment. We did include data with recombinant HEATR5B showing binding in vitro to purified dynein and dynactin complexes. The results are shown in Fig. 2B. We have now made it clearer (from line 153 of the preliminarily revised manuscript) that these experiments used recombinant HEATR5B. We hope in the future to determine the biochemical and structural basis of HEATR5B’s interaction with dynein and dynactin but feel that this goes well beyond the scope of this initial study (which already covers a lot of ground), especially as we have not yet found a way to express HEATR5B fragments (line 151).
This creates one of the few experimental problems with the paper. The authors claim that dynein and dynactin do not compete for Heatr5B binding, and therefore they can bind to both components of the complex at the same time. Unfortunately, I do not think that this claim is justified because concentrations of dynein and dynactin in their pull-down assay are much higher than the concentration of GFP-HEATR5B, and likely that HEATR5B does not saturate the binding sites on the motor complex. Therefore, it is unclear whether dynein and dynactin compete for Heatr5B binding. In any case, the conclusion about the competition cannot be seriously made without analysis of saturation curves.
The purified dynein and dynactin were not in excess to recombinant HEATR5B in this assay (80 pmol HEATR5B, 20 pmol dynein tail and 10 pmol dynactin). Nonetheless, the reviewer makes a very good point that we cannot draw strong conclusions about competition unless we generate saturation curves. We have therefore toned down the interpretation of this experiment and included the caveat raised by the reviewer (from line 157):
‘Compatible with this notion, we did not observe competition between the purified dynein tail and dynactin for HEATR5B binding in our in vitro binding assay when both complexes were added simultaneously to the beads (Figure 2B). However, we cannot rule out the possibility that a competitive interaction was masked by binding sites on one of the components not being saturated. Nonetheless, we can conclude from this set of experiments that HEATR5B complexes with endogenous dynactin and dynein in cell extracts and can interact with both complexes directly.’
Please note that this was only a minor point in our manuscript.
My second concern with this paper is the quality of imaging in mammalian cells. Unfortunately, not much can be done with live cell imaging because GFP-HEATR5B is expressed in cells at a low level (see, for example, Fig. 3A). However, in fixed cells GFP-HEATR5B signal could be easily amplified using anti-GFP antibodies.
The fixed cell images of GFP-HEATR5B cells are stained with anti-GFP antibodies and are the result of extensive optimisation of staining and imaging conditions. Due to its low expression and presence in both cytoplasm and membrane-bound pools, the signal for GFP-HEATR5B is not as striking as, for example, RAB11A and AP1γ. Nonetheless, the punctate signals are sufficiently strong to confidently evaluate co-localisation with membrane markers. We have now added to the relevant legends that the GFP signal is obtained via GFP antibody staining. Please note that the association of GFP-HEATR5B with AP1γ (Fig. 3A, B) was also confirmed by immunoprecipitation (Fig. 2A).
A minor problem with movie presentations is that the authors should include both a timer and a scale bar for all their live cell sequences, especially because the movies are looped. The authors did it for Movie 5, and they should do it for the rest of their live cell sequences.
Although information on the duration of movies (including loops) was included in the legends, we agree that it would be helpful to incorporate timers and scale bars in the movies. We have not been able to include this change in the preliminary revision as we have to co-ordinate with our visual aids team to reapply labels and arrows to the edited movies. This change will be made to the full revision.
In my opinion, the main novelty of this paper is in its pull-down assay, I would like to have it discussed more extensively. The authors state that they "were particularly drawn to Heatr5B". Is there an objective reason for this choice? If so, it should be specified.
We included our two reasons for focusing on HEATR5B in the previous submission, namely that it was the only protein to be enriched on the tail by dynactin in both the N- and C-terminal tethering configuration and that a previous study found it was one of a number of proteins present on dynactin-associated vesicles. We have modified the language in this section (which starts on line 120 of the preliminary revision) by using the connective ‘because’. This change makes it clearer that there were objective reasons for focusing on HEATR5B in the first instance.
Furthermore, I would like to see the authors discuss the other hits. Their list of hits includes a large number of ribosomal proteins. Do ribosomes really interact with dynein? Can the authors speculate on the number of true hits? Finally, it is likely that dynein interacts with some of the cargoes only transiently. How can the assay be modified to capture these transient interactions?
This is another very good suggestion. As requested, we have added a comment to the Discussion (from line 441) about how transient interactions might be captured using a variation of our strategy. We have now added a comment in the Discussion (from line 435) about the capture of ribosomes and other RNA-associated proteins in our screen, as well as the potential significance of this observation. We have also highlighted in this section another dynactin-stimulated hit, Wdr91, which we are following up. We also discussed the STRIPAK complex, which warrants further study, in the Results (line 106). We do not have space to discuss other hits but their identities are listed in Tables S1 and S2 together with a summary of their known functions for easy reference.
Reviewer 2:
Major points:
As a view of non-expert of light microscopy cellular imaging, some confocal images are difficult to accept as proofs of their conclusion that mutation to decrease HEAT5B/AP1 interaction results in diffusion from perinucleolar surface. For example, fluorescent signals in Control of Fig.4A seem more diffused than HR5B KO, which have fluorescence clearly localized on the surfaces of nuclei. Can they have explanation how it ends up with their statistical analysis in Fig.4E?
Fig. 4A is representative of what we typically see in mutant cells, with dispersion of the dimmer AP1γ signal in the cytoplasm and less disturbed localisation of the brighter AP1γ signal at the TGN (see Fig. S6B for quantification of AP1γ signal at the TGN in control and mutant cells). We should have made it clear in the Results that the unbiased image analysis pipeline used to produce Fig. 4E detects the total AP1γ signal not just bright signals (this feature of the pipeline is important given the differences in fluorescent intensity of puncta in the two genotypes). We have now clarified this issue in the Results (line 257) and the Fig. 4E legend. We have also added arrowheads to Fig. 4A to highlight the dispersed dim signal in the mutant cells. We thank the reviewer for leading us to improve the description of this experiment__.__
When they mention statistically more distance between target molecules and the perinuleolar surface, are dynein/dynactin connected to AP1 via HEAT5B stalled on the microtubule before reaching the minus end, or dissociate from the microtubule? Clarifying this will improve impact of this work. If the current data is not enough to answer, this reviewer will propose another confocal microscopy with also tubulin labeled. With this, the location of HEAT5B, AP1 etc. with respect to both nuclei and microtubule cytoskeleton will be clarified.
We would love to know the answer to the question of whether HEATR5B disruption reduces the association of AP1γ with microtubules. We have looked into co-localisation of microtubules and dynein’s cargoes previously using advanced light microscopy and found that it is not possible to draw conclusions about meaningful versus coincidental associations because of the density of the microtubule network. In the case of our current study, this approach would be further confounded by the difference in size in fluorescent AP1 puncta in control and HEATR5B mutant cells. We have also in the past attempted to purify recycling endosomal membranes from cells to determine how loss of HEATR5B influences dynein-dynactin association. However, even after extensive efforts we could not reproduce selective purification of recycling endosomes using the published protocol, or indeed variants of it. What is more, we find in general that there is rapid dissociation of motors during purification of membranes from cells, which would confound our results even if we could purify the recycling compartment. We therefore feel that the only way to address the question of how HEATR5B modulates dynein function at the molecular level is to reconstitute the transport machinery with pure proteins (including the as-of-yet unidentified activating adaptor) and microtubules in vitro, which is beyond the scope of this study. We have discussed the future aim of in vitro reconstitution to dissect mechanism in the Discussion (from line 494).
In Line168-169, they concluded AP1gamma associated with TGN rarely overlapped with HEATR5B, based on Fig.3A (where HR5B and AP1 seem overlapped in HeLa cells), Fig.S2A (where AP1gamma and TGN46 seem overlapped in U2OS cells) and Fig.S2B (where HR5B and TGN46 are not overlapped in HeLa cells). Is Fig.3A not contradictory to their conclusion (AP1gamma and HEATR5B not overlapped)? Why did they not directly check the overlap between AP1gamma and HR5B in the same cell in U2OS cells?
We don’t understand why our co-localisation data might be contradictory to our conclusions. Fig. 3A, together with the associated insets and quantification in Fig. 3B, show overlap of HEATR5B with AP1γ puncta in the cytoplasm of HeLa cells but not the AP1γ that is strong enriched in the perinuclear region, as we stated in the results. Absence of enrichment of HEATR5B with the TGN is additionally shown in Fig. S2B. These observations are commented on further in the Discussion (from line 517). We do, however, agree with the reviewer that is was not ideal that we did not show AP1 and TGN association in a HeLa cell (even though it has been documented in the literature). We have now corrected this oversight by showing HeLa cell data in Fig. S2A. We could not check the overlap of AP1 and HEATR5B in U2OS cells as we do not have a GFP-HEATR5B stable U2OS cell line.
Minor points:
Line100-105 and Fig.1EF are not clear. Is it correct that proteins in red bold letters and in blue letters in Fig.1EF are 28 proteins enriched on the dynactin tail?
We should have been clearer here and thank the reviewer for spotting this. We have modified the figure call outs in the text to include the labelling scheme, which we think helps significantly. We have also clarified the labelling system in the legend. To summarise, bold labelling indicates interactors of the dynein tail that are not core components of the dynein-dynactin machinery (such proteins are labelled in non-bold and italics); the blue bold text shows those ‘none core’ interactors that were only enriched on the dynein tail when exogenous dynactin was spiked into the lysates.
Do authors have any idea why the "dynactin-stimulated" ones (in blue) are localized at left end of this group (relatively less significance of dynactin tail binding, if this reviewer understands correctly)?
This question appears to indicate some confusion about whether we are capturing the dynein tail or dynactin. We believe the changes made in response to the previous comment about the labelling scheme should help clear this up. Being positioned to the left of this grouping shows a lower degree on enrichment vs the control (although still greater than 10 fold), rather than a difference in statistical significance. The observation that core dynein-dynactin subunits are more enriched on the dynein tail indicates that these interactions are the most stable or the most frequent.
Fig.S7: More explanation how to conclude that HR5B KO is dimmer than Ctrl based on this plot would be helpful.
We have added a line to the legend to Figure S7C to clarify this matter.
Reviewer 3:
Minor comments
HEATR5B overexpression in U2OS cells increased perinuclear clustering of Rab11A/AP1/dynactin-associated membrane. To which compartment are these vesicles directed and associated, the Golgi apparatus? Could the authors show which compartment it is?
We plan to perform new experiments to address this minor comment in the full revision. However, given their location near the microtubule organising centre, it is likely that the relocalised membranes will be in the vicinity of the Golgi apparatus.
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Referee #3
Evidence, reproducibility and clarity
Summary:
The goal of the authors is to identify dynein regulators which control how dynein and dynactin complexes orchestrate trafficking of diverse cargoes. To do so, the authors have performed a well thought proteomic screen for novel interacting proteins of the dynein tail potentially enhanced by dynactin. These pull-down experiments identified about 50 new dynein tail-interacting proteins, many of which were enhanced by dynactin.
The authors focused on one candidate, HEATR5B, because it was robustly isolated from the screens and its association with the dynein tail was stimulated by exogenous dynactin. HEATR5B is known to interact with AP1 complex, as adaptors that orchestrate cargo loading of clathrin-coated vesicles from intracellular membranes.
The authors further show that HEATR5B complexes with endogenous dynactin and dynein as reveal by immuno precipitation from human cells extracts and can interact with both complexes directly. Then by using Hela cell line stably expressing GFP-HEATR5B, they show that HEATR5B is selectively enriched on the AP1 structure, some of which can be subjected to long-distance transport. They provide evidences that a large proportion of the HEATR5B-positive structures are associated with endosomal recycling membranes, as revealed by colocalization with RAB11A. They further show that the HEATR5B/ AP1 and HEATR5B/ RAB11 membrane structures show similar dynamics, indicating that HEATR5B associate with endosomal membranes that are capable of directed movement. SiRNA depletion of DYNC1H1 reveals that dynein promotes retrograde trafficking of AP-1 associated endosomal membranes.
The authors then investigate the contribution of HEATR5B to AP1-associated membrane trafficking by CRIPR/cas9-mediated mutagenesis in human U2OS cells that disrupt HEATR5B protein expression. They provide evidences that in HEATR5B mutant cells, there is a reduction in the amount of AP1 signal associated with RAB11A-positive structures indicating that disrupting HEATR5B reduces the association of AP1with endosomal membranes. This indicates that HEATR5B promotes AP1 recruitment to endosomal membranes. HEATR5B overexpression in U2OS cells increased perinuclear clustering of Rab11A/AP1/dynactin-associated membrane, suggesting that HEATR5B can stimulate retrograde trafficking of AP1-associated endosomal membranes by dynein- dynactin.
To assess the importance of HEATR5B function at the organismal level, as well as in polarized cell type the authors investigate its function in Drosophila in which there is a single HEATR5B homologue (Heatr5). They generated via crisper an Heatr5 mutant strain. Heatr5 homozygous mutants are zygotic lethal that died in second larval instar stage. They further provide evidence by investigating nos-cas9 gRNA-Hr51+2 mothers, that Heatr5 plays maternal function essential for embryogenesis. They further show that in early embryos from nos-cas9 gRNA-Hr5 females AP1 puncta are strongly reduced and dimmer.
Next, to understand the effect of Heatr5 disruption on AP1-based trafficking in Drosophila, they used the syncytial blastoderm embryo in which the microtubule cytoskeleton is highly polarized with less apically nucleated ends above the nuclei and more basally extended ends. In this system, the activity of minus end-directed motor, such as dynein, and minus end-directed motor, such as kinesin, can be distinguished by the direction of cargo movement.
By injecting AP1 antibodies into wild-type and Heatr5 mutant embryos, they provide evidence that AP1 undergoes net apical transport in the Drosophila embryo and that this process is strongly promoted by Heatr5. They further show that this process is microtubule and dynein dependent and that Heatr5 selectively promotes dynein-mediated transport of AP1 structures in the embryo. They then show that Heatr5-dependent AP1 trafficking pathways in the embryo involves the endosomal and Golgi membranes and that Heatr5 is also required for Golgi organization.
Major Comments
This study is very comprehensive and multi-scale. It ranges from the identification of a dynein motor adaptor for membrane trafficking by a proteomic screen, to its functional characterization in human cells and then during development with Drosophila embryo as model organism. The data are of high quality and are supported by very convincing quantitative analyses. The results are conclusive and the experiments have been carried out and presented in a very constructive way. This combination makes the manuscript very interesting.
Minor comments
HEATR5B overexpression in U2OS cells increased perinuclear clustering of Rab11A/AP1/dynactin-associated membrane. To which compartment are these vesicles directed and associated, the Golgi apparatus? Could the authors show which compartment it is?
Significance
This study is important in two aspects. Firstly, it has identified HEATR5B as a new adaptor of the dynein motor for intracellular membrane trafficking. It is important to mention that this motor is involved in many transport processes and it is still unclear how a single motor orchestrates the traffic of so many cargoes. Second, this work shed new light on the retrograde trafficking from endosomal material to the Golgi apparatus, in particular with HEATR5B, a known interactor of the AP1 clathrin adapter complex. This study highlights a role of HEATR5B in a novel dynein-based process for retrograde trafficking of AP1-associated endosomal vesicle to the Golgi apparatus. It also indicates that HEATR5B promotes association of AP1 with endosomal membrane in a dynein-independent manner.
This work is particularly important for the cell biology field.
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Referee #2
Evidence, reproducibility and clarity
Major points:
As a view of non-expert of light microscopy cellular imaging, some confocal images are difficult to accept as proofs of their conclusion that mutation to decrease HEAT5B/AP1 interaction results in diffusion from perinucleolar surface. For example, fluorescent signals in Control of Fig.4A seem more diffused than HR5B KO, which have fluorescence clearly localized on the surfaces of nuclei. Can they have explanation how it ends up with their statistical analysis in Fig.4E?
When they mention statistically more distance between target molecules and the perinuleolar surface, are dynein/dynactin connected to AP1 via HEAT5B stalled on the microtubule before reaching the minus end, or dissociate from the microtubule? Clarifying this will improve impact of this work. If the current data is not enough to answer, this reviewer will propose another confocal microscopy with also tubulin labeled. With this, the location of HEAT5B, AP1 etc. with respect to both nuclei and microtubule cytoskeleton will be clarified.<br /> In Line168-169, they concluded AP1gamma associated with TGN rarely overlapped with HEATR5B, based on Fig.3A (where HR5B and AP1 seem overlapped in HeLa cells), Fig.S2A (where AP1gamma and TGN46 seem overlapped in U2OS cells) and Fig.S2B (where HR5B and TGN46 are not overlapped in HeLa cells). Is Fig.3A not contradictory to their conclusion (AP1gamma and HEATR5B not overlapped)? Why did they not directly check the overlap between AP1gamma and HR5B in the same cell in U2OS cells?
Minor points:
Line100-105 and Fig.1EF are not clear. Is it correct that proteins in red bold letters and in blue letters in Fig.1EF are 28 proteins enriched on the dynactin tail? Do authors have any idea why the "dynactin-stimulated" ones (in blue) are localized at left end of this group (relatively less significance of dynactin tail binding, if this reviewer understands correctly)?
Fig.S7: More explanation how to conclude that HR5B KO is dimmer than Ctrl based on this plot would be helpful.
Significance
In this work, Madan and colleagues studied dynein adaptor proteins, which are stimulated by dynactin, using proteomics, fluorescent microscopy, live cell imaging techniques for U2OS and fly embryo cells. They especially focused on HEATR5B and proved its role to bind AP1 membrane associate protein for intracellular transport. They first conducted proteomic studies and presented novel lists of dynein-associated proteins and proteins stimulated by dynactin. Among them they decided to prioritize HEATR5B protein (it would be interesting to know their motivation to choose this protein) and carried on fluorescent microscopy studies to characterize roles of HEATR5B in microtubule-based motility. Their approach using U2OS cells is to correlate distribution of HEATR5B and such proteins as AP1gamma, TGN46, RAB11A, which they expect interaction with HEATR5B, between WT and mutants. They remarkably demonstrated distance from perinucleolar membrane is heavily influenced by defect of adaptor function of HEATR5B, by fluorescent microscopy and statistical analysis. Next they made HEATR5B depleted Drosophila embryo by CRSPR-CAS9. They proved its influence on AP1 trafficking to Golgi, which is another novel finding of this study, consistent with the case of U2OS cells.
In general the whole study proved importance of HEATR5 proteins on AP1 trafficking. Many data are presented in convincing way and carefully statistically analyzed. This work will attract attention of wide audience from the field of cytoskeleton, motor proteins and membrane trafficking. After addressing a few points, the manuscript will be ready for publication.
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Referee #1
Evidence, reproducibility and clarity
This work is the first systematic attempt to identify and characterize a diverse set of adapters that attach cytoplasmic dynein to its different cargoes and thus activate the motor. It is an important work because in animal cells dynein is the only efficient motor that can perform processive transport toward the minus ends of microtubules, and therefore the specificity of transport for multiple cargoes along microtubules is determined by these adapters.
The authors use the recombinant tail of dynein for pulling down interacting proteins from the cell extract. This is a straightforward approach, but its main problem is the large number of non-specific proteins that bind to the column. To solve the problem, the authors use a very smart approach. It is based on the fact that in all known cases so far dynein does not transport cargoes without dynactin, and, therefore, potential adaptors are unlikely to bind to the affinity column very efficiently. They compare pull-downs in the presence and absence of dynactin paying specific attention to proteins that bind in the presence of both dynein and dynactin but not dynein alone.
Among the proteins that have been identified by this assay is Heatr5B, the protein known to associate with AP1 clathrin adaptor. Functional characterization of the protein can be divided into two parts, work with mammalian Heatr5B in tissue culture cells and analysis of its function in Drosophila.
In my opinion, the main strength of this work is in the development and use of the original assay for adapter identification. As I already indicated, this is a biologically very important problem for cytoplasmic dynein. Another important strength of the paper is the extension of the work to Drosophila. Demonstration of the fact that Heatr5B is an essential gene, and that the product of this gene is involved in dynein-dependent trafficking in fly embryos makes the results significantly more important.
I do not think there are many problems with the results in this manuscript. Generally speaking, the data on biochemical interactions are not as strong as I would like them to be. This is explained mainly by the fact that the authors do not have an expressed recombinant Heatr5B that they can use in biochemical experiments, and they limit their biochemistry by pulling down the protein from cell extracts. This creates one of the few experimental problems with the paper. The authors claim that dynein and dynactin do not compete for Heatr5B binding, and therefore they can bind to both components of the complex at the same time. Unfortunately, I do not think that this claim is justified because concentrations of dynein and dynactin in their pull-down assay are much higher than the concentration of GFP-HEATR5B, and likely that HEATR5B does not saturate the binding sites on the motor complex. Therefore, it is unclear whether dynein and dynactin compete for Heatr5B binding. In any case, the conclusion about the competition cannot be seriously made without analysis of saturation curves.
My second concern with this paper is the quality of imaging in mammalian cells. Unfortunately, not much can be done with live cell imaging because GFP-HEATR5B is expressed in cells at a low level (see, for example, Fig. 3A). However, in fixed cells GFP-HEATR5B signal could be easily amplified using anti-GFP antibodies.
A minor problem with movie presentations is that the authors should include both a timer and a scale bar for all their live cell sequences, especially because the movies are looped. The authors did it for Movie 5, and they should do it for the rest of their live cell sequences.
In my opinion, the main novelty of this paper is in its pull-down assay, I would like to have it discussed more extensively. The authors state that they "were particularly drawn to Heatr5B". Is there an objective reason for this choice? If so, it should be specified. Furthermore, I would like to see the authors discuss the other hits. Their list of hits includes a large number of ribosomal proteins. Do ribosomes really interact with dynein? Can the authors speculate on the number of true hits? Finally, it is likely that dynein interacts with some of the cargoes only transiently. How can the assay be modified to capture these transient interactions?
Significance
The bottom line is very clear. For me, it is an excellent technical paper with biological results that clearly demonstrate the validity of the technique. As such, it can and should be published.
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Reply to the reviewers
Manuscript number: RC-2023-01861
Corresponding author(s): Manuela, Baccarini
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1. General Statements [optional]
We were delighted to learn that all three reviewers found the paper novel and of interest for a cell biology audience. They especially highlighted the carefully conducted screen, whose results will be integrally published with this paper and will be of use for scientists interested in lysosome biology.
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
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The claim that "peripheral accumulation of lysosomes inhibits protrusion formation and limits cell motility" should be tested more rigorously using the RAMP method, preferably in living cells. Other approaches, such as overexpression/siRNA of Arl8b and other motor adaptors, such as SKIP/PLEKHM2, can be used to alter lysosome positioning and confirm this central finding of the manuscript. The authors could also consider including additional mechanistic data in order to comprehend how lysosome positioning controls cell motility. For instance, the RAMP approach could be employed to investigate cortical actin dynamics upon repositioning of lysosomes to the peripheral/perinuclear region.
Answer: We have purchased the RAMP system from Addgene and are adapting it to our color setup to use it in HeLa cells expressing GFP-PLEKHG3 and (hopefully) in PLEKHG3 KO cells, adding LiveAct to investigate cortical actin dynamics upon lysosomal repositioning as well as PLEKHG3 KO.
Reviewer 2
5 - It is not clear if in cells KO for PLEKHG3, the overexpression of KIF1A leads to more lysosomes localizing close to the PM, as well as more protrusions and more cell motility, as the authors only compare cell overexpressing GFP or GFP-PLEKHGL3.
Answer: Currently, we do not have a PLEKHG3 KO. We have, however, redoubled our efforts, so far unsuccessful, to generate a PLEKHG3 CRISPR-Cas KO in HeLa, going up to 10 sg-guides, and hope that we will be successful in the next future. In this case, we will be able to easily address this interesting question.
Reviewer 3
- Data presented in Figure 6 showing cell motility analysis is interesting and has potential to make the manuscript impactful. Similarly, data in Figure 4F (live cell imaging) looks attractive but is not informative in the absence of relevant genetic perturbations as comparisons. These types of experiments would benefit greatly from PLEKHG3 loss of function analysis, as well as mutational analysis in the over-expression setting.*
Answer: We have redoubled our efforts to generate a PLEKHG3 CRISPR-Cas KO in HeLa, going up to 10 sg-guides, and hope that we will be successful in the next future. This cell line will be helpful in answering the Reviewer’s question.
Mutational analysis cannot be performed, because of the lack of binding between LAMTOR3 and PLEKHG3, which leaves us without a read-out.
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.
Reviewer 1:
- The authors should also confirm the specificity of the PLEKHG3 antibody in immunofluorescence using control and PLEKHG3 siRNA in untransfected cells that have not been transfected with GFP-PLEKHG3 (as is shown in Fig. S2C). Numerous antibodies recognize the overexpressed protein but do not recognize the same protein at endogenous expression levels.
Answer: To assess the specificity of the antibody for endogenous PLEKHG3 we have used HEK293T cells, which based on the fact that PLEKHG3 is most highly expressed in neuronal cells (https://www.proteinatlas.org/ENSG00000126822-PLEKHG3/tissue#expression_summary) should yield a clearer endogenous signal. The results of this experiment are shown in the revised Figure S2B-C. The pattern of PLEKHG3-positive bands is similar to that observed in HeLa cells, and only the band around 250 kD is clearly reduced by the siPLEKHG3. The IF images show a selective loss of the PLEKHG3 signal in correspondence of actin filaments close to the plasma membrane, whereas the nuclear signal is preserved, and therefore to be considered non-specific (Figure only shown in attached revision plan and revised Figure S2B-C). In addition, we have redoubled our efforts, so far unsuccessful, to generate a PLEKHG3 CRISPR-Cas KO in HeLa cells, going up to 10 sg-guides, and hope that we will be successful in the next future.
Extract from revised Figure S2B-C: ____PLEKHG3 KD test in HEK293T cells: B) Western blot of HEK293T cells showing downregulation of PLEKHG3 expression upon siPLEKHG3 treatment compared to siScr. Bar plot shows quantification of PLEKHG3 bands from immunoblot above. Error bars = SEM, n=3. * = p values according to student's t-test. C) Immunofluorescence images of HEK293T cells. siPLEKHG3 shows drop in PLEKHG3 intensity in the periphery of the cell and less colocalization with Phalloidin. Scale bar = 50 µm. Line plots show intensity profiles of Phalloidin (green) and PLEKHG3 (red) along the white lines in the merged inset images. Scale bar = 10 µm.
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*The colocalization of endogenous PLEKHG3 and LAMP1 as depicted in figures 3B and 3C (data from fixed cells) is not convincing. PLEKHG3 appears to be present on cortical actin structures as opposed to being colocalized with LAMP1 on lysosomes. *
And related to this point:
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There is no apparent colocalization of PLEKHG3 and lysotracker in the movie S5.
Answer:
We do not claim that the two structures always colocalize. The images in Figure 3C are a schematic representation of the colocalization analysis shown in the plot and were included to explain how we define PLEKHG3 high/low regions or LAMP1 high/low regions, respectively. We agree with the Reviewer and with the previous literature that PLEKHG3 main localization is to cortical actin structures, as shown in Figure 3F of the original version and in Figure S2C (HEK293T cells) and in Figure S3A in HeLa cells in the revised version. The claim is rather that PLEKHG3 has been identified as a vicinal protein of LAMTOR3, seen by a fraction of lysosomes when they traffic into protrusions. We have clarified the text referring to Figure 3F on page 13, line 7-10 as follows:
"Immunofluorescence experiments showed the reported colocalization of endogenous PLEKHG3 (Figure S2C in HEK293T cells, Figure S3A in HeLa cells) and GFP-PLEKHG3 with cortical actin structures and the partial localization of LAMP1-positive vesicles to these structures in correspondence with vinculin-positive focal adhesions."
This specific claim is also based on the observation made in GFP-PLEKHG3-expressing cells (including movie S5, and particularly the stills of the leading edge in Figure 4F). In the text describing Figure 4F, we now clearly state on page 14, line 15-17: “Following a single cell over time, we could observe that __a subset of __lysosomes appears to travel to PLEKHG3 accumulation sites and specifically move into developing protrusions.”
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It is not clear how the authors conclude that Figure 4E graph shows "the LAMP1 signal was stronger in paxillin-labeled FA compared to control regions". The 4E graph shows LAMP1 signal in GFP versus GFP-PLEKHG3 and shows a modest enrichment of LAMP1 in FAs in GFP-PLEKHG3 overexpression. LAMP1 enrichment in FAs is also not obvious in the image shown in Figure 4B.
Answer: We stand corrected – the Figure we referred to was actually not in the manuscript. It has been inserted now, as a plot next to Figure 4B on page 16 Figure 4B (schematic representation of colocalization analysis) was designed to explain how we define focal adhesions (paxillin positive) and adjacent control regions (same size and shape, but paxillin-negative). The actual analysis was missing and has now been inserted. We apologize for this mistake.
We do not claim that PLEKHG3 brings lysosomes to FAs. The enrichment of lysosomes in FA regions of cells expressing GFP-PLEKHG3 compared to GFP-expressing cells shown in 4E, as the Reviewer correctly notes, is marginal and is not highlighted anywhere in the text exactly for this reason.
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In Fig. 2B, there appears to be a labeling error. The lanes 2,4 and 7 appear to be transfected with L3-T-V5 but labeled as GFP-V5-cyto. Here the PLEKHG3 band should be indicated.
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AND -Fig. 2C is an IP experiment as per the manuscript text but it is labeled as pulldown.
Answer: We stand corrected, and the necessary changes have been made in the revised version in Figure 2B on page 11.
Reviewer 2
*1 - Specificity of PLEKHG3 antibody: In Fig. S2, authors show that PLEKHG3 antibody recognizes 3 bands (above 100 kDa, above 130 kDa and 250 kDa) and all of them are reduced by the silencing of PLEKHG3. Then, in Fig. 2A and C, authors only show the band above 130 kDa, despite implying that the specific band should be "much higher than the 134 kDa calculated from the aminoacid sequence of the protein". *
In Fig. 2 B, they show all the bands shown in Fig. S2 and presumably favor that the specific and is the 250 kDa one. Finally, in Fig. 2D, they show all bands and note that the band above 130 kDa is not specific. Therefore, authors need to conclude what is the specific band and always analyze the same one, and, possibly, use a different antibody or purify this one to remove non-specific binding. Without this, the main result of the paper, cannot be substantiated.
Answer: We apologize for this misunderstanding. The antibody recognizes three bands, all reduced by siRNA treatment. These three bands are only resolved in the gels in Figure S2A and B, and in Figure 2B. The reason for this is the high molecular weight of the isoforms, that are resolved in these 8% gels, but collapse into one band in the 15% gels shown in Figure 2A and C. Therefore, the high molecular weight bands are not resolved under these conditions. 8% gels such as the ones in Figure 2B are needed to resolve the high molecular weight bands.
Figure 2D shows an 8% gel, and therefore all bands are visible. The band marked by an arrow is only present in the streptavidin pulldowns but not in the input or in the supernatant and is therefore considered unspecific. This has been clarified in the revised figure legend on page 11. In addition, to assess the specificity of the antibody for endogenous PLEKHG3 we have used HEK293T cells, which based on the fact that PLEKHG3 is most highly expressed in neuronal cells (https://www.proteinatlas.org/ENSG00000126822-PLEKHG3/tissue#expression_summary) should yield a clearer endogenous signal. The results of this experiment are shown in the Figure S2B-C of the revised manuscript. The pattern of PLEKHG3-positive bands is similar to that observed in HeLa cells, and only the band around 250 kD is clearly reduced by the siPLEKHG3. The IF images show a selective loss of the PLEKHG3 signal in correspondence of actin filaments close to the plasma membrane, whereas the nuclear signal is preserved, and therefore to be considered non-specific.
2 - In page 12, authors state that "These results indicated that PLEKHG3 is a transient interactor, or a proximal, not directly binding protein, of L3" and in page 14 that "... PLEKHG3 is a proximal L3 protein rather than a transient physical interactor". It is not clear at all how did the authors reach such conclusions, nor they have data to conclude this. Indeed, they would have to express the proteins in vitro and test their interaction to conclude about a direct binding. They also do not know what is the stability of the interaction.
Answer: This is also a misunderstanding. Unfortunately, we mislabeled Figure 2C as “pulldown”, rather than “IP”, as it is characterized in the text. The fact that we cannot co-ip PLEKHG3 by immunoprecipitating L3 using a V5 antibody led us to conclude that the interaction between the proteins is not direct or stable enough to survive a co-ip. Therefore, the most likely conclusion is that PLEKHG3 is a vicinal protein rather than an interactor of L3 – we changed the labeling of Figure 2C to clarify the issue on page 11.
Based on these negative data, we did not proceed to test the possibility of complex formation in vitro.
3 - Still in page 12, authors state that "... two different membrane structures, protrusions and ruffles". What do the authors mean exactly by "protrusions", as there are several different ones (e.g., lamellipodia, filopodia, pseudopods)? And how can they distinguish between ruffles and, for example, lamellipodia? They need to use markers and more carefully analyze their morphology to be able to distinguish these. Like this, it is too preliminary.
Answer: It was our intention to indicate with the arrows the trajectories in the figure along which we measured the MFI of LAMP1 and PLEKHG3. Although this is indicated in the figure legend, it had apparently given the impression that the arrows indicated specific membrane structures. Since we are focusing on different types of membrane protrusions rather than ruffles, we replaced the terms "ruffles" and "protrusions" with the terms "elongated protrusions" (Figure 3D upper panel) and then compared these with "non" elongated protrusions” (Figure 3D lower panel). Indeed, we note that PLEKHG3 accumulation is possible below and along the plasma membrane, but colocalization with lysosomes occurs preferentially in elongated protrusions. We therefore amended the text on page 12, line 24 – page 13, line 5 as follows:
„More specifically, we found that PLEKHG3 colocalized more strongly with LAMP1-positive vesicles in elongated membrane structures (Figure 3D-E). Focal adhesion sites, which anchor the intracellular cortical actin network to the extracellular matrix and are remodeled with the help of late endosomes/lysosomes during protrusion formation and cell motility, can also be found in such elongated membrane protrusions (reviewed in Burridge and Burridge, 2017; Schiefermeier et al., 2014).”
6 - Regarding the statistical analysis, authors assert that it was done using Student's t tests, unless otherwise stated. However, they never refer in figure legends other statistical analysis methods. If so, they cannot use such test, for example, in cases where more than two groups are compared.
Answer: in all our experiments we performed two-group comparisons. We have now deleted “unless otherwise stated” from the Materials and Methods section on page 41, lines 1-2.
*Minor comments: *
*1 - In the abstract, authors refer that cytosolic proteins are recruited to platforms on the limiting membrane of lysosomes. What do they mean by "platforms"? Is it microdomains? *
Answer: We apologize for this unclarity and have now changed the first sentence in the abstract on page 1 to “Lysosomes are key organelles involved in metabolic signaling pathways through their ability to recruit cytosolic molecules to protein platforms bound to the lysosomal membrane”. We refer to protein platforms as multifunctional protein complexes that can recruit and assemble signaling components (e.g., the recruitment of mTORC1 activating proteins by the LAMTOR complex).
*2 - In the Introduction, there is a period before the reference at the end of the first paragraph. *
Answer: We stand corrected. See changes on page 3, line 8.
3 - In the results, Fig. 1E is mentioned before Fig. 1D and Figure S1F before Fig S1E, which can be confusing.
Answer: Figure S1E on page 6 was mislabeled as Figure 1E and Figure S1K on page 9 was mislabeled as Figure 1K. We stand corrected. See changes on page 6, line 20 and page 9, line 4.
4 - All the immunofluorescence images need to be bigger, in general, and have zoom-ins, except Fig. 3A, 4B, 4F, and S2C. Also, in Fig. S1F, the green channel has different intensities and the V5-lyso signal is clearly saturated. Finally, Fig. S1D, S1I and S3F must be enlarged, too.
Answer: We appreciate the Reviewer's suggestion, but enlarging all the immunofluorescence images and including zoom-ins would make the manuscript overly crowded and could distract from the main findings. Regarding the expression levels of the baits, as mentioned in the manuscript, we aimed to express them at near-endogenous levels. However, TMEM192 is expressed at higher levels than LAMTOR3 in these cells, which may have resulted in the observed discrepancy. We hope the Reviewer will understand our decision and find the current presentation of the data clear and informative.
5 - In page 9, where it reads "Figure 1K", should read "Figure S1K".
Answer: See answer to minor point 3.
6 - The observation that PLEKHG3 silencing leads to loss of the perinuclear clustering of LAMP1-positive vesicles, and increase in their accumulation at the cell tips, is not referred in the text.
Answer: While this might seem the case in part of the cells shown in the representative image in Figure S2C, quantification of lysosome distribution did not show a significant difference throughout the population as displayed in the figure below (Figure only shown in attached revision plan).
__Figure 1 for Reviewer 2: __Lysosomal distribution in HeLa cells transfected with either siScr or siPLEKHG3. X-axis is relative distance from the nucleus and Y-axis the normalized intensity of the LAMP1 channel. Results are averages of >30 cells from one experiment.
7 - Fig. 2C is not referred in the legend.
Answer: We stand corrected and have changed the legend of Figure 2 accordingly on page 11.
8 - Figure S3A and B: authors should show the colocalization of endogenous PLEKHG3 with phalloidin and not only the GFP-tagged protein.
Answer: We thank the Reviewer for this comment and have performed this experiment showing the colocalization of endogenous PLEKHG3 with F-actin structures stained by Phalloidin. Even though the endogenous PLEKHG3 staining in HeLa cells is rather weak, sites where membrane protrusions are formed are clearly marked with PLEKHG3 staining below the plasma membrane. These data confirm the specific colocalization of PLEKHG3 with Phalloidin shown in the revised Figure S3A. See also the extract from Figure S3A below (Figure only shown in attached revision plan and revised Figure S3A).
Extract from revised Figure S3A: Immunofluorescence images of HeLa cells. A) HeLa cells stained with PLEKHG3 (red) and Phalloidin (green). The nucleus is indicated by DAPI staining (blue). Scale bar = 50 µm. Insets on the right as indicated by white box in image on the left. Scale bar = 10 µm. Line plot corresponds to white line in merged inset.
*9 - In page 14, authors refer to Fig. 3G, which does not exist. *
Answer: We stand corrected, the sentence on page 14, line 9 refers to Figure S3G.
10 - In page 30 and page 32, different antibodies for LAMP1 and PLEKHG3 are mentioned, but in the figure legends authors do not refer which one they used.
Answer: We tried different PLEKHG3 antibodies but ended up using only one. The other antibody has been excluded from the list on page 32, line 18. We have specified which LAMP1 antibodies were used in which Figure in the Material and Methods on page 30, lines 17.20-23.
11 - In page 33, where it reads "300 µm protein", it should probably read "300 µg protein".
Answer: We stand corrected and thank the Reviewer. See changes on page 33, line 17.
Reviewer 3
- A key issue … is that the authors focus solely on peripheral lysosomes as target compartments for PLEKHG3. This is not self-evident, particularly in light of images presented in Figures 2 and 3, where colocalization of PLEKHG3 with perinulcear lysosomes appears very likely. The authors should make differences/similarities they observe between effects on perinuclear versus peripheral lysosomes explicit both with data and in the text, if such differences exist.*
Answer: The Reviewer is likely addressing the images in Figure 3, which have been obtained by staining endogenous PLEKHG3 and do show diffuse staining around the nucleus. This perinuclear staining is resistant to siPLEHG3 (revised Figure S2C) and is not observed with the GFP-PLEKHG3 fusion protein (revised Figure S2E-F; including PLEKHG3 knockdown), which gives a less diffuse signal. This is why we are confident about the colocalization of PLEKHG3 with peripheral lysosomes. This said, we have redoubled our efforts to generate a PLEKHG3 CRISPR-Cas KO in HeLa, going up to 10 sg-guides, and hope that we will be successful in the next future. This cell line will be helpful in answering the Reviewer’s question.
Minor point: 1. Multicolor overlays with one of the channels in white is in my view not reader-friendly. Appreciating colocalization between endosomes/lysosomes, actin and G is very important for this study, and while is typically reserved to show overlay between green and magenta or green (standard for 2 channels), red and blue (standard for 3-channels). I therefore advise the authors to choose a different color combination throughout the figures when presenting microscopy images.
Answer: White as a channel color has been substituted for with red (in the 2- and 3-color images) or with blue (in the 4-color images) throughout the images of the revised manuscript, except for the stills from the videos that have not been changed because no colocalization analysis has been performed in this case.
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 2
4 - At least Fig. 2F and 3A need quantification. Regarding cell motility, there is no quantification and the authors must perform a quantitative assay (despite stating that "As another measure of cell motility, analysis of the number of forming protrusions and retracting membranes..."). Not only this is not a measure of cell motility, but there the issue of what are "protrusions" referred above. Therefore, authors need to quantify the distance that the cells move and/or perform quantitative motility/migration assays.
Answer: We appreciate the Reviewer’s attention to detail and agree that the quantification of these figures is essential to understand the results. We believe that the Reviewer is referring to Figure 3F and Figure 4A, as there is no Figure 2F, and Figure 3A only confirms the localization of endogenous PLEKHG3, as previously reported in (Nguyen et al., PNAS 2016). If our assumption is correct, then the salient aspects of Figure 3F, which is a representative image, are quantified in Figure 3C-E (endogenous PLEKHG3 colocalization colocalization with LAMP1/lysosomes) and Figure 4E and 5F-G (FA with LAMP1/lysosomes). Figure 4A is quantified in Figure 4C-E (GFP-PLEKHG3 colocalization with FAs, this time labeled with paxillin, and LAMP1 colocalization with FAs).
In response to the Reviewer's comment regarding the absence of quantification for cell movement/migration in our study, we apologize for any confusion that may have arisen from our use of the term "cell motility." We did not use this term to describe exclusively directed cell movement, but rather in a broader sense, to encompass the entirety of membrane remodeling processes involved in migration. In this context, our statement that lysosomal subcellular localization plays a role in cell motility remains valid. The relationship between membrane protrusive activity and motility is evident from our observations in cells overexpressing KIF1A-mCherry, where both membrane remodeling/protrusive activity and movement are significantly impaired compared to control cells (refer to Movie S7 vs. S6 and S10 vs. S9).
To address the Reviewer's concern, we have clarified our definition of motility in the introduction by stating on page 5, lines 1-4: "We demonstrate that PLEKHG3 colocalizes with lysosomes at focal adhesion and protrusion sites, and that the localization and function of this protein, as well as cell motility – which we define as the sum of membrane remodeling processes involved in migration – depend on lysosomal dynamics." This revision ensures that our results are accurately described and minimizes any potential confusion. Additionally, we have removed the statement on page 23, line 1 of the original manuscript. We apologize for any confusion our original wording may have caused and appreciate the opportunity to clarify our intentions.
Reviewer 3
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- The mechanism of PLEKHG3 action on lysosomes/late endosomes is underdeveloped in my view. In the absence of for instance mutational analyses to examine what drives the interaction of PLEKHG3 with LAMTOR3, as well as delineation of at least some molecular consequences of this binding, the study remains incomplete.*
Answer: We are grateful for the Reviewer's feedback and concur that gaining insight into the mechanistic details of PLEKHG3's interaction with LAMTOR3 would be beneficial. However, our investigation revealed that PLEKHG3 is a transient interactor/proximal protein of LAMTOR3, and due to the absence of direct binding between LAMTOR3 and PLEKHG3 (Figure 2C on page 11), we are unable to perform a mutational analysis of this interaction, as it lacks a direct read-out.
Furthermore, as demonstrated in Figure S3H-L, LAMTOR3 ablation does not affect PLEKHG3 subcellular localization, suggesting that delving deeper into the molecular consequences of their interaction may be highly complex and beyond the scope of this study. We kindly ask the Reviewer to bear with us on this point, considering the novelty of our findings, which illuminate the interplay between lysosomes and actin dynamics as well as the role of PLEKHG3 in regulating cell protrusions—findings not previously reported in the literature.
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Referee #3
Evidence, reproducibility and clarity
The manuscript by Ettelt et al describes the identification of PLEKHG3 as a collaborator of the LAMTOR complex on lysosomes using proximity-based biotinylation. The biotinylation screen is well executed and controlled. The authors choose to follow up on PLEKHG3, a protein involved in actin dynamics, which they refer to as understudied (I let the validity of the latter statement to be evaluated by the editor). Generally speaking, the data are of good quality, and the manuscript is clear and well written. However, much of the evidence on the role of PLEKHG3 on lysosomes is suggestive at best and further investigation into its mechanisms of action is warranted. Some important points to address prior to publication are detailed below.
Major Points:
- The mechanism of PLEKHG3 action on lysosomes/late endosomes is underdeveloped in my view. In the absence of for instance mutational analyses to examine what drives the interaction of PLEKHG3 with LAMTOR3, as well as delineation of at least some molecular consequences of this binding, the study remains incomplete.
- A key issue possibly (but not necessarily) related to the point above is that the authors focus solely on peripheral lysosomes as target compartments for PLEKHG3. This is not self-evident, particularly in light of images presented in Figures 2 and 3, where colocalization of PLEKHG3 with perinulcear lysosomes appears very likely. The authors should make differences/similarities they observe between effects on perinuclear versus peripheral lysosomes explicit both with data and in the text, if such differences exist.
- Data presented in Figure 6 showing cell motility analysis is interesting and has potential to make the manuscript impactful. Similarly, data in Figure 4F (live cell imaging) looks attractive but is not informative in the absence of relevant genetic perturbations as comparisons. These types of experiments would benefit greatly from PLEKHG3 loss of function analysis, as well as mutational analysis in the over-expression setting.
Minor point
- Multicolor overlays with one of the channels in white is in my view not reader-friendly. Appreciating colocalization between endosomes/lysosomes, actin and G is very important for this study, and while is typically reserved to show overlay between green and magenta or green (standard for 2 channels), red and blue (standard for 3-channels). I therefore advise the authors to choose a different color combination throughout the figures when presenting microscopy images.
Significance
In principle, I consider this study to be of interest to the community of cell biologists working on the endolysosomal system and/or the actin cytoskeleton and its relationship to intracellular membranes. However, the authors find themselves in a rather crowded field. I feel that developing the mechanism of action of PLEKHG3 on lysosomes beyond this first submission could help with boosting the impact of the study. There is clearly something interesting going on, but what that is exactly, remains unclear in my view.
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Referee #2
Evidence, reproducibility and clarity
Summary: The authors use proximity-dependent labelling and mass spectrometry to identify cytoplasmic proteins that interact with lysosomes. They show that PLEKHG3 interacts with the LAMTOR complex; that PLEKH3 accumulates in focal adhesion sites, where it colocalizes with peripheral lysosomes; and that the increased translocation of lysosomes to the periphery leads to less "protrusions", as well as rounder cells and less motile cells.
Major comments: While the study is generally carefully performed and thorough, there are major shortcomings that affect the conclusions taken, namely the specificity of the PLEKHG3 antibody, the identification of "protrusions" and ruffles, several quantifications missing, and the data used to conclude about cell motility. There are also conclusions for which there is no concrete or solid evidence.
Specific issues:
- Specificity of PLEKHG3 antibody: In Fig. S2, authors show that PLEKHG3 antibody recognizes 3 bands (above 100 kDa, above 130 kDa and 250 kDa) and all of them are reduced by the silencing of PLEKH3. Then, in Fig. 2A and C, authors only show the band above 130 kDa, despite implying that the specific band should be "much higher than the 134 kDa calculated from the aminoacid sequence of the protein". In Fig. 2 B, they show all the bands shown in Fig. S2 and presumably favor that the specific and is the 250 kDa one. Finally, in Fig. 2D, they show all bands and note that the band above 130 kDa is not specific. Therefore, authors need to conclude what is the specific band and always analyze the same one, and, possibly, use a different antibody or purify this one to remove non-specific binding. Without this, the main result of the paper, cannot be substantiated.
- In page 12, authors state that "These results indicated that PLEKHG3 is a transient interactor, or a proximal, not directly binding protein, of L3" and in page 14 that "... PLEKHG3 is a proximal L3 protein rather than a transient physical interactor". It is not clear at all how did the authors reach such conclusions, nor they have data to conclude this. Indeed, they would have to express the proteins in vitro and test their interaction to conclude about a direct binding. They also do not know what is the stability of the interaction.
- Still in page 12, authors state that "... two different membrane structures, protrusions and ruffles". What do the authors mean exactly by "protrusions", as there are several different ones (e.g., lamellipodia, filopodia, pseudopods)? And how can they distinguish between ruffles and, for example, lamellipodia? They need to use markers and more carefully analyze their morphology to be able to distinguish these. Like this, it is too preliminary.
- At least Fig. 2F and 3A need quantification. Regarding cell motility, there is no quantification and the authors must perform a quantitative assay (despite stating that "As another measure of cell motility, analysis of the number of forming protrusions and retracting membranes..."). Not only this is not a measure of cell motility, but there the issue of what are "protrusions" referred above. Therefore, authors need to quantify the distance that the cells move and/or perform quantitative motility/migration assays.
- It is not clear if in cells KO for PLEKHG3, the overexpression of KIF1A leads to more lysosomes localizing close to the PM, as well as more protrusions and more cell motility, as the authors only compare cell overexpressing GFP or GFP-PLEKHGL3.
- Regarding the statistical analysis, authors assert that it was done using Student's t tests, unless otherwise stated. However, they never refer in figure legends other statistical analysis methods. If so, they cannot use such test, for example, in cases where more than two groups are compared.
Minor comments:
- In the abstract, authors refer that cytosolic proteins are recruited to platforms on the limiting membrane of lysosomes. What do they mean by "platforms"? Is it microdomains?
- In the Introduction, there is a period before the reference at the end of the first paragraph.
- In the results, Fig. 1E is mentioned before Fig. 1D and Figure S1F before Fig S1E, which can be confusing.
- All the immunofluorescence images need to be bigger, in general, and have zoom-ins, except Fig. 3A, 4B, 4F, and S2C. Also, in Fig. S1F, the green channel has different intensities and the V5-lyso signal is clearly saturated. Finally, Fig. S1D, S1I and S3F must be enlarged, too.
- In page 9, where it reads "Figure 1K", should read "Figure S1K".
- The observation that PLEKHG3 silencing leads to loss of the perinuclear clustering of LAMP1-positive vesicles, and increase in their accumulation at the cell tips, is not referred in the text.
- Fig. 2C is not referred in the legend.
- Figure S3A and B: authors should show the colocalization of endogenous PLEKHG3 with phalloidin and not only the GFP-tagged protein.
- In page 14, authors refer to Fig. 3G, which does not exist.
- In page 30 and page 32, different antibodies for LAMP1 and PLEKHG3 are mentioned, but in the figure legends authors do not refer which one they used.
- In page 33, where it reads "300 µm protein", it should probably read "300 µg protein".
Significance
The study provides evidence that lysosome positioning can affect cortical actin cytoskeleton dynamics, as well as cell shape and motility. Experiments are in general thorough and data subjected to quantification. However, there are fundamental conclusions that are preliminary at this stage, as some of the data is not yet solid enough. Therefore, it needs to be further strengthened to be considered for publication. In general, it reads well but the amount of abbreviations (e.g. in the case of the constructs) makes it somehow difficult to follow. The study will be interesting for the cell biology, membrane trafficking and cytoskeleton dynamics communities.
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Referee #1
Evidence, reproducibility and clarity
The manuscript by Ettelt et al., describes identification of Rho guanine nucleotide exchange factor- PLEKHG3 as one of the positive hits from a TurboID proximity-dependent labeling screen using LAMTOR3 (one of the subunits of the pentameric LAMTOR complex/Ragulator) as a bait protein. The authors find that PLEKHG3 colocalizes with lysosomes at focal adhesions and that peripheral clustering of lysosomes promotes PLEKHG3 localization near the plasma membrane, and also inhibits protrusion formation and cell motility. The experiments, particularly the Turbo ID proximity-dependent labeling screen, are well-executed, and the imaging data is aptly quantified. The manuscript explores an exciting question of how lysosome positioning regulates cortical actin dynamics and thereby cell motility.
Major comments:
- The colocalization of endogenous PLEKHG3 and LAMP1 as depicted in figures 3B and 3C (data from fixed cells) is not convincing. PLEKHG3 appears to be present on cortical actin structures as opposed to being colocalized with LAMP1 on lysosomes. The authors should also confirm the specificity of the PLEKHG3 antibody in immunofluorescence using control and PLEKHG3 siRNA in untransfected cells that have not been transfected with GFP-PLEKHG3 (as is shown in Fig. S2C). Numerous antibodies recognize the overexpressed protein but do not recognize the same protein at endogenous expression levels.
Moreover, do the authors observe colocalization between GFP-PLEKHG3 and lysotracker in living cells? There is no apparent colocalization of PLEKHG3 and lysotracker in the movie S5. - The authors observe that GFP-PLEKHG3 is concentrated at the cell's periphery when KIF1A is overexpressed, whereas RUFY3 overexpression results in more cytosolic staining. To bolster their conclusion that a change in lysosomal positioning alters the subcellular localization of PLEKHG3, it is preferable to employ inducible techniques, such as the recently described "reversible association with motor proteins" (RAMP) (PMID: 31100061). The method is a rapid and reversible method for altering organelle positioning. It is still unknown whether PLEKHG3 is associated with lysosomes and mechanism of how positioning of lysosomes affects PLEKHG3 localization. - Similarly to the preceding point, the claim that "peripheral accumulation of lysosomes inhibits protrusion formation and limits cell motility" should be tested more rigorously using the RAMP method, preferably in living cells. Other approaches, such as overexpression/siRNA of Arl8b and other motor adaptors, such as SKIP/PLEKHM2, can be used to alter lysosome positioning and confirm this central findings of the manuscript. The authors could also consider including additional mechanistic data in order to comprehend how lysosome positioning controls cell motility. For instance, the RAMP approach could be employed to investigate cortical actin dynamics upon repositioning of lysosomes to the peripheral/perinuclear region. - It is not clear how the authors conclude that Figure 4E graph shows "the LAMP1 signal was stronger in paxillin-labeled FA compared to control regions". The 4E graph shows LAMP1 signal in GFP versus GFP-PLEKHG3 and shows a modest enrichment of LAMP1 in FAs in GFP-PLEKHG3 overexpression. LAMP1 enrichment in FAs is also not obvious in the image shown in Figure 4B. - In Fig. 2B, there appears to be a labeling error. The lanes 2,4 and 7 appear to be transfected with L3-T-V5 but labeled as GFP-V5-cyto. Here the PLEKHG3 band should be indicated. - Fig. 2C is an IP experiment as per the manuscript text but it is labeled as pulldown.
Significance
Using a TurboID proximity-dependent labelling screen, the authors identified an interesting subset of actin-remodeling proteins that interact with the lysosomal protein LAMTOR3. The authors further characterized one of these proteins, PLEKGH3, and found that lysosome positioning regulates PLEKGH3 localization, as well as plasma membrane protrusion formation and cell motility. This study suggests that lysosome peripheral accumulation could regulate cortical actin remodelling and consequently cell migration by regulating PLEKGH3 localization (although this is not tested in the manuscript). This study adds to the previous findings that microtubule-based transport of late endosomes regulate delivery of late endosomal LAMTOR proteins to the vicinity of focal adhesions, which in turn, regulate focal adhesion dynamics. The mechanism of how lysosomes can influence actin remodeling will be important in the context of cancer cell migration. My area of expertise is lysosome fusion and motility and I have limited expertise in regulation of actin dynamics and how Rho family members regulate actin remodeling.
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Reply to the reviewers
Manuscript number: RC-2023-01846
Corresponding author(s): Anastassis Perrakis
1. General Statements
We thank the reviewers for the feedback, highlighting the synergy between computational modeling approaches and the experimental techniques we used to study the interaction between JBP1 and J-DNA. We would like to re-iterate that this approach has led to new findings regarding JBP1 and J-DNA interactions, namely:
- We identified and validated an additional interface in DNA binding domain of JBP1 (JDBD), that contributes to J-DNA binding.
- Through analysis of the AlphaFold model of JBP1, we propose how the Thymidine Hydroxylase domain (THD) of JBP1 binds J-DNA, and how the JDBD and THD domains are connected flexibly but explicitly to each other.
- The AlphaFold model allowed to hypothesize that the N-terminus of JBP1 is contributing to J-DNA binding, which we confirmed experimentally. These findings collectively suggest a mechanistic and structural basis on the synergy between the JDBD, the THD and the N-terminus of JBP1, providing a possible explanation to the previously observed conformational changes of JBP1 upon J-DNA binding. Our findings on the conservation of the N-terminus region and the new interface of JDBD, could be offering an explanation on the differences on how essential base-J is for different Trypanosomidaespecies. They also offer a first glimpse of how these domains synergize to provide new insights in the semi-conservative replication mechanisms of the base-J epigenetic marker in kinetoplastids.
2. Point-by-point description of the revisions
Reviewer #1____: ____Evidence, reproducibility and clarity
Summary:
The paper presents a combined experimental (X-ray, SAXS, mutational analysis) and computational (MD, docking, AlphaFold) work that elucidates the mechanism of JDBD:JDNA complex formation.
Major comment:
- How did the authors decide the timescale of the production run? Wouldn't the loop motion (which can be necessary for this study) occur on a timescale of 300+ ns?
While our simulations showed overall stability of the simulated protein (as reflected by the RMSD time series), the RMSF provided clear indications for differences in flexibility in the loops and termini of JBP1. We believe that performing an MD simulation of 100 ns in duplo samples the flexibility and behavior of the JBP1 DNA binding domain (JDBD) sufficiently for obtaining templates for docking studies, which was the purpose of running the simulations. We emphasized this in the manuscript (page 10) by adding: “and obtain additional templates for further docking studies”.
Minor comments:
- Did I understand correctly that the LINCS algorithm constrained only hydrogen-involving bonds? It is not mentioned explicitly. Or am I missing something?
LINCS was indeed used to only constrain hydrogen-involving bonds. We made this more explicit in the MD protocol described in the method section of the manuscript: “The LINCS algorithm (40) was used to constrain hydrogen-involving bond lengths to their zero-energy value”.
- The authors should increase the resolution of figures S1 and S3. They look a bit blurry.
We apologize for that; we tried to improve that by adjusting the figure sizes, but we are constrained by the output from e.g., the Bitclust software. We sincerely hope that the current resolution does not present an obstacle to the reader.
Significance:
The J DNA base is critical for transcription termination at the ends of the polycistronic gene clusters in Leishmania and related species. Hence, understanding the formation mechanism of the JDBD:J-DNA complex can provide an opportunity to develop novel chemotherapeutic treatments against these diseases. This work provides the first crystal structure of JDBD with the disordered loop and suggests that R448 and N455, as well as the N-terminus, are involved in the J-DNA binding process. The article is well-written and can interest readers from biological and biochemical societies. However, my field of expertise is computational chemistry and biochemistry; therefore, I cannot adequately evaluate the accuracy of the experimental techniques used in this work.
We thank the reviewer, but would like to emphasize that our work goes well beyond the new interface of the JDBD, offering significant new insights on the synergy between the THD, the JDBD and the newly identified N-terminus binding to J-DNA, as also outlined in the general summary above.
__Reviewer #2_:_ Evidence, reproducibility and clarity __
The manuscript by de Vries et al. reported the crystal structure of the J-DNA binding domain of JBP1. Although, the structure was already solved, the new structure allows to observe a loop that was disordered in the previous structure. This structure was next used to propose models of DNA complex analyzed by MD. The proposed model was then validated by mutagenesis.
Overall, the findings are interesting and the technical quality of the work is high.
We believe, as we outlined in the summary, that our work goes well beyond showing the new structure and validate the new interface by mutagenesis. In our view, the major findings of the paper have to do with the AlphaFold modeling analysis and validation, and the finding that the N-terminus of JBP1 is involved in DNA binding, something that is not only new, but has also been totally unexpected.
Comments:
-For clarity, a figure showing the domain organization of JBP1 could help the reader in the introduction part.
The domain architecture of JBP1 was added to Figure 1 as panel B.
-In addition to Figure 2 showing the newly observed loop in 2Fo-Fc map, an omit map should be included in Supp data.
A figure of the omit map was added to the supplemental information as Supplemental Figure S1.
-Figure S6 legend should be more precise about the type of HDX MS analysis.
As the HDX-MS data and methods were described in detail in previous work (Heidebrecht et al. 2011), we left the details out in the current manuscript. The reference to this paper was added to Figure S6 for clarity.
-The authors performed MD simulations. But what about DNA curvature upon complex formation?
For the JDBD MD simulations, we did not add at all the (J-)DNA and the current simulations provide no information about its curvature. As mentioned in the discussion, we do expect conformational changes when the J-DNA:JBP1 complex forms, and this likely includes DNA curvature as well as conformational changes between the protein domains. We felt that the current data would not allow to extract new insights from such complicated simulations.
-p.12 Some mutants were characterized, notably their melting temperatures. One mutant shows decreased stability while R448A shows increased stability. What is the structural explanation?
Indeed, the E437A mutant (that showed lower expression compared to the other mutants) showed decreased thermal stability. The R448A shows an increase in stability (~3o C), and so does the H440 mutant (~2o C). While there is no specific structural explanation for these observations, in general mutation to alanine reduces the entropy-loss upon protein folding. The reason we comment about the stability is to point out that the dramatically decreased binding of the N455A and R448A mutants is not due to a decrease of the protein stability. This is now clarified in the manuscript: “the other mutants are as stable or slightly more stable compared to the wild-type, suggesting that the DNA-binding analysis is not affected significantly by altered protein stability.”
-Figure 6E: The chi2 value for the comparison of the experimental curve for THD domain and calculated curve is very high indicating a poor fit. What is the explanation?
The χ2 value indeed reflects differences between the JBP1 THD selected from the AlphaFold model and the structure used in the SAXS experiment. The experimental model is the so-called ΔDBD, which is the full length JBP1, where the JDBD is missing (it has been “spliced out”). Hence, the connecting loops and the N-terminus are present in this ΔDBD structure, whereas in the THD of the AlphaFold model, these parts of the structure were left out. In other words, while the full-length computational model refers to the exact same purified protein, the computationally truncated model and the purified protein for the experiments, have actual differences. Thus, the shape and fit of the experimental curve to the calculated curve can be considered pretty good. This is now clarified in the manuscript by adding: “The χ2 value of the fit is slightly elevated due to presence of the connecting loops between the THD and the JDBD and the N-terminus in the protein used for measuring the SAXS curve, which were removed from the computational model.”.
Significance:
The novelty of the manuscript mainly relies on the description of the crystal structure of JDBD protein without DNA and proposed models of DNA complex within full length protein, models that were validated by mutations or truncations. The current manuscript well suited for a specialized journal.
These findings are indeed novel, especially the discovery and validation of the new interface of JDBD to J-DNA. We want to iterate that we are most excited by the totally unexpected and mechanistically important discovery of the role of the N-terminus of JBP1, that brings together legacy data and raises interest for additional structural studies.
__Reviewer #3_: _Evidence, reproducibility and clarity __
Base J, also known as β-D-glucopyranosyloxymethyluracil, is a modified form of thymidine that has been identified in kinetoplastids and related organisms. It is worth noting that the distribution of Base J in the genome may vary depending on the organism and its life stage and influences its genome dynamics. The synthesis of this hypermodified nucleotide occurs in two steps, which involve the participation of two distinct thymidine hydroxylases, namely J-binding protein 1 and 2 (JBP1 and JBP2), along with a β-glucosyl transferase. In this study, the authors have presented a crystal structure of JBP1 J-DNA binding domain (J-DBD), which includes a previously reported disordered loop that might be involved in JBP1:J-DNA contact. Using this disordered structure as a starting point, the authors conducted Molecular Dynamics simulations and computational docking studies to propose models for the recognition of J-DNA by JBP1 J-DBD. The results from these studies were validated by punctual mutagenesis experiments, which provided additional data for docking and revealed a binding pattern for JBP1 J-DBD on J-DNA. By combining the crystallographic structure of the TET2 JBP1-homologue in complex with DNA and the AlphaFold model of full-length JBP1, the authors have hypothesized that the flexible N-terminus of JBP1 contributes to DNA-binding, which they have confirmed experimentally. However, according to the authors, to gain a deeper understanding of the unique molecular mechanism that underlies the replication of epigenetic information, an experimental determination of a high-resolution JBP1:J-DNA complex involving conformational changes would be necessary. Nevertheless, the present proposed objectives were fully contemplated by the authors.
Major comments:
In my opinion, the present article effectively achieved all the described objectives using appropriate and reproducible methodology, including protein expression and crystallization analysis, Molecular Dynamics analysis using GROMACS-2020.2 software, docking analysis, punctual mutations analyses, and modeling of JBP1:J-DNA complex using the AlphaFold tool. The authors presented the results in a logical and organized manner, making it easy for readers to extract the most important points. However, I believe that the section titled "Results and Discussion" contains more "results" than "discussion". While I understand that the literature on JBPs and base J is still in its early stages, other species of kinetoplastids have JBP1, in which mutations were not lethal as in L. tarentolae (e.g. T. brucei). Therefore, providing information about the structure of JBP1 and how the present results relate to what is known about JBP1 in other species in terms of structure and J-DNA interactions would significantly enrich the discussion of the findings and reinforce their significance and impact. Thus, the authors should have been clearer about the impact of their findings. When discussing the results, the authors should have answered questions such as how the identification of the new residues involved in JBP1 J-DNA binding impacts the current model of JBP1:J-DNA interactions, how this improved model contributes to the understanding of base J synthesis, and if the new model can be extrapolated to other species of kinetoplastids, according to the conservation of JBP1 among them.
Although the article is more focused on protein research rather than parasite general molecular biology and medical studies, the findings may have implications for the development of new treatments for leishmaniases. Therefore, the authors should have discussed the potential of their new improved model as a target for lacking treatments of leishmaniases or at least brought up the point at conclusion section.
We thank the reviewer for pointing out that the comparison between kinetoplastid species could be described more explicit to highlight the impact of the presented results with respect to the variety in JBP1 sequence, and possibly contribute to understanding the role of base-J in the differences in lethality and transcription regulation within these species. We now elaborate on our results in multiple places in the manuscript:
- In the introduction we introduce the differences in lethality and transcription regulation within Leishmania and Trypanosoma (see also minor comment 2 below).
- An alignment of full-length JBP1 sequences of different Trypanosomatidae species was added as Supplemental Figure S10 to support the discussion below.
- The section describing the docking model of JDBD:J-DNA has been ammended with a description regarding the conservation of the residues involved in the binding interface: “The residues described in the JDBD:J-DNA interface are in general highly conserved (Supplemental Figure S12). Asp525 is fully conserved in Leishmania, Trypanosoma, Leptomonas and Bodo saltans species, so are Lys522, Arg532 and ArgR448. Asn455, which we identify in this study, is not conserved in Leptomonas, and Arg517 is not conserved in Trypanosoma also.”
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We renamed the final section to “Conclusions and Outlook” and added some discussion focusing on the conservation of the residues in the N-terminus and in the JDBD between different Trypanosomatidae Specifically, we now discuss how these could contribute in understanding the differences in lethality and transcription termination between Leishmania and Trypanosoma in the absence of base-J.
Minor Comments:
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Please, re-check the affirmation "99% of base-J is found in telomeric repeats, mainly in GGGTTA repeats wherein the second thymine is modified to base-J (2-4)" in the Introduction. I believe that the distribution of base-J varies among different species of trypanosomatids and, therefore, cannot be generalized. Moreover, among different life stages in some organisms such as T. brucei and Leishmania major, differences on base-J distribution are found. The 99% of telomeric base-J mentioned would be a feature of Leishmania genus. Please, re-check the references 3 and 4.
Indeed, the referee is right to mention that the 99% is a Leishmania-specific observation. We have modified the introduction accordingly. “Base-J is found mainly in telomeric repeats and other repetitive sequences. In Leishmania 99% of base-J is found in telomers, mainly in GGGTTA repeats, wherein the second thymine is modified to base-J (2–4).”
Please, enrich the introduction topic with information about the model species, such as importance as pathological agent, its genomic organisation (core, subtelomeres, telomeres, what is present in subtelomeres, including base j) and polycistronic transcription and base J relevance on this aspect. That way, the reader will have a broad and more complete overview of the relevance of the present study.
We have enriched the introduction with a paragraph (“Leishmania species are uni-cellular […] essentiality of base-J for the life circle of these parasites.”) outlining the issues raised by the referee. As suggested by the referee, this makes it easier to both understand the relevance of the present study and to enrich the discussion about our findings discussed earlier in this letter.
Please, inform the expression vector for Leishmania tarentolae JBP1 used to express the mentioned protein on BL21(DE3)T1R.
The expression vector for JDBD JBP1 used for the crystallization was mentioned in Heidebrecht et al. 2011, which we refer to in the text. For clarity we added the vector to the first sentence in the protein expression and purification section in the material and methods: “using the pETNKI-his-3C-JBP1-JDBD plasmid”.
Please, supply the picture of the gel containing the extracted protein.
The gel of the JDBD mutants and the JBP1 N-terminus truncations was added to the supplemental information as Figure S10.
Significance:
Overall, this study provides important insights into the JBP1 and DNA interactions, which were lacking in the literature. The use of techniques such as protein expression and crystallization analysis, molecular dynamics, and docking analysis is in line with the research objectives. However, the lack of some information about methodology needs to be addressed (minor comments 3 and 4). Personally, methodology such as molecular dynamics and docking analysis is not easy to critique but the results are clear and understandable.
Although the authors should have been clearer about the impact of their findings, as addressed on my major comments, I believe that protein focused molecular parasitologists would benefit from the finds and methodology presented on this manuscript, since the article is more focused on protein research rather than parasite general molecular biology and medical studies, as mentioned on my major comments.
In summary, this study provides new insights into JBP1 and DNA interactions and uses appropriate and reproducible techniques to achieve its objectives. However, the authors should provide more clarity on the impact of their findings and discuss the potential of their new improved model.
My area of expertise: Cell and molecular biology; stem cells and factor controlling their fate; DNA, RNA, and molecular biology related techniques; Trypanosomatids telomere and telomerase
We would like to thank the referee for his positive and constructive outlook, which we believe resulted in changes that put the impact of our findings in clearer perspective.
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Referee #3
Evidence, reproducibility and clarity
Base J, also known as β-D-glucopyranosyloxymethyluracil, is a modified form of thymidine that has been identified in kinetoplastids and related organisms. It is worth noting that the distribution of Base J in the genome may vary depending on the organism and its life stage and influences its genome dynamics. The synthesis of this hypermodified nucleotide occurs in two steps, which involve the participation of two distinct thymidine hydroxylases, namely J-binding protein 1 and 2 (JBP1 and JBP2), along with a β-glucosyl transferase. In this study, the authors have presented a crystal structure of JBP1 J-DNA binding domain (J-DBD), which includes a previously reported disordered loop that might be involved in JBP1:J-DNA contact. Using this disordered structure as a starting point, the authors conducted Molecular Dynamics simulations and computational docking studies to propose models for the recognition of J-DNA by JBP1 J-DBD. The results from these studies were validated by punctual mutagenesis experiments, which provided additional data for docking and revealed a binding pattern for JBP1 J-DBD on J-DNA. By combining the crystallographic structure of the TET2 JBP1-homologue in complex with DNA and the AlphaFold model of full-length JBP1, the authors have hypothesized that the flexible N-terminus of JBP1 contributes to DNA-binding, which they have confirmed experimentally. However, according to the authors, to gain a deeper understanding of the unique molecular mechanism that underlies the replication of epigenetic information, an experimental determination of a high-resolution JBP1:J-DNA complex involving conformational changes would be necessary. Nevertheless, the present proposed objectives were fully contemplated by the authors.
Major comments:
In my opinion, the present article effectively achieved all the described objectives using appropriate and reproducible methodology, including protein expression and crystallization analysis, Molecular Dynamics analysis using GROMACS-2020.2 software, docking analysis, punctual mutations analyses, and modeling of JBP1:J-DNA complex using the AlphaFold tool. The authors presented the results in a logical and organized manner, making it easy for readers to extract the most important points. However, I believe that the section titled "Results and Discussion" contains more "results" than "discussion". While I understand that the literature on JBPs and base J is still in its early stages, other species of kinetoplastids have JBP1, in which mutations were not lethal as in L. tarentolae (e.g. T. brucei). Therefore, providing information about the structure of JBP1 and how the present results relate to what is known about JBP1 in other species in terms of structure and J-DNA interactions would significantly enrich the discussion of the findings and reinforce their significance and impact. Thus, the authors should have been clearer about the impact of their findings. When discussing the results, the authors should have answered questions such as how the identification of the new residues involved in JBP1 J-DNA binding impacts the current model of JBP1:J-DNA interactions, how this improved model contributes to the understanding of base J synthesis, and if the new model can be extrapolated to other species of kinetoplastids, according to the conservation of JBP1 among them. Although the article is more focused on protein research rather than parasite general molecular biology and medical studies, the findings may have implications for the development of new treatments for leishmaniases. Therefore, the authors should have discussed the potential of their new improved model as a target for lacking treatments of leishmaniases or at least brought up the point at conclusion section.
Minor Comments:
I have some minor comments regarding the text:
- Please, re-check the affirmation "99% of base-J is found in telomeric repeats, mainly in GGGTTA repeats wherein the second thymine is modified to base-J (2-4)" in the Introduction. I believe that the distribution of base-J varies among different species of trypanosomatids and, therefore, cannot be generalized. Moreover, among different life stages in some organisms such as T. brucei and Leishmania major, differences on base-J distribution are found. The 99% of telomeric base-J mentioned would be a feature of Leishmania genus. Please, re-check the references 3 and 4.
- Please, enrich the introduction topic with information about the model species, such as importance as pathological agent, its genomic organisation (core, subtelomeres, telomeres, what is present in subtelomeres, including base j) and polycistronic transcription and base J relevance on this aspect. That way, the reader will have a broad and more complete overview of the relevance of the present study.
- Please, inform the expression vector for Leishmania tarentolae JBP1 used to express the mentioned protein on BL21(DE3)T1R.
- Please, supply the picture of the gel containing the extracted protein.
Significance
Overall, this study provides important insights into the JBP1 and DNA interactions, which were lacking in the literature. The use of techniques such as protein expression and crystallization analysis, molecular dynamics, and docking analysis is in line with the research objectives. However, the lack of some information about methodology needs to be addressed (minor comments 3 and 4). Personally, methodology such as molecular dynamics and docking analysis is not easy to critique but the results are clear and understandable.
Although the authors should have been clearer about the impact of their findings, as addressed on my major comments, I believe that protein focused molecular parasitologists would benefit from the finds and methodology presented on this manuscript, since the article is more focused on protein research rather than parasite general molecular biology and medical studies, as mentioned on my major comments.
In summary, this study provides new insights into JBP1 and DNA interactions and uses appropriate and reproducible techniques to achieve its objectives. However, the authors should provide more clarity on the impact of their findings and discuss the potential of their new improved model.
My area of expertise: Cell and molecular biology; stem cells and factor controlling their fate; DNA, RNA, and molecular biology related techniques; Trypanosomatids telomere and telomerase
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Referee #2
Evidence, reproducibility and clarity
The manuscript by de Vries et al. reported the crystal structure of the J-DNA binding domain of JBP1. Although, the structure was already solved, the new structure allows to observe a loop that was disordered in the previous structure. This structure was next used to propose models of DNA complex analyzed by MD. The proposed model was then validated by mutagenesis.
Overall, the findings are interesting and the technical quality of the work is high.
Comments:
- For clarity, a figure showing the domain organization of JBP1 could help the reader in the introduction part.
- In addition to Figure 2 showing the newly observed loop in 2Fo-Fc map, an omit map should be included in Supp data.
- Figure S6 legend should be more precise about the type of HDX MS analysis.
- The authors performed MD simulations. But what about DNA curvature upon complex formation?
- p.12 Some mutants were characterized, notably their melting temperatures. One mutant shows decreased stability while R448A shows increased stability. What is the structural explanation?
- Figure 6E: The chi2 value for the comparison of the experimental curve for THD domain and calculated curve is very high indicating a poor fit. What is the explanation?
Significance
The novelty of the manuscript mainly relies on the description of the crystal structure of JDBD protein without DNA and proposed models of DNA complex within full length protein, models that were validated by mutations or truncations. The current manuscript well suited for a specialized journal.
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Referee #1
Evidence, reproducibility and clarity
Summary:
The paper presents a combined experimental (X-ray, SAXS, mutational analysis) and computational (MD, docking, AlphaFold) work that elucidates the mechanism of JDBD:JDNA complex formation.
Major comment:
- How did the authors decide the timescale of the production run? Wouldn't the loop motion (which can be necessary for this study) occur on a timescale of 300+ ns?
Minor comments:
- Did I understand correctly that the LINCS algorithm constrained only hydrogen-involving bonds? It is not mentioned explicitly. Or am I missing something?
- The authors should increase the resolution of figures S1 and S3. They look a bit blurry.
Significance
The J DNA base is critical for transcription termination at the ends of the polycistronic gene clusters in Leishmania and related species. Hence, understanding the formation mechanism of the JDBD:J-DNA complex can provide an opportunity to develop novel chemotherapeutic treatments against these diseases. This work provides the first crystal structure of JDBD with the disordered loop and suggests that R448 and N455, as well as the N-terminus, are involved in the J-DNA binding process. The article is well-written and can interest readers from biological and biochemical societies.
However, my field of expertise is computational chemistry and biochemistry; therefore, I cannot adequately evaluate the accuracy of the experimental techniques used in this work.
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Reply to the reviewers
We thank the reviewers for their comments and constructive suggestions to improve the manuscript. We are encouraged to see that both reviewers acknowledge how the results from our manuscript uses state-of-art technologies to advance molecular underpinnings of centriole length, integrity and function regulation. Both reviewers also highlighted that the manuscript is well laid out and presents clear, rigorous, and convincing data. Reviewer#1 described our manuscript of highest experimental quality and broad interest to the field of centrosome and cell biology form a basic research and genetics/clinical point of view. Here, we explain the revisions, additional experimentations and analyses planned to address the points raised by the referees. We will perform most of the experimentations and corrections requested by the reviewers. We have already made several revisions and are currently working on additional experiments.
Our responses to each reviewer comment in bold are listed below. References mentioned here are listed in the references section included at the of this document.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary: __In this manuscript, Arslanhan and colleagues use proximity proteomics to identify CCDC15 as a new centriolar protein that co-localizes and interacts with known inner scaffold proteins in cell culture-based systems. Functional characterization using state-of-the-art expansion microscopy techniques reveals defects in centriole length and integrity. The authors further reveal intriguing aberrations in the recruitment of other centriole inner scaffold proteins, such as POC1B and the SFI1/centrin complex, in CCDC15-deficient cells, and observe defects in primary cilia. __
We thank the reviewer for the accurate summary of the major conclusions of our manuscript.
Major points:
1) The authors present a high-quality manuscript that identifies a novel centriolar protein by elegantly revealing and comparing the proximity proteomes of two known centriolar proteins, which represents an important component for the maintenance of centrioles.
We thank the reviewer for highlighting that our manuscript is of high quality and presents important advances for the field.
__2) Data are often presented from two independent experiments (n = 2), which is nice, but also the minimum for experiments in biology. It is strongly recommended to perform at least three independent experiments. __
We agree with the reviewer that analysis of data form three experimental replicates is ideal for statistical analysis. We performed three replicates for the majority of experiments in the manuscript. However, as the reviewer pointed out, we included analysis from two experiments for the following figures:
- Fig. 4H: quantification of CCDC15 total cellular levels throughout the cell cycle by western blotting
- Fig. 5A: CCDC15-positive centrioles in control and CCDC15 siRNA-transfected cells
- Fig. 6B: % centriolar coverage of POC5, FAM161A, POC1B and Centrin-2 in control and CCDC15 siRNA-transfected cells
- Fig. 6C, 6E: Centrin-2 or SFI1-positive centrioles in control and CCDC15 siRNA-transfected cells
- Fig. 6J, K: normalized tubulin length and percentage of defective centrioles in cells depleted for CCDC15 or co-depleted for CCDC15 and POC1B
- Fig. 7F, H: SMO-positive cilia and basal body IFT88 levels in control and CCDC15 siRNA-transfected cells
- Fig. S3H: centriole amplification in HU-treated control and CCDC15 siRNA-transfected cells (no)
- Fig. S3A: centrosomal levels upon CCDC15 depletion There are two reasons for why we performed two experimental replicates for these experiments: 1) results from the two experimental replicates were similar, 2) quantification of data by U-ExM is laborious. To address the reviewer’s comments, we will perform the third experimental replicate for the sets of data that led to major conclusions of our manuscript, which are Figures 4H, 6C, 6E, 6J, 6K, 7F, 7H and S3A.
3) The protein interaction studies presented in Fig. 3 could be of higher quality. While it is great that the authors compared interactions to the centriolar protein SAS6, which is not expected to interact with CCDC15, the presented data raise many questions.
__a) In most cases, co-expression of tagged CCDC15 stabilizes the tested interaction partners, such that the overall abundance seems to be higher. The increase in protein abundance is substantial for Flag-FAM161A (Fig. 3D) and GFP-Centrin-2 (Fig. 3E) and is even higher for the non-interactor SAS6 (Fig. 3G), while it cannot be assessed for GFP-POC1B (Fig. 3F). Hence, the higher expression levels under these conditions make it more likely that these proteins are "pulled down" and therefore do not represent appropriate controls. __
We agree with the reviewer that the differences in protein abundance of the prey proteins upon expression of CCDC15 relative to control might impact the interpretation of the interaction data. To address this concern, we will perform the following experiments:
- To account of the potential stabilizing effects of CCDC15 expression, we will change the relative ratio of plasmids expressing proteins of interest and assess the expression of bait and prey protein levels. We will then repeat the co-immunoprecipitation experiments in conditions where prey expression levels are similar.
- To avoid the potential stabilizing effects of CCDC15 overexpression, we will perform immunoprecipitation experiments in cells expressing GFP or V5-tagged inner scaffold proteins and assess their potential physical or proximity interaction by blotting for endogenous CCDC15. __b) All Co-IP experiments are lacking negative controls in the form of proteins that are not pulled down under the presented conditions. __
For the co-IP experiments, we only included a specificity control for the interaction of the bait protein with the tag of the prey protein (i.e. GBP pulldown of GFP or GFP-CCDC15-expressing cells). As the reviewer suggested, we will also include a specificity control for the interaction of bait with the tag of the prey protein for co-immunoprecipitation experiments (i.e. GFP pulldown of cells expressing GFP-CCDC15 with V5-BirA* or V5-BirA*-FAM161A).
__c) The amounts of co-precipitation of the tested proteins appears very different. Could this reflect strong or weak interactors, or does it reflect the abundance of the respective proteins in centrioles? __
We agree with the reviewer that the quantity of the co-precipitated prey proteins might be a proxy for the interaction strength if the abundance of the bait proteins is similar. However, the expression levels of bait and prey proteins in co-transfected cells are different and thus, cannot be used to derive a conclusion on the interaction strength. For the revised manuscript, we will repeat the IP experiments and comment on this in the discussion section.
__4) The observation that IFT88 is supposedly decreased at the base of cilia in CCDC15-depleted cells requires additional experiments/evidence. Fig. 7G shows the results of n = 2 and more importantly, a similar reduction of gamma-tubulin in siCCDC15. Could the observed reduction in IFT88 be explained by a decrease in accessibility to immunofluorescence microscopy? Would the reduction in IFT88 at the base also be apparent when the signals were normalized to gamma-tubulin signals? __
To address the reviewer’s concern, we quantified the basal body gamma-tubulin and IFT88 levels in control and CCDC15-depleted cells and plotted the basal body IFT88 levels normalized to gamma-tubulin levels in Fig. 7H. Similar to the reduction in IFT88 levels, gamma-tubulin-normalized IFT88 levels was significantly less relative to control cells. Moreover, the gamma-tubulin basal body levels were similar between control and CCDC15 cells. We revised the gamma-tubulin micrographs in Fig. 7G to represent this. These results indicate that the reduction in basal body IFT88 levels upon CCDC15 depletion in specific.
__5) The observed Hedgehog signaling defects are described as follows: "CCDC15 depletion significantly decreased the percentage of SMO-positive cells". It is similarly described in the figure legend. If this was true, the simplest explanation would be that it reflects the reduction in ciliation rate (which is in a similar range). If SMO-positive cilia (instead of "cells") were determined, the text needs to be changed accordingly. __
As the reviewer pointed out, we quantified SMO-positive cilia, but not cells. We are sorry for this typo. We corrected SMO-positive cells as SMO-positive cilia in the manuscript text, Fig. 7 and figure legends.
__6) OPTIONAL: While expansion microscopy is slowly becoming one of the standard super-resolution microscopy methods, which is particularly well validated for studying centrioles, the authors should consider confirming part of their findings (as a proof of principle, surely not in all instances) by more established techniques. This could serve to convince critical reviewers that may argue that the expansion process may induce architectural defects of destabilized centrioles, as observed after disruptions of components, such as in Fig. 6. Alternatively, the authors could cite additional work that make strong cases about the suitability of expansion microscopy for their studies, ideally with comparisons to other methods. __
- SIM imaging was previously successfully applied for nanoscale mapping of other centriole proteins including CEP44, MDM1 and PPP1R35 (Atorino et al., 2020; Sydor et al., 2018; Van de Mark et al., 2015). To complement the U-ExM analysis, we have started imaging cells stained for CCDC15 and different centriole markers (i.e. distal appendage, proximal linker, centriole wall) using a recently purchased 3D-SIM superresolution microscope. We already included the SIM imaging data for CCDC15 localization in centrosome fractions purified from HEK293T cells in Fig. S5B. In the revised manuscript, we will replace confocal imaging data in Fig. 3A and 3B with SIM imaging data.
- As the reviewer noted, expansion microscopy has been successfully used for the analysis of a wide range of cellular structures and scientific questions including nanoscale mapping of cellular structures across different organisms. In particular, U-ExM of previously characterized centrosome proteins various centriole proteins have significantly advanced our understanding of centriole ultrastructure. In our manuscript, we used the U-ExM protocol that was validated for centrioles by comparative analysis of U-ExM and cryo-ET imaging by our co-authors (Gambarotto et al., 2019; Hamel et al., 2017). To clarify these points, we included the following sentence along with the relevant references in the introduction: “Application of the U-ExM method to investigate known centrosome proteins has started to define the composition of the inner scaffold as well as other centriolar sub-compartments (Chen et al., 2015; Gambarotto et al., 2021; Gambarotto et al., 2019; Kong and Loncarek, 2021; Laporte et al., 2022; Mahen, 2022; Mercey et al., 2022; Odabasi et al., 2023; Sahabandu et al., 2019; Schweizer et al., 2021; Steib et al., 2022; Tiryaki et al., 2022; Tsekitsidou et al., 2023).”
Minor points:
1) Text, figures, and referencing are clear and accurate, apart from minor exceptions.
We clarified and corrected the points regarding text, figures and references as suggested by the two reviewers.
__ 2) The title suggests a regulator role for CCDC15 in centriole integrity and ciliogenesis, which has formally not been shown. __
We revised the title as “CCDC15 localizes to the centriole inner scaffold and functions in centriole length control and integrity”.
__3) As the authors observe changes in centriole lengths in the absence of CCDC15, it would be very insightful to compare these phenotypes to other components that affect centriolar length, such as C2CD3, human Augmin complex components (as HAUS6 is identified in Fig. 1) or others. These could be interesting aspects for discussion, additional experiments are OPTIONAL. __
We agree with the reviewer that comparative analysis of centriole length phenotypes for CCDC15 and other components that regulate centriole length will provide insight into how these components work together at the centriole inner core. To this end, we phenotypically compared CCDC15 loss-of-function phenotypes to that of other components of the inner scaffold (POC5, POC1B, FAM161A) that interact with CCDC15. In agreement with their previously reported functions in U2OS or RPE1 cells, we found that POC5 depletion resulted in a 4% slight but significant increase in centriole length and POC1B depletion resulted in a 15% significant decrease. In contrast, FAM161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, our analysis of their centriolar localization dependency and regulatory roles during centriole length suggest that CCDC15 and POC1B might form a functional complex as positive regulators of centriole length. In contrast, POC5 functions as a negative regulator and might be part of a different pathway for centriole length regulation. We integrated the following sub-paragraph in the results section and also included discussion of this data in the discussion section:
“Moreover, we quantified centriole length in control cells and cells depleted for POC5 or POC1B. While POC5 depletion resulted in longer centrioles, POC1B resulted in shorter centrioles (POC5: siControl: 414.1 nm±38.3, siPOC5: 432.7±44.8 nm, POC1B: siControl: 400.6±36.1 nm, siPOC1B: 341.5±44.39 nm,). FAMA161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, these results suggest that CCDC15 might cooperate with POC1B and compete with POC5 to establish and maintain proper centriole length.”
__ 4) While the reduced ciliation rate in the absence of CCDC15 is convincing, the authors did not investigate "ciliogenesis", i.e. the formation of cilia, and hence should re-phrase. The sentence in the discussion that "CCDC15 functions during assembly" should be removed. __
To clarify that we only investigated the role of CCDC15 in the ability of cells to form cilia, we replaced sentences that indicates “CCDC15 functions in cilium assembly” with “CCDC15 is required for the efficiency of cilia formation”.
__5) The existence of stably associated CCDC15 pools with centrosomes (Fig. 2) requires further evidence. The recovery of fluorescence after photobleaching in FRAP experiments is strongly dependent on experimental setups and is only semi-quantitative. A full recovery is unrealistic, hence, it is ideally compared to a known static or known mobile component. I personally think this experiment -as it is presented now- is of little value to the overall fantastic study. The authors may consider omitting this piece of data. __
We agree with the reviewer that FRAP data by itself does not prove the existence of stably associated CCDC15 pool. As controls in these experiments, we use FRAP analysis of GFP-CCDC66, which has a 100% immobile pool at the cilia and 50% immobile pool at the centrosomes as assessed by FRAP (Conkar et al., 2019). To address these points, we toned down the conclusions derived from this experiment by revising the sentence as follows:
Additionally, we note that the following data provides support for the stable association of CCDC15 at the centrioles:
- About 49.6% (± 3.96) of the centrioles still had CCDC15 fluorescence signal at one of the centrioles upon CCDC15 siRNA treatment (Fig. 5A, 5B). The inefficient depletion of the mature centriole pool of CCDC15 is analogous to what was observed upon depletion of other centriole lumen and inner scaffold proteins including WDR90 and HAUS6 (Schweizer et al., 2021; Steib et al., 2020). __6) The data that CCDC15 is a cell cycle-regulated protein is not very convincing (see Fig. 3H), as the signals area weak and the experiment has been performed only once (n= 1). This piece of data does not appear to be very critical for the main conclusions of the manuscript and may be omitted. Otherwise, this experiment should be repeated to allow for proper statistical analysis. __
We will perform these experiments two more times, quantify cellular abundance of CCDC15 in synchronized populations from three experimental replicates and plot it with proper statistical analysis.
__7) Experimental details on how "defective centrioles" are determined are missing. __
We included the following experimental details to the methods section:
“Centrioles were considered as defective when the roundness of the centriole was lost or the microtubule walls were broken or incomplete. In the longitudinal views of centrioles, defective centrioles were visualized as heterogenous acetylated signal along the centriole wall or irregularities in the cylindrical organization of the centriole wall (Fig. 5F). We clarified these points in the methods section.
__ 8) For figures, in which the focus should be on growing centrioles (see Fig. 4), it could be helpful to guide the reader and indicate the respective areas of the micrographs by arrows. __
We added arrows to point to the respective areas of the micrographs in Fig. 4F.
__ 9) Page18: "centriole length shortening" could be changed to "centriole shortening". __
We corrected this description as suggested.
__10) It is unclear how the authors determine distal from proximal ends of centrioles in presented micrographs (see Fig. 5D). __
We determined the proximal and distal ends of the centrioles by taking the centriole pairs as a proxy. Even though we only represent a micrograph containing a single centriole in some of the U-ExM figures including Fig. 5D, the uncropped micrographs contain two centrioles, which are oriented orthogonally and tethered to each other at their proximal ends in interphase cells. We added the following sentence to the methods section to clarify this point:
*“Since centrioles are oriented orthogonally and tethered to each other at their proximal ends in interphase cells, we also used the orientation of the centriole pairs as a proxy to determine the proximal and distal ends of the centrioles.” *
__11) Fig. 7A is missing scale bars and Fig.7 overall is lacking rectangle indicators of the areas that are shown at higher magnification in the insets. __
We added scale bar to Fig. 7A and rectangle indicators for zoomed in regions in Fig. A, E, G.
12) Fig. 7C displays cilia that appear very short, especially when comparing to the micrographs and bar graphs presented. The authors may want to explain this discrepancy.
We thank the reviewer for the comment. The zoomed in representative cilia is 4.1 µM in control cells and 1.4 µM in CCDC15-depleted cells. Therefore, the representative cilia is in agreement with the quantification of cilia in Fig. 7C.
Reviewer #1 (Significance (Required)): • From a technical point of view the authors use two state-of-the-art technologies, namely proximity labeling combined with proteomics and ultrastructure expansion microscopy, that are both challenging and very well suited to address the main questions of this study. ____ • General assessment: The presented study is of highest experimental quality. Despite being very challenging, the expansion microscopy and proximity proteomics experiments have been designed and performed very well to allow solid interpretation. The results of the central data are consistent and allow strong first conclusions about the putative function of the newly identified centriolar protein CCDC15. The study presents a solid foundation for future hypothesis-driven, mechanistic analysis of CCDC15 and inner scaffold proteins in centriole length control and maintaining centriole integrity. The only limitation of the study is that the technically simpler experiments should be repeated to allow proper statistical assessment, which can be addressed easily. • Advance: This is the first study that identifies CCDC15 as a centriolar protein and localizes it to the inner scaffold. It further describes a function for CCDC15 in centriole length control and shows its importance in maintaining centriole integrity with consequences for stable cilia formation in tissue culture. The study provides further functional insights into the interdependence of inner scaffold proteins and the role of CCDC15 in the recruitment of the SFI1/centrin distal complex. • Audience: The manuscript will be of broad interest to the fields of centrosome and cell biology, both from a basic research and genetics/clinical point of view due to the association with human disorders. The state-of-the-art technologies applied will be of interest to a broader cell and molecular biology readership that studies subcellular compartments and microtubules. • Reviewer's field of expertise: Genetics, imaging, and protein-protein interaction studies with a focus on centrosomes and cilia.
We thank the reviewer for recognizing the importance of our work and for supportive and insightful comments that will further strengthen the conclusions of our manuscript. Our planned revisions will address the only major technical limitation raised by the reviewer that requires adding one more experimental replicate for analysis of the data detailed in major point#1. Notably, we also thank the reviewer to specifying the experiments that are not essential or will be out of the scope of our manuscript as “optional”.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary:
__In this study, Arslanhan et al. propose CCDC15 as a novel component of the centriole inner scaffold structure with potential roles in centriole length control, stability and the primary cilium formation in cultured epithelial cells. Using proximity labelling they explore the common interactors of Poc5 and Centrin-2, two resident molecules of the centriole inner scaffold, to hunt for novel regulators of this structure. The authors leverage expansion microscopy-based localization and siRNA-dependent loss-of-function experiments to follow up on one such protein they identify, CCDC15, with the aforementioned roles in centriole and cilia biology.
This study is designed and laid out nicely; however, to be able to support some of the important claims regarding their proximity labelling results and exploration on the roles of CCDC15, there are several major technical and reproducibility concerns that deem major revision. Similarly, the introduction (perhaps inadvertently) omits much of the recent studies on centriole size control that have highlighted the complexity of this biological problem. As such, addressing the following major points will be essential in further considering this work for publication. __
__We thank the reviewer for recognizing the importance of our work and appreciate the positive reflections on our manuscript and the feedback comments that were well thought-out and articulated and will further strengthen the conclusions of our manuscript. Our planned revisions focus on addressing the reviewer’s comments especially in further supporting our conclusions for proximity-labeling, phenotypic characterization and immunoprecipitation experiments, examining CCDC15 centriole localization in an additional cell line and investigating how CCDC15 works together during centriole length control with known components of the inner scaffold. __
Major points:
__1a) The authors use Poc5 and Centrin-2 molecules as joint baits to reveal the interactome of the centriole inner scaffold, however the work lacks appropriate experimental and analytical controls to argue that this is a proximity mapping "at the centriole inner scaffold". In its current state, it is simply an interactome of total Poc5 and Centrin-2, and it might be misleading to call it an interactome at the centriole inner scaffold (the statistical identification of shared interactors cannot do full justice to their biology at the centrosome). Appropriate expression data needed to delineate how large the centrosomal vs. cytoplasmic (or nucleoplasmic) fraction is for either of these molecules, both without and upon the addition of biotin (to see whether the bulk of interaction data stem from the cytoplasm/nucleoplasm or the centrioles themselves). The authors can test this by selectively blotting a lysate fraction containing the centrosomes after centrifugation, and compare them with the simultaneous blot of the supernatant (which were readily used for the blots presented in Fig. 1B). This experiment also becomes very relevant for the case of Centrin-2, as it also heavily localizes to the nucleoplasm as the authors found out (see Fig. 1A and Fig. S1A). __
__ Additionally, an orthogonal approach should be taken to perform bio-image analysis on their biotin/streptavidin imaging data to demonstrate the exact ratios between the centrosomal vs. cytoplasmic/nucleoplasmic biotin activation with appropriate signal normalization between the biotin/streptavidin images. This is particularly important, as although the authors claim that these cells stably express the V5BirA*, it seems that there is partial clonality to the expression. Some cells in both the Poc5 and Centrin-2 fusion constructs appear to lack the V5/Streptavidin signals upon Biotin addition (such as the two cells in the centre right in Poc5, and again a cell in the centre right for Centrin-2 images). In its current form, Fig. 1A lacks signal quantification and does not report any information about the replicates and distributions of the data. I worry that this may raise concerns on the reproducibility if published in its current form. __a) We agree with the reviewer that the proximity maps of POC5 and
a) Centrin-2 are not specific to the centriole inner scaffold and thus, do not represent the inner scaffold interactome. The proximity maps identified interactions across different pools of POC5 and Centrin-2 in nucleus, cytoplasm and centrosomes (Fig. 1, S1). To highlight these important points, we already included extensive analysis of the different cellular compartments and biological processes identified by the POC5 and Centrin-2 proximity maps in the results section (pg. 9-10).
We think that there are two reasons that caused the misinterpretation of the use of these proximity maps as the “inner scaffold interactome”: 1) the way we introduced the motivation for proximity mapping studies, 2) proposing the use of the resulting interactomes as resources for identification of the full repertoire of the inner scaffold proteins. To clarify these points, we revised the manuscript in all relevant parts that might have led to misinterpretation. Following are the specific revisions:
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To clarify that the proximity maps are not specific to the inner scaffold pools of POC5 and Centrin-2, we revised the title of the results section for Fig. 1 and 2 as follows: “Proximity mapping of POC5 and Centrin-2 identifies new centriolar proteins”.
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To indicate that POC5 and Centrin-2 localizes to the cytoplasm and/or nucleus in addition to the centrosome, we added the following sentence to the result section: “In addition to centrosomes, both fusion proteins also localized to and induced biotinylation diffusely in the cytoplasm and/or nucleus (Fig. 1A).”
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In the introduction, we revised the following sentence “Here, we used the known inner scaffold proteins as probes to identify the molecular makeup of the inner scaffold in an unbiased way.” as follows: *“Here, we used the known inner scaffold proteins as probes to identify new components of the inner scaffold”. *
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To highlight the different cellular pools of POC5 and Centrin-2 and identification of their interactors in these pools, we included the following sentence in the results section: “As shown in Fig. S1, Centrin-2 and POC5 proximity interactomes were enriched for GO categories that are relevant for their published functions during centrosomal, cytoplasmic and/or nuclear biological processes and related cellular compartments (Azimzadeh et al., 2009; Dantas et al., 2013; Heydeck et al., 2020; Khouj et al., 2019; Resendes et al., 2008; Salisbury et al., 2002; Steib et al., 2020; Yang et al., 2010; Ying et al., 2019).”
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We replaced the “interactome” statement with “proximity interaction maps” or “proximity interactors” throughout the manuscript to prevent the conclusion that the proximity maps represent the inner scaffold interactome. b) As the reviewer noted, most centrosome proteins have multiple different cellular pools including the centrosome. For most proteins like gamma-tubulin and centrin, their cytoplasmic/nucleoplasmic pools are more abundant than their centrosomal pools (Moudjou et al., 1996; Paoletti et al., 1996). For the Firat-Karalar et al. Current Biology 2015 paper, I compared the biotinylation levels of centrosomal fractions versus cytoplasmic fractions and confirmed that this is also true in cells expressing myc-BirA* fusions of CDK5RAP2, CEP192, CEP152 and CEP63 (unpublished) (Firat-Karalar et al., 2014). For the revised manuscript, we will compare the biotinylation level of centrosomal, nuclear and cytoplasmic pools of V5Bir*-POC5 and V5BirA*-Centrin-2 using the stable lines. To this end, we will use published centrosome purification protocols. We will include this data in Fig. S1 to highlight that the proximity interactomes represent the different pools of the bait proteins and to show the relative levels of the baits across their different pools.
c) BioID approach has been successfully used to probe centrosome interactions by my lab and other labs in the field. In fact, proximity interaction maps of over 50 centrosome proteins were published as resource papers by Pelletier&Gingras labs (Gheiratmand et al., 2019; Gupta et al., 2015). Analogous to our strategy in this manuscript, these studies generated proximity maps of centrosome proteins by creating cell lines that stably express BioID-fusions of centrosome proteins followed by streptavidin pulldowns from whole cell extracts and mass spectrometry analysis. Since majority of centrosome proteins also have pools in multiple cellular locations, the published BioID proximity maps for centrosome proteins are not specific to centrosomes. However, the proximity maps included all known centrosome proteins and identified new proteins, which shows that centrosome interactions are represented in pulldowns form whole cell lysates. Moreover, maps form whole cell lysates are also advantageous as they are are unbiased and can be used in future studies as resources for studying the functions and interactions of the bait proteins in different contexts.
In the Firat-Karalar et al. Current Biology 2015 paper, I combined centrosome purifications with BioID pulldowns to enrich for the centrosomal interactions in the proximity maps of centriole duplication proteins(Firat-Karalar et al., 2014). However, I started the purification with cells transiently transfected with the BioID-fusion constructs, which resulted in high ectopic expression of the fusions in the cytoplasm and/or nucleus. Therefore, centrosome enrichments were useful as an additional step before mass spectrometry. Comparative analysis of the data for proximity maps of 4 centrosome proteins generated from stable lines or centrosome fractions of transiently transfected cells substantially overlap as compared in the Gupta et al. Cell 2015 study and were more comprehensive (Table S2) (Gupta et al., 2015). Therefore, we are confident that the proximity interactomes we generated for POC5 and Centrin-2 include their centrosomal interactions.
__1b) Similarly, it is not clear whether the expression of Poc5 and Centrin-2 fusion molecules somehow interfere with their endogenous interactions or function. At least some loss-of-function (e.g., RNAi) experiments should be performed where the depletion of endogenous proteins should be attempted to rescue by the fusion constructs. This will help evaluate whether the fusion proteins can rescue the depletion of their endogenous counterparts and behave as expected from a wild-type scenario. __
The reviewer raises an important concern regarding the physiological relevance of the POC5 and Centrin-2 proximity maps. In the manuscript, we showed and discussed the validation of their proximity interactomes by two lines of evidence, which are: 1) the interactomes identified the previously described cellular compartments, biological processes or interactors of POC5 and Centrin-2, 2) the interactomes led to the identification of CCDC15 as a new inner scaffold protein.
As the reviewer indicated, stable expression of POC5 and Centrin-2 in the presence of their endogenous pools might affect cellular physiology and thereby the landscape of the interactomes. We plan to address this using the following experiments:
a) We will perform a set of functional assays to assess whether stable V5BirA*-Centrin-2 and V5BirA*-POC5 cells behaves like control cells in terms of their centrosome number, cell cycle profiles and mitotic progression. We will specifically quantify:
- centrosome number (immunofluorescence analysis for gamma-tubulin and centrin)
- their mitotic index (immunofluorescence analysis by DAPI)
- spindle polarity and percentage of multinucleation (immunofluoerescence analysis for microtubules, gamma-tubulin and DAPI)
- cell cycle profiles (flow cytometry and immunofluorescence)
- apoptosis (immunoblotting for caspase 3) Together, results from these experiments indicate that the V5BirA*-POC5 or Centrin-2-expressing stable lines do not exhibit defects associated with their stable expression.
b) We will perform expansion microscopy in V5BirA*-Centrin-2 and V5BirA*-POC5 cells to assess whether the fusion protein specifically localizes to the centriole inner scaffold, which will provide support for the presence of inner scaffold proteins in their proximity maps. Specifically, we plan to stain the fusion proteins by V5 or BirA antibodies and include the data for the antibody that works for expansion microscopy. This experiment will address whether their stable expression results in specific localization of these proteins at the centriole inner scaffold.
1c) Overall, as the entire claim around the proximity mapping revolve around its assumption about the centriole inner scaffold, these controls seem imperative to substantiate the ground truth of the biology presented in the manuscript.
In the revised manuscript, we toned down and made it clear that Centrin-2 and POC5 proximity maps are not specific to the inner scaffold and do not represent the inner scaffold interactome. Since the maps were generated from the whole cell extract, they will provide a resource for future studies aimed at studying functions and mechanisms of POC5 and Centrin-2 across their different cellular pools including the centrosome.
We would like to also highlight that the proximity maps of POC5 and Centrin-2 are not the major advances of our manuscript. The major advance of our manuscript is the identification of CCDC15 as a new inner scaffold protein that is required for regulation of centriole size and architectural integrity and thereby, for maintaining the ability of centrioles to template the assembly of functional cilia. Importantly, our results identified CCDC15 as the first dual regulator of centriolar recruitment of inner scaffold protein POC1B and the distal end SFI1/Centrin complex and provided important insight into how inner scaffold proteins work together during centriole integrity and size regulation. The new set of experiments we will perform for the revisions of the paper will strengthen these conclusions.
__2) I am curious about the choices of the cell lines in this work. The proximity mapping to reveal CCDC15 as a candidate protein for centriole inner scaffold was performed in HEK293T cells (human embryonic kidney), however its immunostaining was performed using RPE1 and U2OS cells (human retinal and osteosarcoma epithelial cells respectively). This raises questions regarding the generality of CCDC15 as a centriole inner scaffold protein. Could CCDC15 be simply unique to the centriole inner scaffold of epithelial cells such as RPE1 and U2OS cells? Or could the authors demonstrate any information/data on whether it's similarly localized to the inner scaffold in embryonic kidney cells or other cell types? If not, the claims should be moderated to reflect this fine detail. __
To test whether CCDC15 localizes to the inner scaffold in other cell types, we performed U-ExM analysis of CCDC15 localization relative to the centriolar microtubules in differentiating multiciliated epithelial cultures (MTEC). As shown in Fig. S3A, CCDC15 localized to the inner scaffold in the centrioles in MTEC ALI+4 cells. Given that the inner scaffold proteins including CCDC15 and previously characterized ones have not been studied in multiciliated epithelia, this result is important and provides support for potential role of the inner scaffold in ensuring centriole integrity during ciliary beating. Additionally, we examined CCDC15 localization by 3D-SIM in centrosomes purified from HEK293T cells, which showed that CCDC15 localizes between the distal centriole markers CEP164 and Centrin-3 and proximal centriole markers gamma-tubulin and rootletin (Fig. S3B).
3) Discussions and data on the localization of CCDC15 to centriolar satellites appear anecdotal and not fully convincing (Fig. S2D). Given that the authors test the relevance of PCM1 for CCDC15's centriolar localization, it is key to have quantitative data supporting their claim that centriolar satellites can help recruit CCDC15 to the centriole. Could the authors quantify what proportion of CCDC15 localize to the centriolar satellites? One way to do this could be to quantify the colocalization coefficience of CCDC15 and PCM1 signals.
We only observed co-localization of CCDC15 with the centriolar satellite marker PCM1 in cells transiently transfected with mNG-CCDC15. In Fig. S2E, we included the quantification of the percentage of U2OS and RPE1 cells that exhibit co-localization of PCM1 (100% of U2OS cells, about 80% of RPE1 cells). Like CCDC15, ectopic expression of WDR90 revealed its centriolar satellite localization, suggesting a potential link between centriolar satellites and inner scaffold proteins that can be investigated in future studies (Steib et al., 2020). We now included these results in the discussion section as follows:
“As assessed by co-localization with the centriolar satellite marker PCM1, mNG-CCDC15 localized to centriolar satellites in all U2OS cells and in about 80% of RPE1 cells (Fig. S2C-E). Association of CCDC15 with centriolar satellites is further supported by its identification in the centriolar satellite proteomes(Gheiratmand et al., 2019; Quarantotti et al., 2019).”
Even though endogenous staining for CCDC15 did not reveal its localization to centriolar satellites, following lines of data support the presence of a dynamic and low abundance pool of CCDC15 at the centriolar satellites: 1) CCDC15 was identified in the centriolar satellite proteome and interactome (Gheiratmand et al., 2019; Quarantotti et al., 2019). 2) CCDC15 centrosomal targeting is in part regulated by PCM1 (Fig. S2F, S2G). For majority of the proteins identified in the centriolar satellite proteome, their satellite pool can only be observed upon ectopic expression. This might be because their centriolar satellite pool is of low abundance and transient as satellite interactions are extensively identified only in proximity mapping studies, but not in traditional pulldowns
__4) Similar to above (#3), there is no quantitative information on the co-localization or partial co-localization of the signal foci in Fig. 3A and 3B. The authors readily study CCDC15's localization in wonderful detail in their expansion microscopy data, so they could actually consider taking out Fig. 3A and 3B, as the data seem redundant without any quantification. __
To address the reviewer’s concern, we included plot intensity profile analysis of CCDC15 and different centriole markers along a line drawn at the centrioles in Fig. 3A and 3B, which shows the extent of their overlap. As part of our revision plan, we will replace the confocal imaging data in Fig. 3A and 3B with 3D-SIM imaging data of CCDC15 relative to different centriole markers together with plot profile analysis. We already included 3D-SIM imaging of centrosomes purified form HEK293T cells in Fig. S3B. 3D-SIM imaging data will complement the localization data revealed by U-ExM.
__5) Do the authors also feel that CCDC15 localize to the core lumen in a somehow helical manner (Fig. 1A, Fig. 1F top and bottom panels, Fig. 5A etc.)? Le Guennec et al. 2020's helical lattice proposal for the inner scaffold further reaffirms that CCDC15 is indeed a likely major component of the inner scaffold. In my view, authors should state this physical similarity explicitly to further support their findings on CCDC15. __
As the reviewer indicated, cryo–electron tomography and subtomogram averaging of centrioles from four evolutionarily distant species showed that centriolar microtubules are bound together by a helical inner scaffold covering ~70% of the centriole length (Le Guennec et al., 2020). Although U-ExM data do not have enough resolution to show that CCDC15 localizes in a helical manner, we agree with the reviewer that the discussion of this possibility is important and thus we included the following sentence in the results:
“Longitudinal views suggest potential helical organization of CCDC15 at the inner scaffold, which is consistent with its reported periodic, helical structure (Le Guennec et al., 2020).”
__6a) The data on the link between the CCDC15 recruitment and the centriole growth (Fig. 4F) or the G2 phase of the cell cycle (Fig. 4H) are not fully convincing without quantitative data. For Fig. 4F, the authors should consider plotting the daughter centriole length vs the daughter CCDC15 intensities against each another, to see whether more elongated daughters truly tend to have more CCDC15. __
To address the reviewer’s concern, we will plot the daughter centriole length versus CCDC15 intensity at different stages of centriole duplication. In asynchronous cultures that we analyzed with U-ExM, we were not able to find enough cells to perform such quantification. To overcome this limitation, we will perform U-ExM analysis of cells fixed at different points after mitotic shake-off and stained for CCDC15 and tubulin. We will include minimum 10 different representative U-ExM data for different stages of centriole duplication in the revised manuscript along with quantification of length versus signal.
As detailed in the results section, the goal of these experiments was to determine when CCDC15 is recruited to the procentrioles during centriole duplication, but not to suggest a role for CCDC15 in centriole growth. We clarified this by including the following sentence:
“To investigate the timing of CCDC15 centriolar recruitment during centriole biogenesis, we examined CCDC15 localization relative to the length of procentrioles that represent cells at different stages of centriole duplication (Fig. 4F).”
__6b) For Fig. 4H, the argument regarding the cell cycle regulation requires quantification of the bands from several WB repeats, normalized to the expression of GAPDH within each blot (this is particularly relevant, as the bands of CCDC15 do not look dramatically different enough to draw conclusions by eye). __
We will perform these experiments two more times, quantify cellular abundance of CCDC15 in synchronized populations from three experimental replicates and plot it with proper statistical analysis.
__7a) The authors find herein that CCDC15 depletion lead to centrioles that are ~10% shorter than the controls. With the depletion of Poc5 and Wdr90 (other proposed components of the inner scaffold), the centrioles end up larger however (Steib et al., 2020). If the role of inner scaffold in promoting centriole elongation is structural, why are these two results the opposite of each other? I realize there is a brief discussion about this at the end of the paper, however, this requires a detailed discussion and speculation on the relevance of these findings. It would be key to clarify whether the inner scaffold as a structure inhibits or promotes centriole growth - or somehow both? If so, how? __
We agree with the reviewer that comparative analysis of centriole length phenotypes for CCDC15 and other components that regulate centriole length will provide insight into how these components work together at the centriole inner core. To this end, we phenotypically compared CCDC15 loss-of-function phenotypes to that of other components of the inner scaffold (POC5, POC1B, FAM161A) that interact with CCDC15. In agreement with their previously reported functions in U2OS or RPE1 cells, we found that POC5 depletion resulted in a 4% slight but significant increase in centriole length and POC1B depletion resulted in a 15% significant decrease. In contrast, FAM161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, our analysis of their centriolar localization dependency and regulatory roles during centriole length suggest that CCDC15 and POC1B might form a functional complex as positive regulators of centriole length. In contrast, POC5 functions as a negative regulator and might be part of a different pathway for centriole length regulation. We integrated the following sub-paragraph in the results section in pg. 19 and also included discussion of this data in the discussion section in pg. 23:
“Moreover, we quantified centriole length in control cells and cells depleted for POC5 or POC1B. While POC5 depletion resulted in longer centrioles, POC1B resulted in shorter centrioles (POC5: siControl: 414.1 nm±38.3, siPOC5: 432.7±44.8 nm, POC1B: siControl: 400.6±36.1 nm, siPOC1B: 341.5±44.39 nm,). FAMA161A depletion did not alter centriole length (siControl: 447.8±59.7 nm, siFAM161A 436.3±64 nm). Together, these results suggest that CCDC15 might cooperate with POC1B and compete with POC5 to establish and maintain proper centriole length.”
__7b) There might be some intriguing opposing regulatory action of Poc5 and CCDC15 as demonstrated here, where CCDC15 depletion leads to slightly over-recruitment of Poc5, and vice versa. Does this suggest that a tug-of-war going on between different molecules that localize to the inner scaffold? Does this provide some dynamicity to this structure, which might in turn regulate centriole length both positively and negatively? This may be analogous to how opposing forces of dyneins and kinesins provide robust length control for mitotic spindles. I am speculating here, but hopefully these may provide some useful grounds for further discussion in the paper. If the authors deem it interesting experimentally, they can test whether the two molecules indeed regulate centriole length by opposing each other's action, by a double siRNA of CCDC15 and Poc5 to see if this retains the centriole length at its control siRNA size (like how they do a similar test for Poc1's potential co-operativity with CCDC15 in Fig. 6J). __
We thank the reviewer for proposing excellent ideas on how inner scaffold proteins work together to regulate centriole length. As proposed by the reviewer, different proteins oppose each other analogous to how dynein and kinesin regulate mitotic spindle length. Loss-of-function and localization dependency data support that CCDC15 cooperates with POC1B, which was supported by phenotypic characterization of co-depleted cells (Fig. 6I-K).
The increase in POC5 levels and coverage at the centrioles upon CCDC15 depletion and vice versa (Fig. 7B, 7G) suggest that CCDC15 and POC5 compete with each other in centriole length regulation. As suggested by the reviewer, we attempted to test this by comparing centriole length in cells co-depleted for CCDC15 and POC5 relative to their individual depletions. Although we tried different depletion workflows, we were not able to co-deplete CCDC15 and POC5. Specifically, we tried transfecting cells with CCDC15 and POC5 siRNAs at the same time or sequentially for 48 h or 96 h. The centrioles in cells that survived co-depletion were positive for both CCDC15 and POC5. This might be because co-depletion of both proteins is toxic to cells. Since CCDC15 and POC5 are likely part of two different pathway in regulation of centrioles and also have other cellular functions, this might have caused cell death. We included the following statement in the discussion to address the excellent model proposed by the reviewer:
“Taken together, our results suggest that CCDC15 cooperates with POC1B and competes with POC5 during centriole length regulation. Moreover, they also raise the exciting possibility that centriole length can be regulated by opposing activities of inner scaffold proteins. Future studies that explore the relationship among centriole core proteins are required to uncover the precise mechanisms by which they regulate centriole integrity and size.”
__8) In their introduction section, the authors discuss how relatively little is known about the size control of centrioles, however they fail to mention a series of recent primary literature that uncover striking, new mechanisms and novel molecular players that highlight the complexity of centriole size control. This complexity appears to arise from the existence of multitude of length control mechanisms that influence the cartwheel or the microtubule length individually, or simultaneously via yet-to-be further explored crosstalk mechanisms. a. As such, when the authors talk about the procentriole size control in the introduction, they should discuss and refer to the following studies, in terms of: • How theoretical and experimental work demonstrate that procentriole length may vary dependent on the levels of its building block Sas-6 in animals (Dias Louro et al., 2021 PMID: 33970906; Grzonka and Bazzi, 2022 bioRxiv). • How a homeostatic Polo-like kinase 4 clock regulates centriole size during the cell cycle (Aydogan et al., 2018 JCB PMID: 29500190), and how biochemistry and genetics coupled with mathematical modelling unravel a conserved negative feedback loop between Cep152 and Plk4 that constitutes the oscillations of this clock in flies (Boese et al., 2018 PMID: 30256714; Aydogan et al., 2020 PMID: 32531200) and human cells (Takao et al., 2019 PMID: 31533936). __
__b. Similarly, when the authors refer to centriole size control induced by microtubule-related proteins, they should highlight the further complexity of this process by referring to: • How a molecule located at the microtubule wall, Cep295/Ana1, can regulate centriole length in flies (Saurya et al., 2016 PMID:27206860) and human cells (Chang et al., 2016 PMID:27185865) - like all the other centriolar MT molecules that the authors discuss in the manuscript. • How a crosstalk between Cep97 and Cep152 influences centriole growth in fly spermatids (Galletta et al., 2016 PMID:27185836). • How a crosstalk between CP110-Cep97 and Plk4 influences centriole growth in flies (Aydogan et al., 2022 PMID:35707992), and this molecular crosstalk is conserved, at least biochemically, in human cells (Lee et al., 2017 PMID:28562169). __
We thank the reviewer for highlighting the papers that uncovered new mechanisms and players of centriole size and integrity control as well as for the detailed explanation of how different studies led to these discoveries in different organisms. We should have discussed these proteins, functional complexes and mechanisms in our manuscript and cited the relevant literature. We inadvertently focused on literature that uncovered centriole length regulation by MAPs and the inner scaffold. In the introduction section of the revised manuscript where we introduced centriole size regulation in pg. 5, we summarized the major findings on the role of different MAPs, cartwheel and PLK4 homeostatic clock in ensuring formation of centrioles at the correct size in different organisms.
__Minor points: __
__1) Introduction section: Literature reference missing for the sentence starting with "Importantly, the stable nature of centrioles enables them to withstand...". __
We cited research articles that show the importance of centriole motility during ciliary motility and cell division.
“Importantly, the stable nature of centrioles enables them to withstand mechanical forces during cell division and upon ciliary and flagellar motility (Abal et al., 2005; Bayless et al., 2012; Meehl et al., 2016; Pearson et al., 2009).
__2) Fig. S1 legend: A typo as follows: CRAPome banalysis should read CRAPome analysis. __
We corrected this typo.
__3) Fig. S2: Info on the scale bar in the legend is missing in Fig. S2A. Scale bars for different panels are missing in general in Fig. S2A. __
We added scale bar information for Fig. S2A and to all other supplementary figure legends that lack scale bar information.
__4) Fig. 3A and 3B: When displaying the data, coloured cartoon diagrams would be beneficial to guide the reader who are not fully familiar with the spatial orientation of these proteins. __
As suggested by the reviewer, we will remove the confocal imaging data for CCDC15 localization from Fig. 3A and 3B. For the revised version, we will include 3D-SIM imaging data along with a diagram that represents the spatial orientation of CCDC15 relative to the chosen centriole markers.
__5) Fig. 3H: No information about the sample number (number of cells or technical repeats examined) reported. __
We included information on the number of experimental replicates and cells analyzed.
__6) Fig. S3B legend: A typo as follows: CCD15-depelted RPE1 cells should read CCDC15-depleted RPE1 cells. __
We corrected this typo.
__7) Fig. S3B legend: A typo as follows: cellswere fixed with should read cells were fixed with. __
We corrected this typo.
__8) There are many spelling mistakes and typos throughout the paper. I have listed a few examples above, but please carefully read through the manuscript to correct all the errors. __
Thank you for indicating the spelling mistakes we missed to correct for initial submission. In the revised manuscript, we carefully read through the manuscript to correct the mistakes.
__9) Fig. S3E: The orange columns depicting % of cells with Sas-6 dots look awkward. Why the columns look larger than the mean line? Please correct as appropriate. __
The total percentage of cells in the two categories (orange and purple) we counted is 100%, which corresponds to the column value at the y-axis. Therefore, the value for each experimental replicate for the orange category is less than 100% and is marked below the 100% line.
__10) Although authors provide microscopy information for the U-ExM and FRAP experiments, there is no information about the microscopy on regular confocal imaging experiments which should be detailed in Materials and Methods. Also, there is no information about the lenses, laser lines and the filter sets that were used in the imaging experiments. These should be provided as well. __
In the methods section, we now included detailed information for the microscopes we used and imaging setup (lenses, laser lines, filter sets, detectors, z-stack size, resolution).
11)
- __ Fig. 2A: lacks a scale bar. __
- __ Fig. 2C legend: lacks info on the scale bar length. __
- __ Fig. 5A legend: lacks info on the scale bar length. __
- __ Fig. 7A: lacks a scale bar. __
- __ Fig. 7G legend: lacks info on the scale bar length. __
- __ Fig. S2C-E: lack scale bars. __
- __ Fig. S3D, F and H: lack scale bars. (Fig. S4 in the revised manuscript)__
- __ Fig. S3J legend: lacks info on the scale bar length. (Fig. S4 in the revised manuscript)__
- __ Fig. S4A, B, D and E: lack scale bars. (Fig. S5 in the revised manuscript)__
- __ Fig. S4C legend: lacks info on the scale bar length. (Fig. S5 in the revised manuscript)__
- __ Fig. S4G legend: lacks info on the scale bar length. (Fig. S5 in the revised manuscript)__ We added the scale bars and the size information to the figures and figure legends for the above figures.
Reviewer #2 (Significance (Required)): __The findings of this study join among the relatively new literature (e.g., Steib et al., 2020 and Le Guennec et al. 2020) on the nature of centriole inner scaffold and its potential roles in centriole formation, integrity and its propensity to form the primary cilium. Therefore, it will be of interest to a group of scientists studying these topics in the field of centrosomes/cilia.
My expertise is on the biochemistry and genetics of centriole formation in animals.__
We thank the reviewer for his/her comments and constructive feedback to improve our manuscript. We are encouraged to see that the reviewer acknowledges how the results from our manuscript advances our understanding of centriole length, integrity and function regulation.
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Referee #2
Evidence, reproducibility and clarity
Summary:
In this study, Arslanhan et al. propose CCDC15 as a novel component of the centriole inner scaffold structure with potential roles in centriole length control, stability and the primary cilium formation in cultured epithelial cells. Using proximity labelling they explore the common interactors of Poc5 and Centrin-2, two resident molecules of the centriole inner scaffold, to hunt for novel regulators of this structure. The authors leverage expansion microscopy-based localization and siRNA-dependent loss-of-function experiments to follow up on one such protein they identify, CCDC15, with the aforementioned roles in centriole and cilia biology.
This study is designed and laid out nicely; however, to be able to support some of the important claims regarding their proximity labelling results and exploration on the roles of CCDC15, there are several major technical and reproducibility concerns that deem major revision. Similarly, the introduction (perhaps inadvertently) omits much of the recent studies on centriole size control that have highlighted the complexity of this biological problem. As such, addressing the following major points will be essential in further considering this work for publication.
Major comments:
- The authors use Poc5 and Centrin-2 molecules as joint baits to reveal the interactome of the centriole inner scaffold, however the work lacks appropriate experimental and analytical controls to argue that this is a proximity mapping "at the centriole inner scaffold". In its current state, it is simply an interactome of total Poc5 and Centrin-2, and it might be misleading to call it an interactome at the centriole inner scaffold (the statistical identification of shared interactors cannot do full justice to their biology at the centrosome). Appropriate expression data needed to delineate how large the centrosomal vs. cytoplasmic (or nucleoplasmic) fraction is for either of these molecules, both without and upon the addition of biotin (to see whether the bulk of interaction data stem from the cytoplasm/nucleoplasm or the centrioles themselves). The authors can test this by selectively blotting a lysate fraction containing the centrosomes after centrifugation, and compare them with the simultaneous blot of the supernatant (which were readily used for the blots presented in Fig. 1B). This experiment also becomes very relevant for the case of Centrin-2, as it also heavily localizes to the nucleoplasm as the authors found out (see Fig. 1A and Fig. S1A).
Additionally, an orthogonal approach should be taken to perform bio-image analysis on their biotin/streptavidin imaging data to demonstrate the exact ratios between the centrosomal vs. cytoplasmic/nucleoplasmic biotin activation with appropriate signal normalization between the biotin/streptavidin images. This is particularly important, as although the authors claim that these cells stably express the V5BirA*, it seems that there is partial clonality to the expression. Some cells in both the Poc5 and Centrin-2 fusion constructs appear to lack the V5/Streptavidin signals upon Biotin addition (such as the two cells in the centre right in Poc5, and again a cell in the centre right for Centrin-2 images). In its current form, Fig. 1A lacks signal quantification and does not report any information about the replicates and distributions of the data. I worry that this may raise concerns on the reproducibility if published in its current form.
Similarly, it is not clear whether the expression of Poc5 and Centrin-2 fusion molecules somehow interfere with their endogenous interactions or function. At least some loss-of-function (e.g., RNAi) experiments should be performed where the depletion of endogenous proteins should be attempted to rescue by the fusion constructs. This will help evaluate whether the fusion proteins can rescue the depletion of their endogenous counterparts and behave as expected from a wild-type scenario.
Overall, as the entire claim around the proximity mapping revolve around its assumption about the centriole inner scaffold, these controls seem imperative to substantiate the ground truth of the biology presented in the manuscript. 2. I am curious about the choices of the cell lines in this work. The proximity mapping to reveal CCDC15 as a candidate protein for centriole inner scaffold was performed in HEK293T cells (human embryonic kidney), however its immunostaining was performed using RPE1 and U2OS cells (human retinal and osteosarcoma epithelial cells respectively). This raises questions regarding the generality of CCDC15 as a centriole inner scaffold protein. Could CCDC15 be simply unique to the centriole inner scaffold of epithelial cells such as RPE1 and U2OS cells? Or could the authors demonstrate any information/data on whether it's similarly localized to the inner scaffold in embryonic kidney cells or other cell types? If not, the claims should be moderated to reflect this fine detail. 3. Discussions and data on the localization of CCDC15 to centriolar satellites appear anecdotal and not fully convincing (Fig. S2D). Given that the authors test the relevance of PCM1 for CCDC15's centriolar localization, it is key to have quantitative data supporting their claim that centriolar satellites can help recruit CCDC15 to the centriole. Could the authors quantify what proportion of CCDC15 localize to the centriolar satellites? One way to do this could be to quantify the colocalization coefficience of CCDC15 and PCM1 signals. 4. Similar to above (#3), there is no quantitative information on the co-localization or partial co-localization of the signal foci in Fig. 3A and 3B. The authors readily study CCDC15's localization in wonderful detail in their expansion microscopy data, so they could actually consider taking out Fig. 3A and 3B, as the data seem redundant without any quantification. 5. Do the authors also feel that CCDC15 localize to the core lumen in a somehow helical manner (Fig. 1A, Fig. 1F top and bottom panels, Fig. 5A etc.)? Le Guennec et al. 2020's helical lattice proposal for the inner scaffold further reaffirms that CCDC15 is indeed a likely major component of the inner scaffold. In my view, authors should state this physical similarity explicitly to further support their findings on CCDC15. 6. The data on the link between the CCDC15 recruitment and the centriole growth (Fig. 4F) or the G2 phase of the cell cycle (Fig. 4H) are not fully convincing without quantitative data. For Fig. 4F, the authors should consider plotting the daughter centriole length vs the daughter CCDC15 intensities against each another, to see whether more elongated daughters truly tend to have more CCDC15. For Fig. 4H, the argument regarding the cell cycle regulation requires quantification of the bands from several WB repeats, normalized to the expression of GAPDH within each blot (this is particularly relevant, as the bands of CCDC15 do not look dramatically different enough to draw conclusions by eye). 7. The authors find herein that CCDC15 depletion lead to centrioles that are ~10% shorter than the controls. With the depletion of Poc5 and Wdr90 (other proposed components of the inner scaffold), the centrioles end up larger however (Steib et al., 2020). If the role of inner scaffold in promoting centriole elongation is structural, why are these two results the opposite of each other? I realize there is a brief discussion about this at the end of the paper, however, this requires a detailed discussion and speculation on the relevance of these findings. It would be key to clarify whether the inner scaffold as a structure inhibits or promotes centriole growth - or somehow both? If so, how?
There might be some intriguing opposing regulatory action of Poc5 and CCDC15 as demonstrated here, where CCDC15 depletion leads to slightly over-recruitment of Poc5, and vice versa. Does this suggest that a tug-of-war going on between different molecules that localize to the inner scaffold? Does this provide some dynamicity to this structure, which might in turn regulate centriole length both positively and negatively? This may be analogous to how opposing forces of dyneins and kinesins provide robust length control for mitotic spindles. I am speculating here, but hopefully these may provide some useful grounds for further discussion in the paper. If the authors deem it interesting experimentally, they can test whether the two molecules indeed regulate centriole length by opposing each other's action, by a double siRNA of CCDC15 and Poc5 to see if this retains the centriole length at its control siRNA size (like how they do a similar test for Poc1's potential co-operativity with CCDC15 in Fig. 6J). 8. In their introduction section, the authors discuss how relatively little is known about the size control of centrioles, however they fail to mention a series of recent primary literature that uncover striking, new mechanisms and novel molecular players that highlight the complexity of centriole size control. This complexity appears to arise from the existence of multitude of length control mechanisms that influence the cartwheel or the microtubule length individually, or simultaneously via yet-to-be further explored crosstalk mechanisms.
a. As such, when the authors talk about the procentriole size control in the introduction, they should discuss and refer to the following studies, in terms of: - How theoretical and experimental work demonstrate that procentriole length may vary dependent on the levels of its building block Sas-6 in animals (Dias Louro et al., 2021 PMID: 33970906; Grzonka and Bazzi, 2022 bioRxiv). - How a homeostatic Polo-like kinase 4 clock regulates centriole size during the cell cycle (Aydogan et al., 2018 JCB PMID: 29500190), and how biochemistry and genetics coupled with mathematical modelling unravel a conserved negative feedback loop between Cep152 and Plk4 that constitutes the oscillations of this clock in flies (Boese et al., 2018 PMID: 30256714; Aydogan et al., 2020 PMID: 32531200) and human cells (Takao et al., 2019 PMID: 31533936).
b. Similarly, when the authors refer to centriole size control induced by microtubule-related proteins, they should highlight the further complexity of this process by referring to: - How a molecule located at the microtubule wall, Cep295/Ana1, can regulate centriole length in flies (Saurya et al., 2016 PMID:27206860) and human cells (Chang et al., 2016 PMID:27185865) - like all the other centriolar MT molecules that the authors discuss in the manuscript. - How a crosstalk between Cep97 and Cep152 influences centriole growth in fly spermatids (Galletta et al., 2016 PMID:27185836). - How a crosstalk between CP110-Cep97 and Plk4 influences centriole growth in flies (Aydogan et al., 2022 PMID:35707992), and this molecular crosstalk is conserved, at least biochemically, in human cells (Lee et al., 2017 PMID:28562169).
Minor comments:
- Introduction section: Literature reference missing for the sentence starting with "Importantly, the stable nature of centrioles enables them to withstand...".
- Fig. S1 legend: A typo as follows: CRAPome banalysis should read CRAPome analysis.
- Fig. S2: Info on the scale bar in the legend is missing in Fig. S2A. Scale bars for different panels are missing in general in Fig. S2A.
- Fig. 3A and 3B: When displaying the data, coloured cartoon diagrams would be beneficial to guide the reader who are not fully familiar with the spatial orientation of these proteins.
- Fig. 3H: No information about the sample number (number of cells or technical repeats examined) reported.
- Fig. S3B legend: A typo as follows: CCD15-depelted RPE1 cells should read CCDC15-depleted RPE1 cells.
- Fig. S3B legend: A typo as follows: cellswere fixed with should read cells were fixed with.
- There are many spelling mistakes and typos throughout the paper. I have listed a few examples above, but please carefully read through the manuscript to correct all the errors.
- Fig. S3E: The orange columns depicting % of cells with Sas-6 dots look awkward. Why the columns look larger than the mean line? Please correct as appropriate.
- Although authors provide microscopy information for the U-ExM and FRAP experiments, there is no information about the microscopy on regular confocal imaging experiments which should be detailed in Materials and Methods. Also, there is no information about the lenses, laser lines and the filter sets that were used in the imaging experiments. These should be provided as well.
- Fig. 2A: lacks a scale bar.
- Fig. 2C legend: lacks info on the scale bar length.
- Fig. 5A legend: lacks info on the scale bar length.
- Fig. 7A: lacks a scale bar.
- Fig. 7G legend: lacks info on the scale bar length.
- Fig. S2C-E: lack scale bars.
- Fig. S3D, F and H: lack scale bars.
- Fig. S3J legend: lacks info on the scale bar length.
- Fig. S4A, B, D and E: lack scale bars.
- Fig. S4C legend: lacks info on the scale bar length.
- Fig. S4G legend: lacks info on the scale bar length.
Significance
The findings of this study join among the relatively new literature (e.g., Steib et al., 2020 and Le Guennec et al. 2020) on the nature of centriole inner scaffold and its potential roles in centriole formation, integrity and its propensity to form the primary cilium. Therefore, it will be of interest to a group of scientists studying these topics in the field of centrosomes/cilia.
My expertise is on the biochemistry and genetics of centriole formation in animals.
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Referee #1
Evidence, reproducibility and clarity
Summary:
In this manuscript, Arslanhan and colleagues use proximity proteomics to identify CCDC15 as a new centriolar protein that co-localizes and interacts with known inner scaffold proteins in cell culture-based systems. Functional characterization using state-of-the-art expansion microscopy techniques reveals defects in centriole length and integrity. The authors further reveal intriguing aberrations in the recruitment of other centriole inner scaffold proteins, such as POC1B and the SFI1/centrin complex, in CCDC15-deficient cells, and observe defects in primary cilia.
Major comments:
- The authors present a high-quality manuscript that identifies a novel centriolar protein by elegantly revealing and comparing the proximity proteomes of two known centriolar proteins, which represents an important component for the maintenance of centrioles.
- Data are often presented from two independent experiments (n = 2), which is nice, but also the minimum for experiments in biology. It is strongly recommended to perform at least three independent experiments.
- The protein interaction studies presented in Fig. 3 could be of higher quality. While it is great that the authors compared interactions to the centriolar protein SAS6, which is not expected to interact with CCDC15, the presented data raise many questions. 1) In most cases, co-expression of tagged CCDC15 stabilizes the tested interaction partners, such that the overall abundance seems to be higher. The increase in protein abundance is substantial for Flag-FAM161A (Fig. 3D) and GFP-Centrin-2 (Fig. 3E) and is even higher for the non-interactor SAS6 (Fig. 3G), while it cannot be assessed for GFP-POC1B (Fig. 3F). Hence, the higher expression levels under these conditions make it more likely that these proteins are "pulled down" and therefore do not represent appropriate controls. 2) All Co-IP experiments are lacking negative controls in the form of proteins that are not pulled down under the presented conditions. 3) The amounts of co-precipitation of the tested proteins appears very different. Could this reflect strong or weak interactors, or does it reflect the abundance of the respective proteins in centrioles?
- The observation that IFT88 is supposedly decreased at the base of cilia in CCDC15-depleted cells requires additional experiments/evidence. Fig. 7G shows the results of n = 2 and more importantly, a similar reduction of gamma-tubulin in siCCDC15. Could the observed reduction in IFT88 be explained by a decrease in accessibility to immunofluorescence microscopy? Would the reduction in IFT88 at the base also be apparent when the signals were normalized to gamma-tubulin signals?
- The observed Hedgehog signaling defects are described as follows: "CCDC15 depletion significantly decreased the percentage of SMO-positive cells". It is similarly described in the figure legend. If this was true, the simplest explanation would be that it reflects the reduction in ciliation rate (which is in a similar range). If SMO-positive cilia (instead of "cells") were determined, the text needs to be changed accordingly.
- OPTIONAL: While expansion microscopy is slowly becoming one of the standard super-resolution microscopy methods, which is particularly well validated for studying centrioles, the authors should consider confirming part of their findings (as a proof of principle, surely not in all instances) by more established techniques. This could serve to convince critical reviewers that may argue that the expansion process may induce architectural defects of destabilized centrioles, as observed after disruptions of components, such as in Fig. 6. Alternatively, the authors could cite additional work that make strong cases about the suitability of expansion microscopy for their studies, ideally with comparisons to other methods.
Minor points:
- Text, figures, and referencing are clear and accurate, apart from minor exceptions.
- The title suggests a regulator role for CCDC15 in centriole integrity and ciliogenesis, which has formally not been shown.
- As the authors observe changes in centriole lengths in the absence of CCDC15, it would be very insightful to compare these phenotypes to other components that affect centriolar length, such as C2CD3, human Augmin complex components (as HAUS6 is identified in Fig. 1) or others. These could be interesting aspects for discussion, additional experiments are OPTIONAL.
- While the reduced ciliation rate in the absence of CCDC15 is convincing, the authors did not investigate "ciliogenesis", i.e. the formation of cilia, and hence should re-phrase. The sentence in the discussion that "CCDC15 functions during assembly" should be removed.
- The existence of stably associated CCDC15 pools with centrosomes (Fig. 2) requires further evidence. The recovery of fluorescence after photobleaching in FRAP experiments is strongly dependent on experimental setups and is only semi-quantitative. A full recovery is unrealistic, hence, it is ideally compared to a known static or known mobile component. I personally think this experiment -as it is presented now- is of little value to the overall fantastic study. The authors may consider omitting this piece of data.
- The data that CCDC15 is a cell cycle-regulated protein is not very convincing (see Fig. 3H), as the signals area weak and the experiment has been performed only once (n= 1). This piece of data does not appear to be very critical for the main conclusions of the manuscript and may be omitted. Otherwise, this experiment should be repeated to allow for proper statistical analysis.
- Experimental details on how "defective centrioles" are determined are missing.
- For figures, in which the focus should be on growing centrioles (see Fig. 4), it could be helpful to guide the reader and indicate the respective areas of the micrographs by arrows.
- Page18: "centriole length shortening" could be changed to "centriole shortening".
- It is unclear how the authors determine distal from proximal ends of centrioles in presented micrographs (see Fig. 5D).
- Fig. 7A is missing scale bars and Fig.7 overall is lacking rectangle indicators of the areas that are shown at higher magnification in the insets.
- Fig. 7C displays cilia that appear very short, especially when comparing to the micrographs and bar graphs presented. The authors may want to explain this discrepancy.
Significance
- From a technical point of view the authors use two state-of-the-art technologies, namely proximity labeling combined with proteomics and ultrastructure expansion microscopy, that are both challenging and very well suited to address the main questions of this study.
- General assessment: The presented study is of highest experimental quality. Despite being very challenging, the expansion microscopy and proximity proteomics experiments have been designed and performed very well to allow solid interpretation. The results of the central data are consistent and allow strong first conclusions about the putative function of the newly identified centriolar protein CCDC15. The study presents a solid foundation for future hypothesis-driven, mechanistic analysis of CCDC15 and inner scaffold proteins in centriole length control and maintaining centriole integrity. The only limitation of the study is that the technically simpler experiments should be repeated to allow proper statistical assessment, which can be addressed easily.
- Advance: This is the first study that identifies CCDC15 as a centriolar protein and localizes it to the inner scaffold. It further describes a function for CCDC15 in centriole length control and shows its importance in maintaining centriole integrity with consequences for stable cilia formation in tissue culture. The study provides further functional insights into the interdependence of inner scaffold proteins and the role of CCDC15 in the recruitment of the SFI1/centrin distal complex.
- Audience: The manuscript will be of broad interest to the fields of centrosome and cell biology, both from a basic research and genetics/clinical point of view due to the association with human disorders. The state-of-the-art technologies applied will be of interest to a broader cell and molecular biology readership that studies subcellular compartments and microtubules.
- Reviewer's field of expertise: Genetics, imaging, and protein-protein interaction studies with a focus on centrosomes and cilia.
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Reply to the reviewers
Manuscript number: RC-2022-01716
Corresponding author(s): Thomas, Langer
1. General Statements
We have performed a comprehensive and time-resolved analysis of the mitochondrial proteome upon induction of cellular senescence and observed rapid metabolic rewiring of mitochondria. In particular, we identified two metabolic pathways, the 1C-folate metabolism and the branched-chain amino acid (BCAA) catabolism that were rapidly rewired upon senescence induction. Our analysis therefore provides unprecedented insight into the function and metabolic adaptations of mitochondria in senescent cells, which could also serve as a reference for future studies. Moreover, we demonstrate that quantification of mitochondrial abundance using the mitochondrial volume allows to reconcile seemingly contradicting conclusions on the function/fitness of mitochondria in senescent cells. In our opinion, our studies therefore represent a valuable and significant contribution to our understanding of the role of mitochondria in senescence.
2. Point-by-point description of the revisions
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In the manuscript "Metabolic rewiring of mitochondria in senescence revealed by the time resolved analysis of the mitochondrial proteome", Kim et al performed the proteomic approach to investigate the mitochondrial programming during senescence induction of cultural fibroblast. The main findings mentioned by author are the enhanced catabolism of branched-chain amino acids and the reduction of 1C-folate metabolism.
- * The author claimed their approaches are "time-resolved analysis" from day 1 to day 7 during the senescence induction. However, they did not adequately describe the transition of molecular signatures and cellular states from normal cells to senescent cells in each timepoint. The authors need to quantify the protein levels of p16, p21, and p53 and transcript levels of SASP factors in each timepoint to define the stages during induction and discuss how their finding related to this transition. * As per the reviewer's requests, we monitored the molecular markers during the transition to the senescent state by decitabine. The mRNA level of CDKN1A (encoding p21) was significantly increased on days 5 and 7, while that of CDKN2A (encoding p16) was moderately but significantly increased (~40 %) on day 7 (updated Suppl. Figure 1B). Furthermore, mRNA levels of two core SASP genes, IL1A and IL6 were significantly increased on day 7.
These results complement our analysis of protein levels of senescent markers including p16 and p21 and several SASP proteins (updated Suppl. Figure 2C). Of note, decreased intracellular protein levels of HMGB1 and HMGB2 indicate a senescent rather than a pre-senescent state (PMID: 27700366; 23649808) and demonstrate that cells display transcriptomic signatures of a senescent state after decitabine treatment for seven days. However, the mass spectrometric analysis of the cellular proteome revealed an accumulation of p21 on day 5 but not on day 7 (updated Suppl. Figure 2C). We therefore performed additional experiments to further corroborate the senescent state of the cells under these conditions and to collectively address concerns raised by reviewer 1 (points 1, 5) and reviewer 2 (points 2, 3). Senescence is defined by an irreversible cell-cycle arrest. Consistently, cells maintained the proliferation-deficient state and did not re-enter the cell cycle for 7 days after the removal of decitabine (updated Suppl. Figure 1D). Moreover, cells reached a plateau of SA-b-Gal positivity on day 7, which was maintained after 7 days of decitabine removal (updated Suppl. Figure 1E). We also examined the protein levels of several senescence markers (updated Suppl. Figure 1F). DNA damage was acutely induced upon decitabine treatment as evidenced by phosphorylated H2A.X at serine 139 (p-H2A.XS139). This was accompanied by the rapid reduction of lamin B1 (LMNB1) which is a hallmark of senescence (PMID: 22496421). In agreement with the EdU data (updated Suppl. Figure 1D), the loss of phosphorylated Rb at serine 807/811 (p-RbS807/811) and cyclin A2 (CCNA2), essential for G1-S transition, from day 3 indicated a cell cycle-arrested state.
Together, we conclude that cells start to become senescent on day 5 and reach the senescent state on day 7 after decitabine treatment. We now show these data in the updated Supplementary figure 1 and modified the text accordingly.
- The authors treated decitabine and doxorubicin in different periods. Sometimes they properly prepared two different control groups, and sometimes they use only one control group. This issue should be unified. *
Proteomic analysis revealed that DMSO treatment for 7 days did not affect the cellular proteome (Reviewer figure 1), indicating that DMSO is as ineffective as H2O in our experimental conditions. When cells treated with decitabine and doxorubicin were assayed in the same experiment, cells treated with DMSO were used as a common control. When decitabine and doxorubicin-treated cells were assayed independently, either DMSO or H2O was used as the control accordingly.
Reviewer figure 1. The pairwise comparison of proteome from cells treated with DMSO at different time points. The x-axis denotes log2FC and y-axis does –log(adj.P-value). The data are of the same origin from the updated Suppl. Figure 2.
- The mitochondria dysfunction and the increasing mitochondrial mass in cellular senescence have been reported in cell culture study previously. The authors described that the mitochondrial activity normalized to mitochondria volume decreased in senescent cells, which raises the importance of the exact value (mitochondria volume) they used for normalization. However, the quantification result in Figure 1 shows obvious batch effects and variation which make their estimation not reliable enough. The authors should increase replicate numbers in image analysis to provide robust quantification results. Besides, the orthogonal method for measuring mitochondrial mass should be also performed to confirm that the FC of volume is reliable. *
We have increased the number of experiments quantifying the mitochondrial volume in senescent cells (updated Figure 1B). Despite some variation between experiments, we observed a significant increase in mitochondrial volume, which could be explained by an increased length of mitochondrial tubules, while the mitochondrial width remained unaltered. New quantification revealed an about 8-fold increase of mitochondrial volume both upon decitabine and doxorubicin treatment (about 30% lower than our original calculation). These experiments are now shown as violin plots, showing the distribution of the experimental data along with the median and quartile values (updated Figure 1B). They further substantiate our conclusion that the bioenergetic activity of mitochondria is increased per senescent cell, but decreased when calculated relative to the mitochondrial volume.
- The normalization and scaling strategy of proteomic data were not described in method. Senescent cells show increasing cell size and protein abundance. The authors should describe how they processed the peptide counts in detail. It is confused whether the up regulation (FC>1) represents the increment per cell, per mitochondrion, or in the protein abundance. *
We apologize for not being clear at this point. For clarification, we have amended the text in the method part on p. 22:
´The proportion of proteins of a certain subcellular compartment with the total cellular proteome was calculated by dividing the sum of the TMT reporter intensities for all proteins of this compartment by the sum of TMT reporter intensities for all quantified proteins. Prior to differential expression analysis, TMT reporter intensities were normalized to within the TMT multiplex using VSN (PMID: 12169536). Intensity normalization and differential expression analysis was carried out using proteins quantified in all 32 samples (total peptide counts) or using the subset of mitochondrial proteins only (mitochondria-specific peptide counts). Thus, the fold-change denotes the change in protein abundance within a given (sub-)proteome.`
- The protein amounts of CDKN1A and CDKN2A were not increased on day 7 in Sup Fig 2C. The authors need to provide the explanation of them to prevent bias in their cellular senescence-dependent findings. In addition, ARF and INK4a should be separately quantified.
*
We have performed a series of additional experiments to corroborate that cells are senescent on day 7 (see point 1). We have not detected p14ARF, but p16INK4A in our proteomic analysis. CDKN2A thus refers to p16INK4A. We have updated Supplementary figure 2C for clarification.
- This comment is also related to comment #4. In line 223, the authors mentioned "This is accompanied by a decrease in mitochondrial translation, consistent with the observed decreased respiratory activity of mitochondria in senescent cells.". First, the linkage between mitochondrial translation and respiratory activity should be further illustrated. Second, the results in Fig. 2G and 2H clearly showed that the overall respiratory activity was enhanced in senescent cells (day 7), and only the activity normalized by mitochondrial volume showed decreased. How the authors normalize proteomic data from whole cell lysates with mitochondrial mass is missed in this manuscript.*
Mitochondrial DNA encodes essential subunits of OXPHOS complexes. Therefore, decreased mitochondrial translation is accompanied by reduced respiratory activity. We have clarified this point on p. 13 of the revised manuscript.
The proteomic data show the abundance of mitochondrial proteins within the cellular proteome. Our proteomic analysis established that the mitochondrial protein mass increases proportionally to that of the cell (updated Figure 3B), consistent with the increase in mitochondrial volume. For clarification, we have now improved the description of our quantification method in the manuscript on p. 22.
Reviewer #1 (Significance (Required)):
Overall, the central findings of the study provide informative evidence to support several concepts and biological observations in previous reports. However, because of the lack of sufficient description and experimental verification, part of the conclusion is not rigorous enough and needed to be further improved.
To address the concerns of the reviewer, we provide now more experimental evidence that the cells attain the senescent state when analyzed by time-resolved proteomics and improved the description of our experimental procedures.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
*Kim et al. applied a new method to demonstrate that senescent cells accumulate with dysfunctional mitochondria. They isolated mitochondrial to profile mitochondrial proteome in a time-dependent manner and revealed a metabolic shift in mitochondria during the senescence process. However, many groups have widely studied mitochondrial biology in senescent cells (Joao F. Passos and Thomas Von Zglinicki et al.). Based on the previous finding, cellular senescence is also known for dramatic changes in mitochondrial mass, dynamics, structure, metabolism, and function. Thus, the current work is descriptive and incremental. *
We kindly disagree with this statement of the reviewer. We do appreciate and acknowledge previous studies on mitochondria in senescent cells, but are convinced that our work provides novel insight, as to how mitochondria are affected upon establishment of senescence. Rather than considering mitochondria as dysfunctional, our proteomic and metabolomic data indicate reprogramming of mitochondria: reduced respiratory activities are accompanied by enhanced BCAA catabolism, fatty acid metabolism, and Ca2+ transport (updated Figure 4A, updated Figure 5).
We would also like to point out that several reports on the role of mitochondria in senescent cells were seemingly contradicting and difficult to reconcile with each other. Some studies observed a decreased membrane potential and increased ROS production in senescent cells, while at the same time, mitochondrial respiration appeared to be increased (PMID: 15018610, 20160708). Other studies reported an increased OXPHOS activity due to enhanced mitochondrial metabolism of glucose/pyruvate and fatty acids (PMID: 23945590, 23685455, 30778219, 22421146). Our work provides a rationale for these apparently disparate findings, highlighting that the assessment of mitochondrial function/fitness in senescent cells requires the accurate determination of mitochondrial mass/volume. We show that senescent cells harbor more mitochondria with reduced respiratory activity.
As a side note, we did not isolate mitochondria but determined the cellular proteome and analyzed organellar proteomes (such as the mitochondrial proteome) based on reference databases (see also updated Suppl. Figure 2D).
I have specific comments listed below:
*Major: 1. The authors stated that mitochondrial DNA (mtDNA) was decreased per mitochondrion. However, in Fig 2A, there is no statistical significance. So, this statement is not valid. *
We have determined mtDNA levels in two additional, independent experiments but did not observe a statistically significant decrease in senescent cells due to a relatively high experimental variability (n=5). We have updated Figure 2A and corrected the text accordingly on p. 6.
- The authors investigated the mitochondrial proteome alterations during CS development (days 1 to 7 post-treatment of decitabine). However, in supplemental Fig. 2C, p16 and p21 did not increase on day 7. So, the mitochondria authors studied are the authors studied in a pre-senescent state. What is the rationale for this study, and why did the authors not examine mitochondria at the fully senescent stage?*
We kindly disagree with the statement of the reviewer that analyzed was a pre-senescent state. As outlined in detail in reply to reviewer 1 (point 1), the analysis of a series of established senescent markers on mRNA and protein levels demonstrates that cells have reached the senescent state after seven days of drug treatment. Most importantly, we show by EdU staining in Suppl. Figure 1D that cells are in cell cycle arrest on day 7 and now provide additional evidence (EdU- and SA-b-Gal staining, senescence and cell cycle markers) that this state is maintained for another seven days, excluding a quiescent state (updated Suppl. Figure 1D, 1E). This includes the loss of lamin B1, which is associated with senescence but not quiescence (PMID: 22496421).
- The authors claimed that the fraction of mitochondrial proteins did not significantly change (Shown in Fig. 3B). Again, this could be due to cells at the pre-senescent stage; I wonder if this change could be significant after cells are fully senescent.*
As discussed above, we provide now additional evidence demonstrating that cells are in a senescent state. Of note, our findings are in agreement with a recent report (PMID: 35987199), showing that mitochondrial and cellular proteomes are altered proportionally in senescent cells.
- The data in Fig. 4E is not statistically significant. Please increase n to confirm your conclusion.*
Considering the causal relationship between mitochondrial translation and OXPHOS deficiency, we feel that this point is rather confirmatory. We therefore present now instead two representative images (updated Figure 4D)
- Are these mitochondrial proteome alterations associated with the senescent cell's functional output or other features? Are these changes cell type-dependent.*
To address the functional impact of the mitochondrial reprogramming of metabolism in senescent cells, we blocked BCAA catabolism by knocking down the rate-limiting enzyme BCKDHA, before treating cells with decitabine or doxorubicin. However, the interpretation of these experiments was hampered by increased cell death upon BCKDHA knockdown independent of DNA damage. Thus, the BCKDHA appears to be essential for cell viability under our cell culture conditions, precluding an assessment of the role of the BCAA catabolism for the functional output of senescent cells. We included these data in the updated Suppl. Figure 5D and briefly mentioned them in the text on p. 10.
- I suggest the authors clarify explicitly the knowledge gap that the current study accomplished.*
We apologize for not being clear and have revised the manuscript to clarify this point. As pointed out in the General Statement, we have performed a comprehensive and time-resolved analysis of the mitochondrial proteome upon induction of cellular senescence and observed rapid metabolic rewiring of mitochondria. In particular, we identified two metabolic pathways, the 1C-folate metabolism and the BCAA catabolism that were rapidly rewired upon senescence induction. Our analysis therefore provides unprecedented insight into the function and metabolic adaptations of mitochondria in senescent cells, which could also serve as a reference for future studies. Moreover, we demonstrate that quantification of mitochondrial abundance using the mitochondrial volume allows to reconcile seemingly contradicting conclusions on the function/fitness of mitochondria in senescent cells. In our opinion, our studies therefore represent a valuable and significant contribution to our understanding of the role of mitochondria in senescence.
Minor: Please carefully check the statistical analysis. N of 2 is not sufficient for One-way ANOVA.
We have revisited the statistical analysis of our experiments and noted a mistake in the original Figure 4E (statistical analysis with n=2). We apologize for this mistake and have corrected it (see reply point 4) as updated Figure 4D.
Reviewer #2 (Significance (Required)):
I do not see the significance of the current work. The work is descriptive and incremental, which reduce the impact of this manuscript.
My expertise is in cellular senescence and aging.
As outlined in the General Statement and in reply to reviewer 2 (point 6), we provide insight into changes in the mitochondrial proteome in senescent fibroblasts in an unprecedented manner. Although metabolic reprogramming of mitochondria has been described, our results highlight the relevance of two metabolic pathways in senescent cells, the one-carbon and the BCAA metabolism, which to our knowledge has not been described before. Moreover, our work reveals the importance to adequately quantify mitochondrial abundance, when assessing the bioenergetic activity of mitochondria in (enlarged) senescent cells.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The manuscript by Kim and colleagues investigated the metabolic and proteomic changes in senescent fibroblasts. The authors performed a time-resolved analysis of the proteome and revealed the impacts on mitochondrial proteome. They also applied tracing approaches to further demonstrate the impact on mitochondrial metabolism and revealed a potential impact of branched-chain amino acid catabolism and carbon-folate metabolism in senescent fibroblasts. They concluded that the reprogramming of mitochondria influences the senescence-associated secretory phenotype (SASP) impacting diseases associated with senescent cells.
-
- The authors quantified the volume of mitochondria to examine mitochondrial functions. Some data were normalized "per cell" and "per mito". Should it read per mito volume? The comparison between the two normalization procedures in Fig 2 is important but also confusing. Can the authors speculate why non-mitochondrial respiration seems to be increased in decitabine/doxorubicin conditions (Fig. 2G/H)? Are the data significantly affected after normalization to non-mitochondrial respiration?* As anticipated by the reviewer, ´per mito` indeed refers to the mitochondrial volume. We have adjusted the text on p. 6 to clarify this point.
An increase in non-mitochondrial respiration in senescent cells was also reported by the von Zglinicki group (PMID: 28330601). A major source of non-mitochondrial OCR is thought to be cytosolic/peroxisomal H2O2 production by cyclooxygenase (COX), and NADPH oxidase, which consume oxygen to produce H2O2. Especially, the cytosolic H2O2 level is known to be higher in senescent cells (PMID: 10075689). Moreover, cyclooxygenase 1 (PTGS1) is significantly upregulated in our proteomics data (Reviewer figure 2), which could explain the reason for the increased non-mitochondrial OCR in senescent cells.
Reviewer figure 2. The pairwise comparison of PTGS1 level at each time point from the proteomics data in Figure 3. **: P Of note, normalization to non-mitochondrial respiration does not significantly alter our conclusions. We observed a significant decrease in basal respiration and spare respiratory capacity both upon decitabine and doxorubicin treatment, which recapitulates our original findings taking mitochondrial abundance into account (Reviewer figure 3).
Reviewer figure 3. Oxygen consumption rates of senescent fibroblasts after normalization to non-mitochondrial OCR. (A, B) Left: representative graphs of OCR data. Right: quantification of respiratory parameters based on the OCR graph. Welch t-test, Bonferroni-Dunn correction, n=5.
- The tracing data are impactful and critical to confirm metabolic changes. Can the authors explain why they added the tracer to the regular growth medium (instead of substituting the metabolite of interest)? The media composition of the proteomic and the metabolic experiments is not identical. For instance, additional 5.5mM 13C glucose has been added to the 13C glucose tracer experiment while all other experiments were performed with 5.5mM 12C glucose only. Changes in media composition certainly affect cell function and metabolism. The authors may want to repeat key tracing experiments to mimic experimental conditions used in proteomics analysis.*
The use of glucose-containing MEM had only practical reasons, because glucose-free MEM is not commercially available. However, this does not confound our proteomic analysis between day 1 and 7, since the tracing experiments in MEM containing glucose and 13C glucose were performed to the established senescent cells on day 7.
- The impact on branched-chain amino acids is interesting. Did the authors observe 13C incorporation into the TCA cycle from BCAA? Increased BCAA catabolism may increase mitochondrial respiration, but the authors observed decreased OCR in senescent cells. Further, does inhibition of BCAA catabolism rescue the phenotype observed in senescent cells?*
We did not observe any significant incorporation of BCAA carbons into malate but found an 3-5 fold increased flux into lipogenic TCA cycle intermediates, such as acetyl-CoA and citrate (updated Figure 5D). In agreement with glucose and glutamine being the major source of lipogenic acetyl-CoAs in cell culture (PMID: 31119666), the absolute changes are rather minor. We therefore carefully discuss the possibility that BCAA carbons are metabolized to supply the lipogenic carbon moieties in senescent cells rather than increasing mitochondrial respiration in the text on p. 12.
To address the functional impact of the mitochondrial reprogramming of metabolism in senescent cells, we blocked BCAA catabolism by knocking down the rate-limiting enzyme BCKDHA, before treating cells with decitabine or doxorubicin (see also Reviewer 2, point 5). However, the interpretation of these experiments was hampered by increased cell death upon BCKDHA knockdown independent of DNA damage. Thus, the BCKDHA appears to be essential for the cell viability under our cell culture conditions, precluding an assessment of the role of the BCAA catabolism for the functional output of senescent cells. We included these data in the updated Suppl. Figure 5D and briefly mentioned them in the text on p. 10.
Reviewer #3 (Significance (Required)):
Understanding the metabolic reprogramming of mitochondria in senescent cells is interesting and of high interest to the research community. However, some clarification is needed on experimental conditions, as media compositions in proteome and metabolome experiments were different which certainly affects cell metabolism and function.
We thank the reviewer for their positive evaluation of the significance of our work. In the revised manuscript, we have now clarified the technical issues raised showing that different culture conditions do not confound our proteomic and metabolomic analysis.
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Referee #3
Evidence, reproducibility and clarity
The manuscript by Kim and colleagues investigated the metabolic and proteomic changes in senescent fibroblasts. The authors performed a time-resolved analysis of the proteome and revealed the impacts on mitochondrial proteome. They also applied tracing approaches to further demonstrate the impact on mitochondrial metabolism and revealed a potential impact of branched-chain amino acid catabolism and carbon-folate metabolism in senescent fibroblasts. They concluded that the reprogramming of mitochondria influences the senescence-associated secretory phenotype (SASP) impacting diseases associated with senescent cells.
- The authors quantified the volume of mitochondria to examine mitochondrial functions. Some data were normalized "per cell" and "per mito". Should it read per mito volume? The comparison between the two normalization procedures in Fig 2 is important but also confusing. Can the authors speculate why non-mitochondrial respiration seems to be increased in decitabine/doxorubicin conditions (Fig. 2G/H)? Are the data significantly affected after normalization to non-mitochondrial respiration?
- The tracing data are impactful and critical to confirm metabolic changes. Can the authors explain why they added the tracer to the regular growth medium (instead of substituting the metabolite of interest)? The media composition of the proteomic and the metabolic experiments is not identical. For instance, additional 5.5mM 13C glucose has been added to the 13C glucose tracer experiment while all other experiments were performed with 5.5mM 12C glucose only. Changes in media composition certainly affect cell function and metabolism. The authors may want to repeat key tracing experiments to mimic experimental conditions used in proteomics analysis.
- The impact on branched-chain amino acids is interesting. Did the authors observe 13C incorporation into the TCA cycle from BCAA? Increased BCAA catabolism may increase mitochondrial respiration, but the authors observed decreased OCR in senescent cells. Further, does inhibition of BCAA catabolism rescue the phenotype observed in senescent cells?
Significance
Understanding the metabolic reprogramming of mitochondria in senescent cells is interesting and of high interest to the research community. However, some clarification is needed on experimental conditions, as media compositions in proteome and metabolome experiments were different which certainly affects cell metabolism and function
-
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Referee #2
Evidence, reproducibility and clarity
Kim et al. applied a new method to demonstrate that senescent cells accumulate with dysfunctional mitochondria. They isolated mitochondrial to profile mitochondrial proteome in a time-dependent manner and revealed a metabolic shift in mitochondria during the senescence process. However, many groups have widely studied mitochondrial biology in senescent cells (Joao F. Passos and Thomas Von Zglinicki et al.). Based on the previous finding, cellular senescence is also known for dramatic changes in mitochondrial mass, dynamics, structure, metabolism, and function. Thus, the current work is descriptive and incremental. I have specific comments listed below:
Major:
- The authors stated that mitochondrial DNA (mtDNA) was decreased per mitochondrion. However, in Fig 2A, there is no statistical significance. So, this statement is not valid.
- The authors investigated the mitochondrial proteome alterations during CS development (days 1 to 7 post-treatment of decitabine). However, in supplemental Fig. 2C, p16 and p21 did not increase on day 7. So, the mitochondria authors studied are the authors studied in a pre-senescent state. What is the rationale for this study, and why did the authors not examine mitochondria at the fully senescent stage?
- The authors claimed that the fraction of mitochondrial proteins did not significantly change (Shown in Fig. 3B). Again, this could be due to cells at the pre-senescent stage; I wonder if this change could be significant after cells are fully senescent.
- The data in Fig. 4E is not statistically significant. Please increase n to confirm your conclusion.
- Are these mitochondrial proteome alterations associated with the senescent cell's functional output or other features? Are these changes cell type-dependent?
- I suggest the authors clarify explicitly the knowledge gap that the current study accomplished.
Minor: Please carefully check the statistical analysis. N of 2 is not sufficient for One-way ANOVA.
Significance
I do not see the significance of the current work. The work is descriptive and incremental, which reduce the impact of this manuscript. My expertise is in cellular senescence and aging.
-
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Referee #1
Evidence, reproducibility and clarity
In the manuscript "Metabolic rewiring of mitochondria in senescence revealed by the time resolved analysis of the mitochondrial proteome", Kim et al performed the proteomic approach to investigate the mitochondrial programming during senescence induction of cultural fibroblast. The main findings mentioned by author are the enhanced catabolism of branched-chain amino acids and the reduction of 1C-folate metabolism.
- The author claimed their approaches are "time-resolved analysis" from day 1 to day 7 during the senescence induction. However, they did not adequately describe the transition of molecular signatures and cellular states from normal cells to senescent cells in each timepoint. The authors need to quantify the protein levels of p16, p21, and p53 and transcript levels of SASP factors in each timepoint to define the stages during induction and discuss how their finding related to this transition.
- The authors treated decitabine and doxorubicin in different periods. Sometimes they properly prepared two different control groups, and sometimes they use only one control group. This issue should be unified.
- The mitochondria dysfunction and the increasing mitochondrial mass in cellular senescence have been reported in cell culture study previously. The authors described that the mitochondrial activity normalized to mitochondria volume decreased in senescent cells, which raises the importance of the exact value (mitochondria volume) they used for normalization. However, the quantification result in Figure 1 shows obvious batch effects and variation which make their estimation not reliable enough. The authors should increase replicate numbers in image analysis to provide robust quantification results. Besides, the orthogonal method for measuring mitochondrial mass should be also performed to confirm that the FC of volume is reliable.
- The normalization and scaling strategy of proteomic data were not described in method. Senescent cells show increasing cell size and protein abundance. The authors should describe how they processed the peptide counts in detail. It is confused whether the up regulation (FC>1) represents the increment per cell, per mitochondrion, or in the protein abundance.
- The protein amounts of CDKN1A and CDKN2A were not increased on day 7 in Sup Fig 2C. The authors need to provide the explanation of them to prevent bias in their cellular senescence-dependent findings. In addition, ARF and INK4a should be separately quantified.
- This comment is also related to comment #4. In line 223, the authors mentioned "This is accompanied by a decrease in mitochondrial translation, consistent with the observed decreased respiratory activity of mitochondria in senescent cells.". First, the linkage between mitochondrial translation and respiratory activity should be further illustrated. Second, the results in Fig. 2G and 2H clearly showed that the overall respiratory activity was enhanced in senescent cells (day 7), and only the activity normalized by mitochondrial volume showed decreased. How the authors normalize proteomic data from whole cell lysates with mitochondrial mass is missed in this manuscript.
Significance
Overall, the central findings of the study provide informative evidence to support several concepts and biological observations in previous reports. However, because of the lack of sufficient description and experimental verification, part of the conclusion is not rigorous enough and needed to be further improved.
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Reply to the reviewers
Detailed Answer to the Reviewers
Reviewer #1
__Summary __
The authors used a novel imaging technique to monitor glutamate release and correlated these measurements with gold standard electrophysiological measurements. The genetically encoded glutamate reporter, iGluSnFR, was expressed in mouse spiral ganglion neurons using the approach described in Ozcete and Moser (2021, EMBO J). The iGluSnFR signals and the postsynaptic currents were measured at the endbulb of Held synapse. A small effect of the expression of iGluSnFR on the mEPSC kinetics was found (but see comment 1). Furthermore, deconvolution of the iGluSnFR signals was performed enabling the comparison of some presynaptic properties assessed with either iGluSnFR or electrophysiology.
We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.
__Major comments __
- The central finding of the study is the prolonged decay time constant of the mEPSC. The difference is small but astonishingly significant (0.172 {plus minus} 0.002 and 0.158 {plus minus} 0.001, P=0.003). The SEM is about 100 times smaller than the measured time constant. This is biologically not plausible. Therefore, I am skeptical about the statistical significance of the results.
We appreciate the feedback of the reviewer. We agree that our presentation of the data was easy to misunderstand and we changed it (see below). We modeled the statistical relationship of kinetic parameters with a mixed effects model (as described in methods). Since the presentation of regression parameters for this kind of data is not very usual in synaptic neuroscience (nor very informative in this study), we instead opted to report SEM and a p-value derived from the fit of the linear mixed effects model. For the SEM, there is no clear way to take into account the clustered nature of the data, so we calculated the SEM over all observations. Since the SEM is proportional to 1/sqrt(n) and the number of recorded mEPSCs is very large, this does indeed yield a very small SEM. We agree that reporting the SEM over all observations is unusual and leads to misunderstandings in this case. Now, we instead report the re-calculated the mean / SEM for all parameters over the median values per cell. We changed the presentation of the data also for the other values presented in the MS in all tables and the relevant parts of the main texts.. We note that the summary statistics do not directly influence the further statistical modeling.
- Analysis of the size of RRP with electrophysiology and iGluSnFR is potentially interesting but iGluSnFR recordings could not resolve the spontaneous fusion of single vesicles. Therefore, it is not possible to estimate RRP with these iGluSnFR recordings. This limitation of the approach should be emphasised more clearly.
Yes, we think the inability to resolve single vesicles is one of the major limitations of the study and we note this in the introduction and in the relevant section of the discussion. We agree that it should be clear in the relevant section that we are not able to measure RRP size without resolving single vesicle release and modified the wording of the relevant results section to reflect this better (line 267, 497). We still believe that the cumulative release analysis is potentially interesting to researchers in the field, as RRP size is not the only parameter that can be estimated in this way. In particular, an estimation of the release probability in resting conditions is possible by dividing the amplitude of the first response (i.e. response to a single stimulus) by the RRP estimate even without knowing the exact number of vesicles that comprise either.
- The control conditions (no surgery/no virus injection) are not the correct conditions for comparison with the experimental conditions (surgery/virus injection and sensor expression). The control group should be operated and injected with saline or ideally with a virus expressing GFP at the extracellular membrane. The authors addressed this issue by citing their previous work (Özcete and Moser, 2021). However, I am not convinced that surgery does not induce subtle changes that could explain the small differences in mEPSCs.
This is an excellent point that should be addressed in further research. A slowed decay would be consistent with the idea that iGluSnFR affects glutamatergic transmission by buffering glutamate, but we cannot rule out subtle changes due to the postnatal surgery or AAV-mediated transgene expression. In response to the reviewer’s comment, we modified the text to reflect the possibility of surgery and / or other parts of the expression system being responsible for the changes. We also discuss further control experiments (line 408). Finally, we believe that our comparison is still relevant for researchers using iGluSnFR in the system, as they will be asking if introducing a measurement system affects the underlying quantity.
__Minor comments __
The supplementary figures are not listed in the order in which they appear in the main text.
We now list the supplementary figures in the order in which they appear in the main text.
Figure 2B and 3 are not referenced in the main text.
We now reference the figures in the text.
The PPR in Figure 3 shows a PPR that cannot be evaluated because of the unusual plot with lines that are too thick.
We updated Fig.3 and chose a more straight forward way to display the PPRs.
Line 105: "...while simultaneously monitoring currents in postsynaptic cells". This sentence is not correct given that the EPSCs have not been shown yet at this point of the manuscript.
We removed this part of the sentence.
Line 110: "SV and are not cause are cause by spontaneous action potentials...". The sentence does not make sense.
We corrected the sentence.
Line 168-9: "...we did not find significant differences in amplitude and kinetics...". According to Table 2 (2mM Ca2+ condition), both Imax and Q appear to be almost twice as high in iGluSnFR as in control (2.05 {plus minus} 0.06 and 1.34 {plus minus} 0.03, respectively; P=0.241). Is this not a significant difference?
The difference was not significant. The misunderstanding likely stems from the same problem in the presentation of the values as for the mEPSCs. We replaced the SEMs with the SEMs of the cell median to avert this.
Table 4. 2mM Ca2+ condition. The Rrefill parameter is about an order of magnitude smaller in the iGluSnFR-expressing group. Is this correct or just a typo?
Thank you for spotting this: it was an error with regards to unit conversion. The value for the control group was off by a factor of 10. We corrected this mistake.
Referees cross-commenting
I also agree with the comments of the other reviewers.
Significance
General assessment
This topic is currently of interest because iGluSnFR techniques are widely used. However, the study is preliminary. The scientific progress in terms of quantity and quality is limited. For example, Figs. 1 and 5 show only images and traces with little scientific significance.
Advance
The main advance of the study is the implementation of the deconvolution of the iGluSnFR signal and the comparison of the back extrapolation with the first stimulus (Fig. 6). This comparison was similar between electrophysiology and iGluSnFR when deconvolution of the iGluSnFR data was performed. These data therefore argue against saturation of iGluSnFR, as expected from a large number of previous analyses of iGluSnFR.
There is little methodological improvements compared with the group's previous study (Ozcete and Moser, 2021 EMBO J). In this earlier study, a different synapse was analyzed but the same iGluSnFR was injected into the scala tympani of the right ear through the round window in the same way as in this study. Surprisingly, the authors do not refer to Ozcete and Moser (2021) in the relevant methods section.
Thank you for spotting this omission. We now cite Özçete and Moser (2021) in the appropriate place in the methods section as well.
Reviewer #2
Summary
In the manuscript 'Optical measurement of glutamate release robustly reports short-term plasticity at a fast central synapse' the authors present a careful analysis of whether direct measurements of transmitter release using the genetically-encoded indicator iGluSnFR, are suitable for assessing changes in transmitter release at the spiral ganglion neuron end bulbs of Held in the mouse cochlear nucleus. What sets this study apart from other studies, which have demonstrated the utility of iGluSnFR measurements, is the use of a camera-based fluorescence readout as opposed to confocal or 2P microscopy methods and that it is performed in the cochlear nucleus.
The primary methodology is the comparison of electrophysiological measurements of excitatory postsynaptic currents from bushy cells with fluorescence changes in the end bulbs of iGluSnFR expressing auditory nerve fibers with and without stimulation of the auditory nerve fibers. The experiments are technically demanding and introducing genetically encoded indicators in neurons of the cochlea is no small accomplishment. An important observation is that mEPSCs are slightly modified (prolonged) due to expression of iGluSnFR in the presynaptic end bulbs. This is perhaps not surprising as iGluSnFR binds glutamate and may act as a buffer to reduce the peak and slightly prolong the increase in cleft glutamate concentration after release from synaptic vesicles. To my knowledge, others have not reported iGluSnFR effects on mEPSCs. Perhaps earlier studies have not checked as carefully, alternatively previous studies had a too-low fraction of presynaptic terminals expressing iGluSnFR (or less expression of iGluSnFR) to detect a change in EPSC parameters, or this is a synapse-specific phenomenon. However, the authors demonstrate that EPSCs evoked by electrical stimulation of the auditory nerve fibers are unaffected by expression of iGluSnFR in the presynaptic neurons. Further findings are that the determined decay time constant is substantially longer than at other synapses (~16 ms at hippocampal synapses, Dürst et al., 2018). Synaptic depression was robustly reported by iGluSnFR at this synapse, but determination of single quantal events and thus quantal analysis was not really possible at this synapse using iGluSnFR in conjunction with the imaging and analysis techniques presented. The manuscript is carefully written and presented.
We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.
Major points
1) The ROIs are selected to be 'outer bounds' of the glutamate spread from the synapses being studied. My concern is that these generously-sized ROIs include signal from many iGluSnFR molecules which are distal to the release sites and thus will be reached only slowly by low concentrations of glutamate or be contributing only noise and no changes in fluorescence. I suggest the temporal resolution could be improved by restricting the analysis of fluorescence changes to fewer pixels within the ROIs with the fastest rising/highest amplitude responses.
Thanks for this helpful comment: The data in our data set should be well-suited to perform this analysis in addition to the presented analysis and so we added this new analysis to the Revision Plan.
2) The observation that despite a 2 fold increase in eEPSCs when changing from 2 mM to 4 mM extracellular calcium there is no change in iGluSnFR peak is curious as pointed out by the authors but not really discussed.
We don’t currently have an obvious explanation but consider saturation of the iGluSnFR peak response likely to contribute. In response to the comment of the reviewer, we have added the analysis of integrated iGluSnFR data, which we previously found to be more robust toward saturation than the peak, to the revision plan. We plan to add the relevant discussion along with the new analysis.
Are the traces presented in Figure 5 examples from the same recording?
Traces in fig. 5 are grand averages (wording modified for clarity). Unfortunately, it was not possible to routinely measure iGluSnFR responses from the same cell in 2mM Ca2+ and 4 mM Ca2+ as the time needed for the protocols was rather long which influenced cell stability and imaging conditions would deteriorate during the exchange of the bath solution. We think it is not quite possible to directly compare the absolute iGluSnFR responses at different extracellular Ca2+ levels.
Assuming the examples are from one cell I first assumed the lack of change of peak was saturation of iGluSnFR but the larger fluorescence change with 100 Hz stimulation suggests otherwise. How many endbulbs are contacting one BC? Do you capture iGluSnFR responses from only one or several? In the previous point I suggested that restricting analysis to the soonest reacting pixels might improve temporal resolution but in the case of detecting the peaks with higher and normal calcium, these fastest reacting signals are probably also more likely to be saturated with glutamate.
The eEPSCs elicited by this stimulation paradigm are monosynaptic (see methods / electrophysiology section), but there might be other iGluSnFR expressing endbulbs on the same bushy cell. Since we reduce the current just enough such that any further reduction leads to a complete failure to elicit an EPSC, we believe these additional endbulbs are not releasing glutamate. We cannot, however, exclude the possibility that iGluSnFR on neighboring structures captures any potential spillover glutamate.
Minor points
- mEPSCs are usually recorded in tetrodotoxin, I didn't find any mention in methods/results
In this system, sEPSCs are not affected by TTX (Oleskevich and Walmsley, 2002) and thus usually recorded without adding TTX. We discuss this more explicitly and added a clarification to reflect this assumption (on line 111).
- the large numbers of abbreviations make it difficult in places to follow the manuscript please at least define them again in the figure legends (e.g. BC, AVCN in figure 1, Q, FWHM in figure 2 etc.)
We went over the manuscript again and removed some abbreviations or redefined them in captions.
- it is a bit unusual to report results of a Wilcoxon test and at the same time mean and SEM instead of medians, if different tests were used then it is important to indicate this where the p values are given or make the sentence in the methods more definitive
We agree that the initial presentation of the data was ambiguous. We changed the presentation to reflect this (see also answer to reviewer 1).
- the liquid junction potential is reported as 12 mV, pretty sure it should be -12 mV (unless the QX-314 or some other of the more exotic ingredients in the extracellular solution is having a dramatic effect on the LJP).
We follow the usual conventions of P. H. Barry, Methods in Enzymology, Vol. 171, p. 678, as described in E. Neher, Methods in Enzymology, Vol. 207, p. 123, in which the LJP is defined as the potential of the bath solution with respect to the pipette solution. We subtracted this positive potential (+12mV) in the end to obtain the membrane potential which therefore was more hyperpolarized than the nominal potential.
I wonder if one of the faster/lower affinity iGluSnFR variants would be better suited for studying this synapse.
We agree with the reviewer that future studies should explore the potential of faster/lower affinity iGluSnFR variants for studying the endbulb synapse. The reasons why we employed the original version include: i) sharing the same mice for studies of cochlear ribbon synapses (Özcete & Moser, 2021) and cochlear nucleus synapses (this MS) for the sake of reducing animal experiments, ii) good signal to background facilitating our first study establishing the recording in brainstem slice, iii) less signal to background and shorter signals with the new variants (as found in preliminary recordings from cochlear ribbon synapses) that would make the endbulb recordings more challenging. We have added the following statement to discussion. “Future imaging studies of glutamate release at calyceal synapses should explore the potential of new iGluSnFR variants with lower affinity that provide more rapid signal decay. This will ideally go along with imaging at higher framerate and might require stronger intensities of the excitation light to boost the fluorescence signal.” on line 430.
The paper would benefit from a careful reading to shorten the text and to check for clarity. For instance page 15 line 436 I don't understand how 'the results can reduce the likelihood of biologically relevant changes'. I think the authors meant something different
Thank you for spotting this. We reworded the sentence (now on line 399): "The data on hand suggests that this is not the case. Firstly, even if a larger sample size may uncover more subtle effects neurotransmission of evoked events, our measurements suggest a small effect size. Secondly, even as we did find changes in mEPSC, it is probable that the biological significance is limited"
- page 5 'width' is misspelled
Fixed.
- page 18 'strychnine' is misspelled
Fixed.
- on many of the figures is text that it much too small
We went through the manuscript and increased the text size in the figures, where appropriate.
__Referees cross-commenting __
I agree with all the comments of the other reviewers - both raise the point that there should be a 'control' AAV injected for comparison of the mEPSCs which I missed but is of course quite important. See https://pubmed.ncbi.nlm.nih.gov/24872574/ for a study of AAV serotype-dependent effects on presynaptic release.
We now added a section on other possible factors influencing the results, citing the study above.
Significance
The main audience for this paper will be fairly specialized. Researchers interested in properties of presynaptic release and some specialists in synaptic transmission in the auditory system will be the main readers/citers of this work.
The work is an important technical/methodological report. It highlights an important effect of expressing iGluSnFR and also demonstrates that the effect is overall not very problematic. Additional problems using iGluSnFR are also indicated.
I am an electrophysiologist, studying synaptic transmission and plasticity with experience using a wide range of optogenetic tools
Reviewer #3
__Summary __
In the present manuscript, the authors explore the information that can be obtained using optical measurement of glutamate release with iGluSnFR on synaptic dynamics in the endbulb of Held.
They virally express iGluSnFR in presynaptic terminals, patch the postsynaptic cells and combine high-frame-rate optical recordings with electrophysiological measurements. Their first finding is that mEPCSs are prolonged when presynaptic cells express the glutamate indicator, which they interpret as buffering of extracellular glutamate by the indicator. Next, they repeated the experiment, this time with stimulating evoked EPSCs. In contrast to the previously observed effects, iGluSnFR did not affect the time course or the amplitude of the evoked EPSCs. The authors then asked whether iGluSnFR signals can be used to study synaptic dynamics, specifically, synaptic depression. In these experiments, the authors observed a change in the paired-pulse ratio with ISI of 10ms, but not longer intervals. They analyzed presynaptic release and did not find statistically significant differences.
Can iGluSnFR signals be used for the analysis of synaptic release? When stimulated at a low frequency of 10Hz (allowing the fluorescence to return close to baseline levels in between pulses), iGluSnFR dynamics were somewhat comparable to postsynaptic signals. At higher frequencies, the slow time course of the indicator prevented the identification of individual responses and the resulting fluorescence had a very different shape. To resolve this problem, the authors used deconvolution analysis (fig 6). This analysis revealed a linear relationship between the optical readout and the patch-clamp data.
I find the manuscript to be clearly written, the findings are well presented and discussed and are novel and of substantial interest to neuroscientists in the field. I do have a number of questions about experiments and analysis that may have an effect on the conclusions of this work.
We thank the reviewer for her/his appreciation of our work and for the comments that have helped/will help us further improve our manuscript.
- In experiments comparing the effects of iGluSnFR expression on release dynamics (figure 1-4), the authors compare infected presynaptic cells to control (uninfected). The assumption is that synaptic buffering by iGluSnFR may affect glutamate diffusion in the synaptic cleft. However, it is possible that viral infection itself changes presynaptic properties. The authors should compare release from cells infected with GFP or a comparable indicator.
We agree that this is an important control experiment to be done in the future and that causal attribution is not in the scope of this study. A slowed decay would be consistent with the idea that iGluSnFR affects glutamatergic transmission by buffering glutamate, but we cannot rule out subtle changes due to the postnatal surgery or AAV-mediated transgene expression. In response to the reviewer’s comment, we modified the text to reflect the possibility of surgery and / or other parts of the expression system being responsible for the changes. We now also discuss further control experiments (line 408). Finally, we believe that our comparison is still relevant for researchers using iGluSnFR in the system, as they will be asking if introducing a measurement system affects the underlying quantity.
- Analysis of pool parameters presented in table 4 indicates almost doubling of RRP size with iGLuSnFR with 2 mM Ca++. While not significant, this result may indicate a real effect that may have been missed due to low power (N=3 and 7 for these experiments). I do not believe the authors did a power analysis in this study. How was the number of experiments determined? I would suggest increasing the number of experiments to avoid type II errors.
We thank the reviewer for this critical comment. Indeed, we would also have liked to have a greater statistical power for these experiments, but had to face the situation that the establishing the method required more animals than expected and the animal license did not offer further animals for the analysis. Moreover, we note that the obtained RRP size estimates were generally lower compared to previous estimates of our lab for the endbulb synapse (e.g. Butola et al., 2021: ~20 nA for 2 mM Ca2+ in Fig. 5). This can partially be attributed to the use of cyclothiazide in previous studies, which we avoided given reports of presynaptic effects of cyclothiazide. As the series resistances of the included recordings were below 8 MOhm (mean series resistances: 2mM Ca, injected: 5.58 MOhm; 2mM Ca, control: 5.93 MOhm; 4mM Ca, injected: 5.75 MOhm; 4mM Ca, control: 6.0 MOhm) and series resistance compensation was set to 80% we do not expect clamp-quality to contribute to the smaller estimates in the present data set.
We have now added a statement noting the preliminary nature of these results and indicated that further experiments will be required to more certainly conclude on potential effects of iGluSnFR or the manipulation on endbulb transmission: “Our preliminary train stimulation analysis of vesicle pool dynamics in the presence and absence of AAV-mediated iGluSnFR expression in SGNs has not revealed significant differences between the two conditions. Further experiments, potentially involving faster versions of iGluSnFR and employing trains of different stimulation rates for model based analysis of vesicle pool dynamics (Neher and Taschenberger, 2021) will help to assess the value and impact of iGluSnFR in the analysis of transmission at calyceal synapses.” on line 381.
- The deconvolution analysis assumes an instantaneous rise time. Yet previous work (Armbruster et al., 2020) that took into account diffusion, suggested potentially slower rise time dynamics. More importantly, the deconvolved waveforms do not match the shapes of the EPSCs (figures 5 and supp 6-2).What is the aim of the deconvolution? It was not clear from the text, but I assume it shows iGluSnFR binding to glutamate - in which case the slow waveforms are indicative of extrasynaptic iGluSnFR activation.
The deconvolution analysis was mainly used to recover the average responses to stimuli in the train without contamination by previous responses (see also Taschenberger et al. 2016, their figure 6).
We did also try to use the average singular response instead of the exponential fit as a kernel for the (Wiener) deconvolution analysis, which more closely resembled the observed (fast) rise. Unfortunately, this led to markedly worse results, likely because of the noise levels in the measurements. We believe that it would be beneficial to model the rise of the signal more precisely if glutamate imaging data is acquired at higher framerates.
The broad wave forms may be due to extrasynaptic binding of glutamate, but we also note that each frame corresponds to ~10ms and there is only ~10 data points between stimuli, so the responses are unlikely to be as sharp as eEPSCs.
However, I suppose that the more interesting question is whether iGluSnFR could be deconvolved to reveal the underlying release events, similar to how calcium signals can be used to inform about single action potentials.
We agree that it would be particularly interesting to use a "mini iGluSnFR" signal to deconvolve the resulting traces. Unfortunately, we failed to detect iGluSnFR signals reporting individual release events at this time, preventing this kind of analysis.
- I suggest referencing and discussing (Aggarwal et al., 2022; Srivastava et al., 2022) . These highly relevant papers analyzed iGluSnFR to probe synaptic release.
References:
Aggarwal, A., Liu, R., Chen, Y., Ralowicz, A. J., Bergerson, S. J., Tomaska, F., Hanson, T. L., Hasseman, J. P., Reep, D., Tsegaye, G., Yao, P., Ji, X., Kloos, M., Walpita, D., Patel, R., Mohr, M. A., Tilberg, P. W., Mohar, B., Team, T. G. P., . . . Podgorski, K. (2022). Glutamate indicators with improved activation kinetics and localization for imaging synaptic transmission. bioRxiv, 2022.2002.2013.480251. https://doi.org/10.1101/2022.02.13.480251
Armbruster, M., Dulla, C. G., & Diamond, J. S. (2020). Effects of fluorescent glutamate indicators on neurotransmitter diffusion and uptake. Elife, 9. https://doi.org/10.7554/eLife.54441
Srivastava, P., de Rosenroll, G., Matsumoto, A., Michaels, T., Turple, Z., Jain, V., Sethuramanujam, S., Murphy-Baum, B. L., Yonehara, K., & Awatramani, G. B. (2022). Spatiotemporal properties of glutamate input support direction selectivity in the dendrites of retinal starburst amacrine cells. Elife, 11. https://doi.org/10.7554/eLife.81533
We thank the reviewer for the suggestions. Some of these studies were not available when we first drafted the manuscript. We now added a section discussing these studies starting on line 466:
Optimizing the imaging technique may reduce noise level, while the development of improved GEGIs could improve the signal to a level, at which spontaneous release events can be identified reliably in the cochlear nucleus. In retinal slices, where quantal events have been reliably observed with two-photon imaging, temporal deconvolution was successfully employed to estimate release rates from iGluSnFR signal (Srivastava et al., 2022; James et al., 2019). Subcellular targeting of iGluSnFR variants to the postsynaptic membrane may reduce measurement errors introduced by contributing extrasynaptic iGluSnFR signal and improve spatial resolution of glutamate imaging data(Hao et al., 2023; Aggarwal et al., 2022).
Referees cross-commenting
I also agree with the comments made by other reviewers!
Significance
Overall, this study addresses an important problem in basic neuroscience research. With the developing reliance on optical measurement of neuronal function, it is important to understand the impact of the indicators on physiological function and the limitations of the technique. The study is well-executed and will be informative to neuroscientists performing optical glutamate recording to study single-cell and circuit function in and beyond the auditory system.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #3
Evidence, reproducibility and clarity
In the present manuscript, the authors explore the information that can be obtained using optical measurement of glutamate release with iGluSnFR on synaptic dynamics in the endbulb of Held.
They virally express iGluSnFR in presynaptic terminals, patch the postsynaptic cells and combine high-frame-rate optical recordings with electrophysiological measurements. Their first finding is that mEPCSs are prolonged when presynaptic cells express the glutamate indicator, which they interpret as buffering of extracellular glutamate by the indicator. Next, they repeated the experiment, this time with stimulating evoked EPSCs. In contrast to the previously observed effects, iGluSnFR did not affect the time course or the amplitude of the evoked EPSCs. The authors then asked whether iGluSnFR signals can be used to study synaptic dynamics, specifically, synaptic depression. In these experiments, the authors observed a change in the paired-pulse ratio with ISI of 10ms, but not longer intervals. They analyzed presynaptic release and did not find statistically significant differences. Can iGluSnFR signals be used for the analysis of synaptic release? When stimulated at a low frequency of 10Hz (allowing the fluorescence to return close to baseline levels in between pulses), iGluSnFR dynamics were somewhat comparable to postsynaptic signals. At higher frequencies, the slow time course of the indicator prevented the identification of individual responses and the resulting fluorescence had a very different shape. To resolve this problem, the authors used deconvolution analysis (fig 6). This analysis revealed a linear relationship between the optical readout and the patch-clamp data.
I find the manuscript to be clearly written, the findings are well presented and discussed and are novel and of substantial interest to neuroscientists in the field. I do have a number of questions about experiments and analysis that may have an effect on the conclusions of this work.
- In experiments comparing the effects of iGluSnFR expression on release dynamics (figure 1-4), the authors compare infected presynaptic cells to control (uninfected). The assumption is that synaptic buffering by iGluSnFR may affect glutamate diffusion in the synaptic cleft. However, it is possible that viral infection itself changes presynaptic properties. The authors should compare release from cells infected with GFP or a comparable indicator.
- Analysis of pool parameters presented in table 4 indicates almost doubling of RRP size with iGLuSnFR with 2 mM Ca++. While not significant, this result may indicate a real effect that may have been missed due to low power (N=3 and 7 for these experiments). I do not believe the authors did a power analysis in this study. How was the number of experiments determined? I would suggest increasing the number of experiments to avoid type II errors.
- The deconvolution analysis assumes an instantaneous rise time. Yet previous work (Armbruster et al., 2020) that took into account diffusion, suggested potentially slower rise time dynamics. More importantly, the deconvolved waveforms do not match the shapes of the EPSCs (figures 5 and supp 6-2).What is the aim of the deconvolution? It was not clear from the text, but I assume it shows iGluSnFR binding to glutamate - in which case the slow waveforms are indicative of extrasynaptic iGluSnFR activation. However, I suppose that the more interesting question is whether iGluSnFR could be deconvolved to reveal the underlying release events, similar to how calcium signals can be used to inform about single action potentials.
- I suggest referencing and discussing (Aggarwal et al., 2022; Srivastava et al., 2022) . These highly relevant papers analyzed iGluSnFR to probe synaptic release.
References:
Aggarwal, A., Liu, R., Chen, Y., Ralowicz, A. J., Bergerson, S. J., Tomaska, F., Hanson, T. L., Hasseman, J. P., Reep, D., Tsegaye, G., Yao, P., Ji, X., Kloos, M., Walpita, D., Patel, R., Mohr, M. A., Tilberg, P. W., Mohar, B., Team, T. G. P., . . . Podgorski, K. (2022). Glutamate indicators with improved activation kinetics and localization for imaging synaptic transmission. bioRxiv, 2022.2002.2013.480251. https://doi.org/10.1101/2022.02.13.480251
Armbruster, M., Dulla, C. G., & Diamond, J. S. (2020). Effects of fluorescent glutamate indicators on neurotransmitter diffusion and uptake. Elife, 9. https://doi.org/10.7554/eLife.54441
Srivastava, P., de Rosenroll, G., Matsumoto, A., Michaels, T., Turple, Z., Jain, V., Sethuramanujam, S., Murphy-Baum, B. L., Yonehara, K., & Awatramani, G. B. (2022). Spatiotemporal properties of glutamate input support direction selectivity in the dendrites of retinal starburst amacrine cells. Elife, 11. https://doi.org/10.7554/eLife.81533
Referees cross-commenting
I also agree with the comments made by other reviewers!
Significance
Overall, this study addresses an important problem in basic neuroscience research. With the developing reliance on optical measurement of neuronal function, it is important to understand the impact of the indicators on physiological function and the limitations of the technique. The study is well-executed and will be informative to neuroscientists performing optical glutamate recording to study single-cell and circuit function in and beyond the auditory system.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
In the manuscript 'Optical measurement of glutamate release robustly reports short-term plasticity at a fast central synapse' the authors present a careful analysis of whether direct measurements of transmitter release using the genetically-encoded indicator iGluSnFR, are suitable for assessing changes in transmitter release at the spiral ganglion neuron end bulbs of Held in the mouse cochlear nucleus. What sets this study apart from other studies, which have demonstrated the utility of iGluSnFR measurements, is the use of a camera-based fluorescence readout as opposed to confocal or 2P microscopy methods and that it is performed in the cochlear nucleus.
The primary methodology is the comparison of electrophysiological measurements of excitatory postsynaptic currents from bushy cells with fluorescence changes in the end bulbs of iGluSnFR expressing auditory nerve fibers with and without stimulation of the auditory nerve fibers. The experiments are technically demanding and introducing genetically encoded indicators in neurons of the cochlea is no small accomplishment. An important observation is that mEPSCs are slightly modified (prolonged) due to expression of iGluSnFR in the presynaptic end bulbs. This is perhaps not surprising as iGluSnFR binds glutamate and may act as a buffer to reduce the peak and slightly prolong the increase in cleft glutamate concentration after release from synaptic vesicles. To my knowledge, others have not reported iGluSnFR effects on mEPSCs. Perhaps earlier studies have not checked as carefully, alternatively previous studies had a too-low fraction of presynaptic terminals expressing iGluSnFR (or less expression of iGluSnFR) to detect a change in EPSC parameters, or this is a synapse-specific phenomenon. However, the authors demonstrate that EPSCs evoked by electrical stimulation of the auditory nerve fibers are unaffected by expression of iGluSnFR in the presynaptic neurons. Further findings are that the determined decay time constant is substantially longer than at other synapses (~16 ms at hippocampal synapses, Dürst et al., 2018). Synaptic depression was robustly reported by iGluSnFR at this synapse, but determination of single quantal events and thus quantal analysis was not really possible at this synapse using iGluSnFR in conjunction with the imaging and analysis techniques presented. The manuscript is carefully written and presented.
Major points:
- The ROIs are selected to be 'outer bounds' of the glutamate spread from the synapses being studied. My concern is that these generously-sized ROIs include signal from many iGluSnFR molecules which are distal to the release sites and thus will be reached only slowly by low concentrations of glutamate or be contributing only noise and no changes in fluorescence. I suggest the temporal resolution could be improved by restricting the analysis of fluorescence changes to fewer pixels within the ROIs with the fastest rising/highest amplitude responses.
- The observation that despite a 2 fold increase in eEPSCs when changing from 2 mM to 4 mM extracellular calcium there is no change in iGluSnFR peak is curious as pointed out by the authors but not really discussed. Are the traces presented in Figure 5 examples from the same recording? Assuming the examples are from one cell I first assumed the lack of change of peak was saturation of iGluSnFR but the larger fluorescence change with 100 Hz stimulation suggests otherwise. How many endbulbs are contacting one BC? Do you capture iGluSnFR responses from only one or several? In the previous point I suggested that restricting analysis to the soonest reacting pixels might improve temporal resolution but in the case of detecting the peaks with higher and normal calcium, these fastest reacting signals are probably also more likely to be saturated with glutamate.
Minor points:
- mEPSCs are usually recorded in tetrodotoxin, I didn't find any mention in methods/results
- the large numbers of abbreviations make it difficult in places to follow the manuscript please at least define them again in the figure legends (e.g. BC, AVCN in figure 1, Q, FWHM in figure 2 etc.)
- it is a bit unusual to report results of a Wilcoxon test and at the same time mean and SEM instead of medians, if different tests were used then it is important to indicate this where the p values are given or make the sentence in the methods more definitive
- the liquid junction potential is reported as 12 mV, pretty sure it should be -12 mV (unless the QX-314 or some other of the more exotic ingredients in the extracellular solution is having a dramatic effect on the LJP). I wonder if one of the faster/lower affinity iGluSnFR variants would be better suited for studying this synapse. The paper would benefit from a careful reading to shorten the text and to check for clarity. For instance page 15 line 436 I don't understand how 'the results can reduce the likelihood of biologically relevant changes'. I think the authors meant something different
- page 5 'width' is misspelled
- page 18 'strychnine' is misspelled
- on many of the figures is text that it much too small
Referees cross-commenting
I agree with all the comments of the other reviewers - both raise the point that there should be a 'control' AAV injected for comparison of the mEPSCs which I missed but is of course quite important. See https://pubmed.ncbi.nlm.nih.gov/24872574/ for a study of AAV serotype-dependent effects on presynaptic release.
Significance
The main audience for this paper will be fairly specialized. Researchers interested in properties of presynaptic release and some specialists in synaptic transmission in the auditory system will be the main readers/citers of this work.
The work is an important technical/methodological report. It highlights an important effect of expressing iGluSnFR and also demonstrates that the effect is overall not very problematic. Additional problems using iGluSnFR are also indicated.
I am an electrophysiologist, studying synaptic transmission and plasticity with experience using a wide range of optogenetic tools
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
Summary
The authors used a novel imaging technique to monitor glutamate release and correlated these measurements with gold standard electrophysiological measurements. The genetically encoded glutamate reporter, iGluSnFR, was expressed in mouse spiral ganglion neurons using the approach described in Ozcete and Moser (2021, EMBO J). The iGluSnFR signals and the postsynaptic currents were measured at the endbulb of Held synapse. A small effect of the expression of iGluSnFR on the mEPSC kinetics was found (but see comment 1). Furthermore, deconvolution of the iGluSnFR signals was performed enabling the comparison of some presynaptic properties assessed with either iGluSnFR or electrophysiology.
Major comments
- The central finding of the study is the prolonged decay time constant of the mEPSC. The difference is small but astonishingly significant (0.172 {plus minus} 0.002 and 0.158 {plus minus} 0.001, P=0.003). The SEM is about 100 times smaller than the measured time constant. This is biologically not plausible. Therefore, I am skeptical about the statistical significance of the results.
- Analysis of the size of RRP with electrophysiology and iGluSnFR is potentially interesting but iGluSnFR recordings could not resolve the spontaneous fusion of single vesicles. Therefore, it is not possible to estimate RRP with these iGluSnFR recordings. This limitation of the approach should be emphasised more clearly.
- The control conditions (no surgery/no virus injection) are not the correct conditions for comparison with the experimental conditions (surgery/virus injection and sensor expression). The control group should be operated and injected with saline or ideally with a virus expressing GFP at the extracellular membrane. The authors addressed this issue by citing their previous work (Özcete and Moser, 2021). However, I am not convinced that surgery does not induce subtle changes that could explain the small differences in mEPSCs.
Minor comments
The supplementary figures are not listed in the order in which they appear in the main text.
Figure 2B and 3 are not referenced in the main text.
The PPR in Figure 3 shows a PPR that cannot be evaluated because of the unusual plot with lines that are too thick.
Line 105: "...while simultaneously monitoring currents in postsynaptic cells". This sentence is not correct given that the EPSCs have not been shown yet at this point of the manuscript.
Line 110: "SV and are not cause are cause by spontaneous action potentials...". The sentence does not make sense.
Line 168-9: "...we did not find significant differences in amplitude and kinetics...". According to Table 2 (2mM Ca2+ condition), both Imax and Q appear to be almost twice as high in iGluSnFR as in control (2.05 {plus minus} 0.06 and 1.34 {plus minus} 0.03, respectively; P=0.241). Is this not a significant difference?
Table 4. 2mM Ca2+ condition. The Rrefill parameter is about an order of magnitude smaller in the iGluSnFR-expressing group. Is this correct or just a typo?
Referees cross-commenting
I also agree with the comments of the other reviewers.
Significance
General assessment This topic is currently of interest because iGluSnFR techniques are widely used. However, the study is preliminary. The scientific progress in terms of quantity and quality is limited. For example, Figs. 1 and 5 show only images and traces with little scientific significance.
Advance The main advance of the study is the implementation of the deconvolution of the iGluSnFR signal and the comparison of the back extrapolation with the first stimulus (Fig. 6). This comparison was similar between electrophysiology and iGluSnFR when deconvolution of the iGluSnFR data was performed. These data therefore argue against saturation of iGluSnFR, as expected from a large number of previous analyses of iGluSnFR.
There is little methodological improvements compared with the group's previous study (Ozcete and Moser, 2021 EMBO J). In this earlier study, a different synapse was analyzed but the same iGluSnFR was injected into the scala tympani of the right ear through the round window in the same way as in this study. Surprisingly, the authors do not refer to Ozcete and Moser (2021) in the relevant methods section.
Audience „basic research"
My field of expertise imaging and electrophysiology; basic research
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- Apr 2023
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
Manuscript number: RC-2022-01586
Corresponding author(s): Hammond, Gerald
1. General Statements
Our manuscript details a novel homeostatic feedback loop for the master plasma membrane regulatory molecule, PI(4,5)P2. In this loop, the PIP4K family of PI(4,5)P2-synthesizing enzymes act in a novel, non-enzymatic capacity: they sense PI(4,5)P2 levels and directly inhibit the lipid’s synthesis by inhibiting the major enzyme involved in the terminal step of synthesis, PIP5K. The three reviewers seem largely convinced of our data, and provided detailed, insightful and plausible suggestions for revision, which we have now comprehensively provided. This includes substantial new experimental work, including the generation of genomically tagged cell lines to localize all endogenous PIP4K isoforms.
However, all three reviewers questioned the paper’s novelty and significance based on recent studies in the literature demonstrating PIP5K inhibition by PIP4Ks [refs 25 & 53 in the manuscript]. We feel that this is an inaccurate and somewhat unfair assessment of our findings, since it does not consider our central (and completely unprecedented) finding that PIP4Ks directly sense PI(4,5)P2 levels through low-affinity binding. As well as being a novel finding, this places the previously observed inhibition of PIP5K by PIP4Ks into a completely new paradigm consisting of a complete, enclosed homeostatic feedback loop. This was not demonstrated previously in the literature.
Of course, the reviewers’ convergent opinions almost certainly reflect a deficit in our articulation of the novel findings in the original manuscript. We have therefore revised the current version to more clearly emphasize our novel findings.
2. Point-by-point description of the revisions
Reviewer #1
__Summary: __In this manuscript, authors address how PIP4K regulates tonic plasma membrane (PM) PI(4,5)P2 levels which are generated by major PI(4,5)P2 synthesis enzyme, PIP5K by using PIP4K and PIP5K overexpressing cells or acutely manipulating PM PI(4,5)P2 levels by the chemically induced dimerization (CID) system. Additionally, authors assessed effect of direct interaction between PIP4K and PIP5K by using supported lipid bilayers (SLBs) and purified PIP4K and 5K. Authors also were successful in monitoring dynamics of endogenous PIP4K by using a split fluorescent protein approach. Through this study, authors propose a model of PI(4,5)P2 homeostatic mechanism that PIP4Ks sense elevated PM PI(4,5)P2 by PIP5Ks, are recruited to the PM, and bind to PIP5Ks to inhibit PIP5Ks activity.
# 1.1: Although authors mention methods of statistical analysis in materials and methods, they did not present the results of statistical analysis in the figures. The quantitative data should be presented with statistical analysis data, which is important for showing where convincing differences between treatment groups are found.
We agree that statistics are important to fully interpret the data; we have now included the results of statistical tests (non-parametric statistics were used, as the data are not normally distributed) with correction for multiple comparisons. Significant changes are denoted using asterisk notation in figs. 1A-C, 2B, 5B & 7A. The full results are now reported as tables:
Fig 1A = table 1; Fig 1B = table 2; Fig. 1C = table 3; Fig. 2B = table 4; Fig. 5B = table 5; Fig 7A = tables 6 & 7.
__#1.2a: __Fig. 1D. Fig. 1D and Fig. 3A should be presented together because these are exactly same set of cells and information of each PIP4K and PIP5K membrane localization could be important for understanding mechanisms of inhibitory effect of PIP4Ks.
We struggled when writing the manuscript to reconcile these data into a single figure. The manuscript flows from showing inhibition of PIP5Ks by PIP4Ks in living cells (figs. 1 & 2), then showing low affinity PI(4,5)P2 binding by endogenous PIP4Ks (figs. 3-6) and finally to a direct interaction between PIP4K and PIP5K (fig. 7). We therefore felt that reconciling the data showing attenuated PI(4,5)P2 synthesis with the interaction between PIP4Ks and PIP5Ks, despite being demonstrated in the same experiments, would disrupt the flow of the paper. We therefore request to leave the data in Figs. 2B and 7A, whilst remaining explicit that the data derive from a single experiment.
#1.2b: Authors claimed that over-expression of all three PIP4K isoforms were able to attenuate the elevated PM PI(4,5)P2 levels caused by PIP5K over-expression. However, in Fig. 3A, PIP4K2A was recruited to PM by both PIP5K1A and PIP5K1C but looks only attenuated PIP5K1A, but not PIP5K1C, overexpression mediated PM PI(4,5)P2 elevation (Fig. 1D). PIP4K2C was less recruited to the PM than PIP4K2A and 2B in PIP5K1A overexpressing cell (Fig. 3A) but PIP4K2A, B and C isoforms equally attenuated increase of PM PI(4,5)P2 in PIP5K1A overexpressing cell (Fig. 1D). It is likely that efficiency of inhibitory effect of each PIP4K isoform is different by co-overexpressed PIP5K isoform. These images should be more carefully documented with Fig. 1D and Fig. 3A together.
As the reviewer suggests, we have now expanded our description of these data in both results and discussion; firstly, for the attenuating effects on PI(4,5)P2 synthesis, we write on the 3rd paragraph of p4: “We also reasoned that co-expression of PIP4K paralogs with PIP5K might attenuate the elevated PI(4,5)P2 levels induced by the latter. Broadly speaking, this was true, but with some curious paralog selectivity (fig. 2B, statistics reported in table 4): PIP4K2A and PIP4K2B both attenuated PI(4,5)P2 elevated by PIP5K1A and B, but not (or much less so) PIP5K1C; PIP4K2C, on the other hand, attenuated PIP5K1A and was the only paralog to significantly attenuate PIP5K1C’s effect, yet it did not attenuate PIP5K1B at all.”
On the relative ability of PIP5Ks to localize PIP4Ks we focus on the key result, writing on the 2nd paragraph of p7: “When co-expressing EGFP-tagged PIP5Ks and TagBFP2-tagged PIP4K2s, we found that PIP5K paralogs’ PM binding is largely unaffected by PIP4K over-expression (fig. 7A, upper panel and table 6), whereas all three paralogs of PIP4K are strongly recruited to the PM by co-expression of any PIP5K (fig. 7A, lower panel and table 7)…”
And finally, we describe a more nuanced discussion of the possible implications for differential inhibition of PIP5K isoforms by PIP4Ks in the discussion, starting in the first paragraph on p. 11: “Despite minor differences in the ability of over-expressed PIP5K paralogs to recruit over-expressed PIP4K enzymes (fig. 7A), we observed major differences in the ability of PIP4K paralogs to inhibit PI(4,5)P2 synthesis when over-expressed alone (fig. 1C) or in combination with PIP5K (fig. 2B). It is unclear what drives the partially overlapping inhibitory activity, where each PIP5K paralog can be attenuated by 2 or 3 PIP4Ks. This is however reminiscent of the biology of the PIPKs, where there is a high degree of redundancy among them, with few unique physiological functions assigned to specific paralogs [49]. There may be hints of paralog-specific functions in our data; for example, enhanced PI(4,5)P2 induced by over-expressed PIP5K1C is only really attenuated by PIP4K2C (fig. 2B). This could imply a requirement for PIP4K2C in regulating PI(4,5)P2 levels during PLC-mediated signaling, given the unique requirements for PIP5K1C in this process [50,51]. Regardless, a full understanding of paralog selectivity will need to be driven by a detailed structural analysis of the interaction between PIP4Ks and PIP5Ks - which is not immediately apparent from their known crystal structures, especially since PIP4Ks and PIP5Ks employ separate and distinct dimerization interfaces [49].”
#1.3: Fig. 1F. It seems that PIP4K2A accelerated PIP5K, but not Mss4, dependent PI(4,5)P2 generation before PI(4,5)P2 reaches 28,000 lipids/um2. Is this significant? If so, why did this happen?
We have answered this question with a sentence added to the 1st paragraph on p 8: *“The ability of PIP4K to bind to PIP5K on a PI(4,5)P2-containing bilayer also potentially explains the slightly accelerated initial rate of PI(4,5)P2synthesis exhibited by PIP5K1A that we reported in fig. 2C, since PIP4K may initially introduce some avidity to the membrane interaction by PIP5K, before PI(4,5)P2 reaches a sufficient concentration that PIP4K-mediated inhibition is effective.” *
#1.4: Fig. 3B. In this figure, authors only presented images after Rapa treatment. Therefore, it is not clear what these results mean. Before Rapa treatment, where did bait proteins and NG2-PIP4K2C localize? If ePIP4K2C delta PM intensity (ER:PM/PM) increase, does that mean increase in ER:PM intensity or decrease in PM intensity? According to Figure legend, PI(4,5)P2 indicator TubbycR332H was co-transfected, but those images are not shown in the figure. Images of PI(4,5)P2 indicator also should be presented to show whether after Rapa treatment PI(4,5)P2 increased at ER-PM contact sites, because that could be critical for the conclusion that "The use of Mss4 ruled out an effect of enhanced PI(4,5)P2 generation at contact sites, since this enzyme increases PI(4,5)P2 as potently as PIP5K1A (Fig. 1A), yet does not cause recruitment of PIP4K2C". Is this conclusion consistent with Fig. 2F and G?
These data now appear in Fig. 7B. We have added images showing the pre-rapamycin state to the revised figure. The reference to tubbycR332H co-expression was an error. In fact, the cells expressed the ER:PM contact site marker MAPPER, which allowed us to quantify ER:PM contact site localization before and after rapamycin induced capture of the baits at these sites. The revised figure appears as follows:
The failure of Mss4 to recruit endogenous PIP4K2C is entirely consistent with the old Fig. 2F and G (now 5A and C), since these show PIP4K interaction with PI(4,5)P2 containing lipid bilayers (in Fig. 5C, the PI(4,5)P2 was synthesized by Mss4). We demonstrated that Mss4 is unable to interact with PIP4K2A in Fig. 7D.
#1.5: Fig. 3C and D. Based on results of Fig. 3C and D, authors concluded that "PIP4K2C binding to PI(4,5)P2-containing SLBs was greatly enhanced by addition of PIP5K to the membranes, but not Mss4". I don't think Fig. 3C and D are comparable because experimental conditions are different. While lipid composition of SLB used in Fig. 3C was 2% PI(4,5)P2, 98% DOPC, in Fig. 3D, it was 4% PI(4,5)P2, 96% DOPC. And also, in Fig. 3C, PIP5K1A was added to SLB at the time about 50 sec, whereas in Fig. 3D, Mss4 was added at 600 sec. It seems that in Fig. 3D, PIP4K2A was already saturated on SLB before adding Mss4. These two experiments must be performed under the same conditions.
We have repeated these experiments (which now appear in Fig. 7C & D) under identical conditions, with the same result.
#1.6: Overall results discussed in the text are very compressed referring readers to the 4 multi-panel complex figures with elaborate figure legends. While it is possible to figure out what the authors' studies and results are, it is quite a laborious process.
We have revised the manuscript to be less compressed and easier to read, with the data now organized as eight figures and the results section split into four sub-sections.
Minor comments:
#1.7: Fig. 2D. The purified 5-phosphatase used in Fig. 2D is INPP5E but described in figure legend and materials and methods ass OCRL. Which one is correct?
Purified OCRL was indeed used in the supported lipid bilayer experiments. The figure (now Fig. 4A) and legend have been corrected – thank you for spotting the error.
#1.8: Fig. 3B. Indicate which trace represents PIP5K1A, Lyn11 or Mss4.
The data now appears in Fig. 7B, with the traces separated into separate graphs for greater clarity (see response to #1.4).
#1.9: Fig. 4C. X-axis label. Is "Time (min)" correct? Or should it be "Time (sec)".
Thank you for spotting this typo. It should have indeed been seconds, and this is corrected in the new fig. 8C.
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Reviewer #1 (Significance (Required)): The finding that PIP4K itself is a low-affinity PI(4,5)P2 binding protein and sense increases of PM PI(4,5)P2 generated by PIP5K to control tonic PI(4,5)P2 levels by inhibiting PIP5K activity is a novel concept. However, inhibition of PIP5K by PIP4K and importance of the inhibitory effect of PIP4K in PI3K signaling pathway have previously been reported (ref 24). This reduces the novelty of the current work somewhat however, the authors do provide evidence for dual interactions of PIP4K (PIP2, PIP5K), which the previous report did not.
We appreciate the reviewer’s insightful comments and overall appreciation of our work. We agree that previous studies did not detect the dual interaction of PIP4Ks with PIP5Ks and PI(4,5)P2; as we argue strongly in the general comments, we think this actually fits as a complete, enclosed homeostatic feedback loop – which is a significant and novel finding.
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Reviewer #2
Summary: This paper proposes that the enzyme PIP4K2C is a negative regulator of the synthesis of PI(4,5)P2 and that it does so by dampening the activity of PIP5K which is the enzymatic activity responsible for producing the major pool of PI(4,5)P2 in cells.
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Reviewer #2 (Significance (Required)): Although the findings of the paper are presented as a major new advance, the observation that PIP4K might acts as a negative regulator of PIP2 synthesis has been previously presented in two previous publications. The significance of this paper is that it also shows the same point in another model system.
PIP4Ks Suppress Insulin Signaling through a Catalytic-Independent Mechanism
Diana G Wang 1, Marcia N Paddock 2, Mark R Lundquist 3, Janet Y Sun 3, Oksana Mashadova 3, Solomon Amadiume 3, Timothy W Bumpus 4, Cindy Hodakoski 3, Benjamin D Hopkins 3, Matthew Fine 3, Amanda Hill 3, T Jonathan Yang 5, Jeremy M Baskin 4, Lukas E Dow 6, Lewis C Cantley 7
PMID: 31091439; PMCID: PMC6619495;DOI: 10.1016/j.celrep.2019.04.070
and
Phosphatidylinositol 5 Phosphate 4-Kinase Regulates Plasma-Membrane PIP3 Turnover and Insulin Signaling.
Sharma S, Mathre S, Ramya V, Shinde D, Raghu P.Cell Rep. 2019 May 14;27(7):1979-1990.e7. doi: 10.1016/j.celrep.2019.04.084.PMID: 31091438
Both of these studies show that in cells lacking PIP4K, during signalling the levels of PIP2 rise much greater than in wild type cells. Indeed the Cantley lab paper (Wang et.al) have shown that this is likely due to an increase in PIP5K activity, using an in vitro assay. They have further disrupted the interaction between PIP4K and PIP5K and demonstrated the importance of this interaction in the enhanced levels of PIP2.
Respectfully, we disagree with this assessment, because we believe it doesn’t consider the novel, central findings we report: that PIP4Ks sense PI(4,5)P2 levels through direct interaction with the lipid, and that this is what facilitates PIP5K inhibition. These findings were not reported in the prior studies. Nonetheless, the studies are foundational for ours and were cited in our original manuscript (and are still, as refs 25 and 53).
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#2.1: Likewise although the authors have claimed that no mechanisms have claimed that there are no mechanisms reported to sense and downregulate PIP2 resynthesis. It is suggested that they read and consider the following recent paper which studies Pip2 resynthesis during GPCR triggered PLC signalling.
Kumari A, Ghosh A, Kolay S and Raghu P*. Septins tune lipid kinase activity and PI(4,5)P 2 turnover during G-protein-coupled PLC signalling in vivo. Life Sci Alliance. 2022 Mar 11;5(6):e202101293. doi: 10.26508/lsa.202101293. Print 2022 Jun.
We have now included a full discussion of this paper in the discussion starting on the last paragraph of p 9: “Since this paper was initially submitted for publication, another study has reported a similar homeostatic feedback loop in Drosophila photoreceptors, utilizing the fly homologue of septin 7 as the receptor and control center [38]. This conclusion is based on the observation that cells with reduced septin 7 levels have enhanced PIP5K activity in lysates, and exhibit more rapid PI(4,5)P2 resynthesis after PLC activation. However, changes in septin 7 membrane localization in response to acute alterations in PI(4,5)P2 levels, as well as direct interactions between PIP5K and septin 7, have yet to be demonstrated. Nevertheless, septin 7 has distinct properties as a potential homeostatic mediator; as a foundational member of the septin family, it is essential for generating all major types of septin filament [39]. Therefore, a null allele for this subunit is expected to reduce the prevalence of the septin cytoskeleton by half. Given that septin subunits are found in mammalian cells at high copy number, around ~106 each [29], and the fact that septins bind PI4P and PI(4,5)P2 [40,41], it is likely that septin filaments sequester a significant fraction of the PM PI4P and PI(4,5)P2 through high-avidity interactions. In addition, membrane-bound septins appear to be effective diffusion barriers to PI(4,5)P2 and other lipids [42]. We therefore speculate that septins may play a unique role in systems such as the fly photoreceptor with extremely high levels of PLC-mediated PI(4,5)P2 turnover: The septin cytoskeleton can act as a significant buffer for PI4P and PI(4,5)P2 in such systems, as well as corralling pools of the lipids for use at the rhabdomeres were the high rate of turnover occurs. This is in contrast to the role played by the PIP4Ks, where PI(4,5)P2 levels are held in a narrow range under conditions of more limited turnover, as found in most cells.”
__#2.2: __Likewise there are other earlier papers in the literature which have studied possible PIP2 binding proteins as sensors for this lipid.
We are only aware of a single, specific example of a similar negative feedback, which is discussed in the 3rdparagraph of p 10: “Curiously, although phosphatidylinositol phosphate kinases are found throughout eukarya, PIP4Ks are limited to holozoa (animals and closely related unicellular organisms) [47]. Indeed, we found the PIP5K from the fission yeast, Saccharomyces cerevisiae, does not interact with human PIP4Ks (fig. 7) and cannot modulate PI(4,5)P2 levels in human cells without its catalytic activity (fig. 1). This begs the question: how do S. cerevisiae regulate their own PI(4,5)P2 levels? Intriguingly, they seem to have a paralogous homeostatic mechanism: the dual PH domain containing protein Opy1 serves as receptor and control center [48], in an analogous role to PIP4K. Since there is no mammalian homolog of Opy1, this homeostatic mechanism appears to have appeared at least twice through convergent evolution. Combined with hints of a role for septins in maintaining PI(4,5)P2 levels [38], the possibility arises that there may yet be more feedback controls of PI(4,5)P2 levels to be discovered.”
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Technical standards: The work is done to a high technical standard.
#2.3: Does catalytically dead isoform of PIP4K2B and 2C also yield the same result as a catalytically dead version of PIP4K2A in Fig 1B?
In a word: yes. We have added these experiments, which are now presented in Fig. 2A:
The results are described in the results in the 2nd paragraph of p. 4: “To directly test for negative regulation of PIP5K activity by PIP4K in cells, we wanted to assay PI(4,5)P2 levels after acute membrane recruitment of normally cytosolic PIP4K paralogs. To this end, we triggered rapid PM recruitment of cytosolic, FKBP-tagged PIP4K by chemically induced dimerization (CID) with a membrane targeted FRB domain, using rapamycin [27]. As shown in fig. 2A, all three paralogs of PIP4K induce a steady decline in PM PI(4,5)P2 levels within minutes of PM recruitment. Catalytically inactive mutants of all three paralogs produce identical responses (fig. 2A).”
#2.4: The labelling on y-axis for PI(4,5)P2 biosensor intensity ratio is PM/cell at some places, PM/Cyt or PM/Cyto in some places. It is recommended to make it uniform across all the panels.
PM/Cyto was a typo, now corrected to PM/Cyt. PM/Cell and PM/Cyt are two subtly different metrics used to normalize PM fluorescence intensity across varying transient expression levels. This is clarified in the methods in the 3rdparagraph on p.22: “For confocal images, the ratio of fluorescence intensity between specific compartments was analyzed as described previously [59]. In brief, a custom macro was used to generate a compartment of interest specific binary mask through à trous wavelet decomposition[68]. This mask was applied to measure the fluorescence intensity within the given compartment while normalizing to the mean pixel intensity in the ROI. ROI corresponded to the whole cell (denoted PM/Cell ratio) or a region of cytosol (PM/Cyt), as indicated on the y axis of individual figures.”
#2.5: The claim that PI(4,5)P2 production is sufficient to recruit PIP4K2C to the PM can be ascertained further if one is able to do an experiment where PI(4,5)P2 is ectopically expressed in some compartment of the cell which is non-native to PI(4,5)P2 and as a consequence of this PIP4K2C is recruited to this non-native compartment.
We have now removed the assertion that PI(4,5)P2 is sufficient to localize PIP4Ks to the membrane, since our conclusion is that the coincident presence of PI(4,5)P2 and PIP5Ks in the PM is what ultimately localizes the PIP4Ks. We did not detect recruitment of endogenous PIP4Ks to lysosomes when ectopic PI(4,5)P2 synthesis was induced, although fluorescence levels are so low as to be inconclusive, and therefore not appropriate for inclusion in the manuscript.
#2.6: In the entire figure 2, to establish that PI(4,5)P2 is necessary and sufficient for PM localisation of PIP4K, PIP4K2C is used as the PIP4K isoform on the basis that it is highly abundant in HEK293 cells. But PIP4K2A is localised mainly at the plasma membrane and here we are discussing about PI(4,5)P2 regulation at the PM . Can experiments be done with isoforms 2A and 2B as well? Can acute depletion of PI(4,5)P2 lead to the membrane dissociation of the isoform 2A as well? This will help us in understanding if there is an isoform specific difference in sensing PI(4,5)P2 levels which will help us in targeting specific isoform as therapeutic targets.
We have now generated endogenously tagged PIP4K2A and PIP4K2B; these cell lines are characterized in the revised fig. 3:
With the dependence on PI(4,5)P2 for PM binding for all isoforms shown in fig. 4:
32 cells that were imaged across three independent experiments. (E) Depletion of PI(4,5)P2 causes NG2-PIP4K2C to dissociate from the membrane. As in C, NG2-PIP4K2C (blue) cells were transfected with FKBP-tagged proteins, TubbyC (orange) and Lyn11-FRB, scale bar is 2.5 µm; cells were stimulated with 1µM rapa, as indicated. TubbyC traces represent mean change in fluorescence intensity (Ft/Fpre) ± s.e. The NG2-PIP4K2C traces represent the mean change in puncta per µm2 ± s.e. of > 38 cells that were imaged across three independent experiments. " v:shapes="Text_x0020_Box_x0020_5">
And increased binding by elevated PI(4,5)P2 levels shown in fig. 5B:
The results are described in the accompanying results text “PIP4K are low affinity sensors of PM PI(4,5)P2”, pp.4-7. In short, endogenous PIP4K isoforms behave similarly with respect to PI(4,5)P2-dependent PM recruitment.
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#2.7: In Figure 1A, it is shown that overexpression of a catalytically dead PIP5K 1A/1B/1C is still able to increase PI(4,5)P2 levels. In the figure 2E, expression of homodimeric mutant of PIP5K domain which is a way to increase catalytic activity of PIP5K, increases PI(4,5)P2 levels which is consistent with the inferences from Fig, 1 , but what is surprising is a catalytically dead variant not being able to do so. Why is there a discrepancy between Fig. 1A and Fig. 2E? If the homodimeric mutant is the reason, then it is not clear in the explanation.
We have added the following clarification to the results on the second paragraph of p.6: “We next tested for rapid binding to acutely increasing PI(4,5)P2 levels in living cells, using CID of a homodimeric mutant PIP5K domain (PIP5K-HD), which can only dimerize with itself and not endogenous PIP5K paralogs [34]. This domain also lacks two basic residues that are crucial for membrane binding [35], and only elevates PM PI(4,5)P2 when it retains catalytic activity (fig. 5D), unlike the full-length protein (fig. 1A).” We currently do not fully understand why these well characterized residues of PIP5Ks are necessary for PM binding and inhibition by PIP4K. This is a focus of ongoing studies in the lab for the structural basis of PIP5K inhibition by PIP4K.
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#2.8: Show the loading control in Fig 2A western.
We have added the loading control using alpha tubulin in the revised fig. 3B.
#2.9: In the figure 2D, in the legend OCRL is written. So, the labelling in the panel should also be changed to OCRL from INPP5E. It is intermixed.
Reviewer 1 also spotted this inconsistency (#1.7): Purified OCRL was indeed in the supported lipid bilayer experiments. The figure (now Fig. 4A) and legend have been corrected – thank you for spotting the error.
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#2.10: In the figure 2E, can the labelling be changed from HD to something more self-explanatory for homodimeric mutant of PIP5K domain?
We prefer to keep the “HD” notation in the revised figure 5D for brevity’s sake, but now define the abbreviation in the text in the second paragraph of p.6: “…a homodimeric mutant PIP5K domain (PIP5K-HD)…”.
#2.11: In Fig. 2E, PIP5K expression is acute and in Fig. 2F Mss4 expression is chronic, both of which is able to recruit PIP4K2C to the plasma membrane. How can a likewise argument be drawn out of these two experiments when one is acute and the other one is a chronic expression? It is suggested to do an FRB-FKBP experiment for Mss4 as well.
We agree with the reviewer that an FKBP-Mss4 would have been an excellent experiment. As can be seen from Fig. __1A, Mss4 is constitutively PM localized in mammalian cells. However, we were unable to identify a truncation of Mss4 that lost constitutive membrane binding whilst retaining catalytic activity. Therefore, we could only perform chronic overexpression as shown in __fig. 5B. The lack of an acute demonstration is why we went on to develop the PIP5K-HD constructs, results of which are reported in __fig. 5D. __
#2.12: In the text, Fig. 2G and 2H is written for PIP4K2C, but in the corresponding panels and legends, it is an assay for purified PIP4K2A on SLBs. Kindly resolve the discrepancy.
We thank the reviewer for spotting this discrepancy. PIP4K2A is the protein that was used in the SLB experiments now reported in fig. 5A & C and the accompanying results on pp.5-6. This is now corrected in the manuscript.
#2.13: Kindly explain a bit in detail why the baits were now targeted to ER-PM contact sites. It is not self-explanatory.
We have now added a more detailed description to the third paragraph of p. 7: “We therefore sought to distinguish between a direct PIP5K-PIP4K binding interaction versus PI(4,5)P2-induced co-enrichment on the PM. To this end, we devised an experiment whereby a bait protein (either PIP5K or control proteins) could be acutely localized to subdomains of the PM, with the same PI(4,5)P2 concentration. This was achieved using CID of baits with an endoplasmic reticulum (ER) tethered protein, causing restricted localization of the bait protein to ER-PM contact sites – a subdomain of the PM (fig. 7B).”
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#2.14: The conclusions for Fig. 3 most likely hints towards the possibility of PIP4K and PIP5K interaction being independent of PI(4,5)P2 levels. Well, Fig. 3C and 3D does suggest a direct interaction, but can other protein-protein interaction assays be used to establish the direct interaction of PIP4K with PIP5K such as FRET or Yeast two hybrid as assays scoring for interaction?
We respectfully diverge from the reviewer’s assessment of the data, presented in the revised fig. 7. Figs. 7A & B__show PIP4K and PIP5K interacting in the context of a PI(4,5)P2 replete PM; __fig. 7C shows this in the context of a PI(4,5)P2 replete SLB. Therefore, we make no assertion that the PIP4K/PIP5K is independent of PI(4,5)P2 levels. We also contend that the latter experiment is a more direct demonstration than a Y2H assay, or even FRET (which can occur among non-interacting proteins localized to a membrane surface, see e.g. 10.1074/jbc.m007194200).
#2.15: Conceptually a direct interaction can be explained to some extent from Fig. 3 but extending it to be an inhibitory interaction is not right without a direct experiment. Can an experiment be done with PI4P enriched SLB, wherein you put just PIP5K purified protein vs PIP5K+PIP4K combination and measure the % mol of PI(4,5)P2 produced using a probe. That will be suggestive of a negative interaction.
This is a great experiment, the results of which are reported in fig. 2C, described in the third full paragraph of p. 4: “To more directly examine inhibition of PIP5K by PIP4K, we tested activity of purified PIP5K1A on PI4P-containing supported lipid bilayers (SLBs). Addition of PIP4K2A exhibited delayed inhibition of PIP5K1A activity (fig. 2C): Once PI(4,5)P2 reached approximately 28,000 lipids/µm2 (~2 mol %), PIP5K dependent lipid phosphorylation slowed down, which doubled the reaction completion time (fig. 2C, right). In contrast, we observed no PIP4K dependent inhibition of Mss4 (fig. 2C, inset). These data recapitulate the prior finding that PIP4K only inhibited purified PIP5K in the presence of bilayer-presented substrate [25]. We therefore hypothesized that inhibition of PIP5K by PIP4K requires recruitment of the latter enzyme to the PM by PI(4,5)P2 itself.”
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__#2.15: __ In Figure 3B, the FRB tagged constructs are magenta coded and PIP4K2C is cyan. Kindly change the labelling of the FRB constructs on the y axis to magenta so that it goes with what is written in the legend. It will also be appreciated to show a colocalization quantification between the magenta (FRB constructs) and cyan (PIP4K2C) post rapamycin addition and not just the intensity for ER-PM recruited PIP4K2C.
These modifications and some additional points have been added in response to reviewer 1’s #1.4 to the revised fig. 7B. Note, we quantified the co-localization with an ER-PM contact site marker, MAPPER. Co-localization with the FRB-tagged construct would be misleading, because this construct is localized across the membrane at the start of the experiment and would thus have a high degree of co-localization. As can be seen from the inset graphs in the new analysis, however, all FRB-tagged constructs co-localize with MAPPER after rapamycin addition, but only FRB-PIP5K1A causes endogenous PIP4K2C to increase co-localization with this compartment.
# 2.16: Again, in the text , the description is written for PIP4K2C but in the result panel and legend (Fig. 3C and Fig. 3D), PIP4K2A is mentioned. Kindly resolve the discrepancy
We have corrected the results text on the last paragraph of p. 7: “Finally, we also demonstrate that PIP4K2A binding to PI(4,5)P2-containing supported lipid bilayers was greatly enhanced by addition of PIP5K to the membranes (fig. 7C), but not by Mss4 (fig. 7D).”
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# 2.17: In the Fig. 4B, it will be appreciated to show statistical significance in terms of R2 value for commenting on the linear response.
“Linear response” was not the best description of what we were trying to articulate in the revised fig. 8B; we have now amended the results in the 2nd paragraph of p.8 to read: “Of these, Tubbyc showed the largest degree of change in PM localization across all changes in PI(4,5)P2 levels (fig. 8B).”
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#2.18: Discussion can be in general a bit more detailed which is suggestive of future experiments to do that can shed more light on the interaction such as which residues in PIP4K interacts with PIP5K to negatively regulate it.
The revised manuscript contains a greatly expanded discussion, as described in detail in our responses to comments #1.2b, #2.1 and __#2.2. __
#2.19: In the discussion, more light can be shed on the fact that Mss4 in spite of being a 5- kinase is not negatively regulated by PIP4K and the fact that PIP4K is present only in metazoans suggests that this fine tuning of PI(4,5)P2 levels is specific to metazoans. Another insight could be in the direction, that Fig 4. tells PI3K, but not calcium signaling is modulated by this fine tuning and interestingly class I PI3K is also an enzyme specific to metazoans. Hence, unlike yeast, metazoans rely on growth factor signalling processes, hence regulation of PI(4,5)P2 by PIP4K and hence Class I PI3K and PI(3,4,5)P3 could be a process relevant to metazoans.
We have addressed the restriction of PIP4K to holozoa as described in our response to #2.2, wherein we describe a previously proposed paralogous mechanism in fungi. The reviewer’s point about the homeostatic process being related to class I PI3K signaling in growth control of multicellular organisms is interesting, but the presence of the PIP4Ks in some unicellular organisms complicates this view. We are of the view that a discussion of this important topic is a little nuanced for inclusion in the current manuscript.
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Reviewer #3
__Summary: __Using state of the art imaging techniques the authors try to address how cells sense PI(4,5)P2 levels and regulate PIP5Ks to maintain an optimal level since any dysregulation of PI(4,5)P2 levels can have significant effects on the functioning of the cell and led to numerous disease states, such as cancers.
The key conclusions are convincing and importantly validate previous disputed findings made by Wang et al. (Cell Reports 2019) using different and more rigorous methods, however unfortunately due to the Wang et al publication the overall novelty of this study is lacking. A suggestion to the authors is to state/explain with text more clearly how their findings are more precise and higher quality than the previous report and why their findings are necessary and significant to drive the field forward.
We have revised the manuscript to more clearly state our novel finding that PIP4Ks are PI(4,5)P2 sensing proteins that inhibit PIP5Ks on the membrane in a PI(4,5)P2-dependent manner, which was not previously described in the literature.
Further, experiments in the study were performed in vitro in cultured cells using overexpression methods making the physiological significance a bit unclear and the enthusiasm of the main discovery dampened. With that being said these findings are worthy of publication in order to advance the field and understanding of how the PIP kinase families are regulated and maintain PIP2 homeostasis which is important for life.
We feel that this assessment is slightly unfair, since most of the key experiments have been validated using purified proteins in supported lipid bilayers, and endogenous proteins were studied using genomic tagging approaches, rather than over-expression.
Minor and easily addressable experiments should be performed by the authors the following. Further, many of these experimental issues can easily go in supplemental materials
#3.1: Include western blots for the constructs to compare expression levels.
We agree that it is important to take into account differences in expression levels for the experiments presented in fig. 1. However, since these are single cell assays, Western blotting of whole populations of transiently transfected cells is not the best control. Instead, having acquired the images under consistent excitation and detection parameters, we compared the fluorescence intensity, expressed as relative expression in Fig. 1A and C, which is discussed in the results text in the first two paragraphs of the results on p. 3: “Notably, expression of the catalytically inactive mutants was usually somewhat less strong compared to the wild-type enzymes, yet effects on PI(4,5)P2 levels were similar (fig. 1A).” and “Again, differences in expression level between isoforms do not explain differences in activity, since all achieved comparable expression levels as assessed by fluorescence intensity (fig. 1C).”
#3.2: For Figure 1A, what is the source of the observed increase in PI(4,5)P2, how do the authors take into account the role of endogenous PIP5Ks?
We added a new experiment in the revised Fig. 1B showing that the increased PI(4,5)P2 occurs at the expense of PM PI4P:
This is described in the first paragraph of the results on p.3: “PI(4,5)P2 levels are expected to increase at the expense of PM PI4P levels when over-expressing any of the three isoforms of human PIP5K (A-C) or the single paralog from the budding yeast, Saccharomyces cerevisiae (Mss4). Indeed, this was precisely what we observed (fig. 1A and B, statistics reported in tables 1 and 2).”
The role for endogenous PIP5Ks is clarified on the sentence that spans pp. 3-4: “We therefore reasoned that saturation of endogenous, inhibitory PIP4K molecules by PIP5K over-expression, regardless of catalytic activity of the PIP5K, would free endogenous, active PIP5K enzyme from negative regulation (fig. 1D).”
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#3.3: For Figure 1B, could the authors comment on the intracellular distribution of PI(4,5)P2. How are they able to reliably distinguish their signal between plasma membrane and intracellular localizations and conclude that PIP2 on the plasma membrane is decreased?
As detailed in the now expanded methods section covering image analysis on p. 22, our analysis specifically quantifies fluorescence in the plasma membrane.
#3.4: Please include statistics for all image- based quantitation analysis.
We have added details of statistical analysis and tabulated the results, as detailed in our response to __#1.1. __
__#3.5: __ Could the authors comment on the ability of PIP4K to have affinity for its own product? How does PIP4K sense membrane PI(4,5)P2 since these kinases are mostly cytoplasmic?
We have added a comment to the 1st paragraph of the Discussion on p.9: “PIP4K’s low affinity and highly co-operative binding to PI(4,5)P2 makes it an excellent sensor for tonic PI(4,5)P2 levels. It is poised to sense PI(4,5)P2generated in excess of the needs of the lipids’ legion effector proteins, ensuring these needs are met but not exceeded. Nevertheless, the relatively low PIP4K copy number of around 2.5 x 105 per cell [29] is a small fraction of the total PI(4,5)P2 pool, estimated to be ~107 [33], ensuring little impact on the capacity of the lipid to interact with its effectors.”
__#3.6: __Do the authors have any other experiments to substantiate the binding of the two PIP kinases, similar to the Wang et al findings? Is the N-term motif required? Is it possible to disrupt that interaction and show the phenotype?
We do not have additional, conclusive experiments to share at this time, and believe that characterization of the inhibitory interaction is beyond the scope of the current manuscript. We do however add a comment on this topic to the 1st paragraph of p. 11: “Regardless, a full understanding of paralog selectivity will need to be driven by a detailed structural analysis of the interaction between PIP4Ks and PIP5Ks - which is not immediately apparent from their known crystal structures, especially since PIP4Ks and PIP5Ks employ separate and distinct dimerization interfaces [50].”
#3.7: With the overexpression studies in Figure 1, do the authors see any changes in signaling when they just overexpress PIP5Ks versus in combination with PIP4Ks to show that the changes in plasma membrane PI(4,5)P2 can affect downstream signaling?
We agree with the reviewer that attenuating PIP5K-mediated PI(4,5)P2 increases with PIP4K should affect downstream signaling. However, we believe that these will not add additional insight compared to the already included experiments (fig. 8), whereby signaling output in response to graded changes in PI(4,5)P2 levels was investigated.
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Reviewer #3 (Significance (Required)): Overall, as mentioned above because of the 2019 Wang et al report the novelty is diminished, however using completely alternate methods and sophisticated microscopy this body of work indeed advances the field and provides further believable evidence of the PIP kinase families communicating in higher organisms which is required to maintain PIP2 levels shedding light on many of the findings that were previously unexplained surrounding the PIP4K studies. Further, the use of biosensors to describe these findings are new and will enable others in the field to begin to use such tools to investigate potential crosstalk between other lipid kinases.
As we argued in the general comments, we do feel that this evaluation misses the key finding that PIP4Ks are PI(4,5)P2 sensors, and that this regulates PIP5K regulation as part of a feedback loop.
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Referee #3
Evidence, reproducibility and clarity
Using state of the art imaging techniques the authors try to address how cells sense PI(4,5)P2 levels and regulate PIP5Ks to maintain an optimal level since any dysregulation of PI(4,5)P2 levels can have significant effects on the functioning of the cell and led to numerous disease states, such as cancers.
The key conclusions are convincing and importantly validate previous disputed findings made by Wang et al. (Cell Reports 2019) using different and more rigorous methods, however unfortunately due to the Wang et al publication the overall novelty of this study is lacking. A suggestion to the authors is to state/explain with text more clearly how their findings are more precise and higher quality than the previous report and why their findings are necessary and significant to drive the field forward. Further, experiments in the study were performed in vitro in cultured cells using overexpression methods making the physiological significance a bit unclear and the enthusiasm of the main discovery dampened. With that being said these findings are worthy of publication in order to advance the field and understanding of how the PIP kinase families are regulated and maintain PIP2 homeostasis which is important for life.
Minor and easily addressable experiments should be performed by the authors the following. Further, many of these experimental issues can easily go in supplemental materials
- Include western blots for the constructs to compare expression levels.
- For Figure 1A, what is the source of the observed increase in PI(4,5)P2, how do the authors take into account the role of endogenous PIP5Ks?
- For Figure 1B, could the authors comment on the intracellular distribution of PI(4,5)P2. How are they able to reliably distinguish their signal between plasma membrane and intracellular localizations and conclude that PIP2 on the plasma membrane is decreased?
- Please include statistics for all image- based quantitation analysis.
- Could the authors comment on the ability of PIP4K to have affinity for its own product? How does PIP4K sense membrane PI(4,5)P2 since these kinases are mostly cytoplasmic?
- Do the authors have any other experiments to substantiate the binding of the two PIP kinases, similar to the Wang et al findings? Is the N-term motif required? Is it possible to disrupt that interaction and show the phenotype?
- With the overexpression studies in Figure 1, do the authors see any changes in signaling when they just overexpress PIP5Ks versus in combination with PIP4Ks to show that the changes in plasma membrane PI(4,5)P2 can affect downstream signaling?
Significance
Overall, as mentioned above because of the 2019 Wang et al report the novelty is diminished, however using completely alternate methods and sophisticated microscopy this body of work indeed advances the field and provides further believable evidence of the PIP kinase families communicating in higher organisms which is required to maintain PIP2 levels shedding light on many of the findings that were previously unexplained surrounding the PIP4K studies. Further, the use of biosensors to describe these findings are new and will enable others in the field to begin to use such tools to investigate potential crosstalk between other lipid kinases.
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Referee #2
Evidence, reproducibility and clarity
Summary:
This paper proposes that the enzyme PIP4K2C is a negative regulator of the synthesis of PI(4,5)P2 and that it does so by dampening the activity of PIP5K which is the enzymatic activity responsible for producing the major pool of PI(4,5)P2 in cells.
Significance
Nature and Significance of the advance:
Although the findings of the paper are presented as a major new advance, the observation that PIP4K might acts as a negative regulator of PIP2 synthesis has been previously presented in two previous publications. The significance of this paper is that it also shows the same point in another model system.
PIP4Ks Suppress Insulin Signaling through a Catalytic-Independent Mechanism Diana G Wang 1, Marcia N Paddock 2, Mark R Lundquist 3, Janet Y Sun 3, Oksana Mashadova 3, Solomon Amadiume 3, Timothy W Bumpus 4, Cindy Hodakoski 3, Benjamin D Hopkins 3, Matthew Fine 3, Amanda Hill 3, T Jonathan Yang 5, Jeremy M Baskin 4, Lukas E Dow 6, Lewis C Cantley 7 PMID: 31091439; PMCID: PMC6619495;DOI: 10.1016/j.celrep.2019.04.070
and
Phosphatidylinositol 5 Phosphate 4-Kinase Regulates Plasma-Membrane PIP3 Turnover and Insulin Signaling. Sharma S, Mathre S, Ramya V, Shinde D, Raghu P.Cell Rep. 2019 May 14;27(7):1979-1990.e7. doi: 10.1016/j.celrep.2019.04.084.PMID: 31091438
Both of these studies show that in cells lacking PIP4K, during signalling the levels of PIP2 rise much greater than in wild type cells. Indeed the Cantley lab paper (Wang et.al) have shown that this is likely due to an increase in PIP5K activity, using an in vitro assay. They have further disrupted the interaction between PIP4K and PIP5K and demonstrated the importance of this interaction in the enhanced levels of PIP2.
Likewise although the authors have claimed that no mechanisms have claimed that there are no mechanisms reported to sense and downregulate PIP2 resynthesis. It is suggested that they read and consider the following recent paper which studies Pip2 resynthesis during GPCR triggered PLC signalling.
Kumari A, Ghosh A, Kolay S and Raghu P*. Septins tune lipid kinase activity and PI(4,5)P 2 turnover during G-protein-coupled PLC signalling in vivo. Life Sci Alliance. 2022 Mar 11;5(6):e202101293. doi: 10.26508/lsa.202101293. Print 2022 Jun.
Likewise there are other earlier papers in the literature which have studied possible PIP2 binding proteins as sensors for this lipid.
Technical standards: The work is done to a high technical standard.
Major and Minor Comments
Comments for Figure 1
- Does catalytically dead isoform of PIP4K2B and 2C also yield the same result as a catalytically dead version of PIP4K2A in Fig 1B?
- The labelling on y-axis for PI(4,5)P2 biosensor intensity ratio is PM/cell at some places, PM/Cyt or PM/Cyto in some places. It is recommended to make it uniform across all the panels.
Comments for Figure 2
- The claim that PI(4,5)P2 production is sufficient to recruit PIP4K2C to the PM can be ascertained further if one is able to do an experiment where PI(4,5)P2 is ectopically expressed in some compartment of the cell which is non-native to PI(4,5)P2 and as a consequence of this PIP4K2C is recruited to this non-native compartment.
- In the entire figure 2, to establish that PI(4,5)P2 is necessary and sufficient for PM localisation of PIP4K, PIP4K2C is used as the PIP4K isoform on the basis that it is highly abundant in HEK293 cells. But PIP4K2A is localised mainly at the plasma membrane and here we are discussing about PI(4,5)P2 regulation at the PM . Can experiments be done with isoforms 2A and 2B as well? Can acute depletion of PI(4,5)P2 lead to the membrane dissociation of the isoform 2A as well? This will help us in understanding if there is an isoform specific difference in sensing PI(4,5)P2 levels which will help us in targeting specific isoform as therapeutic targets.
- In Figure 1A, it is shown that overexpression of a catalytically dead PIP5K 1A/1B/1C is still able to increase PI(4,5)P2 levels. In the figure 2E, expression of homodimeric mutant of PIP5K domain which is a way to increase catalytic activity of PIP5K, increases PI(4,5)P2 levels which is consistent with the inferences from Fig, 1 , but what is surprising is a catalytically dead variant not being able to do so. Why is there a discrepancy between Fig. 1A and Fig. 2E? If the homodimeric mutant is the reason, then it is not clear in the explanation.
- Show the loading control in Fig 2A western.
- In the figure 2D, in the legend OCRL is written. So, the labelling in the panel should also be changed to OCRL from INPP5E. It is intermixed.
- In the figure 2E, can the labelling be changed from HD to something more self-explanatory for homodimeric mutant of PIP5K domain?
- In Fig. 2E, PIP5K expression is acute and in Fig. 2F Mss4 expression is chronic, both of which is able to recruit PIP4K2C to the plasma membrane. How can a likewise argument be drawn out of these two experiments when one is acute and the other one is a chronic expression? It is suggested to do an FRB-FKBP experiment for Mss4 as well.
- In the text, Fig. 2G and 2H is written for PIP4K2C, but in the corresponding panels and legends, it is an assay for purified PIP4K2A on SLBs. Kindly resolve the discrepancy.
Comments for Figure 3
- Kindly explain a bit in detail why the baits were now targeted to ER-PM contact sites. It is not self-explanatory.
- The conclusions for Fig. 3 most likely hints towards the possibility of PIP4K and PIP5K interaction being independent of PI(4,5)P2 levels. Well, Fig. 3C and 3D does suggest a direct interaction, but can other protein-protein interaction assays be used to establish the direct interaction of PIP4K with PIP5K such as FRET or Yeast two hybrid as assays scoring for interaction?
- Conceptually a direct interaction can be explained to some extent from Fig. 3 but extending it to be an inhibitory interaction is not right without a direct experiment. Can an experiment be done with PI4P enriched SLB, wherein you put just PIP5K purified protein vs PIP5K+PIP4K combination and measure the % mol of PI(4,5)P2 produced using a probe. That will be suggestive of a negative interaction.
- In Figure 3B, the FRB tagged constructs are magenta coded and PIP4K2C is cyan. Kindly change the labelling of the FRB constructs on the y axis to magenta so that it goes with what is written in the legend. It will also be appreciated to show a colocalization quantification between the magenta (FRB constructs) and cyan (PIP4K2C) post rapamycin addition and not just the intensity for ER-PM recruited PIP4K2C.
- Again, in the text , the description is written for PIP4K2C but in the result panel and legend (Fig. 3C and Fig. 3D), PIP4K2A is mentioned. Kindly resolve the discrepancy
Comments for Figure 4
- In the Fig. 4B, it will be appreciated to show statistical significance in terms of R2 value for commenting on the linear response.
Comments for Discussion
- Discussion can be in general a bit more detailed which is suggestive of future experiments to do that can shed more light on the interaction such as which residues in PIP4K interacts with PIP5K to negatively regulate it.
- In the discussion, more light can be shed on the fact that Mss4 in spite of being a 5- kinase is not negatively regulated by PIP4K and the fact that PIP4K is present only in metazoans suggests that this fine tuning of PI(4,5)P2 levels is specific to metazoans. Another insight could be in the direction, that Fig 4. tells PI3K, but not calcium signaling is modulated by this fine tuning and interestingly class I PI3K is also an enzyme specific to metazoans. Hence, unlike yeast, metazoans rely on growth factor signalling processes, hence regulation of PI(4,5)P2 by PIP4K and hence Class I PI3K and PI(3,4,5)P3 could be a process relevant to metazoans.
Audience: cell biologists and biochemists interested in PIp2 signalling and PIP kinases
My expertise: PIP2 and PIP kinases
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, authors address how PIP4K regulates tonic plasma membrane (PM) PI(4,5)P2 levels which are generated by major PI(4,5)P2 synthesis enzyme, PIP5K by using PIP4K and PIP5K overexpressing cells or acutely manipulating PM PI(4,5)P2 levels by the chemically induced dimerization (CID) system. Additionally, authors assessed effect of direct interaction between PIP4K and PIP5K by using supported lipid bilayers (SLBs) and purified PIP4K and 5K. Authors also were successful in monitoring dynamics of endogenous PIP4K by using a split fluorescent protein approach. Through this study, authors propose a model of PI(4,5)P2 homeostatic mechanism that PIP4Ks sense elevated PM PI(4,5)P2 by PIP5Ks, are recruited to the PM, and bind to PIP5Ks to inhibit PIP5Ks activity.
- Although authors mention methods of statistical analysis in materials and methods, they did not present the results of statistical analysis in the figures. The quantitative data should be presented with statistical analysis data, which is important for showing where convincing differences between treatment groups are found.
- Fig. 1D. Fig. 1D and Fig. 3A should be presented together because these are exactly same set of cells and information of each PIP4K and PIP5K membrane localization could be important for understanding mechanisms of inhibitory effect of PIP4Ks. Authors claimed that over-expression of all three PIP4K isoforms were able to attenuate the elevated PM PI(4,5)P2 levels caused by PIP5K over-expression. However, in Fig. 3A, PIP4K2A was recruited to PM by both PIP5K1A and PIP5K1C but looks only attenuated PIP5K1A, but not PIP5K1C, overexpression mediated PM PI(4,5)P2 elevation (Fig. 1D). PIP4K2C was less recruited to the PM than PIP4K2A and 2B in PIP5K1A overexpressing cell (Fig. 3A) but PIP4K2A, B and C isoforms equally attenuated increase of PM PI(4,5)P2 in PIP5K1A overexpressing cell (Fig. 1D). It is likely that efficiency of inhibitory effect of each PIP4K isoform is different by co-overexpressed PIP5K isoform. These images should be more carefully documented with Fig. 1D and Fig. 3A together.
- Fig. 1F. It seems that PIP4K2A accelerated PIP5K, but not Mss4, dependent PI(4,5)P2 generation before PI(4,5)P2 reaches 28,000 lipids/um2. Is this significant? If so, why did this happen?
- Fig. 3B. In this figure, authors only presented images after Rapa treatment. Therefore, it is not clear what these results mean. Before Rapa treatment, where did bait proteins and NG2-PIP4K2C localize? If ePIP4K2C delta PM intensity (ER:PM/PM) increase, does that mean increase in ER:PM intensity or decrease in PM intensity? According to Figure legend, PI(4,5)P2 indicator TubbycR332H was co-transfected, but those images are not shown in the figure. Images of PI(4,5)P2 indicator also should be presented to show whether after Rapa treatment PI(4,5)P2 increased at ER-PM contact sites, because that could be critical for the conclusion that "The use of Mss4 ruled out an effect of enhanced PI(4,5)P2 generation at contact sites, since this enzyme increases PI(4,5)P2 as potently as PIP5K1A (Fig. 1A), yet does not cause recruitment of PIP4K2C". Is this conclusion consistent with Fig. 2F and G?
- Fig. 3C and D. Based on results of Fig. 3C and D, authors concluded that "PIP4K2C binding to PI(4,5)P2-containing SLBs was greatly enhanced by addition of PIP5K to the membranes, but not Mss4". I don't think Fig. 3C and D are comparable because experimental conditions are different. While lipid composition of SLB used in Fig. 3C was 2% PI(4,5)P2, 98% DOPC, in Fig. 3D, it was 4% PI(4,5)P2, 96% DOPC. And also, in Fig. 3C, PIP5K1A was added to SLB at the time about 50 sec, whereas in Fig. 3D, Mss4 was added at 600 sec. It seems that in Fig. 3D, PIP4K2A was already saturated on SLB before adding Mss4. These two experiments must be performed under the same conditions.
- Overall results discussed in the text are very compressed referring readers to the 4 multi-panel complex figures with elaborate figure legends. While it is possible to figure out what the authors' studies and results are, it is quite a laborious process.
Minor comments:
- Fig. 2D. The purified 5-phosphatase used in Fig. 2D is INPP5E but described in figure legend and materials and methods ass OCRL. Which one is correct?
- Fig. 3B. Indicate which trace represents PIP5K1A, Lyn11 or Mss4.
- Fig. 4C. X-axis label. Is "Time (min)" correct? Or should it be "Time (sec)".
Significance
The finding that PIP4K itself is a low-affinity PI(4,5)P2 binding protein and sense increases of PM PI(4,5)P2 generated by PIP5K to control tonic PI(4,5)P2 levels by inhibiting PIP5K activity is a novel concept. However, inhibition of PIP5K by PIP4K and importance of the inhibitory effect of PIP4K in PI3K signaling pathway have previously been reported (ref 24). This reduces the novelty of the current work somewhat however, the authors do provide evidence for dual interactions of PIP4K (PIP2, PIP5K), which the previous report did not.
The reviewers have expertise in PLC- and PIP5K-related signaling pathways.
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Reply to the reviewers
Manuscript number: RC-2022-01723
Corresponding author(s): Daphne Avgousti, Srinivas Ramachandran
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary This study by Lewis et al. examines the role of heterochromatin in the nuclear egress of herpesvirus capsids. They show that heterochromatin markers macroH2A1 and H3K27me3 are enriched at specific genome regions during the infection. They also show that when macroH2A1 is removed or H3K27me3 is depleted (both of which reduce the amount of heterochromatin at the nuclear periphery), the capsids are not able to egress as effectively. This is interesting since it could be argued that heterochromatin acts as a hindrance to the transport of viral capsids to the nuclear envelope and that the loss of it would allow capsids to reach the nuclear envelope more easily. However, this paper seems to show that heterochromatin formation, on the contrary, is necessary for efficient egress. Overall, the study seems comprehensive. The methodology is solid, and the experiments are very well controlled. However, some issues need to be addressed before publication.
Major comments
1) In line 49, the authors state, "Like most DNA viruses, herpes simplex virus (HSV-1) takes advantage of host chromatin factors both by incorporating histones onto its genome to promote gene expression and by reorganizing host chromatin during infection". In addition, HSV1 expression can be hindered by the host's interferon response via histone modifications. Ref. Johnson KE, Bottero V, Flaherty S, Dutta S, Singh VV, Chandran B. IFI16 restricts HSV-1 replication by accumulating on the HSV-1 genome, repressing HSV-1 gene expression, and directly or indirectly modulating histone modifications. PLoS Pathog. 2014 Nov 6;10(11):e1004503. doi: 10.1371/journal.ppat.1004503. Erratum in: PLoS Pathog. 2018 Jun 6;14(6):e1007113. PMID: 25375629; PMCID: PMC4223080.
We agree with the reviewer and have amended our text and added the reference. See line 57.
2) Reference 5 is misquoted in the sentence, "This redistribution of host chromatin results in a global increase in heterochromatin". In that reference, the amount of heterochromatin is not analyzed in any way. However, that particular paper shows that the transport of capsid through chromatin is the rate-limiting step in nuclear egress, which is important considering this study. Further, the article by Aho et al. shows that when the infection proceeds capsids can more easily traverse from the replication compartment into the chromatin, which means that infection can modify chromatin for easier capsid transport. For that reason, the article is an important reference, but it needs to be cited correctly.
We agree with the reviewer that this citation was misquoted and have corrected the citation. See lines 55 and 62-64.
3) The term heterochromatin channel at lines 54, 102, and 303 is misleading since the channels seen in the original referred paper are less dense chromatin areas. Also, this term is not used in the original paper where the phenomenon was first described. These less dense interchromatin channels were found by soft-X-ray tomography imaging and analyses, not by staining.
We thank the reviewer for pointing out this discrepancy and have amended the text to accurately describe the methods used in the appropriate citations. See lines 65, 115, and 383.
4) It is difficult to visualize chromatin using TEM microscopy. The values of peripheral chromatin thickness given in Figure 1e (5-15 nm) do not seem realistic given that the thickness of just one strand of histone-wrapped DNA is 11 nm. Why are the two values for WT different? If you can get so different values for WT, it is a bit worrisome (switching the WT results between the top and bottom parts of Fig. 1e would for example result in very different conclusions on the effect of macroH2A1 KO for the thickness of the chromatin layer).
*We agree with the reviewer that it is difficult to visualize chromatin by TEM. It is also important to note that comparisons can only be made between samples treated on the same day in the same way. Taking this into account, we chose to compare macroH2A1 KO cell stains to controls done at the same time, and the same for H3K27me3 depleted conditions compared to DMSO treated and prepare for EM at the same time. Visually, it is apparent that the staining in the macroH2A1 KO control cells is somewhat different than those of the H3K27me3 depleted control cells, which represents the inherent variability of this method. It is also true that one nucleosome is around 11nm, however, since the cells contain highly compacted chromatin with many other proteins present, this measurement is not appropriate to apply. Adding up the millions of nucleosomes that make up the chromosomes at 11nm each would result in a space much larger than the nucleus, therefore we focus on comparing between control and experimental conditions restricted to this assay as a relative qualitative comparison. Nevertheless, we agree with the reviewer that the notion of changing chromatin is difficult to quantify by EM and so we have taken an additional approach to test our hypothesis and confirm EM interpretations (discussed lines 391-393). We have utilized live capsid trafficking to visualize capsid movement in nuclei in the presence or absence of macroH2A1. The results from these new experiments are presented in new Figure 5 and EV5 and support our model. *
5) In lines 134-137 it says that "The enrichment of macroH2A1 and H3K27me3 was observed as large domains that were gained upon viral infection (Fig 2a), suggesting that the host landscape is altered upon infection. These gains were reflected in an increase in total protein levels measured by western blot (Fig 2b)." However, the protein levels of H3K27me3 do not seem to increase during infection. In other presented data as well (Figs. 2a, 2b, 2c, S2a) it is difficult to justify the statement that H3K27me3 is enriched in infection. When this is the case, the conclusion that the amount of heterochromatin increases in the infection (the quotation above and the one in line 315) is not supported. The statement in line 315 is also not specific since it is unclear what "newly formed heterochromatin increases" means.
We agree with the reviewer that our original description was misleading. We now have edited the text to clarify that there is redistribution of macroH2A1 and H3K27me3. In the revised manuscript, we have also included mass spectrometry data mined from Kulej et al. that show peptide counts that reflect increases in the heterochromatin markers described (see new Figure EV1a). Despite this quantitative measure, upon rigorous replicates of our western blots as requested by Reviewer 2, we concluded that the increases originally described are somewhat inconsistent by western blot. This discrepancy between mass spectrometry data and western blot is likely due to the non-linear nature of antibody binding and developing of western blots by the ECL enzymatic reaction. Therefore, our revised manuscript focuses on this redistribution as a reaction to infection and stress responses instead of a global increase as the original manuscript stated. See lines 174, 182, 196, 397 and Fig EV4d in main text and discussion sections.
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6) Quantitation of viral capsid location in H3K27me3-depleted cells seems somewhat arbitrary. It would have been more robust to calculate the number of capsids per unit length of the nuclear envelope with and without depletion.
We agree with the reviewer that the quantification of capsids in the H3K27me3-depleted conditions was arbitrary. In our revised manuscript, we have now repeated this quantification to accurately measure the phenotype observed, that is the chains of capsids lined up at the inner nuclear membrane. To do this, we used two measures: 1) the distance from the INM as less than 200nm and 2) the distance from other capsids as less than 300nm. Taking into account these two measures, we quantified the frequency with which multiple capsids lined up at the INM in WT and H3K27me3-depleted conditions. This is represented in the new Figure 5d. In the WT setting, we observe most often 1 single capsid at the INM, with a small fraction of 2 capsids. However, in the H3K27me3-depleted condition, we observe much greater numbers of capsids at the INM more frequently, as many as 16 at a time, leading to an average of 2-3 capsids at any single location. The source data for this figure are also provided. See lines 589 and Fig5d.
7) In lines 300-302 it says "Elegant electron microscopy work showed that HSV-1 infection induces host chromatin redistribution to the nuclear periphery2,8." However, the redistribution data in reference 8 is based on soft x-ray tomography and not on electron microscopy."
We have amended the text to accurately describe the methods used in the citations. See line 384.
8) The authors bundle together the effects of macroH2A1 removal and H3K27me3 depletion by saying that they both decrease the amount of heterochromatin at the nuclear periphery and therefore hinder capsid egress. This seems overly simplistic and macroH2A1 and H3K27me3 seem to act very differently, which is manifested in the drastic difference in nuclear capsid localization between the two cases. This difference needs to be discussed more.
We agree with the reviewer that there is a nuanced difference in the effect on nuclear egress in the absence of the two heterochromatin marks. Specifically, that macroH2A1 loss results in greater numbers of capsids dispersed throughout the nucleus, whereas depletion of H3K27me3 results in capsids reaching the INM and not escaping. To examine these differences further, we have carried out live imaging of capsid trafficking in macroH2A1 KO cells compared to control and found that capsids move much more slowly, consistent with our model, see new Figure 5h-I and EV5h-i. Conversely, H3K27me3 depletion does not prevent the capsids from reaching the INM, raising the question of whether they are successfully able to dock at the nuclear egress complex (NEC). To investigate this further, we obtained an antibody against the NEC component UL34 and probed during infection in our heterochromatin disrupted conditions. We found that UL34 levels are unchanged upon loss of macroH2A1 or depletion of H3K27me3, suggesting the levels of UL34 do not account for the decrease in titers. These data are now presented in new Figure EV3g-h. Furthermore, we have amended our model to include the two different scenarios upon loss of different types of heterochromatin (see new Figure 6) and discussion of these differences. See line 428.
Minor comments Line 45: Nuclear replicating viruses -> Nuclear-replicating viruses Line 56: is -> are Line 64: 25kDa -> 25 kDa Line 159: macroH2A1 cells -> macroH2A1 KO cells Line 289: The term gDNA is rarely used for viral DNA. Replace gDNA with viral DNA. Line 405: 8hpi -> 8 hpi Line 449: mm2 -> μm2 "Scale bar as indicated" words can be removed in the figure legends or at least should not be repeated many times within one figure legend.
We have amended the text to address these comments. See lines 52, 68, 76, 179, 334, 513, and 585.
Reviewer #1 (Significance (Required)):
These findings would appeal to a broad audience in the field of virology. Specifically, the researcher in the fields of virus-cell and virus-nucleus interactions. This manuscript analyses herpesvirus-induced structural changes in the chromatin structure and organization in the nucleus that are also likely to affect the intranuclear transport of viral capsids.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The manuscript "HSV-1 exploits heterochromatin for egress" describes the effects of heterochromatin at the nuclear periphery, macroH2A1 or H3K27me3 on HSV-1 replication and egress. Knocking out macroH2A1 or depleting H3K27me3 with high concentrations of tazemetostat depleted heterochromatin at the nuclear periphery, may not have affected HSV-1 protein expression and modestly inhibited the production of cell-free infectivity and HSV-1 genomes. macroH2A1 deposition was affected by infection, creating new heterochromatin domains which did not correlate directly with the levels of expression of the genes in them. The authors conclude that heterochromatin at the nuclear periphery dependent on macroH2A1 and H3K27me3 are critical for nuclear egress of HSV-1 capsids.
The experiments leading to the conclusion that HSV-1 capsids egress the nucleus through channels in the peripheral chromatin confirm previously published results (https://doi.org/10.1038/srep28844). The previously published EM micrographs show a much larger number of nuclear capsids, more consistent with the images in the classical literature, even in conditions when nuclear egress was not inhibited. Figures 1 and 4 show scarce nuclear capsids, even under the conditions when nuclear egress should be inhibited according to the model and analyses. The large enrichment in nuclear capsids in KO cells predicted by the model is not reflected in figure 4a, which shows only a modest increase in nuclear capsid density (the total number of nuclear capsids would be more informative). The number or density of nuclear capsids is not shown in H3K27 "depleted" cells. The robustness of the analyses of the number of capsids at the membrane in H3K27 "depleted" cells is unclear. For example, the analyses could be repeated with different cut offs, such as 2 or 4. If they are robust, then the conclusions will not change when the cutoff value is changed.
We appreciate the reviewer’s observation that to number of capsids we show differs from those published in the publication by Myllys et al. (Sci Rep 2016 PMID 27349677). It is important to note there are several differences between our study and that of Myllys et al. that explain the difference. First, as reviewer 1 pointed out, the Myllys et al. study used three-dimensional soft X-ray tomography combined with cryogenic fluorescence and electron microscopy to observe capsids in 3D rendered nuclei. Since our method uses only single ultrathin 50nm slices of cells, we cannot visualize the total number of capsids per nucleus, rather only per slice, which is why we have averaged slices of many nuclei to generate a statistical comparison between macroH2A1 KO or H3K27me3-depleted and control cells treated at the same time (see response to reviewer 1). Furthermore, these other methods are specialized techniques for 3D imaging that are beyond the scope of our study. Second, the Myllys et al. paper used B cells which are much smaller than HFFs, lending themselves to better tomography studies but not commonly used to study HSV-1 biology. Third, the Myllys et al. paper also used a different MOI and time point than we have. Taken together, these differences account for the disparity in visualizing capsids which is why we quantified capsid number across many images.
We agree with the reviewer that our quantification in the H3K27me3-depleted cells compared to control was somewhat arbitrary. As stated in the response to Reviewer 1 above, in our revised manuscript we have now repeated this quantification to accurately reflect the phenotype observed, that is the chains of capsids lined up at the inner nuclear membrane. To do this, we used two measures: 1) the distance from the INM as less than 200nm and 2) the distance from other capsids as less than 300nm. Taking into account these two measures, we quantified the frequency with which multiple capsids lined up at the INM in WT and H3K27me3-depleted conditions. This is represented in the new Figure 5d. In the WT setting, we observe most often 1 single capsid at the INM, with a small fraction of 2 capsids. However, in the H3K27me3-depleted condition, we observe much greater numbers of capsids at the INM more frequently, as many as 16 at a time, leading to an average of 2-3 capsids at any single location. The source data for this figure are also provided. See lines 589 and Fig 5d.
Furthermore, we have now also carried out live-imaging analysis of single capsids during infection which show the appropriate number of capsids expected when the full nucleus is visible. These results are presented in the new Figure 5 and EV5.
The quantitation of the western blots present no evidence of reproducibility and/or variability. The number of biologically independent experiments analyzed must be stated in each figure and the standard deviation must be presented. As presented, the results do not support the conclusions reached. The quality of western blots should also be improved. it is unclear why figure 2b shows viral gene expression in wild-type cells only, and not in KO or H3K27me3 depleted cells, which are only shown in the supplementary information. These blots presented in Figure S5a and S5b are difficult to evaluate as the signal is rather weak and the controls appear to indicate different loading levels. These blots do not appear to be consistent with the conclusions reached. Some blots (VP16, ICP0 in HFF) appear to indicate a delay in protein expression whereas others (VP16, ICP0 in RPE) appear to indicate earlier expression of higher levels. The claimed "depletion of H3K27me3 is not clear in in figure S5d, in which the levels appear to be highly variable in all cases, without a consistent pattern, with no evidence of reproducibility and/or variability, and using a mostly cytoplasmic protein as loading control. All western blots should be repeated to a publication level quality, the number of independent experiments must be clearly stated in each figure, and the reproducibility and/or variability must be indicated by the standard deviation.
*As reviewer 1 also pointed out, we appreciate that there is some variability with respect to the stated ‘increase’ in these heterochromatin marks during infection. As stated in response to reviewer 1, in our revised manuscript we have included a deeper analysis of these marks from global mass spectrometry that indicates an increase in total levels. Please see response to reviewer 1. *
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In the revised manuscript, we have now included mass spectrometry data mined from Kulej et al. that show peptide counts that reflect increases in the heterochromatin markers described (see new Figure EV1a). Despite this quantitative measure, upon rigorous replicates of our western blots as requested by Reviewer 2, we concluded that the increases originally described are somewhat inconsistent by western blot. This discrepancy between mass spectrometry data and western blot is likely due to the non-linear nature of antibody binding and developing of western blots by the ECL enzymatic reaction. Nevertheless, our genome-wide chromatin profiling showed consistent, reproducible, and statistically significant redistribution of macroH2A1 and H3K27me3 upon HSV-1 infection. Therefore, our revised manuscript now focuses on this redistribution as a reaction to infection and stress responses instead of a global increase as the original manuscript stated. See lines 174, 182, 196, 397 and Fig EV4b-c.
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With respect to viral protein levels, although there is slight variation in the levels of VP16 or ICP0 in RPEs compared to HFFs, we do not feel that this difference is biologically significant as several other measures of viral infection progression are unchanged (viral RNA, viral genome accumulation within infected cells). Furthermore, the significant difference in titers we observe is not explained by slight differences in ICP0 or VP16. Nevertheless, to document this variability in western blot and assuage any concern of impact infection progression, we have repeated each western blot presented in the paper three separate times and used these blots to quantify each relevant protein. Graphs of western blot quantitation can be found in each figure accompanying a western blot as follows:
Western blots:
Figures 3b-c, 4ab, EV1b, EV5a
Quantitation of western blots:
Figures 3d, 4c, EV1c, EV5b-f
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An enhanced analyses of the RNA-seq data, analyzing all individual genes rather than pooling them together, would provide better support to these conclusions. Then, the western blots are useful to show that the changes in mRNA result in changes in the levels of selected proteins.
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*We appreciate the reviewer’s interest in the RNA-seq data, however, we feel that reviewer has not understood the analysis we presented in the initial submission. To clarify, we calculated fold changes for individual genes and did not pool RNA-seq data anywhere in the manuscript. We show boxplots of log2 fold changes of individual genes. Boxplots enable summarization of the salient features of a distribution while still representing individual gene analysis. Here, the distribution being plotted is the log2 fold change of individual genes that intersect with macroH2A1 domains that change due to infection. As such, clusters 1-3 of macroH2A1 domains feature a loss in macroH2A1 due to infection and the boxplots show that the majority of genes are upregulated. To highlight this point further, in our revised manuscript we have included volcano plots of genes intersecting with each cluster also showing the split between the number of genes significantly upregulated and downregulated in each cluster at each time point (see new Figure EV3c). As expected from the boxplots, clusters 1-3 feature a much higher fraction of genes are significantly upregulated, whereas cluster 5 features a higher fraction of genes downregulated with concomitant increase in macroH2A1 due to infection. Taken together with the gene ontology analysis (new Figure Sd), these results support our model in which macroH2A1 is deposited in active regions to block transcription and promote heterochromatin formation. To further support these conclusions, we have also carried out analysis of 4sU-RNA data generated upon salt stress or heat shock and found that the regions defined by gain of macroH2A1 (i.e. clusters 5 and 6) also exhibit significant decreases in new transcription at just 1-2 hours after treatment. These data, which are presented in new Figure EV3b-c, strongly support our model in which macroH2A1 is deposited in genes downregulated upon stress response to generate new heterochromatin. *
Figure S1 raises some questions about the specificity of the macroH2A1 antibody used for CUT&Tag. As expected CUT&Tagging the cellular genome in the KO cells with the specific antibody results in lower signal than with the IgG control antibody. In contrast, viral DNA is CUT&Tagged as efficiently in the KO as in the WT cells, and in both cases significantly above the IgG controls. The simplest interpretation of these results is that the antibody cross-reacts with a protein that binds to HSV-1 genomes. The manuscript must experimentally address this possibility.
We agree with the reviewer that there is a possibility that antibodies cross react. However, we are confident that this is not the case in this scenario for the following reasons:
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*1 – We have carried out immunofluorescence analysis of macroH2A1 or H3K27me3 during HSV-1 infection and observe no overlap with ICP8 staining. We have included these images together with a histogram documenting the lack of overlap in the new Figure EV2f-g. *
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2 – CUT&Tag relies on the Tn5 transposase to insert barcodes into accessible regions of the genome. An inherent limitation of this method during viral infection is that the replicating viral genome is very dynamic and accessible, leading to easier and less specific insertion by the transposase. This is evidenced by the pattern of signal across the viral genome that is completely overlapping in the macroH2A1, H3K27me3 and IgG conditions. Snapshots of the full viral genome are now included in the new Figure EV2c-d.
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*Furthermore, using CUT&Tag with macroH2A1 antibody, we expect the transposition rate to be identical between WT and macroH2A1 KO conditions for the Ecoli and viral genomes. This is because we assume that the transposition in these two genomes is non-specific since there is no macroH2A1 present. Then, we expect the spike-in normalized CUT&Tag enrichment on the viral genome to be the same between WT and macroH2A1 KO conditions. Since IgG should not be affected by macroH2A1 KO, we expect the IgG enrichment to be same between WT and macroH2A1 KO conditions. Thus, non-specific background would result in higher enrichment in an apparent signal on viral genome in the macroH2A1 KO condition. *
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Combined with this expectation for background transposition and the following: 1) the distribution of the CUT&Tag signal across the viral genome is virtually identical between IgG, macroH2A1, and H3K27me3 CUT&Tag signal in WT and macroH2A1 KO cells (see new Figure EV2c-d), 2) that there is no colocalization between macroH2A1 or H3K27me3 with viral genomes by immunofluorescence (see new Figure EV2f-g), and 3) the whole genome correlation of the signals across CUT&Tag samples on the viral genome, but not the host, are virtually identical as presented in a heat map (see new Figure EV1g vs EV2e), we conclude that the viral CUT&Tag signal is noise. Therefore, any analysis of the signal on the viral genomes would not be biologically meaningful.
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Also, Figure S1 shows that the viral genome is CUT&Tag'ed with H3K27me3 antibody as efficiently in macro H2A1 WT and KO cells, and in both cases above the background signal from IgG control antibody. The authors conclude that the signal with the specific antibody "mirrors" that of the control antibody, but "mirroring" is not defined and the actual data show that there is a large increase in signal with the specific antibody. Not surprisingly, the background signal also increases, as the number of genomes increase while infection progresses. The authors conclude that "these results indicated that there was a significant background signal from the viral genome that could not be accounted for", but no evidence supporting this conclusion is presented. The data show clear signal above the background from the viral genome and that this signal is not affected by the presence or absence of macroH2A1. This section of the manuscript has to be thoroughly re-analyzed as there is clear H3K27 signal.
*We agree with the reviewer that as presented in the current manuscript it seems as though there is a real H3K27me3 signal. However, as stated in the above comment, the pattern of this signal matches that of all other conditions, including IgG, suggesting it is not a real signal, cross-reacted or otherwise, but rather an artifact of the methodology. See new Figure EV2. *
The concentration of tazemetostat used is high. Normally, concentrations of around 1µM are used in cells, and 10µM is often cytotoxic (for examplehttps://doi.org/10.1038/s41419-020-03266-3; https://doi.org/10.1158/1535-7163.MCT-16-0840). The effects on H3K27me3 presented in figure S1b appear to be normalized to mock infected treated cells. If so, they do not allow to evaluate the effectivity of the treatment. Cell viability after the four days treatment must be evaluated, the claimed "depletion" of H3K27me3 must be clearly demonstrated (the blots in figure S5 are not sufficient as presented), and levels of different histone methylations must be tested to support the claimed specificity of tazemetostat for H3K27me3 at the high concentrations used.
*While we agree with the reviewer that the cytotoxicity of any inhibitor is an important aspect to take into account, in this instance the reviewer is incorrect. The reviewer has cited papers that highlight the potential use of tazemetostat as a cancer-cell specific treatment for colorectal and B-cell cancers. In both of these cases, the primary conclusion is that tazemetostat’s cytotoxic property is largely corelated to mutation in EZH2. In fact, WT EZH2 treated cells had a more “cytostatic” response, which shows that tazemetostat is not toxic with WT EZH2 (Brach et al. Mol Cancer Ther. 2017, PMID 28835384) as is the case in our system. Furthermore, the Tan et al. study shows a non-transformed human fibroblast (CCD-18co) and embryonic colon epithelial (FHC) as “healthy controls” for their work in colorectal cancer cell lines in Figure 1D. These 2 cell lines, which are comparable to the WT HFF cells we used, show no reduction in viability at a log fold greater concentration than the 10 µM used in our paper. *
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*Nevertheless, we agree with the reviewer that cytotoxicity should be formally ruled out. In our original experiment, we recorded cell counts at the harvested mock, 4-, 8-, and 12 hpi and found no difference in the number of cells over the course of infection (see new Figure EV3e). We also used trypan blue staining as a measure of cell viability upon tazemetostat treatment and found no toxicity. These results are presented in new Figure EV3f. *
Furthermore, we agree with the reviewer that total H3 levels by western blot should be included in any comparison of H3 modification. While these were included in some figures, they were unintentionally omitted in others. In our revised manuscript we have now included these blots together with quantification of triplicate biological samples of H3K27me3 levels normalized to total H3. See new Figures 3, 4, EV1, and EV5.
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Minor comments. Reference No.27 is misquoted in lines 250-251, which state that it shows that "HSV-1 titers, but not viral replication, where reduced upon EZH2 inhibition." The reference actually shows inhibition of HSV-1 infectivity, DNA levels and mRNA for ICP4, ICP22 and ICP27. This reference uses much shorter treatments (12 h and only after infection). It also shows that inhibition of EZH2/1 up regulates expression of antiviral genes.
*We appreciate that the reviewer has pointed out a discrepancy between our results using an EZH2 inhibitor (tazemetostat) and those from reference 27 (Arbuckle et al., mBio, 2017 PMID 28811345) that requires clarification. The reviewer states that the treatments were 12 hours after infection, however, this is incorrect. In the Arbuckle et al. study, the authors used multiple different inhibitors at high doses for short treatments before infection and noted that this caused an upregulation in antiviral genes that blocked infection progression of multiple viruses including HCMV, Ad5 and ZIKA. Importantly, these genes include multiple immune signaling and interferon stimulated genes. In our study, we specifically use a much lower dose of EZH2 inhibitor, with respect to the IC50 value, and waited 3 days to ensure a steady state. In our system, any initial burst of immune response from the inhibitor would likely have subsided by the time we do our infection. Furthermore, supplemental figure EV1 from the Arbuckle et al. study states that EZH1/2 inhibitors do not affect nuclear accumulation of viral genomes and suppress HSV-1 IE expression in an MOI-independent manner (Arbuckle et al. Supplemental Figure 1). These results in fact support our conclusions that it is not any antiviral effect of inhibition of EZH2 that causes the decrease in titers that we observe. *
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To clarify, the IC50 value of the inhibitors used in the Arbuckle et al. study are 10 nmol/L (GSK126) and 4 nmol/L (GSK343). The IC50 is a measurement used to denote the amount of drug needed to inhibit a biological process by 50% and is commonly used in pharmacology to compare drug potency. In the Arbuckle et al. study, GSK126 was used at a concentration range of 15-30 µM, that is 1500-3000x more than the IC50 level as converted from nmol/L to µM, and GSK343 was used at a concentration range of 20-35 µM, that is 5000-8750x more than the IC50 level, to see changes in viral mRNA levels. The IC50 value for tazemetostat is 11 nmol/L which means that one would need to use a much higher molarity of tazemetostat, at least 28 µM which would be 2500x the IC50 value, to achieve the comparable biological changes as the inhibitors used in the Arbuckle et al. study. Thus, we are confident that the 10 µM concentration used in our study is an appropriate and non-toxic amount that would not impact antiviral responses at the dose and times that we used. As shown above and reported in multiple studies (for example: Knutson et al. Molecular Cancer Therapy 2014 PMID 24563539, Tan et al. Cell Death and Disease 2020 PMID 33311453 cited above, and Zhang et al. Neoplasia 2021 PMID 34246076, among others) the concentration of tazemetostat that we used is not toxic to the cells. Importantly, it was also reported that a global decrease in H3K27me3 by EZH2 inhibition using a 10 µM concentration of tazemetostat (here referred to by the identifier EPZ6438) did not impact HSV-1 RNA transcript accumulation measured by bulk sequencing (Gao et al. Antiviral Res 2020 PMID 32014498), consistent with our findings.
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In our revised manuscript, we have now included a discussion of these important points. See lines 409-428.
HFF are primary human cells but they are fibroblasts whereas the primary target of HSV-1 replication is epithelial cells. The wording used "they represent a common site of infection in humans" must be edited
We agree with the reviewer and have updated the text. See lines 109.
Disruption of macroH2A (1 and 2) results in general defects in nuclear architecture, not just peripheral chromatin (https://doi.org/10.1242/jcs.199216;, see also figure 1c and 5a, presenting invaginated and lobulated nuclei). The manuscript would benefit from including a broader discussion of the effects of macroH2A defects on the general nuclear architecture.
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We agree with the reviewer and our revised manuscript now includes a more in-depth discussion of the impact of macroH2A and other heterochromatin marks on nuclear structure. See lines 373-374 and 394.
The title should be edited, as "egress" in virology is commonly used to refer to the egress of virions from the cell, not to the nuclear egress of capsids. Adding the words nuclear and capsid should be sufficient to address this issue.
*We agree with the reviewer and will update the title to read “HSV-1 exploits host heterochromatin for nuclear egress”. Given that we are measuring multiple aspects of infection, we feel that adding the word ‘capsid’ is not necessary. *
It is unclear why preferential changes in expression of housekeeping genes would indicate "stress responses to infection". The rationale for this conclusion must be fully articulated and supported.
We agree with the reviewer that it may not be immediately clear as to why changes in house-keeping gene expression represent a stress response. In a recent study that we cite in our manuscript, Hennig et al. (PLOS Path 2018 PMID 29579120) demonstrate that changes in chromatin accessibility and gene transcription during HSV-1 infection resemble those that occur upon heat shock or salt stress. These results strongly support the model that global transcription changes caused upon stress (heat, salt, infection etc.) result in dramatic alterations to chromatin structure. In support of this notion, in our revised manuscript we now include analysis of these datasets based on our macroH2A1-defined clusters. Importantly, we found that the regions defined by gain of macroH2A1 (i.e. clusters 5 and 6) also exhibit significant decreases in new transcription at just 1-2 hours of exposure to salt and heat stress. These data, which are presented in new Figure EV3b-c, strongly support our model in which macroH2A1 is deposited on active genes to generate heterochromatin as a response to the stress of infection. We also discuss these results further in the revised manuscript, see lines 210-220, 233-236, and 424-426.
Statistical methods must be fully described in materials and methods and the number of biologically independent experiments must be stated in each figure.
*We agree with the reviewer and have included these details in each figure legend. *
Reviewer #2 (Significance (Required)):
The major strengths of the manuscript lie on the comprehensive analyses of the effects of knocking histone macroH2A in the nuclear architecture and chromatin organization. These analyses indicate that peripheral heterochromatin is defective in the KO. Another strength lies on the analyses of the news heterochromatin domains in HSV-1 infected cells. The relationship between the lack of correlation between the changes in gene expression and global heterochromatin domains defined by macroH2A1 with the main conclusion is less clear.
The major weakness is that the data presented do not strongly support the conclusions. Additional experiments are required to support the main conclusion that the effects in peripheral heterochromatin result in a biologically significant effect on capsid egress. The authors should also consider that the additional experimentation may not support the conclusion that macroH2A or H3K27me3 play critical roles in the nuclear egress of capsids.
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*To support our conclusions, we have carried out an entirely different set of experiments to track capsid movement. Bosse et al. PNAS 2015 PMID 26438852 and Aho et al. PLOS Path 2021 PMID 34910768 use live-imaging and single-particle tracking to characterize capsid motion relative to host chromatin. These approaches allowed the authors to discover that infection-induced chromatin modifications promote capsid translocation to the INM. They showed that 1) HSV-1 infection alters host heterochromatin such that open space is induced at heterochromatin boundaries, termed "corrals", in which viral capsids diffuse and 2) the movement of viral capsids through the host heterochromatin is the rate limiting step in HSV-1 nuclear egress. *
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To test our hypothesis that macroH2A1-dependent heterochromatin specifically is required, we collaborated with Dr. Jens Bosse to carry out these same experiments in our macroH2A1 KO and paired control cells. We tracked RFP-VP26 using spinning-disk confocal live imaging to track individual capsid movement within the nucleus. We found that capsids in cells lacking macroH2A1 traveled much shorter distances on average. This is represented graphically by the mean-square displacement (MSD) of capsid movement in macroH2A1 KO cells plateauing at ~0.4 µm2 vs 0.6 µm2 in WT cells, which represents the size of the “corral”, or space through which capsids diffuse. The average corral size in macroH2A1 KO cells is ~300 nm less than the average corral size in WT cells (two-thirds the size). These results are consistent with the finding that macroH2A1 limits chromatin plasticity both in vitro (Muthurajan et al. J Biol Chem 2011 PMID 21532035) and in cells (Kozlowski et al. EMBO Rep 2018 PMID 30177554). These data strongly support our hypothesis that macroH2A1-dependent heterochromatin is critical for the translocation of HSV-1 capsids through the host chromatin to reach the INM. Furthermore, these data support the model in which macroH2A1 allows for the increase of open space induced during infection. Loss of this open space restricts the movement of capsids in the nucleus, as quantified by our live-imaging experiments. These data are now included in the new Figure 5 and EV5 and described in lines 348-372 and 1011-1037.
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NOTE: These experiments were done in a separate lab using the same cells and MOI we used for our TEM studies. It is important to note that because this was done by live imaging where the full nucleus and cell are visible, the appropriate number of capsids is apparent.
Another major weakness is that the results of CUT&Tag of the viral genome are dismissed without proper justification. The authors conclude that the results invalidate the assays, but the results are consistent with cross-reactivity of the macroH2A1 antibody with another protein that interacts with the viral genomes and with H3K27me3 being associated with the viral genomes irrespectively of macroH2A1.
*We agree with the reviewer that as presented the viral genome reads were dismissed without thorough justification. As stated above, we are confident that the patterns we detected do not represent a biologically relevant signal but rather an artifact of the experimental set up. Furthermore, it is well known in the field that normalizing replicating viral genomes during lytic infection in any kind of chromatin profiling technique is fraught with inconsistencies as each cell may have a different copy number of viral genomes at any given time point. Therefore, we feel strongly that any analysis of the viral genome chromatin profile during a lytic replication at this point in time would require single cell sequencing which is beyond the scope of this study. We appreciate that this was not clearly presented in the original manuscript and in our revised submission we have included a full supplemental figure documenting the negative data that support our conclusions (see new Figure EV2). *
If the authors had additional data supporting the claim that these results do not reflect cross-reactivity or association with the viral genomes, these data must be presented. Without that additional data, the conclusions are not supported and these discussions must be removed from the manuscript. The authors may still opt to not analyze any association with the viral genomes, but they should not dismiss them as artifactual without actual evidence to support this claim. Previously published literature is also misquoted.
This study makes an incremental contribution to the previously published evidence showing that HSV-1 capsids egress the nucleus through channels in between the peripheral chromatin. It shows that disruption of the heterochromatin at the nuclear periphery, and the nuclear architecture in general, may have a modest effect on capsid egress. This information may be of interest mostly to a specialized audience focused on the egress of nuclear capsids.
While we agree with the reviewer on many points as stated above, we respectfully disagree that our study is merely an incremental contribution of interest only to a specialized audience focused on nuclear egress. As reviewer 2 states earlier, the strength of our study lies in the “comprehensive analyses of the effects of knocking histone macroH2A in the nuclear architecture and chromatin organization”, which would be of interest to a broad chromatin audience as well as virologists. Together with the new data presented here and a revised manuscript, we feel that our study would be of interest to a broad audience in the chromatin and virology fields as reviewers 1 and 3 also pointed out. Chromatin is generally analyzed in the context of how it might affect gene expression and the impact of chromatin on biological processes such as viral infections, and its structural role in the nucleus is not commonly considered. Here, we demonstrate an important example of the glaring effects of chromatin structure on the biological nuclear process of infection.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Lewis et al. reveal an unexpected role for heterochromatin formation in remodeling the nucleus to facilitate egress of the nuclear-replicating virus HSV1. By performing TEM in HSV1-infected primary human fibroblasts, the authors show that capsids accumulate at the inner nuclear membrane in regions of less densely stained heterochromatin, in agreement with studies in established cell lines. The authors go on to reveal that heterochromatin in the nuclear periphery of HSV1-infected primary fibroblasts was dependent on the histone variant macroH2A1 and is enriched with H3K27me3.CUT & Tag was used to profile macroH2A1 over time during lytic HSV1 infection and showed that both macroH2A1 and H3K27me3 were enriched over newly formed heterochromatic regions 10s-100s of Kb in length in active compartments. Remarkably, loss of macroH2A1 or H3K27me3 reduced released, cell free infection virus progeny and increased intranuclear capsid accumulation without detectably impacting the proportion of mature genome containing capsids, virus genome or protein accumulation. Their finding that newly remodeled heterochromatin forms in HSV infected cells and is a critical determinant for the association of capsids with the inner nuclear membrane is consistent with a critical role in egress.
I have only relatively minor editorial suggestions listed below to improve the manuscript:
Line 92: This subtitle should be revised to more precisely state the findings shown in the Fig 1 data. While the first part of the statement "HSV1 capsids associate with regions of less dense chromatin" is consistent with what is shown, the final phrase "...to escape the nucleus" is an interpretation of the data inferred from the static image.
We agree with the reviewer and have amended our text to more accurately describe the figure. See lines 138-139.
Line 96: I am not sure the statement that fibroblasts represent a "common" site of infection is supported by ref 15. FIbroblasts do, as indicated in ref 15, express the appropriate receptor(s) for virus entry and in culture support robust virus productive growth. However, in human tissue, infection of dermal fibroblasts appears rare, suggesting it may not be a "common" site of infection (PMCID: PMC8865408). Maybe simply revise wording to indicate fibroblasts represent "a site of infection or can be infected in tissue?".
We agree with the reviewer, as was also pointed out by reviewer 2, and have amended the text. See lines 109.
Line 126-127: As written it states that "....regions of the host genome that increase during infection", implying these genome regions are amplified (increase). I think the authors mean that infection increases binding of mH2A1 and H3K27me3 to broad regions of the host genome. Please clarify.
We agree with the reviewer that this was written ambiguously. As was pointed out by reviewers 1 and 2, the increase in these marks depends on the type of measurement. Therefore, we have modified the text in a revised manuscript to focus instead on the redistribution of these marks during infection. See line 138-139.
FIgS1, a,b,c,d: please indicate that 4,8,12 indicate hpi, correct? And indicate that in the legend M indicates Mock.
This is correct and we have updated this in the figure legend. See lines 625-627.
Line 197: "active compartments". Do the authors mean transcriptionally active compartments? Please clarify
This is correct and have clarified this in the text. See line 248.
Line 232: please replace "productive" with "infectious"
We agree with the reviewer and have amended our text. See line 295.
Line 233 - The authors conclude mH2A1 is important for egress, ruling out assembly before even bringing it up. As I read on, it is clear the authors addressed this important issue later on in the manuscript. That said, it was a bit jarring to conclude egress is important without addressing the assembly possibility at this juncture in the manuscript. One way to remedy this would be to move the Fig S6 assembly/capsid type data (lines 286-297, Fig S6) and surrounding text earlier to support the conclusion that mH2A1 did not detectably influence assembly, but is important for egress.
*We agree with the reviewer that the order of presentation makes it difficult to follow. Our revised manuscript now includes these important data within the same figure. See new Figure 5. *
Line 244: "progeny production" - it would be helpful to specify "cell free or released infectious virus progeny"
Line 248: change "produced" to released"
Line 273 replace "productive" with "infectious virus progeny released from infected cells"
Fig S5c: Was the plaque assay performed on cell free supernatants? This should be indicated.
We agree with the reviewer and have made all these changes in the text. See lines 285-287.
Reviewer #3 (Significance (Required)):
The experiments are well executed, the data are solid with appropriate statistical analysis and their analysis sufficiently rigorous, and the manuscript is clearly written. Moreover, the finding that HSV manipulates host heterochromatin marks to facilitate nuclear egress is significant and exciting. The work reveals an unexpected role for newly assembled heterochromatin in egress of nuclear replicating viruses like HSV1.
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Referee #3
Evidence, reproducibility and clarity
Lewis et al. reveal an unexpected role for heterochromatin formation in remodeling the nucleus to facilitate egress of the nuclear-replicating virus HSV1. By performing TEM in HSV1-infected primary human fibroblasts, the authors show that capsids accumulate at the inner nuclear membrane in regions of less densely stained heterochromatin, in agreement with studies in established cell lines. The authors go on to reveal that heterochromatin in the nuclear periphery of HSV1-infected primary fibroblasts was dependent on the histone variant macroH2A1 and is enriched with H3K27me3.CUT & Tag was used to profile macroH2A1 over time during lytic HSV1 infection and showed that both macroH2A1 and H3K27me3 were enriched over newly formed heterochromatic regions 10s-100s of Kb in length in active compartments. Remarkably, loss of macroH2A1 or H3K27me3 reduced released, cell free infection virus progeny and increased intranuclear capsid accumulation without detectably impacting the proportion of mature genome containing capsids, virus genome or protein accumulation. Their finding that newly remodeled heterochromatin forms in HSV infected cells and is a critical determinant for the association of capsids with the inner nuclear membrane is consistent with a critical role in egress.
I have only relatively minor editorial suggestions listed below to improve the manuscript:
Line 92: This subtitle should be revised to more precisely state the findings shown in the Fig 1 data. While the first part of the statement "HSV1 capsids associate with regions of less dense chromatin" is consistent with what is shown, the final phrase "...to escape the nucleus" is an interpretation of the data inferred from the static image.
Line 96: I am not sure the statement that fibroblasts represent a "common" site of infection is supported by ref 15. FIbroblasts do, as indicated in ref 15, express the appropriate receptor(s) for virus entry and in culture support robust virus productive growth. However, in human tissue, infection of dermal fibroblasts appears rare, suggesting it may not be a "common" site of infection (PMCID: PMC8865408). Maybe simply revise wording to indicate fibroblasts represent "a site of infection or can be infected in tissue?".
Line 126-127: As written it states that "....regions of the host genome that increase during infection", implying these genome regions are amplified (increase). I think the authors mean that infection increases binding of mH2A1 and H3K27me3 to broad regions of the host genome. Please clarify.
FIgS1, a,b,c,d: please indicate that 4,8,12 indicate hpi, correct? And indicate that in the legend M indicates Mock.
Line 197: "active compartments". Do the authors mean transcriptionally active compartments? Please clarify
Line 232: please replace "productive" with "infectious"
Line 233 - The authors conclude mH2A1 is important for egress, ruling out assembly before even bringing it up. As I read on, it is clear the authors addressed this important issue later on in the manuscript. That said, it was a bit jarring to conclude egress is important without addressing the assembly possibility at this juncture in the manuscript. One way to remedy this would be to move the Fig S6 assembly/capsid type data (lines 286-297, Fig S6) and surrounding text earlier to support the conclusion that mH2A1 did not detectably influence assembly, but is important for egress.
Line 244: "progeny production" - it would be helpful to specify "cell free or released infectious virus progeny"
Line 248: change "produced" to released"
Line 273 replace "productive" with "infectious virus progeny released from infected cells"
Fig S5c: Was the plaque assay performed on cell free supernatants? This should be indicated.
Significance
The experiments are well executed, the data are solid with appropriate statistical analysis and their analysis sufficiently rigorous, and the manuscript is clearly written. Moreover, the finding that HSV manipulates host heterochromatin marks to facilitate nuclear egress is significant and exciting. The work reveals an unexpected role for newly assembled heterochromatin in egress of nuclear replicating viruses like HSV1.
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Referee #2
Evidence, reproducibility and clarity
The manuscript "HSV-1 exploits heterochromatin for egress" describes the effects of heterochromatin at the nuclear periphery, macroH2A1 or H3K27me3 on HSV-1 replication and egress. Knocking out macroH2A1 or depleting H3K27me3 with high concentrations of tazemetostat depleted heterochromatin at the nuclear periphery, may not have affected HSV-1 protein expression and modestly inhibited the production of cell-free infectivity and HSV-1 genomes. macroH2A1 deposition was affected by infection, creating new heterochromatin domains which did not correlate directly with the levels of expression of the genes in them. The authors conclude that heterochromatin at the nuclear periphery dependent on macroH2A1 and H3K27me3 are critical for nuclear egress of HSV-1 capsids.
The experiments leading to the conclusion that HSV-1 capsids egress the nucleus through channels in the peripheral chromatin confirm previously published results (https://doi.org/10.1038/srep28844). The previously published EM micrographs show a much larger number of nuclear capsids, more consistent with the images in the classical literature, even in conditions when nuclear egress was not inhibited. Figures 1 and 4 show scarce nuclear capsids, even under the conditions when nuclear egress should be inhibited according to the model and analyses. The large enrichment in nuclear capsids in KO cells predicted by the model is not reflected in figure 4a, which shows only a modest increase in nuclear capsid density (the total number of nuclear capsids would be more informative). The number or density of nuclear capsids is not shown in H3K27 "depleted" cells. The robustness of the analyses of the number of capsids at the membrane in H3K27 "depleted" cells is unclear. For example, the analyses could be repeated with different cut offs, such as 2 or 4. If they are robust, then the conclusions will not change when the cutoff value is changed.
The quantitation of the western blots present no evidence of reproducibility and/or variability. The number of biologically independent experiments analyzed must be stated in each figure and the standard deviation must be presented. As presented, the results do not support the conclusions reached. The quality of western blots should also be improved. it is unclear why figure 2b shows viral gene expression in wild-type cells only, and not in KO or H3K27me3 depleted cells, which are only shown in the supplementary information. These blots presented in Figure S5a and S5b are difficult to evaluate as the signal is rather weak and the controls appear to indicate different loading levels. These blots do not appear to be consistent with the conclusions reached. Some blots (VP16, ICP0 in HFF) appear to indicate a delay in protein expression whereas others (VP16, ICP0 in RPE) appear to indicate earlier expression of higher levels. The claimed "depletion of H3K27me3 is not clear in in figure S5d, in which the levels appear to be highly variable in all cases, without a consistent pattern, with no evidence of reproducibility and/or variability, and using a mostly cytoplasmic protein as loading control. All western blots should be repeated to a publication level quality, the number of independent experiments must be clearly stated in each figure, and the reproducibility and/or variability must be indicated by the standard deviation. An enhanced analyses of the RNA-seq data, analyzing all individual genes rather than pooling them together, would provide better support to these conclusions. Then, the western blots are useful to show that the changes in mRNA result in changes in the levels of selected proteins.
Figure S1 raises some questions about the specificity of the macroH2A1 antibody used for CUT&Tag. As expected CUT&Tagging the cellular genome in the KO cells with the specific antibody results in lower signal than with the IgG control antibody. In contrast, viral DNA is CUT&Tagged as efficiently in the KO as in the WT cells, and in both cases significantly above the IgG controls. The simplest interpretation of these results is that the antibody cross-reacts with a protein that binds to HSV-1 genomes. The manuscript must experimentally address this possibility.
Also, Figure S1 shows that the viral genome is CUT&Tag'ed with H3K27me3 antibody as efficiently in macro H2A1 WT and KO cells, and in both cases above the background signal from IgG control antibody. The authors conclude that the signal with the specific antibody "mirrors" that of the control antibody, but "mirroring" is not defined and the actual data show that there is a large increase in signal with the specific antibody. Not surprisingly, the background signal also increases, as the number of genomes increase while infection progresses. The authors conclude that "these results indicated that there was a significant background signal from the viral genome that could not be accounted for", but no evidence supporting this conclusion is presented. The data show clear signal above the background from the viral genome and that this signal is not affected by the presence or absence of macroH2A1. This section of the manuscript has to be thoroughly re-analyzed as there is clear H3K27 signal.
The concentration of tazemetostat used is high. Normally, concentrations of around 1µM are used in cells, and 10µM is often cytotoxic (for example https://doi.org/10.1038/s41419-020-03266-3; https://doi.org/10.1158/1535-7163.MCT-16-0840). The effects on H3K27me3 presented in figure S1b appear to be normalized to mock infected treated cells. If so, they do not allow to evaluate the effectivity of the treatment. Cell viability after the four days treatment must be evaluated, the claimed "depletion" of H3K27me3 must be clearly demonstrated (the blots in figure S5 are not sufficient as presented), and levels of different histone methylations must be tested to support the claimed specificity of tazemetostat for H3K27me3 at the high concentrations used.
Minor comments.
Reference No.27 is misquoted in lines 250-251, which state that it shows that "HSV-1 titers, but not viral replication, where reduced upon EZH2 inhibition." The reference actually shows inhibition of HSV-1 infectivity, DNA levels and mRNA for ICP4, ICP22 and ICP27. This reference uses much shorter treatments (12 h and only after infection). It also shows that inhibition of EZH2/1 up regulates expression of antiviral genes.
HFF are primary human cells but they are fibroblasts whereas the primary target of HSV-1 replication is epithelial cells. The wording used "they represent a common site of infection in humans" must be edited
Disruption of macroH2A (1 and 2) results in general defects in nuclear architecture, not just peripheral chromatin (https://doi.org/10.1242/jcs.199216;, see also figure 1c and 5a, presenting invaginated and lobulated nuclei). The manuscript would benefit from including a broader discussion of the effects of macroH2A defects on the general nuclear architecture.
The title should be edited, as "egress" in virology is commonly used to refer to the egress of virions from the cell, not to the nuclear egress of capsids. Adding the words nuclear and capsid should be sufficient to address this issue.
It is unclear why preferential changes in expression of housekeeping genes would indicate "stress responses to infection". The rationale for this conclusion must be fully articulated and supported.
Statistical methods must be fully described in materials and methods and the number of biologically independent experiments must be stated in each figure.
Significance
The major strengths of the manuscript lie on the comprehensive analyses of the effects of knocking histone macroH2A in the nuclear architecture and chromatin organization. These analyses indicate that peripheral heterochromatin is defective in the KO. Another strength lies on the analyses of the news heterochromatin domains in HSV-1 infected cells. The relationship between the lack of correlation between the changes in gene expression and global heterochromatin domains defined by macroH2A1 with the main conclusion is less clear.
The major weakness is that the data presented do not strongly support the conclusions. Additional experiments are required to support the main conclusion that the effects in peripheral heterochromatin result in a biologically significant effect on capsid egress. The authors should also consider that the additional experimentation may not support the conclusion that macroH2A or H3K27me3 play critical roles in the nuclear egress of capsids. Another major weakness is that the results of CUT&Tag of the viral genome are dismissed without proper justification. The authors conclude that the results invalidate the assays, but the results are consistent with cross-reactivity of the macroH2A1 antibody with another protein that interacts with the viral genomes and with H3K27me3 being associated with the viral genomes irrespectively of macroH2A1. If the authors had additional data supporting the claim that these results do not reflect cross-reactivity or association with the viral genomes, these data must be presented. Without that additional data, the conclusions are not supported and these discussions must be removed from the manuscript. The authors may still opt to not analyze any association with the viral genomes, but they should not dismiss them as artifactual without actual evidence to support this claim. Previously published literature is also misquoted.
This study makes an incremental contribution to the previously published evidence showing that HSV-1 capsids egress the nucleus through channels in between the peripheral chromatin. It shows that disruption of the heterochromatin at the nuclear periphery, and the nuclear architecture in general, may have a modest effect on capsid egress. This information may be of interest mostly to a specialized audience focused on the egress of nuclear capsids.
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Referee #1
Evidence, reproducibility and clarity
Summary
This study by Lewis et al. examines the role of heterochromatin in the nuclear egress of herpesvirus capsids. They show that heterochromatin markers macroH2A1 and H3K27me3 are enriched at specific genome regions during the infection. They also show that when macroH2A1 is removed or H3K27me3 is depleted (both of which reduce the amount of heterochromatin at the nuclear periphery), the capsids are not able to egress as effectively. This is interesting since it could be argued that heterochromatin acts as a hindrance to the transport of viral capsids to the nuclear envelope and that the loss of it would allow capsids to reach the nuclear envelope more easily. However, this paper seems to show that heterochromatin formation, on the contrary, is necessary for efficient egress. Overall, the study seems comprehensive. The methodology is solid, and the experiments are very well controlled. However, some issues need to be addressed before publication.
Major comments
- In line 49, the authors state, "Like most DNA viruses, herpes simplex virus (HSV-1) takes advantage of host chromatin factors both by incorporating histones onto its genome to promote gene expression and by reorganizing host chromatin during infection". In addition, HSV1 expression can be hindered by the host's interferon response via histone modifications. Ref. Johnson KE, Bottero V, Flaherty S, Dutta S, Singh VV, Chandran B. IFI16 restricts HSV-1 replication by accumulating on the HSV-1 genome, repressing HSV-1 gene expression, and directly or indirectly modulating histone modifications. PLoS Pathog. 2014 Nov 6;10(11):e1004503. doi: 10.1371/journal.ppat.1004503. Erratum in: PLoS Pathog. 2018 Jun 6;14(6):e1007113. PMID: 25375629; PMCID: PMC4223080.
- Reference 5 is misquoted in the sentence, "This redistribution of host chromatin results in a global increase in heterochromatin5". In that reference, the amount of heterochromatin is not analyzed in any way. However, that particular paper shows that the transport of capsid through chromatin is the rate-limiting step in nuclear egress, which is important considering this study. Further, the article by Aho et al. shows that when the infection proceeds capsids can more easily traverse from the replication compartment into the chromatin, which means that infection can modify chromatin for easier capsid transport. For that reason, the article is an important reference, but it needs to be cited correctly.
- The term heterochromatin channel at lines 54, 102, and 303 is misleading since the channels seen in the original referred paper are less dense chromatin areas. Also, this term is not used in the original paper where the phenomenon was first described. These less dense interchromatin channels were found by soft-X-ray tomography imaging and analyses, not by staining.
- It is difficult to visualize chromatin using TEM microscopy. The values of peripheral chromatin thickness given in Figure 1e (5-15 nm) do not seem realistic given that the thickness of just one strand of histone-wrapped DNA is 11 nm. Why are the two values for WT (in the top and bottom parts) different? If you can get so different values for WT, it is a bit worrisome (switching the WT results between the top and bottom parts of Fig. 1e would for example result in very different conclusions on the effect of macroH2A1 KO for the thickness of the chromatin layer).
- In lines 134-137 it says that "The enrichment of macroH2A1 and H3K27me3 was observed as large domains that were gained upon viral infection (Fig 2a), suggesting that the host landscape is altered upon infection. These gains were reflected in an increase in total protein levels measured by western blot (Fig 2b)." However, the protein levels of H3K27me3 do not seem to increase during infection. In other presented data as well (Figs. 2a, 2b, 2c, S2a) it is difficult to justify the statement that H3K27me3 is enriched in infection. When this is the case, the conclusion that the amount of heterochromatin increases in the infection (the quotation above and the one in line 315) is not supported. The statement in line 315 is also not specific since it is unclear what "newly formed heterochromatin increases" means.
- Quantitation of viral capsid location in H3K27me3-depleted cells seems somewhat arbitrary. It would have been more robust to calculate the number of capsids per unit length of the nuclear envelope with and without depletion.
- In lines 300-302 it says "Elegant electron microscopy work showed that HSV-1 infection induces host chromatin redistribution to the nuclear periphery2,8." However, the redistribution data in reference 8 is based on soft x-ray tomography and not on electron microscopy."
- The authors bundle together the effects of macroH2A1 removal and H3K27me3 depletion by saying that they both decrease the amount of heterochromatin at the nuclear periphery and therefore hinder capsid egress. This seems overly simplistic and macroH2A1 and H3K27me3 seem to act very differently, which is manifested in the drastic difference in nuclear capsid localization between the two cases. This difference needs to be discussed more.
Major comments
Line 45: Nuclear replicating viruses -> Nuclear-replicating viruses
Line 56: is -> are
Line 64: 25kDa -> 25 kDa
Line 159: macroH2A1 cells -> macroH2A1 KO cells
Line 289: The term gDNA is rarely used for viral DNA. Replace gDNA with viral DNA.
Line 405: 8hpi -> 8 hpi
Line 449: mm2 -> μm2 "Scale bar as indicated" words can be removed in the figure legends or at least should not be repeated many times within one figure legend.
Significance
These findings would appeal to a broad audience in the field of virology. Specifically, the researcher in the fields of virus-cell and virus-nucleus interactions. This manuscript analyses herpesvirus-induced structural changes in the chromatin structure and organization in the nucleus that are also likely to affect the intranuclear transport of viral capsids.
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Reply to the reviewers
__We thank the reviewers for their detailed comments, constructive feedback and insightful suggestions to improve our research and manuscript. Our detailed responses are in bold. __
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary This paper by Styles et al describes the effect of propylene glycol (PG) on a range of enveloped viruses, focusing mainly on IAV and SARS-Cov2. The direct virucidal effect is shown both in vitro and in vivo, as well as the effect of vaporized PG on airborne IAV and SARS-Cov-2. This is a well-performed and very clear study.
Major comments
The claims and conclusions are in general well supported by the data, yet I have some comments.
- Interestingly, there were variations in the effect of PG on the different pseudoviruses. Surprising as I assumed that the effect of PG would be mainly on the lipid envelope, as you also mention in the discussion. It is suggested that PG therefore also has an effect on the conformation of the surface proteins. This can be easily tested, does the addition of PG result in a changed recognition by antibodies targeting these surface proteins? This information would be very valuable for your manuscript.
__Many thanks for this excellent suggestion. To address this we are working in collaboration with Dr Joe Grove (Centre for Virus Research, University of Glasgow) using immobilised purified pseudovirus particles +/- PG treatment. Immunostaining against pseudovirus glycoproteins and their HIV gagpol capsid core enables comprehensive analysis of particle composition and integrity. Our preliminary experiments since submission have shown treatment with >60% PG increased gagpol signal, indicating compromised envelope integrity of equivalent magnitude to direct permeabilisation (positive control condition). At PG concentrations between 25 – 60% we’ve observed a significant reduction in glycoprotein signal preceding substantial envelope disruption. We are repeating these experiments in parallel with infectivity assays to assess how these changes in glycoprotein antibody recognition and envelope permeabilization relate to pseudovirus entry. We anticipate these studies will be completed within 8 weeks. __
__In addition, we are optimising cryo-EM protocols for analysis of SARS-CoV-2 virus particles +/- PG treatment to directly visualise the impact of PG on virus structure, in collaboration with Dr Paul Simpson (EM Centre, Imperial College). __
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Figure S1 shows that although the clinical scores are better, the viral load is not reduced by the addition of PG to the inoculum. This is not mentioned in the main text. This seems very relevant information and should be presented in the main text. Can you please elaborate on this.
We agree that the virological and immunological findings are of interest, and have added the following to the main text “____Analysis of the remaining mice showed PG inhalation reduced clinical score and bronchioalveolar lavage cell counts on day 5, despite equivalent nasal and airway viral loads at this late time post-infection.” Examining longitudinal weight loss and survival was the primary objective of this experimental design, which only allowed analysis of BAL cell counts and viral loads in the remaining mice at the experimental end point (day 5 post-infection). As 3 mice in the IAV only group reached the severity limit on day 3, we did not have the statistical power to detect significant differences in clinical scores, lung infiltrates or viral loads. IAV burden in the nose and lung usually reach peak levels at day 2/3 post-infection, and further experiments to look at the magnitude of viral replication and immunopathology over the course of infection in PG-treated mice will be important for future translational studies. As such, we have added the following to the Fig. S1 legend “____Further investigations are required to determine whether PG treatment reduces inflammatory cell infiltrates or peak IAV loads on days 2/3 post-infection.”
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Optional: It would be very interesting to see the effect of vaporized PG on viral transmission between mice/ferrets of a highly infectious virus (eg Sendai virus). This would give an idea if the PG also works on more biological respiratory droplets.
We wholeheartedly agree. To perform these additional studies requires additional funding and project licence amendments so unfortunately must lie beyond the scope of this study.
Minor comments
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The caption of Fig1D mentions that the mice are inoculated with 50ml total volume. I presume this should be µl.
__Absolutely, thank you for spotting this error and it is now corrected. __
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Please put the axis of the viral titer graph now in Fig s1 in PFU/lung or nasal cavity? This would be more informative.
__Many thanks for this suggestion, now changed to PFU/lung along with BAL cells/lung. __
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Typo in 'PG has broad-spectrum virucidal activity' paragraph: titre should be titer.
__Titre is the British English spelling whereas titer is the American English spelling. We will comply with the journal specification on American versus British English in the final text. __
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Is allergy to PG an issue that could have an effect on further development of this antiviral strategy?
A recent review (Pemberton & Kimber ____https://doi.org/10.1016/j.yrtph.2023.105341____) of the evidence on this topic concludes “..the weight of evidence points to PG possessing no, or only extremely modest, skin sensitising properties.” There is anecdotal evidence of PG potentially acting as a very weak allergen in humans with underlying/pre-disposing skin conditions. Further clinical development of PG as a virucide would need to balance its significant benefits against this when “..the risk for sensitisation to PG on uncompromised skin seems to be extremely low.”
Reviewer #1 (Significance (Required)):
This study is highly relevant. It proposes an easy and possibly efficacious method to prevent airborne transmission of a broad range of (enveloped) viruses.
A strength of this study is the set-up with the virus transmission tunnel. This nicely shows the effect of the vaporized PG on airborne IAV and SARS-Cov-2. A limitation is that the researchers did not analyze non-enveloped viruses, which should be done in a follow-up study.
__Many thanks for these comments. Since submission we have extended our investigations to non-enveloped rotaviruses in collaboration with Dr Alex Borodavka (Department of Biochemistry, University of Cambridge). Preliminary experiments have shown that rotavirus infectivity decreased from ~108 PFU/mL to undetectable levels (2 PFU/mL) following incubation with 50% PG at 37oC for 1h compared to 0% PG control. We are now testing different temperatures, PG concentrations and incubation durations and will include this new data in our revised submission. __
There does not seem to be any recent research investigating this compound as an antiviral tool. Although the compound was tested for its antimicrobial properties in the 1940s, this has not been continued for unclear reasons (?).
__We speculate the rapid development and clinical testing of conventional antibiotics during this period (culminating the Nobel prize for Medicine for Flemming, Florey and Chain in 1945) is responsible for the abrupt cessation of research into PG as an antimicrobial despite its obvious efficacy. We were unaware of these studies when we commenced our research into PG and this literature seems to have flown completely under the radar. __
This is very valuable research in this world recovering from the recent SARS-Cov-2 pandemic. More mechanistic studies need to be performed to understand how this compound exerts its antiviral and antimicrobial effect.
A more specialized audience will be interested in this study.
My field of expertise: RSV, PIV, antivirals
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
SUMMARY: This study investigates the inactivation potential of propylene glycol against a number of important human respiratory viruses, including influenza A virus and SARS-CoV-2. Potent antiviral activity of propylene glycol was demonstrated for viruses in bulk solutions, in 2uL droplets on a variety of surfaces, and within aerosols. Additionally, propylene glycol was added to viruses prior to infection of live animals, and this treatment significantly improved animal survival outcomes and reduced their weight loss and clinical scores compared to animals infected with non-treated virus. Levels of propylene glycol utilised in the study were substantially less than those classified as well-tolerated by mammals. Overall, authors demonstrate that propylene glycol is a strong yet safe virucide that could be used to control the spread of viral infections.
MAJOR COMMENTS:
Claims and conclusions are very well-supported by the data presented. Both the data presentation and method details are sufficient to reproduce the experiments. Authors might like to add precise gram concentrations of PG in addition to the percentages listed in the manuscript, either g/L or g/kg as appropriate. This would also allow easier comparison of the tested PG does to those published as safe doses for mammals, which are often given as g/kg.
Many thanks for this suggestion. These calculations and the concentration are now in a new “supplementary calculations” section in the supplementary material and the Figure 1 legend directs readers to them: “____See supplementary materials for % PG solution (v/v) to g/L conversion and mouse PG dose in g/kg.”
Replicates are more than adequate, and statistical analysis is mostly robust. I have one concern of statistical analyses performed in Figure 2D. In the SARS1 coronavirus panel of this figure, statistical analysis indicates that 10% PG causes significantly more infection (in RLU) than 0% PG. The same is true for the SARS-CoV-2 Alpha panel. The differences in infection level between 0% and 10% PG by eye are minimal, and authors should consider whether this statistical test is the most robust/appropriate, and whether these particular statistical differences are biologically meaningful to report. If analyses remain as is, authors should postulate why this small increase in infection level was observed for some lentivirus pseudotypes at 10% PG compared to controls.
__Many thanks to the reviewer for highlighting this. Whilst Dunnet's post-test we employed does indeed suggest a significant difference between 10% and 0% PG for some of the pseudoviruses, another post-test (Bonferroni's) does not. The reviewer correctly questions the biological significance of these very small differences in luciferase activity. In our experience, effect sizes of less than half a log unit are not biologically meaningful and certainly we make no claims that 10% PG is affecting pseudovirus entry in these experiments. To avoid any ambiguity therefore, we have removed the "*" from the relevant graphs and have restricted reporting of statistical significance to those conditions with p
OPTIONAL - The study could be further enhanced by preliminary mechanistic investigation into the action of propylene glycol (PG) - for example, authors postulate that PG may act via disruption of the lipid membrane, and this could be supported by EM imaging of a few PG-treated viruses. Alternatively, non-enveloped viruses could be tested for sensitivity to determine the importance of the envelope. Authors mention this in the discussion as being outside the scope, though testing one or two non-enveloped viruses would elevate the work substantially, as it opens the possibility for PG to also protect against non-enveloped respiratory viruses such as rhinovirus, as well as enteric viruses.
__As explained in detail in our response to reviewer 1 and our revision plan, we are addressing these excellent suggestions in three ways for the revised manuscript: __
- __Collaboration with Dr Joe Grove’s group to address PG's action on viral surface glycoproteins, virus composition and envelope integrity. __
- EM imaging of PG-treated SARS-CoV-2 with Dr Paul Simpson.
- Collaboration with Dr Alex Borodavka’s group to investigate PG-mediated virucidal activity against non-enveloped rotaviruses.
OPTIONAL - All influenza work in this study used the lab-adapted isolate A/PR8. This is a very useful and representative virus, though the study may benefit from comparison of the PG-mediated inactivation kinetic of A/PR8 with that of a more recent clinical isolate of influenza A. This could be a useful supplementary figure.
__Many thanks for this suggestion. We agree that examining the inactivation kinetics of different flu strains in vitro would be informative and will endeavour to include this in our revised manuscript if these experiments can be performed within an appropriate time frame. We know PG is effective against ____the 2009 pandemic strain H1N1 A/California/7/2009 as this was used for our in vivo experiments as listed in the methods section. For clarity we have added this information into the main text. __
MINOR COMMENTS:
Could authors generate (or reference) a robust correlation curve between IAV plaque area (px^2) that is calculated by the ColonyArea plugin, in relation to actual PFU/mL as counted by eye? This would help the reader to understand the decrease in viral titre that PG mediates from experiments conducted in the aerosol tunnel, e.g. does a decrease from 10^5 px^2 down to 10^3 px^2 equate to a 2-log10 reduction in PFU, or it is less than this?
This correlation could also be used to generate a detection limit for Plaque Area (px^2) that is equivalent to 1 or 10 PFU/well, which could then be added to graphs in Figure 3, S4, S5. This will help the reader understand if detection of 10^3 px^2 (for example) is quite high, or if it is already close to detection limits.
__The reviewer makes an interesting suggestion. As can be seen from the requested representation of those data (reviewer figure 1, replotted from Fig 3D), for lower nebulised input virus amounts where infection did not transmit beyond the first plate there is a very respectable linear correlation between plaque number and plaque area (R2=0.72, Spearman’s r=0.98, p2 – 103 px2 reflects the 1 – 10 plaque detection limit. However, when performing initial controls we found this relationship soon departs from linearity as input virus amount increases; essentially plaques begin to overlap with each other on the plates closest to the nebuliser. We are concerned it might be inappropriate to present PFU/well extrapolated from plaque areas collected from lower input virus experiments, since this could potentially mislead or confuse the reader about the fidelity and nature of the transmission tunnel experimental system. Moreover, for this particular type of assay plaque area affords a much greater dynamic range than PFU/well, which is essential for demonstrating the range of PG’s virucidal activity with higher input virus, range of vapor concentrations and over different transmission distances. Taking these considerations into account, and unavoidable idiosyncrasies of testing virus transmission under more “natural” conditions (e.g. direct virus deposition on cell monolayers prohibiting serial dilution for exact PFU determination), we have decided to continue reporting plaque area only for quantification of transmission tunnel data - the parameter that was actually measured. This accurately reflects the extensive cell clearance under control conditions, where the monolayer is completely disrupted, compared to the protective effect of PG vapor, where the monolayer is largely intact with limited plaques. We hope the reviewer understands our reasoning. __
To communicate this, we have added the following sentence to the methods section:
__“Plaque area shows a strong linear correlation with plaque number at lower viral inputs (R2=0.72, Spearman’s r=0.98, p
Can authors specify if the PEG was mixed with virus immediately prior to inoculation of animals, or was it mixed ahead of time (e.g. 30 mins or 1 hour ahead of administration)? In this case, low-level inactivation of viruses in bulk solution may have occurred. Figure 1C shows minimal inactivation should have occurred with 20% PG over this time-course at room-temperature, but this detail would be helpful to specify.
__Many thanks for bringing this oversight to our attention. IAV was mixed with PG immediately prior to inoculation of animals (
Figure legend of Fig 1. D) currently reads "... inoculated with 50mL..." , should this be 50uL?
__It should, thank you for spotting this error and it is now corrected. __
Reviewer #2 (Significance (Required)):
This study offers a robust proof of concept that PG can be applied to viral disinfection of a large range of enveloped viruses in a variety of settings (aerosol, fomites, in vivo, etc). This work now requires follow-on clinical studies to establish optimal and safe PG levels for viral inactivation in real-world settings, and comprehensive testing of safety risks from long term PG-exposure before this virucide can become clinically applied. This impact of this primary research could be considered broad and translational.
The audiences anticipated to be interested in these results are varied, and include those in virology fields, medical personnel, aerosol scientists, disinfection experts, and public health/ policy makers.
Field of expertise of reviewer: virology, animal infections, immunology, aerosol-borne influenza virus.
-
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Referee #2
Evidence, reproducibility and clarity
Summary
This study investigates the inactivation potential of propylene glycol against a number of important human respiratory viruses, including influenza A virus and SARS-CoV-2. Potent antiviral activity of propylene glycol was demonstrated for viruses in bulk solutions, in 2uL droplets on a variety of surfaces, and within aerosols. Additionally, propylene glycol was added to viruses prior to infection of live animals, and this treatment significantly improved animal survival outcomes and reduced their weight loss and clinical scores compared to animals infected with non-treated virus. Levels of propylene glycol utilised in the study were substantially less than those classified as well-tolerated by mammals. Overall, authors demonstrate that propylene glycol is a strong yet safe virucide that could be used to control the spread of viral infections.
Major comments
Claims and conclusions are very well-supported by the data presented. Both the data presentation and method details are sufficient to reproduce the experiments. Authors might like to add precise gram concentrations of PG in addition to the percentages listed in the manuscript, either g/L or g/kg as appropriate. This would also allow easier comparison of the tested PG does to those published as safe doses for mammals, which are often given as g/kg.
Replicates are more than adequate, and statistical analysis is mostly robust. I have one concern of statistical analyses performed in Figure 2D. In the SARS1 coronavirus panel of this figure, statistical analysis indicates that 10% PG causes significantly more infection (in RLU) than 0% PG. The same is true for the SARS-CoV-2 Alpha panel. The differences in infection level between 0% and 10% PG by eye are minimal, and authors should consider whether this statistical test is the most robust/appropriate, and whether these particular statistical differences are biologically meaningful to report. If analyses remain as is, authors should postulate why this small increase in infection level was observed for some lentivirus pseudotypes at 10% PG compared to controls.
OPTIONAL - The study could be further enhanced by preliminary mechanistic investigation into the action of propylene glycol (PG) - for example, authors postulate that PG may act via disruption of the lipid membrane, and this could be supported by EM imaging of a few PG-treated viruses. Alternatively, non-enveloped viruses could be tested for sensitivity to determine the importance of the envelope. Authors mention this in the discussion as being outside the scope, though testing one or two non-enveloped viruses would elevate the work substantially, as it opens the possibility for PG to also protect against non-enveloped respiratory viruses such as rhinovirus, as well as enteric viruses.
OPTIONAL - All influenza work in this study used the lab-adapted isolate A/PR8. This is a very useful and representative virus, though the study may benefit from comparison of the PG-mediated inactivation kinetic of A/PR8 with that of a more recent clinical isolate of influenza A. This could be a useful supplementary figure.
Minor comments
Could authors generate (or reference) a robust correlation curve between IAV plaque area (px^2) that is calculated by the ColonyArea plugin, in relation to actual PFU/mL as counted by eye? This would help the reader to understand the decrease in viral titre that PG mediates from experiments conducted in the aerosol tunnel, e.g. does a decrease from 10^5 px^2 down to 10^3 px^2 equate to a 2-log10 reduction in PFU, or it is less than this?
This correlation could also be used to generate a detection limit for Plaque Area (px^2) that is equivalent to 1 or 10 PFU/well, which could then be added to graphs in Figure 3, S4, S5. This will help the reader understand if detection of 10^3 px^2 (for example) is quite high, or if it is already close to detection limits.
Can authors specify if the PEG was mixed with virus immediately prior to inoculation of animals, or was it mixed ahead of time (e.g. 30 mins or 1 hour ahead of administration)? In this case, low-level inactivation of viruses in bulk solution may have occurred. Figure 1C shows minimal inactivation should have occurred with 20% PG over this time-course at room-temperature, but this detail would be helpful to specify.
Figure legend of Fig 1. D) currently reads "... inoculated with 50mL..." , should this be 50uL?
Significance
This study offers a robust proof of concept that PG can be applied to viral disinfection of a large range of enveloped viruses in a variety of settings (aerosol, fomites, in vivo, etc). This work now requires follow-on clinical studies to establish optimal and safe PG levels for viral inactivation in real-world settings, and comprehensive testing of safety risks from long term PG-exposure before this virucide can become clinically applied. This impact of this primary research could be considered broad and translational.
The audiences anticipated to be interested in these results are varied, and include those in virology fields, medical personnel, aerosol scientists, disinfection experts, and public health/ policy makers.
Field of expertise of reviewer: virology, animal infections, immunology, aerosol-borne influenza virus.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #1
Evidence, reproducibility and clarity
Summary
This paper by Styles et al describes the effect of propylene glycol (PG) on a range of enveloped viruses, focusing mainly on IAV and SARS-Cov2. The direct virucidal effect is shown both in vitro and in vivo, as well as the effect of vaporized PG on airborne IAV and SARS-Cov-2. This is a well-performed and very clear study.
Major comments
The claims and conclusions are in general well supported by the data, yet I have some comments. - Interestingly, there were variations in the effect of PG on the different pseudoviruses. Surprising as I assumed that the effect of PG would be mainly on the lipid envelope, as you also mention in the discussion. It is suggested that PG therefore also has an effect on the conformation of the surface proteins. This can be easily tested, does the addition of PG result in a changed recognition by antibodies targeting these surface proteins? This information would be very valuable for your manuscript. - Figure S1 shows that although the clinical scores are better, the viral load is not reduced by the addition of PG to the inoculum. This is not mentioned in the main text. This seems very relevant information and should be presented in the main text. Can you please elaborate on this.<br /> - Optional: It would be very interesting to see the effect of vaporized PG on viral transmission between mice/ferrets of a highly infectious virus (eg Sendai virus). This would give an idea if the PG also works on more biological respiratory droplets.
Minor comments
- The caption of Fig1D mentions that the mice are inoculated with 50ml total volume. I presume this should be µl.
- Please put the axis of the viral titer graph now in Fig s1 in PFU/lung or nasal cavity? This would be more informative.
- Typo in 'PG has broad-spectrum virucidal activity' paragraph: titre should be titer.
- Is allergy to PG an issue that could have an effect on further development of this antiviral strategy?
Significance
This study is highly relevant. It proposes an easy and possibly efficacious method to prevent airborne transmission of a broad range of (enveloped) viruses.
A strength of this study is the set-up with the virus transmission tunnel. This nicely shows the effect of the vaporized PG on airborne IAV and SARS-Cov-2. A limitation is that the researchers did not analyze non-enveloped viruses, which should be done in a follow-up study.
There does not seem to be any recent research investigating this compound as an antiviral tool. Although the compound was tested for its antimicrobial properties in the 1940s, this has not been continued for unclear reasons (?). This is very valuable research in this world recovering from the recent SARS-Cov-2 pandemic. More mechanistic studies need to be performed to understand how this compound exerts its antiviral and antimicrobial effect.
A more specialized audience will be interested in this study.
My field of expertise: RSV, PIV, antivirals
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
Reviewer #1
1-1) Authors conclude that "MFN2 and MTCH2 compensate for each other's absence", but the compensation works only when they are overexpressed. On the other hand, upon HBSS or CHX treatment, MFN2 KO or MTCH2 KO cells have elongated/hyperfused mitochondria, but this is not observed in double deficient cells. In this case, MFN2 and MTCH2 show compensatory effects on mitochondria elongation. The authors believe the two conditions, unstressed & OE and stressed conditions, activating same molecular machineries, but it is not fully supported by the data. For example, in unstressed condition, MTCH2 OE can recover MFN2 KO but not of MFN1 KO, suggesting MTCH2-dependent mitochondria fusion requires MFN1, but it is not tested for stressed condition.
Furthermore, even if the machineries are common among stressed and unstressed conditions, authors should discuss why the endogenous MFN2/MTCH2 expression is not enough to activate mitochondria fusion in MTCH2/MFN2 KO cells, respectively, and how the compensatory effects are activated upon HBSS or CHX treatment.
__R: We thank the reviewer for this important comment. __
1) The reviewer’s comment is correct; in resting conditions the endogenous expression of MFN2 in MTCH2 KO and vice-versa are not sufficient to compensate for each other’s absence, since in steady state they both remain largely fragmented. Thus, we corrected the text accordingly by removing this concept. Interestingly, in the revised MS we show that MFN2 KO results in an increase in MTCH2 expression levels in the mitochondria and to a strong decrease in the GPAT3 and 4 expression levels in the ER (Rev Fig. 3B, C). These results suggest that: 1) Expression of MFN2 is important for the stabilization of GPAT3 and 4 (perhaps they form a functional complex together); 2) the expression levels of endogenous MTCH2 are possibly elevated to compensate for the decreased biosynthesis of LPA and increased demand of LPA funneling for mitochondrial fusion. This hypothesis was added to the discussion.
2) In the revised MS, we tested the possibility that MTCH2 overexpression together with mitochondrial fusion stress could enforce mitochondrial fusion in MFN1 KO cells, and found that it could not (Rev Supp Fig. 4 J-K).
3) We have also discussed what might be the compensatory effects of MTCH2 and MFN2 when activated upon enforced mitochondrial fusion induced by protein overexpression and stress (page 20 last paragraph).
1-2) Authors found out that ER-targeted MFN2 can rescue the mitochondria fragmentation in MTCH2 KO MEF cells, but mitochondria-targeted MFN2 has a lower effect than Wt MFN2. (Fig 2A&B). This finding suggests that MTCH2 loss might impair MFN2 localization at the ER. The authors should investigate endogenous MFN2 localization in MTCH2 KO MEFs.
R: We thank the reviewer for this insightful comment. We addressed this point and show that MTCH2 deletion does not change the expression levels or the subcellular localization of endogenous MFN2 (Rev Fig. 3B).
1-3) The analysis to test whether recovery of mitochondrial morphology by ER-targeted MFN2 in MTCH2 KO depends on LPA synthesis or not is missing (Fig 3G). Authors should examine whether mitochondrial elongation induced by ER-localized MFN2 in MTCH2 KO cells is impaired by the GPAT inhibitor.
R: This analysis was performed (we also included the other mutants), and presented the new data in the revised MS (Rev Supp Fig. 3N, O).
1-4) In the discussion section, authors suggest that mitochondrial LPA would be a crucial factor for MFN2 dependent mitochondrial fusion. To test this hypothesis, authors should overexpress mitochondrial GPAT and evaluate its effect on mitochondrial morphology.
R: We thank the reviewer for this important suggestion. We ordered two commercially available plasmids encoding GPAT1 to address this point (DNASU ____HsCD00082324 and HsCD00082324)____ but unfortunately the proteins were not expressed in our cells. In addition, we revised the text and changed the angle of the interpretation of these results, and clarified that inhibiting LPA impairs MTCH2-independent mitochondrial plasticity in response to MFN2 overexpression, rather than MFN2-dependent mitochondrial fusion.
1-5) In the discussion section, authors indicated that ER-targeted MFN2 could recover mito-ER contacts leading to LPA flux from ER to mitochondria and mitochondria elongation in MTCH2 KO. However, MTCH2 KO itself already have more mito-ER contacts (Fig 2D-H), and an artificial linker fails to recover mitochondria fragmentation in MTCH2 KO cells (Fig S2C, D). Thus, increased number of contacts appears not sufficient to recover the phenotype. The authors should consider this point in the discussion.
R: We added a comment on this important point in the results section (page 10, line 9)
2) Certain methods are not appropriate to support the stated conclusions.
2-1) Authors assess "mitochondria fusion" by evaluating mitochondrial morphology. The authors also describe mitochondrial clumping as a fusion-impaired phonotype (Fig 4A&B). Mitochondrial fusion should be evaluated using a PEG assay or a mtPA-GFP analysis.
R: We now provide in the revised MS results of a mtPA-GFP analysis done for MTCH2 KO MEFs exposed to GPATs inhibitor and treated with CHX (Rev Fig. 4G, H). This experiment supports the notion that loss of MTCH2 along with LPA synthesis inhibition largely impairs mitochondrial fusion in response to CHX.
2-2) In figure 2D-G, authors show that MTCH2 KO cells have more and longer mitochondria-ER contacts. The correct experiment is not to compare these cells to WT, but to KO reconstituted with MTCH2.
R: The reviewer is correct however it will take us many more months to generate a stable MTCH2 rescue cell line and to perform EM analysis of these cells, which would significantly slow down the revision of our MS.
__ __2-3) Since staining of MitoTracker depends on mitochondrial membrane potential, mitochondria with low potential would be invisible and excluded from the analysis. Authors should investigate mitochondrial morphology by immunostaining also in Fig 4D, S4A, D, and K.
__R: We agree with the reviewer’s comment, ____but re-doing all these experiments will be too labor-intensive and time consuming. We therefore focused on Supp Fig. 4A, in which the combination of FSG67 (GPATi in the revised MS) and HBSS treatment impaired mitochondrial membrane potential and mitochondria did not uptake the MitoTracker dye. We repeated this experiment using immunofluorescence, performed new quantifications, and incorporated the new data into the MS (Rev Fig. 4A). We did not remove Supp Fig. 4A since we wanted to emphasize the point that the combination of LPA synthesis inhibition and amino-acid deprivation results in loss of mitochondrial membrane potential. __
Minor comments
1) Since authors use FSG67, an inhibitor against GPAT1, 2 and 3, knocking down of each of GPATs will improve the significance of this work.
__ R: We thank the reviewer for suggesting these experiments. Since the contribution of mitochondrial GPATs to mitochondrial fusion was already established, we complemented our studies by silencing ER GPATs 3 and 4. We tested the contribution of ER-GPATs to MTCH2-independent mitochondrial fusion elicited by MFN2 overexpression (Rev Fig. 3L-N) and induced by either HBSS or CHX (Rev Fig. 4I-K).__
2) Recently, a paper about MTCH2 is published (Guna et al., Science), which shows its insertase activity on tail anchored proteins. Authors should include this point of view in the discussion.
R: We performed new experiments to address this important point. We evaluated the effect of MTCH2 deletion on the expression and localization of the fusion and fission proteins and on the LPA synthesis proteins, and found minor changes (Rev Supp Fig. 1D and Rev Fig. 3B, C). Thus, the effects we are seeing in the MTCH2 KO cells do not seem to be directly related to its insertase activity.
3-1) There are some discrepancies with the previous Labbé et al article.: Labbé et al. suggest that MTCH2 activity on mitochondria (from HCT116 cells) fusion is dependent on LPA, based on in vitro fusion assay. On the other hand, this manuscript shows that inhibition of LPA synthesis could not block MTCH2-induced mitochondria elongation in WT MEF and HEK293T cells. MTCH2 KO HCT116 cells are resistant to HBSS- but sensitive to CHX-induced mitochondria elongation. In this manuscript, MTCH2 KO MEF cells are sensitive to both stimuli, and only when MTCH2- and MFN2-deficient MEF cells are resistant to both stimuli. These discrepancies would be caused by difference of assay system or cell lines, but it is not clearly addressed.
R: We thank the reviewer for raising these discrepancies. ____Despite the discrepancies in the response of MTCH2 KO MEFs to HBSS, both manuscripts largely support the model that MTCH2 funnels LPA towards mitochondrial fusion sites. Our data suggests that loss of MTCH2 unmasks the requirement of sufficient LPA synthesis to sustain mitochondrial fusion, and we also show that MTCH2 overexpression can enforce mitochondrial fusion in the presence of GPATs inhibitor. These two results can be conciliated by the model that MTCH2 is able to optimize or funnel the levels of LPA towards the mitochondrial fusion sites, and when MTCH2 is absent and not able to catalyze this process, mitochondria rely on LPA levels to stay elevated to enable mitochondrial fusion but in a less efficient way. Interestingly, since we show that mitochondrial fusion enforced by HBSS shows full dependency on LPA synthesis, it is expected that loss of MTCH2 will have a stronger impact on HBSS-mediated mitochondrial fusion than on CHX. Nevertheless, MEFs clearly and consistently are sensitive to HBSS, yet this does not exclude that MTCH2 deletion in combination with HBSS treatment may be synergistically detrimental for the cell in other aspects of its well-functioning.
Reviewer #2
Specific points
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The authors should comment on recently published work in Science that MTCH1 and likely MTCH2 are outer membrane insertases. The data in the manuscript seem consistent with the model that an undetermined protein may be poorly inserted in a MTCH2 knockout leading to reduced fusion activity mediated by MFN1. Could this explain how MTCH2 overexpression selectively restores fusion to MFN2 KO cells?
R: We thank the reviewer for raising this important point, and we have now performed new experiments to address it. We evaluated the effect of MTCH2 deletion on the expression and localization of the fusion and fission proteins and on the LPA synthesis proteins, and found minor changes (Rev Supp Fig. 1D and Rev Fig. 3B, C). Thus, the effects we are seeing in the MTCH2 KO cells do not seem to be directly related to its insertase activity.
The authors make the claim that "MFN2 and MTCH2 compensate for each other's absence" though this is not supported by their data. For example, MFN2 expression is not affected in an MTCH2 KO but cannot compensate to promote fusion. Rather, the authors find that MTCH2 and MFN2 are capable of promoting fusion when overexpressed in the absence of the other.
__R: We thank the reviewer for this important comment. __
The reviewer’s comment is correct, and in resting conditions the endogenous expression of MFN2 in MTCH2 KO cells and vice-versa are not sufficient to compensate for each other’s absence, since in steady state they both remain largely fragmented. Thus, we corrected the text accordingly by removing this concept. Interestingly, in the revised MS we show that MFN2 KO results in an increase in MTCH2 expression levels in the mitochondria and to a strong decrease in the GPAT3 and 4 expression levels in the ER (Rev Fig. 3B, C). These results suggest that: 1) Expression of MFN2 is important for the stabilization of GPAT3 and 4 (perhaps they form a functional complex together); 2) the expression levels of endogenous MTCH2 are possibly elevated to compensate for the decreased biosynthesis of LPA and increased demand of LPA funneling for mitochondrial fusion. This hypothesis was added to the discussion.
The authors rely heavily on claims that tagged MFN1 and MFN2 are fully functional, but is it possible that MFN1-GFP is only partially functional? Does untagged MFN1 overexpression cause mitochondrial fusion in a MTCH2 KO? The quantification of this is done only with aspect ratio, and not by categorization of mitochondrial morphology (Fig. S1). The authors should present both analyses in this and all other experiments in the manuscript, particularly since aspect ratio is only performed on 15 cells per condition and not on experimental replicates. The authors should clarify if sample identity was blinded prior to analysis.
__R: As suggested by the reviewer, we repeated all the MFN1 overexpression experiments using an untagged version of the protein, which was overexpressed in MFN1 KO, MTCH2 KO and MFN2 KO MEFs. The new data was included in Rev Fig. 1C-E. The data is consistent with our previous observations using MFN1-GFP. Also, mitochondrial morphology classification was added to the majority of the experiments presented in our MS, which represents quantification of three separate technical repetitions of the experiments (this analysis was not performed blinded). __
The constructs that form the basis of conclusions of ER versus mitochondrial-targeted MFN2 require additional controls to support robust conclusions. The immunofluorescence data suggests that MFN2-ACTA to some degree targets outside of mitochondria (Fig. 2A), and also that MFN2-YIFFT seems to localize to some degree to mitochondria (Fig. 2A). The YIFFT construct may also localize more prevalently to mitochondria in the presence of ACTA (Fig. S2A). Mistargeting would make interpretation of these experiments not possible, as these constructs must exclusively localize to their intended organelle to make strong conclusions. Triple labeling with ER and mitochondrial markers would be helpful, as well as western blots to confirm consistent expression levels and protein stability of each construct. The ACTA MFN2 also appears to promote fusion in a MTCH2 KO. How is this reconciled with the conclusion that ER-targeting of MFN2 is required?
R: We thank the reviewer for these important concerns. We repeated all the MFN2 mutant experiments, including the GTPase mutant MFN2 K109A, and included ER labelling to the MFN2-IYFFT and MFN2-ACTA transfections (Rev Fig. 2B; Supp Fig. 2A, C, D). We also included line fluorescence plot analysis to show localization of MFN2 mutants along with ER or mitochondrial markers (Rev Fig. 2C). Because these studies are cell-based analysis, which were performed using transient transfection, and the efficiency of expression of some of these constructs was very low, it would be technically very difficult to detect their expression using subcellular fractionation. Nevertheless, the constructs MFN2-IYFFT-FLAG and MFN2-ACTA used in our MS were previously reported and their subcellular localization was confirmed (____Sugiura, A. et al. (2013) ‘MITOL Regulates Endoplasmic Reticulum-Mitochondria Contacts via Mitofusin2’, Molecular Cell, 51(1), pp. 20–34. doi:https://doi.org/10.1016/j.molcel.2013.04.023)____.
The authors conclude that "MFN2-mediated fusion requires LPA synthesis", but what is shown instead is that GPATi is epistatic to fusion caused by overexpression of MFN2. The authors should be careful about drawing strong conclusions from their overexpression studies. While MTCH2 overexpression causes hyperfusion in the presence of GPATi, this does not mean that LPA doesn't promote MTCH2-dependent fusion, merely that GPATi does not block hyperfusion caused by MTCH2 overexpression.
R: We thank the reviewer for pointing out these issues. We have revised the text accordingly, and instead of "MFN2-mediated fusion requires LPA synthesis" we wrote “GPATi is epistatic to fusion caused by overexpression of MFN2” (page 13, line 14). ____We also added “____reducing LPA levels by inhibiting GPAT activity is insufficient to impair mitochondrial fusion enforced by MTCH2-overxpression____” (page 13, line 9).
The collapse of the mitochondrial network in MTCH2 KO cells treated with cycloheximide + GPATi does not indicate the cells "require newly-synthesized LPA to respond to SIMH". Instead, it suggests that mitochondria in MTCH2 KO cells are sensitized to combined GPATi/cycloheximide treatment. Could this collapse be fusion-independent? If mitochondria are treated with nocodazole to relax the mitochondrial network (as in Smirnova et al, MBoC, 2001 or Yang et al, Nat Comm, 2022), does the mitochondrial network appear hyperfused?
R: Thank you and as the reviewer suggested we rephrased to “mitochondria in MTCH2 KO cells are sensitized to combined ____GPATi/CHX treatment____.” (page 16, line 4).____ In addition, we performed the nocodazol experiment suggested by the reviewer and included the results in the MS (Rev Supp Fig. 4G-I). The results suggest that MTCH2 KO/GPATi generate clumping and collapse of the mitochondrial network that can be relaxed by blocking microtubule polymerization. Importantly even though the network is still highly fragmented, mitochondrial morphology has changed from large rounded and fragmented to short and tubulated mitochondria, suggesting that MTCH2 KO/GPATi does not impair other mitochondrial architectural changes induced by CHX.
The fact that FSG67 kills starved cells in the absence of MTCH2 does not mean LPA is not required for starvation induced fusion as concluded by the authors (p.12, first paragraph).
__R: Thank you and we corrected this part of the MS _(page 14, line 19)_. __
__ __ Reviewer #3
Major comments:
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As FSG67, an inhibitor of glycerol-phosphate acyl transferase (GPAT) for LPA synthesis, blocks GPAT1/2 in the OMM and GPAT3/4 in the ER, it remains possible that OMM-anchored MFN2 cooperates with GPAT1/2 for concentrating LPA at the mitochondrial fusion site. Thus, the authors should test if loss of GPAT3/4, but not GPAT1/2, suppresses mitochondrial elongation in MTCH2 KO cells overexpressing MFN2.
R: We appreciate the reviewer’s comment and value this observation. We now included in the revised MS two different sets of experiments: silencing ER resident GPATs in MTCH2 KO MEFs, and enforcing mitochondrial fusion either by MFN2 overexpression (Rev Fig. 3L-N) or by HBSS/CHX stress (Rev Fig. 4I-K). We found that ER GPATs do have a contribution to MTCH2-independent mitochondrial fusion enforced by MFN2 overexpression, and to HBSS-induced mitochondrial fusion. These new results suggest that in the absence of MTCH2, LPA synthetized at the ER, is utilized for mitochondrial fusion. Unfortunately, we were unsuccessful in silencing GPAT1 (we tried two different sets of siRNAs, each composed of four different oligos).
It seems conceivable that FSG67 treatment causes a decrease in the protein levels of MFN2 and/or MTCH2, thereby leading to mitochondrial fragmentation. The authors should clarify this point by western blotting.
R: We thank the reviewer for this insightful comment. We performed these experiments and the results appear in the MS (Rev Supp Fig. 3A). We analyzed by Western blot the effect of FSG67 (named GPATi in the revised MS) on the expression levels of MTCH2, MFN2, fusion/fission proteins, GPATs, and a few other proteins. Interestingly, GPATi actually resulted in a small increase in MFN2 expression levels but had no effect on MTCH2 expression levels. Moreover, thanks to the reviewer’s suggestion, we also revealed that in non-treated and GPATi-treated MFN2 KO cells, MTCH2 expression levels were increased and GPATs3/4 expression levels were largely decreased (Rev Fig. 3B, C). These results suggest that: 1) Expression of MFN2 is important for the stabilization of GPAT3 and 4 (perhaps they form a functional complex together); 2) the expression levels of endogenous MTCH2 are possibly elevated to compensate for the decreased biosynthesis of LPA and increased demand of LPA funneling for mitochondrial fusion. This hypothesis was added to the discussion.
Minor comments:
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It would be interesting to investigate whether an ER-anchored MFN2 variant defective in GTP hydrolysis can restore mitochondrial elongation in MTCH2 KO cells.
R: We thank the reviewer for this suggestion. We generated a MFN2-IYYFT K109A mutant, but unfortunately it was expressed at very low levels, and in the expressed cells it elicited mitochondrial aggregation.
The authors should add single-color fluorescent images into Figs. 1A, 1C, 1F, S1A, 2H, S2A, S2C, 3C, 3F, S3F, and S3H.
__R: We thank the reviewer and added single-color fluorescent images into all the Figures requested.
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Referee #3
Evidence, reproducibility and clarity
Summary:
In this manuscript, Goldman et al. report the role of mitochondrial carrier homolog 2 (MTCH2), a mammalian atypical transporter, in regulating mitochondrial shape. Although numerous studies have previously suggested that MTCH2 localizes to the outer membrane of mitochondria (OMM) and acts in a myriad of processes including apoptosis, energy production, mitochondrial dynamics, lipid metabolism, and calcium signaling, its primary function remains uncertain. Using extensive fluorescence imaging, the authors reveal a functional relationship between MTCH2 and MFN1/2, large GTPases regulating mitochondrial fusion. Overexpression of MTCH2 restored mitochondrial elongation in MFN2 KO cells, but not MFN1 KO or MFN1/2 DKO cells. Overexpression of MFN2, but not MFN1, recovered mitochondrial elongation in MTCH2 KO cells. These results suggest that MTCH2 and MFN1 cooperatively act in mitochondrial elongation, and that MFN2 promotes mitochondrial fusion independently of MTCH2 and MFN1. Strikingly, ER-anchored MFN2 can rescue mitochondrial shaping defects in MTCH2 KO cells. The authors also investigated the role of lysophosphatidic acid (LPA), a mitochondrial fusion-promoting lipid, in MTCH2- and MFN2-mediated processes, and found that inhibition of LPA synthesis led to suppression of mitochondrial elongation in MTCH2 KO cells overexpressing MFN2, but not MFN2 KO cells overexpressing MTCH2. Collectively, they propose that MFN1 and MFN2 mediates mitochondrial fusion via two distinct mechanisms: one in the OMM depending on MTCH2 and MFN1, and the other in the ER depending on MFN2 and LPA synthesis.
Major comments:
- As FSG67, an inhibitor of glycerol-phosphate acyl transferase (GPAT) for LPA synthesis, blocks GPAT1/2 in the OMM and GPAT3/4 in the ER, it remains possible that OMM-anchored MFN2 cooperates with GPAT1/2 for concentrating LPA at the mitochondrial fusion site. Thus, the authors should test if loss of GPAT3/4, but not GPAT1/2, suppresses mitochondrial elongation in MTCH2 KO cells overexpressing MFN2.
- It seems conceivable that FSG67 treatment causes a decrease in the protein levels of MFN2 and/or MTCH2, thereby leading to mitochondrial fragmentation. The authors should clarify this point by western blotting.
Minor comments:
- It would be interesting to investigate whether an ER-anchored MFN2 variant defective in GTP hydrolysis can restore mitochondrial elongation in MTCH2 KO cells.
- The authors should add single-color fluorescent images into Figs. 1A, 1C, 1F, S1A, 2H, S2A, S2C, 3C, 3F, S3F, and S3H.
Significance
General assessment:
The findings in this study are potentially interesting and could provide new insights into the molecular mechanisms of mitochondrial fusion in mammals. The fluorescence imaging data are of high quality with quantification and statistical evaluation, mostly supporting the conclusion. There are, however, some missing points regarding the relationships among MTCH2, MFN1, MFN2, and GPAT1/2/3/4 in more detail. For example, does ER-anchored MFN2 interact with GPAT3/4? Does MTCH2 interact with MFN1 to promote mitochondrial elongation? Is LPA required for MFN1-mediated mitochondrial fusion? Nevertheless, this study would significantly be strengthened if the authors clarify the major and minor comments.
Advance:
This study raises the possibilities that ER-anchored MFN2 may act in transport of LPA from the ER to mitochondria in cooperation with GPAT3/4, and that MTCH2 may promote MFN1-mediated mitochondrial fusion independently of LPA.
Audience:
Given the findings that ER-anchored MFN2 and LPS synthesis cooperatively acts in promoting mitochondrial fusion, it will attract a broad range of researchers who study mitochondria, ER, membrane fusion, lipids, and interorganellar communication.
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, Goldman et al examine the role of the mitochondrial protein MTCH2 in mitochondrial fusion. Using a combination of overexpression of MTCH2, MFN1, and MFN2 in respective knockout cells, pharmacological inhibition of GPATs, and stress-induced mitochondrial hyperfusion, the authors explore the relationship between MTCH2, the mitofusins, and LPA levels. These experiments are particularly interesting in light of recent work by Labbe et al which propose that MTCH2 coordinates with LPA to promote mitochondrial fusion. The authors find a key difference from the work of Labbe et al, presenting data suggesting that the role of MTCH2 in starvation-induced mitochondrial hyperfusion varies depending on cell line. They also make the interesting observation that overexpression of MTCH2 is able to bypass GPATi treatment and promote mitochondrial fusion. The authors instead utilize differentially targeted MFN2 to argue that ER-localized MFN2 promotes mitochondrial fusion cooperatively with LPA synthesis. Based on these and other results, they conclude that MTCH2 works with MFN1 to stimulate fusion in a pathway parallel to MFN2 and LPA.
While the assays are mostly well performed and the findings will be of interest to those in the mitochondrial dynamics field, many of the conclusions drawn by the authors are not supported by the experiments shown. This in turn causes the the text to suffer from a lack of clarity and made the logic of the manuscript hard to follow. Additional controls are also needed to draw robust conclusions from MFN2 targeting and MFN1 overexpression experiments. Finally, the rigor of quantification should be clarified and expanded to all assays in the manuscript.
Specific points
- The authors should comment on recently published work in Science that MTCH1 and likely MTCH2 are outer membrane insertases. The data in the manuscript seem consistent with the model that an undetermined protein may be poorly inserted in a MTCH2 knockout leading to reduced fusion activity mediated by MFN1. Could this explain how MTCH2 overexpression selectively restores fusion to MFN2 KO cells?
- The authors make the claim that "MFN2 and MTCH2 compensate for each other's absence" though this is not supported by their data. For example, MFN2 expression is not affected in an MTCH2 KO but cannot compensate to promote fusion. Rather, the authors find that MTCH2 and MFN2 are capable of promoting fusion when overexpressed in the absence of the other.
- The authors rely heavily on claims that tagged MFN1 and MFN2 are fully functional, but is it possible that MFN1-GFP is only partially functional? Does untagged MFN1 overexpression cause mitochondrial fusion in a MTCH2 KO? The quantification of this is done only with aspect ratio, and not by categorization of mitochondrial morphology (Fig. S1). The authors should present both analyses in this and all other experiments in the manuscript, particularly since aspect ratio is only performed on 15 cells per condition and not on experimental replicates. The authors should clarify if sample identity was blinded prior to analysis.
- The constructs that form the basis of conclusions of ER versus mitochondrial-targeted MFN2 require additional controls to support robust conclusions. The immunofluorescence data suggests that MFN2-ACTA to some degree targets outside of mitochondria (Fig. 2A), and also that MFN2-YIFFT seems to localize to some degree to mitochondria (Fig. 2A). The YIFFT construct may also localize more prevalently to mitochondria in the presence of ACTA (Fig. S2A). Mistargeting would make interpretation of these experiments not possible, as these constructs must exclusively localize to their intended organelle to make strong conclusions. Triple labeling with ER and mitochondrial markers would be helpful, as well as western blots to confirm consistent expression levels and protein stability of each construct. The ACTA MFN2 also appears to promote fusion in a MTCH2 KO. How is this reconciled with the conclusion that ER-targeting of MFN2 is required?
- The authors conclude that "MFN2-mediated fusion requires LPA synthesis", but what is shown instead is that GPATi is epistatic to fusion caused by overexpression of MFN2. The authors should be careful about drawing strong conclusions from their overexpression studies. While MTCH2 overexpression causes hyperfusion in the presence of GPATi, this does not mean that LPA doesn't promote MTCH2-dependent fusion, merely that GPATi does not block hyperfusion caused by MTCH2 overexpression.
- The collapse of the mitochondrial network in MTCH2 KO cells treated with cycloheximide + GPATi does not indicate the cells "require newly-synthesized LPA to respond to SIMH". Instead, it suggests that mitochondria in MTCH2 KO cells are sensitized to combined GPATi/cycloheximide treatment. Could this collapse be fusion-independent? If mitochondria are treated with nocodazole to relax the mitochondrial network (as in Smirnova et al, MBoC, 2001 or Yang et al, Nat Comm, 2022), does the mitochondrial network appear hyperfused?
- The fact that FSG67 kills starved cells in the absence of MTCH2 does not mean LPA is not required for starvation induced fusion as concluded by the authors (p.12, first paragraph).
Significance
see above
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, authors investigate the role of MTCH2 in mitochondrial morphology, in several conditions. The authors showed compensatory effect of MFN2 and MTCH2 on stress induced mitochondria hyperfusion (SIMH) in HBSS or CHX treated condition. Since mitochondria hyperfusion upon CHX treatment is impaired in MTCH2 KO cells treated with a GPAT inhibitor, but not in MFN2 KO cells, authors suggest two modes of SIMH, one MTCH2 dependent, the second MFN2/LPA dependent.
This effect seems to be phenocopied in unstressed condition using overexpression system. Mitochondrial fragmentation in MFN2 KO cells can be recovered by MTCH2 overexpression, and vice versa. The fragmentation of mitochondria in MTCH2 KO MEF is reversed also by an ER-targeted MFN2, suggesting the importance of MFN2 ER localization. The authors also point out that MTCH2 KO have increased mitochondria-ER contacts.
Major comments
- Each of the finding is interesting, but the results are not well discussed and logical links leading to the key conclusions are sometimes missing.
1-1) A previous report (Bahat et al., 2018) and this manuscript show that MFN2 OE can restore mitochondrial elongation in MTCH2 KO cells and MTCH2 OE can do the same in MFN2 KO cells. Based on these data, authors conclude that "MFN2 and MTCH2 compensate for each other's absence", but the compensation works only when they are overexpressed. On the other hand, upon HBSS or CHX treatment, MFN2 KO or MTCH2 KO cells have elongated/hyperfused mitochondria, but this is not observed in double deficient cells. In this case, MFN2 and MTCH2 show compensatory effects on mitochondria elongation. The authors believe the two conditions, unstressed&OE and stressed conditions, activating same molecular machineries, but it is not fully supported by the data. For example, in unstressed condition, MTCH2 OE can recover MFN2 KO but not of MFN1 KO, suggesting MTCH2-dependent mitochondria fusion requires MFN1, but it is not tested for stressed condition. Furthermore, even if the machineries are common among stressed and unstressed conditions, authors should discuss why the endogenous MFN2/MTCH2 expression is not enough to activate mitochondria fusion in MTCH2/MFN2 KO cells, respectively, and how the compensatory effects are activated upon HBSS or CHX treatment.
1-2) Authors found out that ER-targeted MFN2 can rescue the mitochondria fragmentation in MTCH2 KO MEF cells, but mitochondria-targeted MFN2 has a lower effect than Wt MFN2. (Fig 2A&B). This finding suggests that MTCH2 loss might impair MFN2 localization at the ER. The authors should investigate endogenous MFN2 localization in MTCH2 KO MEFs.
1-3) The analysis to test whether recovery of mitochondrial morphology by ER-targeted MFN2 in MTCH2 KO depends on LPA synthesis or not is missing (Fig 3G). Authors should examine whether mitochondrial elongation induced by ER-localized MFN2 in MTCH2 KO cells is impaired by the GPAT inhibitor.
1-4) In the discussion section, authors suggest that mitochondrial LPA would be a crucial factor for MFN2 dependent mitochondrial fusion. To test this hypothesis, authors should overexpress mitochondrial GPAT and evaluate its effect on mitochondrial morphology.
1-5) In the discussion section, authors indicated that ER-targeted MFN2 could recover mito-ER contacts leading to LPA flux from ER to mitochondria and mitochondria elongation in MTCH2 KO. However, MTCH2 KO itself already have more mito-ER contacts (Fig 2D-H), and an artificial linker fails to recover mitochondria fragmentation in MTCH2 KO cells (Fig S2C, D). Thus, increased number of contacts appears not sufficient to recover the phenotype. The authors should consider this point in the discussion. 2. Certain methods are not appropriate to support the stated conclusions.
2-1) Authors assess "mitochondria fusion" by evaluating mitochondrial morphology. The authors also describe mitochondrial clumping as a fusion-impaired phonotype (Fig 4A&B). Mitochondrial fusion should be evaluated using a PEG assay or a mtPA-GFP analysis.
2-2) In figure 2D-G, authors show that MTCH2 KO cells have more and longer mitochondria-ER contacts. The correct experiment is not to compare these cells to WT, but to KO reconstituted with MTCH2.
2-3) Since staining of MitoTracker depends on mitochondrial membrane potential, mitochondria with low potential would be invisible and excluded from the analysis. Authors should investigate mitochondrial morphology by immunostaining also in Fig 4D, S4A, D, and K. 3. Other points
3-1) There are some discrepancies with the previous Labbé et al article.: Labbé et al. suggest that MTCH2 activity on mitochondria (from HCT116 cells) fusion is dependent on LPA, based on in vitro fusion assay. On the other hand, this manuscript shows that inhibition of LPA synthesis could not block MTCH2-induced mitochondria elongation in WT MEF and HEK293T cells. MTCH2 KO HCT116 cells are resistant to HBSS- but sensitive to CHX-induced mitochondria elongation. In this manuscript, MTCH2 KO MEF cells are sensitive to both stimuli, and only when MTCH2- and MFN2-deficient MEF cells are resistant to both stimuli. These discrepancies would be caused by difference of assay system or cell lines, but it is not clearly addressed.
Minor comments
- Since authors use FSG67, an inhibitor against GPAT1, 2 and 3, knocking down of each of GPATs will improve the significance of this work.
- Recently, a paper about MTCH2 is published (Guna et al., Science), which shows its insertase activity on tail anchored proteins. Authors should include this point of view in the discussion.
Significance
Mitochondrial carrier homologue 2 (MTCH2/MIMP/SLC25A50) was found as a mitochondrial solute carrier family member but the substrates are unknown. MTCH2 has roles on apoptosis with Bid (Zaltsman et al., 2010, the authors' group), lipid homeostasis (Rottiers et al., 2017), and mitochondrial morphology (Bahat et al., 2018, the authors' group, and Labbé et al., 2021).
Stress induced mitochondria hyperfusion (SIMH) was reported in 2009 by Tondera et al.. Under stress condition, such as UV-C, cycloheximide (CHX), or actinomycin D treatment, hyperfused mitochondria were observed and the event was named as SIMH. They also showed that SIMH is dependent on L-Opa1, MFN1 and SLP-2, which is later found as Opa1 regulator, but not on MFN2, BAX/BAK.
In this manuscript, authors show compensatory effect of MFN2 and MTCH2 on SIMH in HBSS or CHX treated condition. This compensatory effect seems to be reproduced in unstressed condition: mitochondrial fragmentation in MFN2 KO cells can be recovered with MTCH2 overexpression, and vice versa. Authors indicate that LPA synthesis and its mitochondrial localization would be crucial for MFN2 dependent fusion. The compensatory effect of MFN2 and MTCH2 is potentially interesting for a large audience in multiple cell biology fields (mitochondrial biology, ER-mitochondria contact sites, lipid biology).
Expertise: Mitochondria; fusion/fission; ER-mitochondria contact sites
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Reply to the reviewers
Manuscript number: RC-2022-01784
Corresponding author(s): Felipe, Court
1. General Statements [optional]
We submit a revision plan for our manuscript “Senescent Schwann cells induced by aging and chronic denervation impair axonal regeneration after peripheral nerve injury” by Fuentes-Flores et al. from the groups of Felipe Court, Judith Campisi, Jose Gomez, and Ahmet Hoke.
One of the greatest challenges in the field of peripheral nerve regeneration is the decrease in the nerve regenerative capacity in aged patients or after delayed repair, a condition also known as chronic denervation. For the last two decades, several research groups have focused on understanding this phenomenon, but the main drivers of unsuccessful regeneration and poor functional recovery have been elusive, remaining an important clinical problem.
In the work described in this manuscript we found an unexpected property of Schwann cells in the denervated nerves. Aged and chronically denervated Schwann cells are not just passive participants in the impaired regeneration process, but they actively inhibit the regeneration of peripheral axons. Using a combination of morphological, behavioral and molecular techniques in a collaborative multi-lab approach we demonstrate for the first time that senescent Schwann cells accumulate in aged or chronically denervated peripheral nerves modifying the nerve environment, increasing proinflammatory and regeneration-inhibitory factors. Elimination of senescent Schwann cells using a systemic intervention with senolytic or genetically targeting p16-positive senescent cells, greatly improve axonal regeneration in both chronic denervation and aging conditions. Importantly, the enhanced axonal regeneration observed after senescent cell elimination is accompanied by improved functional recovery after chronic denervation. Chronic denervation and aging are the main clinical problems associated to peripheral nerve injuries. Our approach, using FDA approved drugs currently in clinicals trials for its application as senotherapeutics, effectively broadens the spectrum of its clinical use and effectiveness.
We foresee this work will be of interest to a wide audience, including experts in nerve regeneration, senescent cells, aging and those studying the effect of chronic insults in regenerative medicine.
We have now received the comments from two reviewers and we are prepared to experimentally approach the issues raised. We thank their criticism and suggestions, as well as their very enthusiastic comments. We are extremely pleased as both reviewers recognized the important implication of this work, from reviewer 1:
“The findings reported in this manuscript are very interesting and will move the field of nerve repair forward. This paper will be of interest for basic science audience in the fields of aging and neurobiology and has also potential interest to the broader clinical and translational fields. Indeed, this paper provides data that Schwann cells entering a senescent stage not only fail to support axon regeneration in aged animals, but actively inhibit axon regeneration…. Furthermore, the use of an FDA approved drug, currently in clinicals trials for its application as senotherapeutics, to increase axon regeneration in aged and chronic denervation conditions will provide new avenues for clinical applications”.
Which is backed up by reviewer 2:
“Overall, this is an interesting study that undertake fundamental question in the field of nerve physiopathology and also could open a good opportunity in developing therapeutic strategies for translational research”.
We understand the reviewers have raised issues associated with the manuscript format and we are prepared to profoundly edit the manuscript as suggested. In addition, after discussion the experimental issues raised by the reviewers, we are prepared to perform all the experiments and controls suggested (some of them are currently underway), including new animal experiments and in vitro work. This information is detailed in the point-by point revision plan below.
Thank you in advance for the consideration and we look forward to hearing from you in due course. Please do not hesitate to contact me if you want to discuss anything associated to the manuscript and the revision plan.
2. Description of the planned revisions
Point-by point Reponses and revision plan in blue
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary This manuscript by Fuentes-Flores et al reports that elimination of senescent Schwann cells by systemic senolytic drug treatment or genetic targeting improves nerve regeneration and functional recovery in aging and chronic denervation. This improved regeneration is associated with an upregulation of c-Jun expression. Mechanistically the authors provide data to show that senescent Schwann cells secrete factors that are inhibitory to axon regeneration. These findings are very interesting and move the field forward beyond the notion that Schwann cells fail to support axon regeneration in aged animals and identify potential targets to enhance nerve repair. The use of a senolytic drug to increase regeneration in aged and chronic denervation conditions provides new avenues for clinical interventions. However, some of the claims are overstated since this is not the first characterization of senescent Schwann cells and the manipulations used in the study are not entirely specific for Schwann cells. The manuscript is also poorly written and difficult to follow, given the complex set of surgeries and terminology, and lack of explanation of the rationale for the surgery model used. Figures are poorly labeled and difficult to follow without figure legends, and figure legends do not match the figures.
We thank the reviewer for the positive comments, we also acknowledge the problems detected in the manuscript format, including the lack of a clear explanation of the complex procedures used. We are prepared to work carefully on the format, including clear explanations of the procedures and new schemes to complement the text. As detailed below we are also prepared to perform all the experimental work proposed by the reviewer, which will strengthen the conclusion of this manuscript.
Below are suggestions for improvements:
Major comments:
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In the axon regeneration assays, how is the reconnection site defined in longitudinal images stained for SCG10? Of particular concern is that Figure 1B "adult chronic dmg" nerve section image appears to be identical to the image in Figure 5A "Vehicle adult (47dpi)". However, the reconnection site is located at different sites along the nerve. Also, the scale bar appears identical but the legend states different sizes. In Figure 1 chronic damage is 42dpi, and figure 5 is 47dpi, yet with what appears as the same image.
Revisions incorporated in the transferred manuscript, see section 3, below.
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The authors need to provide a rationale for the choice of this complex injury model and what are the advantages over other models. Please clearly describe the timepoints for each experiment and why the time points were chosen for analysis. Provide the scheme of injury in the main Figures to ease comprehension. A scheme is provided in what appears to be Figure S2, but the legend of Figure S2 does not match. Please compare same time points between aged and adults. Days post injury is sometimes referred to 7 or 42, and it is difficult to follow if it is days post initial transection of the tibial nerve or days post reconnection of transected tibial to peroneal. Revise all Figure legends and supplementary Figure legends to match figures.
We thank the reviewer for this comment. In a revised manuscript we will provide a clear explanation for the injury model used, as well as references, including one from the group of Tessa Gordon that describe for the first time this model in rats (PMID: 30215557), and the one applying this model to the mouse from the groups of Rhona Mirsky and Kristjan Jessen (PMID: 33475496). Briefly, this model has two advantages: first, it allows to generate chronic denervation for months and then be able to connect the distal denervated stump with a proximal one without the need of a nerve bridge; And second, neurons in the different groups that have different denervation times (1 week versus 6 weeks) are all damaged at the same time, eliminating variability associated to chronic axonal damage. We will include this information in the results section of a revised manuscript along with the above references.
We will include schemes of the injuries performed in each experiment in each figure, also adding a timeline. This is an excellent suggestion to clearly understand the different procedures performed. We will also check all figures and legends, including correcting the problem detected by the reviewer (legends of Figures 2 and 5 were swapped). We understand the problem of referring to days post-injury, then we will introduce a new form of referring to the initial transection and the experiment, which include reconnection. Adding schemes per figure will also help to understand the different timelines used in different experiments, including the ones using the senolytics.
As detailed above, we will perform a very careful revision of the text and legends for consistency.
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The authors' main conclusion is that Senescent Schwann cells inhibit axon regeneration. The authors need to tune down this statement and acknowledge that their manipulations are not entirely Schwann cells specific. While the data nicely shows a contribution of senescent Schwann cells, it does not sufficiently acknowledge the possibility that other senescent cells in the nerve contribute to this effect. First, the authors refer in the discussion that 60% of the senescent cells are SOX10 negative, and thus represent other cells beyond Schwann cells. This quantification needs to be shown in Figure 1. Second, the genetic and pharmacology manipulation eliminate all senescent cells, including Schwann cells. Third, while the culture experiment may be Schwann cells specific, the authors need to provide detailed information on how they purify these cells, how they induce repair Schwann cells (rSC) as claimed in Figure 3, and demonstrate whether these are pure Schwann cells. This is important because other cells in the nerve contribute to nerve repair, including mesenchymal cells. Finally, the claim that using Mpz-cre will lead to c-jun overexpression only in SC also needs to be demonstrated, since Mpz is also expressed in satellite glial cells in the DRG.
We thank the reviewer for these comments and suggestions. We will tone down the statement that senescence Schwann cells are the only cell candidates for modulating regeneration. We discussed this in the original manuscript, but we agree we need to review this statement, including new data detailed below.
We will include the data requested by the reviewer (60% SOX-10 negative senescent cells) in a new graph in Figure 1. Also, we are currently performing new experiments and quantifications using specific markers for macrophages, epithelial cells, and fibroblasts, to identify the cell identity of the 40% SOX-10 negative senescent cells in aging and chronic denervation.
Regarding in vitro experiments, we will provide detailed methods for Schwann cell purification, and induction of rSC phenotype. Related to the purity of these cultures, in past experiments we have obtained numbers ranging from 95-98% of Schwann cell purity; we will repeat these experiments and quantification for this manuscript and include this data in the method section of a revised text.
Regarding c-jun overexpression in the Mpz-cre, we agree with the reviewer that there is probably overexpression in satellite glial cells in the DRG. Satellite glial cells (SGCs) are a subset of cells in the Schwann cell (SC) lineage that express several early myelination markers, such as Mbp, Mag, and Plp, and the transcription factor Sox10. SGCs express early SC markers, such as CDH19, and are transcriptionally and morphologically similar to SCs, even in the absence of axonal contact. Regarding the possibility that SGCs are contributing to the enhanced regeneration presented by mice with c-jun overexpression, this issue was somehow approached previously by Wagstaff et al. (PMID: 33475496), as they showed that in this mouse strain, increased axonal regeneration was equally observed in sensory neurons, in contact with SGCs, and motor neurons, which are not associated to SGCs. This observation suggests that the effect is associated with c-jun overexpressing Schwann cells in the distal stump. In addition, in our work, the changes in senescent cells observed in the c-jun overexpressed mouse, were associated to the distal nerve stump, which was mechanically separated from the proximal region. We agree it is important to include this discussion, and we will do so in the revised manuscript.
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In Figure 5, c-jun is shown after denervation (42 dpi). The results describe 28 days of denervation, 5 days of GCV and 7 days post reconnection, which makes 40 days. If that is not the case, results need to better explain timeline of this procedure. Also, what is the basal c-jun expression in p16-3MR mice? In addition to the number of c-jun positive cells shown in Figure 5G, the authors need to quantify the percent of c-jun puncta that co-localize with Sox10. The size of the c-jun puncta appears different in size in vehicle and GCV, is that an expected phenotype?
As expressed above, we will include schemes and timelines for all the surgical experiments in a revised manuscript, including detailed information for the experiments using the p16-3MR mice.
Regarding c-jun expression in the p16-3MR mice, we are currently performing the suggested control experiment which is important to draw conclusions of this research. We will use immunofluorescence, but also include western blots as an extra analytical method in this and other experiments. All this information will be included in a revised manuscript.
The observation of the apparent difference c-jun puncta is intriguing. Is not an expected phenotype, but it will important to check if there is a quantifiable change in the pattern of expression. We will quantify this in the different groups and include the results in a revised Figure 5.
Minor comments
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Improve labeling of Figures or at the very least describe in the Figure legend. For example: Figure 5B-C, which of the graphs is from adult mice and which is from aged mice?
We are sorry about the lack of clear labeling in the figures; we will carefully review all figures in the manuscript and their corresponding legends, adding better labeling. Labelling of Figure 5B-C has been corrected.
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The authors need to carefully describe where the high magnification images were taken in the injured nerve and keep the comparison at same site between groups. Please check the scale bar for each image. For example, the images in Figure 1D/F/I/K used same scale, but the cell size and cell morphology are different. The images for split individual channels need to match the merge channel images. For example, the individual channel and merge images are not properly aligned in Figure 4C, ABY-263 group.
As suggested by the reviewer, we will show the regions in which high magnification were taken. All quantifications were performed in comparable sites, but we will include information in a revised manuscript to clearly describe the methodology used. We will check all scale bars in a revised manuscript.
For the comment on alignment problems we have incorporated this in the transferred manuscript, see section 3 below.
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The analysis method used to quantify axon regeneration should be consistent throughout. For example, in Figure 1C, number of axons/nerve width(um) was used for regeneration assay, but axon density (width corrected) was used in Figure 5B-C in regeneration assay.
Revisions incorporated in the transferred manuscript, see section 3, below.
**Referees cross-commenting**
I agree with all Referee #2's comments. Both sets of comments are important, complementary and point to the same major concerns that need to be addressed. Agree as well that both reviewer think this is an interesting and relevant study for the field of nerve repair, if revised appropriately.
Reviewer #1 (Significance (Required)):
__Significance____ __The findings reported in this manuscript are very interesting and will move the field of nerve repair forward. This paper will be of interest for basic science audience in the fields of aging and neurobiology and has also potential interest to the broader clinical and translational fields. Indeed, this paper provides data that Schwann cells entering a senescent stage not only fail to support axon regeneration in aged animals, but actively inhibit axon regeneration. While this reviewer raises questions on whether only senescent Schwann cells or other senescent cells in the nerve contribute to this effect, the identification of potential targets to enhance nerve repair is highly significant. Furthermore, the use of an FDA approved drug, currently in clinicals trials for its application as senotherapeutics, to increase axon regeneration in aged and chronic dennervation conditions will provide new avenues for clinical applications.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary The reported study by Fuentes-Flores et al. shows that Schwann cells (SCs) in peripheral nerves undergo senescence with aging or in chronic denervation. This senescent SC phenotype correlates with downregulation of c-Jun expression and axon regeneration capacity and consequently, affecting functional recovery. The study has been undertaken by using in vivo mice model of chronically denervated sciatic nerve and in vitro of rat-primary cell cultures (Schwann cell, DRG-explants, and their coculture). Schwann cell exosome manipulation was also included to exploit their released factor as media for cell cultures.
Major comments:
- __ __ Chronic denervated nerve model and Schwann cell phenotype
*Tibial nerve transection and chronic denervated nerve: As the referee have no information about this model (no reference is cited), a detailed description should be provided highlighting the interest of such model compared to standard sciatic nerve lesion model.
We thank the reviewer for this comment. We will provide a clear explanation for the injury model used, as well as references, including one from the group of Tessa Gordon that describe for the first time this model in rats (PMID: 30215557), and the one applying this model to the mouse from the groups of Rhona Mirsky and Kristjan Jessen (PMID: 33475496). Briefly, this model has two advantages: first, it allows to generate a chronic denervation for months and then be able to connect the distal denervated stump with a proximal one without the need of a nerve bridge; second, neurons in the different groups that have different denervation times (1 week versus 6 weeks) are all damaged at the same time, eliminating variability associated to chronic axonal damage. We will include this information in the result section of a revised manuscript along with the above references.
*Should be shown, histological analysis of denervated tibial branch prior reconnection with freshly cut proximal peroneal branch with specific immunostainings of rSCs v.s. sSC associated with dapi nuclear staining (as used along this study). Specific staining for other cells should be also provided (i.e., macrophage and endothelial cells). In simple words, "how chronically denervated nerve looks like and what is his cellular content? This is necessary to responds to the following main referee question: does the increase/decrease of rSCs or sSC under specific condition all through the study concerns the SCs that have migrated from freshly cut peroneal branch into denervated tibial distal branch, or resident SCs that have survived in chronically denervated tibial distal branch. In other words, whether rSCs that migrate (and accompanying regenerating axons) into chronically denervated branch nerve undergo phenotype change into sSC because of the environment of chronically denervated nerve. This is not clearly described or discussed, and remain confusing for reader.
We are sorry about the lack of clarity in the text and figures. The immunostaining analysis of denervated tibial branch prior reconnection is included in the original manuscript, specifically in Figure 1D-K, and Figure 4. In a revised manuscript we will include schemes in the Figures to shown the regions analyzed in each case.
We thank for the suggestion of including staining for other cell types. As suggested by the reviewer we are currently performing these experiments and analysis for macrophages, endothelial cells and fibroblasts, together with staining for cell senescence (p16), in both aged and chronically denervated conditions. We will include this data in a revised manuscript
About the specific question of the reviewer: “does the increase/decrease of rSCs or sSC under specific condition all through the study concerns the SCs that have migrated from freshly cut peroneal branch into denervated tibial distal branch, or resident SCs that have survived in chronically denervated tibial distal branch”. Our data demonstrate that senescence Schwann cells appear in the distal nerve stump in aged mice and after chronic denervation. The distal stump is physically disconnected from the proximal part of the nerve. Therefore, after reconnection the regenerating axons encounters a tissue which is already populated with senescent cells. To clearly explain this, we will add extra text in the results and discussion section to clarify these findings.
Support of up- and down-regulation of gene expression illustrated in fig.4
The conclusions and statements on up- or down-regulation of c-jun, yH2AX, beta-gal, P16, arise from quantitative and qualitative analysis from immunostaining of these specific markers by determining the number of positive cells rSCs vs. sSC. For these strong statements appropriate methods for quantification of protein levels such as western blots are required. For example, the statement of down regulation of c-jun expression, the quantitative graph shows strong increase in c-jun cell number under ABT263 treatment but the histological photo does not illustrate such decrease in number of the cell. It shows rather an increase in brightness of c-jun staining. Thus, only appropriate method for protein level quantification could be conclusive. This would also remove the doubt that some photos are under- or over- exposed as it appears in the figure. For example, in aged animal under vehicle condition, there is no variability in staining intensity. Accordingly, one question to the authors: for quantification of cell number, are weakly stained cells considered as positive cell?
We agree with the reviewer that a more quantitative method is required to complement the immunofluorescence data. As the reviewer correctly states, quantification of the immunofluorescence data corresponds to cell positive for the specific marker, expressed as % of cell positive for that maker. Therefore, we will perform western blot for c-jun, yH2AX, and p16 for the different models, including treatments with senolytics.
Regarding the method for quantification, we performed all these quantifications using Imaris software, in which we set up the same threshold for all conditions for a specific antibody marker. Then, in addition to the quantitative western blot analysis, we will include a graph representing the distribution of the labelling (intensity histogram) for all cell number quantification from immunofluorescence data, comparing control with the experimental condition. Finally, the methods used for quantification will be expanded in a revised manuscript.
The method section should be revised in general
Methods could be described in brief only when are supported by provided refs in which the reader could find details. Several refs are missing, i.e., 4.4 for thermal allodynia, 4.5 for ABT263 gavage administration; senescence induction, ...
Quantification methods should be more detailed, several information are missing and not found in result section or legends (i.e., number of nerve section per animal, neurite length, ...).
We completely agree with the reviewer that the method section was not developed adequately in the original manuscript. As described in previous responses, we will detail the methods used, especially those associated with quantifications performed. We will also include references for the different methods used, including those detailed by the reviewer.
The use of rat for in vitro DRG and SC culture while in vivo study is undertaken on mice The switch of species from in vivo to in vitro (mice vs. rat), is not justified as mice DRG and SC culture are also commonly used. In addition, the use of transgenic mice (used here only for in vivo) could also be exploited to address specific and reinforce the data.
We agree with the reviewer that using mouse SC in in vitro experiments will be a better approximation to support our findings. We have been using rat SC in this and other publications as they were the standard model used in in vitro experiments. Nevertheless, as the author states, now there are suitable methods for culturing mouse SC, that we have incorporated in our lab. Therefore, we will perform key in vitro experiments using mouse SC together with mouse DRGs.
Regarding the use of the transgenic mice (3MR), we thank the reviewer for this suggestion; we will perform new experiments using SC derived from 3MR mice in order to demonstrate induction of senescence (by expression of the red fluorescent protein in this transgenic line) and senolysis in vitro.
Use of conditioned exosome/media
Should be explained why the use of exosomes directly in cell culture was not tested. This would be close to physiological condition, regarding the concentration of released factors.
This is an important point that was not explored. As we have plenty of experience using SC-derived exosomes, we will perform the suggested experiments comparing the effect of exosomes from conditioned media from senescent-induced SC and include the results from these experiments in a revised manuscript.
The statement on the effect of rSC vs. sSC cell on growth cone dynamic
The provided data illustrated in fig. 3 are not in support that sSC affect growth cone dynamics. Only what would be "suggested" is that the decrease in neurite length could be associated to changes of growth cone morphology, on fixed tissue, that appeared to be affected. If such statement has to be maintained, time-laps is required. The image does not reflect a retracting neurite nor collapsed growth cone. In addition, other mechanisms could be at the basis of observed decrease in neurite length, which are not evaluated here. This is an important point to address as the authors state that sSC release inhibitory factors.
We completely agree with the reviewer: we are not exploring growth cone dynamics. We will change the manner these results are presented as we are not demonstrating a dynamic process in our results. We prefer to modify the text associated with these experiments rather than perform a time-lapse analysis at this moment. This is part of a future exploration we want to achieve, that will take some time to develop, and we consider at this moment lies outside the scope of the present work. Included in section 4, below.
other comments
- The surgical description is complicated, also annotation to be added in supp fig #2A; provide
We will work in the description of the model, including references to other papers using this nerve anastomosis model for assessing regenerative potential. As stated above we will also include schemes in all figures to help the reader with the surgical procedure and different timelines used.
- M&M 4.2: lign #8, error referring to Fig 2A, correct by. Supp fig 2A
Revisions incorporated in the transferred manuscript, see section 3, below.
- Review refs list, ref#17, full info needed
Revisions incorporated in the transferred manuscript, see section 3, below.
- Fig 3H would be interesting only if contain a column of the 21 proteins exclusively expressed in senescent-induced SCs
Revisions incorporated in the transferred manuscript, see section 3, below.
- The immunostaining of Lamin B1 positive nuclear invaginations in fig S4 should better described in results for non-familiar reader
We will describe better this staining pattern in the result section of the revised manuscript.
- Title of Fig 3, the expression "neuronal growth" is not appropriate here (neurite outgrowth)
Revisions incorporated in the transferred manuscript, see section 3 below.
**Referees cross-commenting**
I agree with referee#1's comments. He/she has raised complementary and important points that should be taken into account by the authors as well as we share the same major concerns. Furthermore, we both expressed the interest of such study if revised appropriately.
Reviewer #2 (Significance (Required)):
Significance
Overall, this is an interesting study that undertake fundamental question in the field of nerve physiopathology and also could open a good opportunity in developing therapeutic strategies for translational research. However, additional investigations are needed to support the main conclusions.
3. Description of the revisions that have already been incorporated in the transferred manuscript
Reviewer 1
Major comments
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In the axon regeneration assays, how is the reconnection site defined in longitudinal images stained for SCG10? Of particular concern is that Figure 1B "adult chronic dmg" nerve section image appears to be identical to the image in Figure 5A "Vehicle adult (47dpi)". However, the reconnection site is located at different sites along the nerve. Also, the scale bar appears identical but the legend states different sizes. In Figure 1 chronic damage is 42dpi, and figure 5 is 47dpi, yet with what appears as the same image.
We thank the reviewer for detecting this issue. The problem arises as the data shown in Figure 1a corresponds to the controls (vehicle) of Figure 5a. The data in Figure 1 is a known phenomenon in the field of peripheral regeneration (i.e., decreased regeneration in aged animals as well as in chronically denervated nerves); nevertheless, we decided to add this data at the start of the manuscript to clearly shown the reader (thinking in a broader scientific audience) the baseline of the evident decrease in axonal regeneration in these two conditions. To make this very clear, we have included the same image Figure 1 and 5 for the controls and detailed this in the legends of both Figure 1 and 5 in the uploaded manuscript.
We have checked the scales and modify the scale in Figure 5 as it was not correct. We have also corrected the nomenclature for days post injury in this image as well as in the corresponding legend.
In addition, for transparency, we have uploaded in a public repository (EBI BioStudies database, https://www.ebi.ac.uk/biostudies/) all the microscopy images used in this work, which is detailed in the uploaded manuscript in a new section named data availability.
Regarding the localization of the reconnection site, this is identified using the whole z-stack of the nerve and not a single section, the region in the z-stack can be recognized using two parameters: the difference in diameter between the proximal and distal stump and by identifying the filament used to suture both stumps. We have included a description of this procedure in the method section of the revised manuscript. As this is not always a perpendicular line, in the revised Figures we have now used an arrowhead to denote the reconnection site.
We are sorry for the confusion generated by the labeling of some images. We will review the text and figures and fix errors. In a revised manuscript we will also add schemes for several figures in order to explain better the experimental procedure and timelines.
Minor comments
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Improve labeling of Figures or at the very least describe in the Figure legend. For example: Figure 5B-C, which of the graphs is from adult mice and which is from aged mice?
We have included the suggested labelling for Figure 5B-C.
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The images for split individual channels need to match the merge channel images. For example, the individual channel and merge images are not properly aligned in Figure 4C, ABY-263 group.
We thank the reviewer for spotting the error in the split channels, we have now fixed this in Fig 4C, but also corrected other alignment problems detected in Fig 4A and 5F.
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The analysis method used to quantify axon regeneration should be consistent throughout. For example, in Figure 1C, number of axons/nerve width(um) was used for regeneration assay, but axon density (width corrected) was used in Figure 5B-C in regeneration assay.
We have included the procedure used to quantify axonal regeneration in the method section of the uploaded manuscript, which is the same throughout the manuscript. We are sorry for the different texts in the axes of graphs included in Figure 1 and Figure 5. In the first version of the figures, we were using the term “axon density (width corrected)”, but then we decided to change it to “number of axons/nerve width (mm)”, which was more precise. Unfortunately, the text of the graph axis in Figure 5 was not changed by mistake. We have now fix this in the revised version.
Reviewer 2
- M&M 4.2: lign #8, error referring to Fig 2A, correct by. Supp fig 2A
We have corrected this error in the uploaded manuscript.
- Review refs list, ref#17, full info needed
We have fixed this reference in the uploaded manuscript.
- Fig 3H would be interesting only if contain a column of the 21 proteins exclusively expressed in senescent-induced SCs
We are sorry about this omission in Figure 3H. We included a list of all the identified proteins of repair and senescent-induced SCs in Supplementary Table 4 (Table S4) of the original manuscript, including the identity of the 21 proteins exclusively expressed in senescent-induced SCs. In the revised version, we have incorporated the information of the 21 proteins in Figure 3H as suggested by the reviewer.
- Title of Fig 3, the expression "neuronal growth" is not appropriate here (neurite outgrowth)
We thank the reviewer for detecting this error, we have changed the expression as suggested in the uploaded manuscript.
Other changes included in the revised manuscript and Figures
- Numeric data for graphs We have included a new supplementary excel file: Supplementary Table 8, including the data for each replicate associated to the graphs of text and supplementary figures.
Revision Figure 5G.
During our review on all the individual replicates of the manuscript data to upload into BioStudies, the first author noticed that the data in graph of Figure 5G corresponded to a pilot experiment performed to set up the protocol. The final experiment was not included, then we uploaded the correct images and included the final quantification. Data is comparable, and statistical differences remains.
Revision Figure 3A.
We have modified the pseudocolors of the S100 antibody channel from magenta to green for ease of visualization. The image and quantification remain exactly the same.
4. Description of analyses that authors prefer not to carry out
Reviewer 2
The statement on the effect of rSC vs. sSC cell on growth cone dynamic
The provided data illustrated in fig. 3 are not in support that sSC affect growth cone dynamics. Only what would be "suggested" is that the decrease in neurite length could be associated to changes of growth cone morphology, on fixed tissue, that appeared to be affected. If such statement has to be maintained, time-laps is required. The image does not reflect a retracting neurite nor collapsed growth cone. In addition, other mechanisms could be at the basis of observed decrease in neurite length, which are not evaluated here. This is an important point to address as the authors state that sSC release inhibitory factors.
We completely agree with the reviewer: we are not exploring growth cone dynamics. We will change the manner these results are presented as we are not demonstrating a dynamic process in our results. We prefer to modify the text associated with these experiments rather than perform a time-lapse analysis at this moment. This is part of a future exploration we want to achieve, that will take some time to develop, and we consider at this moment lies outside the scope of the present work.
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Referee #2
Evidence, reproducibility and clarity
The reported study by Fuentes-Flores et al. shows that Schwann cells (SCs) in peripheral nerves undergo senescence with aging or in chronic denervation. This senescent SC phenotype correlates with downregulation of c-Jun expression and axon regeneration capacity and consequently, affecting functional recovery. The study has been undertaken by using in vivo mice model of chronically denervated sciatic nerve and in vitro of rat-primary cell cultures (Schwann cell, DRG-explants, and their coculture). Schwann cell exosome manipulation was also included to exploit their released factor as media for cell cultures.
Major comments:
-
Chronic denervated nerve model and Schwann cell phenotype
-
Tibial nerve transection and chronic denervated nerve: As the referee have no information about this model (no reference is cited), a detailed description should be provided highlighting the interest of such model compared to standard sciatic nerve lesion model.
- Should be shown, histological analysis of denervated tibial branch prior reconnection with freshly cut proximal peroneal branch with specific immunostainings of rSCs v.s. sSC associated with dapi nuclear staining (as used along this study). Specific staining for other cells should be also provided (i.e., macrophage and endothelial cells). In simple words, "how chronically denervated nerve looks like and what is his cellular content? This is necessary to responds to the following main referee question: does the increase/decrease of rSCs or sSC under specific condition all through the study concerns the SCs that have migrated from freshly cut peroneal branch into denervated tibial distal branch, or resident SCs that have survived in chronically denervated tibial distal branch. In other words, whether rSCs that migrate (and accompanying regenerating axons) into chronically denervated branch nerve undergo phenotype change into sSC because of the environment of chronically denervated nerve. This is not clearly described or discussed, and remain confusing for reader.
- Support of up- and down-regulation of gene expression illustrated in fig.4 The conclusions and statements on up- or down-regulation of c-jun, yH2AX, beta-gal, P16, arise from quantitative and qualitative analysis from immunostaining of these specific markers by determining the number of positive cells rSCs vs. sSC. For these strong statements appropriate methods for quantification of protein levels such as western blots are requiered. For example, the statement of down regulation of c-jun expression, the quantitative graph shows strong increase in c-jun cell number under ABT263 treatment bu the histological photo does not illustrate such decrease in number of the cell. It shows rather an increase in brightness of c-jun staining. Thus, only appropriate method for protein level quantification could be conclusive. This would also remove the doubt that some photos are under- or over- exposed as it appears in the figure. For example, in aged animal under vehicle condition, there is no variability in staining intensity. Accordingly, one question to the authors: for quantification of cell number, are weakly stained cells considered as positive cell?
- The method section should be revised in general Methods could be described in brief only when are supported by provided refs in which the reader could find details. Several refs are missing, i.e., 4.4 for thermal allodynia, 4.5 for ABT263 gavage administration; senescence induction, ... Quantification methods should be more detailed, several information are missing and not found in result section or legends (i.e., number of nerve section per animal, neurite length, ...).
- The use of rat for in vitro DRG and SC culture while in vivo study is undertaken on mice The switche of species from in vivo to in vitro (mice vs. rat), is not justified as mice DRG and SC culture are also commonly used. In addition, the use of transgenic mice (used here only for in vivo) could also be exploited to address specific and reinforce the data.
- Use of conditioned exosome/media Should be explained why the use of exosomes directly in cell culture was not tested. This would be close to physiological condition, regarding the concentration of released factors.
- The statement on the effect of rSC vs. sSC cell on growth cone dynamic The provided data illustrated in fig. 3 are not in support that sSC affect growth cone dynamics. Only what would be "suggested" is that the decrease in neurite length could be associated to changes of growth cone morphology, on fixed tissue, that appeared to be affected. If such statement has to be maintained, time-laps is required. The image does not reflect a retracting neurite nor collapsed growth cone. In addition, other mechanisms could be at the basis of observed decrease in neurite length, which are not evaluated here. This is an important point to address as the authors state that sSC relase inhibitory factors.
Other comments
- The surgical description is complicated, also annotation to be added in supp fig #2A; provide
- M&M 4.2: lign #8, error referring to Fig 2A, correct by. Supp fig 2A
- Review refs list, ref#17, full info needed
- Fig 3H would be interesting only if contain a column of the 21 proteins exclusively expressed in senescent-induced SCs
- The immunostaining of Lamin B1 positive nuclear invaginations in fig S4 should better described in results for non-familiar reader
- Title of Fig 3, the expression "neuronal growth" is not appropriate here (neurite outgrowth)
Referees cross-commenting
I agree with referee#1's comments. He/she has raised complementary and important points that should be taken into account by the authors as well as we share the same major concerns. Furthermore, we both expressed the interest of such study if revised appropriately.
Significance
Overall, this is an interesting study that undertake fundamental question in the field of nerve physiopathology and also could open a good opportunity in developing therapeutic strategies for translational research. However, additional investigations are needed to support the main conclusions.
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-
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Referee #1
Evidence, reproducibility and clarity
Summary
This manuscript by Fuentes-Flores et al reports that elimination of senescent Schwann cells by systemic senolytic drug treatment or genetic targeting improves nerve regeneration and functional recovery in aging and chronic denervation. This improved regeneration is associated with an upregulation of c-Jun expression. Mechanistically the authors provide data to show that senescent Schwann cells secrete factors that are inhibitory to axon regeneration. These findings are very interesting and move the field forward beyond the notion that Schwann cells fail to support axon regeneration in aged animals and identify potential targets to enhance nerve repair. The use of a senolytic drug to increase regeneration in aged and chronic denervation conditions provides new avenues for clinical interventions. However, some of the claims are overstated since this is not the first characterization of senescent Schwann cells and the manipulations used in the study are not entirely specific for Schwann cells. The manuscript is also poorly written and difficult to follow, given the complex set of surgeries and terminology, and lack of explanation of the rationale for the surgery model used. Figures are poorly labeled and difficult to follow without figure legends, and figure legends do not match the figures. Below are suggestions for improvements:
Major comments:
- In the axon regeneration assays, how is the reconnection site defined in longitudinal images stained for SCG10? Of particular concern is that Figure 1B "adult chronic dmg" nerve section image appears to be identical to the image in Figure 5A "Vehicle adult (47dpi)". However, the reconnection site is located at different sites along the nerve. Also, the scale bar appears identical but the legend states different sizes. In Figure 1 chronic damage is 42dpi, and figure 5 is 47dpi, yet with what appears as the same image.
- The authors need to provide a rationale for the choice of this complex injury model and what are the advantages over other models. Please clearly describe the timepoints for each experiment and why the time points were chosen for analysis. Provide the scheme of injury in the main figures to ease comprehension. A scheme is provided in what appears to be Figure S2, but the legend of Figure S2 does not match. Please compare same time points between aged and adults. Days post injury is sometimes referred to 7 or 42, and it is difficult to follow if it is days post initial transection of the tibial nerve or days post reconnection of transected tibial to peroneal. Revise all figure legends and supplementary figure legends to match figures.
- The authors' main conclusion is that Senescent Schwann cells inhibit axon regeneration. The authors need to tune down this statement and acknowledge that their manipulations are not entirely Schwann cells specific. While the data nicely shows a contribution of senescent Schwann cells, it does not sufficiently acknowledge the possibility that other senescent cells in the nerve contribute to this effect. First, the authors refer in the discussion that 60% of the senescent cells are SOX10 negative, and thus represent other cells beyond Schwann cells. This quantification needs to be shown in Figure 1. Second, the genetic and pharmacology manipulation eliminate all senescent cells, including Schwann cells. Third, while the culture experiment may be Schwann cells specific, the authors need to provide detailed information on how they purify these cells, how they induce repair Schwann cells (rSC) as claimed in Figure 3, and demonstrate whether these are pure Schwann cells. This is important because other cells in the nerve contribute to nerve repair, including mesenchymal cells. Finally, the claim that using Mpz-cre will lead to c-jun overexpression only in SC also needs to be demonstrated, since Mpz is also expressed in satellite glial cells in the DRG.
- In Figure 5, c-jun is shown after denervation (42 dpi). The results describe 28 days of denervation, 5 days of GCV and 7 days post reconnection, which makes 40 days. If that is not the case, results need to better explain timeline of this procedure. Also, what is the basal c-jun expression in p16-3MR mice? In addition to the number of c-jun positive cells shown in Figure 5G, the authors need to quantify the percent of c-jun puncta that co-localize with Sox10. The size of the c-jun puncta appears different in size in vehicle and GCV, is that an expected phenotype?
Minor comments
- Improve labeling of Figures or at the very least describe in the Figure legend. For example: Figure 5B-C, which of the graphs is from adult mice and which is from aged mice?
- The authors need to carefully describe where the high magnification images were taken in the injured nerve and keep the comparison at same site between groups. Please check the scale bar for each image. For example, the images in Figure 1D/F/I/K used same scale, but the cell size and cell morphology are different. The images for split individual channels need to match the merge channel images. For example, the individual channel and merge images are not properly aligned in Figure 4C, ABY-263 group.
- The analysis method used to quantify axon regeneration should be consistent throughout. For example, in Figure 1C, number of axons/nerve width(um) was used for regeneration assay, but axon density (width corrected) was used in Figure 5B-C in regeneration assay.
Referees cross-commenting
I agree with all Referee #2's comments. Both sets of comments are important, complementary and point to the same major concerns that need to be addressed. Agree as well that both reviewer think this is an interesting and relevant study for the field of nerve repair, if revised appropriately.
Significance
The findings reported in this manuscript are very interesting and will move the field of nerve repair forward. This paper will be of interest for basic science audience in the fields of aging and neurobiology and has also potential interest to the broader clinical and translational fields. Indeed, this paper provides data that Schwann cells entering a senescent stage not only fail to support axon regeneration in aged animals, but actively inhibit axon regeneration. While this reviewer raises questions on whether only senescent Schwann cells or other senescent cells in the nerve contribute to this effect, the identification of potential targets to enhance nerve repair is highly significant. Furthermore, the use of an FDA approved drug, currently in clinicals trials for its application as senotherapeutics, to increase axon regeneration in aged and chronic dennervation conditions will provide new avenues for clinical applications.
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Reply to the reviewers
General Statements
Thank you for providing an initial assessment of our manuscript. We went through all the raised comments and suggestions aiming to improve our manuscript. Our manuscript will benefit from addressing them.
Our main impression is that the concerns regarding the novelty of our work by Reviewers #1 and #3 come from the fact that we apply a known flexible statistical framework (group factor analysis) to novel applications in single-cell data analysis, namely the estimation of multicellular programs and sample-level unsupervised analysis. The core methodology of our work is indeed based on the popular tool Multi-omics factor analysis (MOFA). We see the novelty of our study in the formulation of these relatively new applications within this framework, and the demonstration of the added value that this formulation provides building on MOFA’s strengths, in particular by expanding the possibilities of downstream analysis of single-cell data including the meta-analysis of distinct single-cell patient cohorts and its integration to complementary bulk and spatial data modalities.
The simultaneous estimation of multicellular programs together with sample-level unsupervised analysis is only possible with a single available tool, scITD, which is limited by its modeling strategy, based on tensor decomposition: with tensor decomposition, multicellular programs can not be estimated from distinct feature sets across cell-types, making this method less flexible and sensitive to technical effects, such as background expression. We compared our proposed methodology with scITD and showed the benefits of using group factor analysis as implemented in MOFA for this task. Moreover, as of now, no other methodology is able to estimate multicellular programs and perform sample-level unsupervised analysis, simultaneously in multiple independent single-cell atlases. We also showed how multicellular programs are traceable in bulk transcriptomics data and show that they are better fit to classify heart failure patients compared to classic cell-type deconvolution approaches.
Altogether, we believe that our current manuscript complements existing literature and puts forward an approach with distinct features to analyze single-cell atlases. We will edit the text to make more explicit the novelty and advantages of our proposed methodology, and we will emphasize that our work does not mean to propose a new method, but rather demonstrate how group factor analysis can be used for novel sample-level analysis of single-cell data. We plan to incorporate the suggestions by Reviewer #1 regarding the inclusion of additional datasets, model validations, and novel applications involving a direct modeling of cell-compositions and spatial organization of cells. Moreover, we plan to discuss perspectives on how cell communications can be incorporated in the analysis of multicellular programs as suggested by Reviewer #2. Additionally, we will correct all the figure and text typos identified by the reviewers. Finally, we will provide an R package (https://github.com/saezlab/MOFAcellulaR) and python implementations (https://liana-py.readthedocs.io/en/latest/notebooks/mofacellular.html) that facilitate the use of our approach.
Please find below the point-by-point response to the reviewers in blue, numbered for convenience.
__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __
Remark to authors
Flores et al. present a pipeline in which they leverage MOFA framework, a matrix factorization algorithm to infer multi-cellular programs (MCPs). Learning and using MCP has already been proposed by others. Yet, authors pursue a similar goals by using MOFA, providing a cell*sample matrix for different cell types as different views (instead of multiple modalities/views) as the input. They later apply MOFA using this data format on a series of applications to analyze acute and chronic human heart failure single-cell datasets using MCPs. Authors further try to expand their analysis by incorporating other modalities.
Major points:
1.1 As briefly outlined in the remarks, the current manuscript needs novel findings and methodology to grant a research article which I can' see here. The underlying matrix factorization is the original MOFA (literally imported in the code) with no modification to further optimize the method toward the task. While I appreciate and acknowledge the author's efforts resulting in a detailed analysis of heart samples, I think all of these could have been part of MOFA's existing tutorials.
Response 1.1 As the reviewer correctly states, we used the framework and code of MOFA. The novelty lies in its application for the unsupervised analysis of samples from cross-condition single-cell data and the inference of MCPs. MOFA is a statistical framework implementing a generalization of group factor analysis with fast inference and its current version fits the task of MCP inference and unsupervised analysis of samples across cell-types that provides a more flexible modeling alternative than current available methods (as presented in Table 1 of the manuscript). Current work on MCP inference is based on the premise of multi-view factorization with distinct statistical modeling alternatives. As mentioned in the discussion of our manuscript, three main points distinguish our discussed methodology from present alternatives and provide evidence about its relevance and uniqueness over available tools:
Simultaneous unsupervised analysis of samples across cell-types and inference of MCPs, together with comprehensive interpretable descriptions of the reconstruction of the original multi-view dataset. This is only currently possible with scITD (Mitchel et al, 2022) and is compared in the manuscript. DIALOGUE (Jerby-Arnon & Regev, 2022) is limited to the generation of MCPs and Tensor-cell2cell (Armingol et al, 2021) is only focused in cell-communications with limited interpretability.
Flexible non-overlapping feature set that handles better technical effects such as background expression, as discussed in section “__2.2 Multicellular factor analysis for an unsupervised analysis of samples in single-cell cohorts”. __Moreover, as mentioned by the reviewer in a later point (Reviewer comment 1.2), this enables joint modeling of distinct aspects of the tissue, such as cell compositions, cell communications (preliminary work: https://liana-py.readthedocs.io/en/latest/notebooks/mofatalk.htm) and spatial organization.
Joint-modeling of independent atlases that enables meta-analysis at the sample level of cross-condition single-cell data. No currently available methodology is capable of performing similar modeling. For these reasons, we believe that our work is worth being discussed and presented to the community as a research article. We will modify the discussion to put more emphasis on the added value of group factor analysis as implemented in MOFA.
Moreover, we now provide an R package (https://github.com/saezlab/MOFAcellulaR) and python implementations within our analysis framework LIANA (https://liana-py.readthedocs.io/en/latest/notebooks/mofacellular.html) that facilitates the usage of our proposed methodology. The R and python implementations are compatible with current Bioconductor and scverse pipelines, respectively.
Application of our methodology to heart failure datasets also revealed novel knowledge about heart disease processes:
In myocardial infarction, we found that our MCPs associated with cardiac remodeling capture cell-state-independent gene expression changes. This provides a novel understanding on the effect of disease contexts in the expression profiles of specialized cells. This finding was not reported in the original atlas publication.
In chronic heart failure, we identified a conserved MCP of cardiac remodeling across patient cohorts and etiologies, suggesting a common chronic phase between distinct initial causes of heart failure.
Moreover, we showed that deconvoluted chronic heart failure MCPs from bulk transcriptomics better classify patients in comparison to classic cell-type composition deconvolution of bulk data. To our knowledge, this finding was not presented in any of the manuscripts of other methodologies focused on MCPs.
Altogether, our current work shows a novel application of group factor analysis for the simultaneous estimation of MCPs and the sample-level unsupervised analysis of cross-condition single cell data. We showed the unique features compared to current available tools. Distinct post-hoc analysis in combination with other data modalities shows the biological relevance of our proposed methodology to complement the tissue-centric knowledge of disease.
1.2 How can you explain that the results in donor-level analyses are not due to technical artifacts (batch variation)? Can this be used to infer a new patient similarity map? For example, I would test this by leaving out a few patients from training, projecting them, and seeing where they would end up in the manifold or classifying disease conditions for new patients and explaining the classification by MCPs responsible for that condition.
Response 1.2 When knowledge of the technical batches is available it is possible to test for association between these labels and the factors encoding MCPs as shown in Figure 2.
In our current applications, we additionally showed the biological relevance of our estimated MCPs by mapping them to spatial and bulk data sets, which is a direct way of testing how generalizable were our findings:
In the application of MOFA to human myocardial infarction data, we mapped the gene loadings conforming the MCP associated with cardiac remodeling to paired spatial transcriptomics datasets. We showed that in general, the cell-type specific expression of the MCP of cardiac remodeling encompassed larger areas in ischemic and fibrotic samples compared to myogenic (control) samples.
In the application of MOFA to chronic human end-stage heart failure data, we mapped the gene loadings conforming the MCP associated with cardiac remodeling to 16 independent bulk transcriptomics datasets of heart failure. There we showed that the cell-type specific expression of the MCP of cardiac remodeling separates heart failure patients from control individuals. Regarding the generation of new patient similarity maps, it is possible to estimate the positions of new samples in the manifold formed by the factors representing the MCPs. As suggested by the reviewer we will show this by classifying heart failure single-cell samples using MCPs of two independent patient cohorts (presented in section 2.7).
1.3 The bulk and spatial analysis are used posthoc after running MOFA, I think since MOFA can use non-overlapping features set, it would be interesting to see if deconvoluted bulk or ST data can be encoded as another view (one view from scRNAseq data for each cell-type and another view from bulk RNA-seq or ST, you can get normalized expression per spot (for ST) or per sample (for bulk) and use them as input.
Response 1.3 Thanks for the suggestion. We agree that the possibility of using non-overlapping features opens options of complex models that include the cell-type compositional and organizational aspects of tissues. However these features must be quantified in the same sample, thus it is limited to samples profiled simultaneously at different scales.
We will present the results of a sample-level joint model of multicellular programs together with cell-proportions and spatial dependencies using the myocardial infarction dataset presented in section 2.2. For this dataset based on our previous work we have the compositions of major cell-types and their spatial relationships based on spatially contextualized models (Kuppe et al, 2022). We will run a MOFA model and show how it can be used to find factors associated with structural and molecular features of tissues.
__Minor: __
1.4 Some figure references are not correct (e.g., "the single-cell data into a multi-view data representation by estimating pseudo bulk gene expression profiles for each cell-type across samples (Figure 1b)." should be figure 2b)
Response 1.4 Thanks for pointing this out. We apologize for these mistakes and we will adjust all labels correctly.
1.5 The paper is well written, but there could be some more clarifications about what authors consider as cell-type and cell-state, condition, MCPs which I think is critical to current analysis (see here https://linkinghub.elsevier.com/retrieve/pii/S0092867423001599) for the reader not familiar with those concepts.
Response 1.5 We agree with the reviewer that it is important to introduce these concepts in more detail to avoid confusion. We will adapt the current manuscript to incorporate these definitions in the introduction.
__Reviewer #1 (Significance (Required)): __
1.6 While I find the concept of MCPs interesting, the current work seems like a series of vignettes and tutorials by simply applying MOFA on different datasets (The authors rightfully state this). However, It needs to be clarified what the novelty is since there is no algorithmic improvement to current MCP methods (because there is no new method) nor novel biological findings. Additionally, even in the current form, the applications are limited to the heart, and the generalization of this proposed analysis pipeline to other tissues and datasets is not explored. Overall, the paper lacks focus and novelty, which is required to grant a publication at this level.
Response 1.6 As mentioned in response 1.1, we show that group factor analysis as implemented in MOFA has advantages given its flexibility of the feature space, the joint-modeling of independent datasets, and the interpretability of the model. We will make these advantages clearer in the discussion, and we will explicitly mention the disadvantages and lack of functionalities of available methods.
The applications were mainly done in heart data for consistency although they represent four distinct single-cell datasets, one spatial transcriptomics dataset, and 16 independent bulk transcriptomics datasets. For completeness, as suggested by the reviewer, we will show the application of our methodology to peripheral blood mononuclear cell data of lupus samples (preliminary results: https://liana-py.readthedocs.io/en/latest/notebooks/mofacellular.html)
__expertise: Computational biology, single-cell genomics, machine learning __
__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __
Summary:
The authors use MOFA, an unsupervised method to analyze multi-omics data, to create multicellular programs of cross-condition multi-sample studies. First, for each cell-type, a pseudobulk expression matrix per sample is created. The cell-type now functions as the separate view, typically reserved for the different omics layers in MOFA. This then results in a latent space with a certain number of factors across samples. The factors, representing coordinated gene expression changes across cell-types, can then be checked for associations with covariates of interest across the samples.
MOFA is well-suited for this task, as it can handle missing data and it is a linear model facilitating the interpretation of the factors. Users should be aware that MOFA can estimate the number of factors, but the pseudobulk profiles require a rigorous selection of cell-type specific marker genes. The result will be most suited for downstream analysis if there is a clear association with one factor and a clinical covariate of interest. In a final step, a positive or negative gene signature can be created by setting a cut-off on the gene weights for that specific factor.
The method is applied on 3 separate data sets of heart disease, each time demonstrating that at least one of the factors is associated with a disease covariate of interest. The authors also compare the method to a competitor tool, scITD, and explore to what extent a factor mainly captures variance associated with (i) a general condition covariate or rather (ii) specific cell states.
The multicellular programs are also mapped to spatial data with spot resolution. Though this analysis does not bring any novel biological insight in the use case, it does support the claim that the programs are associated with the covariate of interest.
The most interesting applications of MOFA are in my opinion the potential for meta-analysis of single-cell studies and validation of cell-type specific gene signatures with publicly available bulkRNAseq data sets.
The authors provide various data sets and data types to support their claims and the paper is well written. The relevant code and data has been made available.
We thank the reviewer for the positive comments to our work.
__Major comments __
2.1 What is the added value of the gene signatures obtained from MOFA compared to e.g. a naive univariate approach? In theory, a similar collection of genes or gene signature could be obtained by running a differential gene expression analysis across the samples for each cell-type (e.g. myogenic vs ischemic ) and applying a set of relevant cut-offs or filters on the results. In other words, does MOFA detect genes that would otherwise be missed?
Response 2.1 Thank you for the relevant comment. The original motivation of our work is the unsupervised analysis of samples based on a manifold formed by a collection of multicellular molecular programs. We envisioned that this unsupervised analysis would be relevant in situations where a clear histological or clinical classification of samples is not possible with reliability. As mentioned by Reviewer #1 in comment 1.2, one advantage of these approaches is that they create patient similarity maps, which have been shown useful to stratify patients in a recent analogous work in multiple sclerosis (Macnair et al, 2022). The cell-type signatures obtained from relevant factors explaining the patient stratification avoid the likelihood of performing “double dipping” by avoiding the need of a direct differential expression analysis between newly formed groups.
In our applications, the generation of cell-type signatures (here called multicellular programs) associated to a specific clinical covariate (eg. control vs perturbation) are post-hoc analyses of the generated manifold. And as the reviewer correctly points out, these signatures should be similar to performing direct differential expression analysis between those patient conditions. In the related work of scITD (Mitchel et al, 2022) the authors showed high concordance between the cell-type signatures and the results of differential expression analysis. For completion, we will similarly quantify the degree of overlap between genes of our generated signatures with the ones coming from differential expression analysis.
It is relevant to mention that in complex experimental designs with multiple conditions, our approach facilitates patient ordering, which allows the understanding of one condition in the context of all the others, avoiding the need of multiple testing and the definition of multiple contrasts, as mentioned in the text.
We will incorporate these points in the discussion section of the manuscript.
2.2 Could scITD also be used for meta-analysis or could the obtained gene signatures of that method also be mapped to bulkRNAseq data? If so, it would be interesting to show the relative performance with MOFA. If not, this specific advantage should be highlighted.
Response 2.2 Thank you for pointing this out. scITD does not provide a group-based model to perform meta-analysis, and this feature is one of the main advantages of group factor analysis as currently implemented in MOFA. We will highlight this feature in Table 1 and in the discussion.
Although scITD signatures of a single study could be mapped to bulk transcriptomics data, the stringent tensor representation leads to the generation of signatures that may be influenced by technical effects as shown in the manuscript section 2.2. Thus we believe that the flexibility of the feature space in MOFA is an advantage for this task. We will add this observation to the discussion.
2.3 Users need to specify gene set signatures based on the weights for a factor of interest. This might suggest a limitation to categorical covariates of interest. If the authors see potential for a continuous covariate of interest, this should at least be highlighted in the text and if possible demonstrated on a use case.
Response 2.3 In our applications we limited ourselves to categorical variables, however, it is possible to associate factors to continuous variables. An implementation of the association with continuous variables is already available in our newly created R package “MOFAcellulaR”: https://github.com/saezlab/MOFAcellulaR/blob/main/R/get_associations.R.
The datasets we analyzed have no continuous clinical covariates to showcase this functionality, but as suggested by the reviewer we will highlight this feature in the text.
__Minor comments __
2.4 In Figure 2c the association between factor 2 and the technical factor shows a very strong outlier. Please verify that the association is still significant after applying a more robust statistical test (e.g. non-parametric test as Wilcoxon).
Response 2.4 Thanks for the observation, we will test these differences with a non-parametric test.
2.5 For mapping the cell-type specific factor signatures to bulk transcriptomics, the exact performed comparison or model is unclear. There are seven cell-type signatures for each sample in every study. Was there a t-test run for each cell-type or was a summary measure taken across the cell-types? he thresholding is also rather lenient (adj. p-val 0.1).
Response 2.5 We are sorry for not being clear about our procedure. After identifying the multicellular program associated with heart failure estimated from the two single cell studies meta-analyzed, we calculated the weighted mean expression of the seven cell-type signatures independently to every sample of the 16 bulk studies. In other words each sample within each bulk study will be represented by a vector of 7 values representing the relative expression of a cell-type specific signature (Figure 6D-left). For each bulk transcriptomics study, first, we centered the gene expression data before calculating the weighted mean.
In supplementary figure 4-e we show the results of performing a t-test of the cell-type scores between heart failure and control samples within each study. Given the relative low sample size of most of the studies (affecting the power of the test), we chose a not so stringent adjusted p-value. For completion, we will show the results of a more classical threshold (adj. p-value
2.6 typo in abstract: In sum, our framework serves as an exploratory tool for unsupervised analysis of cross-condition single-cell ***atlas*** and allows for the integration of the measurements of patient cohorts across distinct data modalities
Response 2.6 Thanks for pointing out this typo. We will modify the text.
2.7 In Figure 4a it is not clear to me why on the one hand we see marker enrichment vs loading enrichment with healthy and disease.
Response 2.7 We apologize, this is a typo after editing the labels. Both should contain the marker enrichment label. We will fix this.
2.8 IN Figure 4b it would help if the same color scheme would be maintained throughout the paper (here now black and white) and if for the cell states the boxplots would be connected per condition, emphasizing the (absence) of change across cell states within a condition.
Response 2.8 We thank the reviewer for the suggestion. We will reorganize the panels showing the gene expression per condition and fix the color scheme.
__Reviewer #2 (Significance (Required)): __
__General assessment: __
2.9 MOFA is well-suited for detecting multicellular programs because it can handle missing data and allows for easy interpretation of the factors as a linear method. It might have particular potential for meta-analysis across multiple studies and reevaluating bulkRNAseq data sets, but in the current manuscript it is unclear to what extent this is a specific advantage of MOFA or could also be done with competitors. The authors show how the obtained results and associations with clinical covariates can be validated across multiple data types. How the resulting multicellular programs can provide additional biological insight or form the starting point for additional downstream analysis (e.g. cell communication) is not covered in the paper.
Response 2.9 We thank the reviewer for highlighting the methodological advantages of group factor analysis for the estimation of multicellular programs and the unsupervised analysis of samples from cross-condition single-cell atlas. As mentioned in response 1.1 and 2.2, the added value of our methodology is the flexibility of feature views (that goes beyond gene expression) and simultaneous modeling of independent single-cell datasets, a feature not present in any of the currently available methods that facilitates the meta-analysis of datasets across modalities.
While we interpret the presented multicellular programs in the context of cellular functions and the division of labor of cell states, it is true that we did not attempt to provide mechanistic hypotheses, for example, via cell-cell communication, on how this coordination across cell-types emerges.
Previous work of the related tool Tensor-cell2cell (Armingol et al, 2021) has presented the idea of the estimation of multicellular programs from cell-cell communications and group factor analysis can also be used for this task (preliminary work: https://liana-py.readthedocs.io/en/latest/notebooks/mofatalk.html). We will discuss in the text perspectives on how the estimation of multicellular programs can be linked to the inference of cell communications from single-cell data together with analysis alternatives previously proposed by scITD and Tensor-cell2cell. However, we believe that this question requires further work and it is out of scope of our current manuscript.
__Audience: This paper will be mainly of interest to a specialized public interested in unsupervised methods for large scale multi-sample and multi-condition studies. __
__Reviewer: main background in the analysis of scRNAseq data. __
__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __
This manuscript by Saez-Rodriguez and colleagues proposes to repurpose Multi-Omics Factor Analysis for the use of single cell data. The initial open problem stated by the paper is the need for a framework to map multicellular programs (such as derived from factor analysis) to other modalities such as spatial or bulk data. The authors propose to repurpose MOFA for use in single cell data. Case studies involve human heart failure datasets (and focuses on spatial and bulk comparisons).
There are particular issues with clarity regarding the key methodological contribution (and assessment of it), discussed under significance.
__Reviewer #3 (Significance (Required)): __
3.1 I am very puzzled by the repeated claims the manuscript makes that their central methodological contribution and innovation is to use MOFA for single cell data. One of their citations for MOFA is to MOFA+, which is precisely that (in a relatively popular manuscript published by the original authors of MOFA and not overlapping with the present authors). I am left to wonder what I missed.
Response 3.1 We apologize for the misunderstanding, as mentioned in the response to review 1.1 and explained by reviewer 2’s summary, the main objective of our work is to use the statistical framework of group factor analysis for the inference of multicellular programs and the sample-level unsupervised analysis of cross-condition single-cell data, which is a distinct task to multimodal integration (Argelaguet et al, 2021).
While it is true that MOFA+ introduced expansions to the model for the modeling of single-cell data, namely fast inference and group-based modeling, the main focus in their applications is the multimodal integration of data, where each cell is represented by a collection of distinct collection of features (e.g. chromatin accessibility and gene expression). Unlike multimodal integration, here we propose a different approach to analyze single-cell data at the sample level instead of the cell level, without modifying the underlying statistical model (see section 2.1 of the manuscript).
In detail, what we assume is that samples of single-cell transcriptomics data (e.g. tissue from a patient) can be represented by a collection of independent vectors collecting the gene expression information of cell types composing the tissue analyzed. Decomposition of these multiple views with group factor analysis produces a manifold that captures multicellular programs (coordinated expression processes across cell-types), or shared variability across cell-types simultaneously. Altogether, this represents a novel usage of group factor analysis in an application for the inference of multicellular programs, where the main focus is not at the cell-level but at the patient level.
As a side note, Britta Velten, one of main developers of MOFA and coauthor of both the MOFA and MOFA+ papers, is a contributor and coauthor of this manuscript, and Ricard Argelaguet, who also led both versions of MOFA, gave us helpful feedback and is acknowledged as such on this work.
3.2 Multimodal integration methods are fairly numerous and even if they're not all exactly factor analyses, it's strange to argue that MOFA fills some unique conceptual gap. I agree it fills something of an interesting gap (except for MOFA+ already filling it), but it's not like the quite popular spatial to single-cell integration approaches aren't doing similar things. If this is a methods paper (as it is presented) then there would have to be very substantially more comparative evaluation to these other approaches.
Response 3.2 As presented in the previous response (3.1) our current work is not focused on multimodal integration, but rather the inference of multicellular programs and the sample-level unsupervised analysis of single-cell data. Given this, in the current manuscript we compared our proposed methodology with the only three other available methods that address at least partially the inference of multicellular programs (see Table 1 in our manuscript). In response 1.1 and 3.2 we discussed the advantages of our proposed methodology compared to available methods. In the manuscript section 2.2 we compared group factor analysis with tensor decomposition and showed that the former better deals with technical artifacts and better identifies known patient groups.
We will distinguish our work from multimodal integration explicitly in the introduction and the manuscript section 2.1 to avoid confusions.
3.3 The biological use cases are comparatively interesting and dominate the manuscript (but are still presented principally as use cases rather than a compelling biological narrative of their own).
Response 3.3 The focus of our manuscript was the reintroduction of group factor analysis for the novel applications of the inference of multicellular programs and the sample-level unsupervised analysis from single-cell data. Given the distinct possibilities of post-hoc analyses, we mainly used acute and chronic heart failure data to showcase the utility of MOFA to connect spatial and bulk modalities with single-cell data.
That said, as discussed in response 1.1, our analyses allowed to generate novel hypotheses of these datasets:
In myocardial infarction, we found that our estimated multicellular programs associated with cardiac remodeling capture cell-state-independent gene expression changes. This provides a novel understanding of the effect of disease contexts in the expression profiles of specialized cells. In other words, we found that cell-states, regardless of their specialized function, share a common response in the tissue context.
In chronic heart failure, we identified a conserved multicellular program of cardiac remodeling across patient cohorts and etiologies, suggesting a common chronic phase between distinct initial causes of heart failure, which again may be linked to the dominating response to the tissue context that is shared across etiologies.
These two results support the observation that deconvoluted chronic heart failure multicellular programs from bulk transcriptomics better classify patients in comparison to classic cell-type composition deconvolution of bulk data. To our knowledge, this finding was not presented in any of the manuscripts of other methodologies focused on MCPs. We summarize these results in the third paragraph of the discussion in the manuscript:
“In an application to a collection of public single-cell atlases of acute and chronic heart failure, we found evidence of dominant cell-state independent transcriptional deregulation of cell-types upon myocardial infarction. This may suggest that while certain functional states within a cell-type are more favored in a disease context, most of the cells of a specific type have a shared transcriptional profile in disease tissues. If part of this shared transcriptional profile is interpreted as a signature of the tissue microenvironment that drives cells in tissues towards specific functions, this result may also indicate that a major source of variability across tissues, besides cellular composition, is the degree in which the homeostatic transcriptional balance of the tissue is disturbed. By combining the results of multicellular factor analysis with spatial transcriptomics datasets, we explored this hypothesis and identified larger areas of cell-type-specific transcriptional alterations in diseased tissues. Given these observations on global alterations upon myocardial infarction, we meta-analyzed single-cell samples from two additional studies of healthy and heart failure patients with multiple cardiomyopathies. Here, we found a conserved transcriptional response across cell-types in failing hearts, despite technical and clinical variability between patients. Further, we could find traces of these cell-type alterations in independent bulk data sets. These observations suggest that our approach can estimate cell-type-specific transcriptional changes from bulk data that, together with changes in cell-type compositions, describe tissue pathophysiology. Altogether, these results highlight how MOFA can be used to integrate the measurements of independent single-cell, spatial, and bulk datasets to measure cell-type alterations in disease.”
To fully assess the relevance of these observations, they should be investigated in more datasets and analyses, where shared functional cell-states across distinct heart failure etiologies are identified and then compared at their compositional and molecular level. This, in our opinion, represents an independent study on its own.
3.4 Altogether, I found the framing of this manuscript very puzzling. It is possible the result would be more clearly presented if the use case was the major focus rather than the more conceptual point about factor analysis.
Response 3.4 Thanks for the suggestion. The major aim of this manuscript is to highlight the versatility of the generalization of group factor analysis as implemented in MOFA for novel applications in single-cell data analysis, beyond multimodal integration of single cells. The definition of multicellular programs from single-cell data and its sample-level unsupervised analysis are relatively new analyses in the field, and thus we believe that it is timely to show how a known statistical framework can be used for these applications.
We believe that a detailed analysis of single-cell datasets of heart failure deserves its own focus and it is out of scope of our current objective with this manuscript. We apologize for the apparent misunderstanding of the objective of our methodology. We will add these distinctions in the introduction of the manuscript.
References
Argelaguet R, Cuomo ASE, Stegle O & Marioni JC (2021) Computational principles and challenges in single-cell data integration. Nat Biotechnol 39: 1202–1215
Armingol E, Baghdassarian H, Martino C, Perez-Lopez A, Knight R & Lewis NE (2021) Context-aware deconvolution of cell-cell communication with Tensor-cell2cell. BioRxiv
Jerby-Arnon L & Regev A (2022) DIALOGUE maps multicellular programs in tissue from single-cell or spatial transcriptomics data. Nat Biotechnol 40: 1467–1477
Kuppe C, Ramirez Flores RO, Li Z, Hayat S, Levinson RT, Liao X, Hannani MT, Tanevski J, Wünnemann F, Nagai JS, et al (2022) Spatial multi-omic map of human myocardial infarction. Nature 608: 766–777
Macnair W, Calini D, Agirre E, Bryois J, Jaekel S, Kukanja P, Stokar-Regenscheit N, Ott V, Foo LC, Collin L, et al (2022) Single nuclei RNAseq stratifies multiple sclerosis patients into three distinct white matter glia responses. BioRxiv
Mitchel J, Gordon MG, Perez RK, Biederstedt E, Bueno R, Ye CJ & Kharchenko P (2022) Tensor decomposition reveals coordinated multicellular patterns of transcriptional variation that distinguish and stratify disease individuals. BioRxiv
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Referee #3
Evidence, reproducibility and clarity
This manuscript by Saez-Rodriguez and colleagues proposes to repurpose Multi-Omics Factor Analysis for the use of single cell data. The initial open problem stated by the paper is the need for a framework to map multicellular programs (such as derived from factor analysis) to other modalities such as spatial or bulk data. The authors propose to repurpose MOFA for use in single cell data. Case studies involve human heart failure datasets (and focuses on spatial and bulk comparisons).
There are particular issues with clarity regarding the key methodological contribution (and assessment of it), discussed under significance.
Significance
- I am very puzzled by the repeated claims the manuscript makes that their central methodological contribution and innovation is to use MOFA for single cell data. One of their citations for MOFA is to MOFA+, which is precisely that (in a relatively popular manuscript published by the original authors of MOFA and not overlapping with the present authors). I am left to wonder what I missed.
- Multimodal integration methods are fairly numerous and even if they're not all exactly factor analyses, it's strange to argue that MOFA fills some unique conceptual gap. I agree it fills something of an interesting gap (except for MOFA+ already filling it), but it's not like the quite popular spatial to single-cell integration approaches aren't doing similar things. If this is a methods paper (as it is presented) then there would have to be very substantially more comparative evaluation to these other approaches.
- The biological use cases are comparatively interesting and dominate the manuscript (but are still presented principally as use cases rather than a compelling biological narrative of their own).
Altogether, I found the framing of this manuscript very puzzling. It is possible the result would be more clearly presented if the use case was the major focus rather than the more conceptual point about factor analysis.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
Summary:
The authors use MOFA, an unsupervised method to analyze multi-omics data, to create multicellular programs of cross-condition multi-sample studies. First, for each cell-type, a pseudobulk expression matrix per sample is created. The cell-type now functions as the separate view, typically reserved for the different omics layers in MOFA. This then results in a latent space with a certain number of factors across samples. The factors, representing coordinated gene expression changes across cell-types, can then be checked for associations with covariates of interest across the samples. MOFA is well-suited for this task, as it can handle missing data and it is a linear model facilitating the interpretation of the factors. Users should be aware that MOFA can estimate the number of factors, but the pseudobulk profiles require a rigorous selection of cell-type specific marker genes. The result will be most suited for downstream analysis if there is a clear association with one factor and a clinical covariate of interest. In a final step, a positive or negative gene signature can be created by setting a cut-off on the gene weights for that specific factor. The method is applied on 3 separate data sets of heart disease, each time demonstrating that at least one of the factors is associated with a disease covariate of interest. The authors also compare the method to a competitor tool, scITD, and explore to what extent a factor mainly captures variance associated with (i) a general condition covariate or rather (ii) specific cell states. The multicellular programs are also mapped to spatial data with spot resolution. Though this analysis does not bring any novel biological insight in the use case, it does support the claim that the programs are associated with the covariate of interest. The most interesting applications of MOFA are in my opinion the potential for meta-analysis of single-cell studies and validation of cell-type specific gene signatures with publicly available bulkRNAseq data sets. The authors provide various data sets and data types to support their claims and the paper is well written. The relevant code and data has been made available.
Major comments
- What is the added value of the gene signatures obtained from MOFA compared to e.g. a naive univariate approach? In theory, a similar collection of genes or gene signature could be obtained by running a differential gene expression analysis across the samples for each cell-type (e.g. myogenic vs ischemic ) and applying a set of relevant cut-offs or filters on the results. In other words, does MOFA detect genes that would otherwise be missed?
- Could scITD also be used for meta-analysis or could the obtained gene signatures of that method also be mapped to bulkRNAseq data? If so, it would be interesting to show the relative performance with MOFA. If not, this specific advantage should be highlighted.
- Users need to specify gene set signatures based on the weights for a factor of interest. This might suggest a limitation to categorical covariates of interest. If the authors see potential for a continuous covariate of interest, this should at least be highlighted in the text and if possible demonstrated on a use case.
Minor comments
- In Figure 2c the association between factor 2 and the technical factor shows a very strong outlier. Please verify that the association is still significant after applying a more robust statistical test (e.g. non-parametric test as Wilcoxon).
- For mapping the cell-type specific factor signatures to bulk transcriptomics, the exact performed comparison or model is unclear. There are seven cell-type signatures for each sample in every study. Was there a t-test run for each cell-type or was a summary measure taken across the cell-types? he thresholding is also rather lenient (adj. p-val 0.1).
- typo in abstract: In sum, our framework serves as an exploratory tool for unsupervised analysis of cross-condition single-cell atlas and allows for the integration of the measurements of patient cohorts across distinct data modalities
- In Figure 4a it is not clear to me why on the one hand we see marker enrichment vs loading enrichment with healthy and disease.
- IN Figure 4b it would help if the same color scheme would be maintained throughout the paper (here now black and white) and if for the cell states the boxplots would be connected per condition, emphasizing the (absence) of change across cell states within a condition.
Significance
General assessment:
MOFA is well-suited for detecting multicellular programs because it can handle missing data and allows for easy interpretation of the factors as a linear method. It might have particular potential for meta-analysis across multiple studies and reevaluating bulkRNAseq data sets, but in the current manuscript it is unclear to what extent this is a specific advantage of MOFA or could also be done with competitors. The authors show how the obtained results and associations with clinical covariates can be validated across multiple data types. How the resulting multicellular programs can provide additional biological insight or form the starting point for additional downstream analysis (e.g. cell communication) is not covered in the paper.
Audience: This paper will be mainly of interest to a specialized public interested in unsupervised methods for large scale multi-sample and multi-condition studies.
Reviewer: main background in the analysis of scRNAseq data.
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Referee #1
Evidence, reproducibility and clarity
Remark to authors
Flores et al. present a pipeline in which they leverage MOFA framework, a matrix factorization algorithm to infer multi-cellular programs (MCPs). Learning and using MCP has already been proposed by others. Yet, authors pursue a similar goals by using MOFA, providing a cell*sample matrix for different cell types as different views (instead of multiple modalities/views) as the input. They later apply MOFA using this data format on a series of applications to analyze acute and chronic human heart failure single-cell datasets using MCPs. Authors further try to expand their analysis by incorporating other modalities.
Major points:
As briefly outlined in the remarks, the current manuscript needs novel findings and methodology to grant a research article which I can' see here. The underlying matrix factorization is the original MOFA (literally imported in the code) with no modification to further optimize the method toward the task. While I appreciate and acknowledge the author's efforts resulting in a detailed analysis of heart samples, I think all of these could have been part of MOFA's existing tutorials.
How can you explain that the results in donor-level analyses are not due to technical artifacts (batch variation)? Can this be used to infer a new patient similarity map? For example, I would test this by leaving out a few patients from training, projecting them, and seeing where they would end up in the manifold or classifying disease conditions for new patients and explaining the classification by MCPs responsible for that condition.
The bulk and spatial analysis are used posthoc after running MOFA, I think since MOFA can use non-overlapping features set, it would be interesting to see if deconvoluted bulk or ST data can be encoded as another view (one view from scRNAseq data for each cell-type and another view from bulk RNA-seq or ST, you can get normalized expression per spot (for ST) or per sample (for bulk) and use them as input.
Minor:
Some figure references are not correct (e.g., "the single-cell data into a multi-view data representation by estimating pseudo bulk gene expression profiles for each cell-type across samples (Figure 1b)." should be figure 2b)
The paper is well written, but there could be some more clarifications about what authors consider as cell-type and cell-state, condition, MCPs which I think is critical to current analysis (see here https://linkinghub.elsevier.com/retrieve/pii/S0092867423001599) for the reader not familiar with those concepts.
Significance
While I find the concept of MCPs interesting, the current work seems like a series of vignettes and tutorials by simply applying MOFA on different datasets (The authors rightfully state this). However, It needs to be clarified what the novelty is since there is no algorithmic improvement to current MCP methods (because there is no new method) nor novel biological findings. Additionally, even in the current form, the applications are limited to the heart, and the generalization of this proposed analysis pipeline to other tissues and datasets is not explored. Overall, the paper lacks focus and novelty, which is required to grant a publication at this level.
expertise: Computational biology, single-cell genomics, machine learning
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
The work presented here examined the combined contribution of intermediate gray matter spinal interneurons of the spinal lumbar enlargement (L2-L4) to locomotion in rats. By targeting this region with kainic acid, we were able to produce a specific locomotor signature that was not compensated for over time, indicating the need for cellular replacement therapies in the treatment of such spinal cord injuries leading to the loss of spinal enlargement intermediate gray matter. Further, the newly developed techniques of a combinatorial behavioral assessment using Random Forest classification and a machine learning intermediate gray matter neuronal loss assessment established in this work add an unbiased, in-depth approach that we are making available to others.
The reviewers have critically evaluated our work and highlighted points of weakness either in the research itself or in connecting with our audience. Below is our detailed response to all the comments as well as our revision plan for submission. We believe we have been able to sufficiently address the concerns that were voiced to strengthen our manuscript and express our gratitude for the feedback.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): __ In this paper, Kuehn and colleagues report on the analysis of functional impairments following intermediate gray matter lesion with kainic acid. The image convincingly show that mostly purely grey matter lesion can be achieved throughout the paper. The authors took care to do a battery of well-designed behavioral tests and sophisticated analysis in order to access functional impairment. They then correlate their behavioral assessment to lesion size, the number of NeuN positive cells in layers V-VII epicenters as well motoneuron numbers and the percentage of white matter. Overall, the manuscript is well written, nicely framed in the existing literature, very clear and the experiments are simple but well designed. The behavioral testing and evaluations including random forest ranking are well performed. The methodology is complete and would allow reproducing the experiments. Statistics are used appropriately. We have however some reserves and comments on some of the results and interpretations. Addressing these comments would not involve new experiments but new re-analysis of the existing datasets.
Major comments:__
__ While the claims that grey matter lesions trigger major behavioral impairments is convincing in particular with the refine behavioral experiments performed, the key claim that only interneuron loss in layer V-VII mediates those deficits is currently not supported by the presented data. In particular, we would suggest that the lesions performed, in contrast to the claims, are not purely and selectively impacting layer V-VII but might also impact layers VIII-IX. We think that presenting neuronal counts based on NeuN staining separately for layer I-IV, V-VII, VIII-IX and comparing control vs KA is necessary. Only with these data can conclusions be supported either in the direction suggested by the authors or otherwise.__
- Although primarily targeting laminae V-VII, we realize this is not exclusively doing so with our lesion model. We understand the value of what you request and are retraining our computer models to be able to do the additional neuronal quantification in laminae I-IV, VIII, IX. We will then combine lamina VIII with laminae V-VII to make up the intermediate gray matter NeuN counts. Completion of all manually validated new analysis is ongoing and will be finished shortly. We plan on adding this additional analysis to the paper, which means much of Figure 6 and Supplementary Figure 3 will be altered and partially for Figure 7, but we won’t know exactly how until we finish the analysis. Tracked changes are shown in the updated manuscript PDF and highlighted text may change depending on results of this analysis.
Another claim relative to the lack of involvement of motoneurons in the related behavioral deficits is also difficult to resolve with the current data. Motoneurons have been identified based on NeuN staining and size. While this is not the state of the art (ChAT staining would have been preferable), it remains acceptable. However, the data presented figures 7 and 8 show a very wide range in the motoneuron count (15 to 50) indicating either motoneuron loss or a count performed at different lumbar levels in the animals. This raises questions on the model (is it really involving only layers V-VII?) or on the interpretation of the data. Therefore we believe that motoneurons counts need to be presented separately (see above) in control vs KA groups and data need to be discussed in this perspective. Authors should also tone down the specificity of the model and involvement of motoneurons accordingly (page 20 for example).
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Although we agree with the reviewers that ChAT staining would have been preferable, we had a limited amount of tissue available. Our unbiased, machine-learning-based analysis of neuronal loss by NeuN required much of the existing tissue. However, neuronal staining has been previously established to identify motoneurons based on size inclusion (Hadi et al., 2000; Wen et al., 2015), as we have used here. Additionally, we will be including total neuronal analysis from lamina IX as requested (please see answer to previous comment).
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By including the Controls along with the KA rats, we postulate that the wide range of motoneuron numbers is due to natural individual variation as well as due to variation at each spinal level, and not due to the KA lesion, as the KA animals have a range of motoneuron counts, sometimes even greater than the controls (Figure 7 and 8). However, as requested, we have split L2, L3 and L4 (graphs below) and still do not see a correlation with behavioral performance (BBB and inclined beam). The variation due to spinal level may partially be explained by the fact that there are different numbers of motoneurons at each spinal level, dependent upon the number of muscles each spinal level is responsible for and the number of motor columns at a given level (Mohan et al., 2015; Nicolopoulos-Stournaras & Iles, 1983). These counts are taken from a given section and not the entirety of the spinal level, adding further possible variation. Moreover, we have removed the controls as suggested (graphed below) for motoneuron analysis and still do not see a correlation between the number of motoneurons and behavioral performance (BBB and inclined beam). We do not find this the correct way to graphically represent the data as it does not allow the reader to see the natural number of motoneurons that exist at each spinal level and variation within as well as knowing that this is not due to injury correlating with behavioral differences, and therefore we would like to keep these graphs with controls in the manuscript.
We have toned down the specificity of the model and involvement of motoneurons as requested on pages 20-21.
Most of the conclusions rely on correlations that include control animals (injected with saline hence with no lesions and no behavioral deficits; Fig 6 and 7). This artificially skews the correlations as those animals show no lesions and good performance in the behavioral tests. These correlations need to be performed only with KA injected animals to determine the respective involvements of interneurons and motoneurons.
- To address your concern, we first did as you asked and removed the controls and performed the correlation analysis for Figure 6, shown below. There are no significant correlations between neurons at each spinal level and behavior. We would further argue that unlike a contusion injury where control animals only receive a laminectomy, our control animals have very minor neuronal loss due to the saline injection itself and therefore do have a minor lesion. An example of this is seen in Figure 6 for the control animal at spinal level L2 where the pipette track is visible. Therefore, to show that the observed behavioral deficits are from the kainic acid and not the injection itself, we would argue that it is important that the control animals remain in the correlation analysis.
The long-term study (Fig 8) is performed with very few animals and hence, drawing conclusions from these animal numbers is difficult. All correlations are performed including control animals which is even more of a problem here as in Figure 6 and 7 due to the low number of animals. The authors should either add animals or remove the figure. When control animals (injected with saline) are removed (as they do not show any lesion and perform accurately in the behavior), one would actually see a correlation between the number of motoneurons and the behavioral performance (Fig. 8E,F) but not with the lesion size (Fig.8C,D).
- The long-term study was planned with more animals, but due to exclusion criteria by lesion length, the numbers remain low. We had discussed extensively whether to include this data in the manuscript or not. We decided for several reasons to include it in the manuscript within the main figures. First, it demonstrates that once these interneurons are lost, there are no compensatory mechanisms that restore function, which is quite striking given that the ones that lose weight support by 2 weeks do not regain it over a 3-month observational period. Further indicating that loss of lumbar gray matter interneurons is essential to locomotor function of hindlimbs and should be targeted in SCI replacement therapeutics. However, we do not agree with removing controls to examine the motoneuron number as there is motoneuron number variation within the lesion area and the motoneuron number from the KA animals is within the Control motoneuron range, which can be seen with the graph including the Controls. We can provide the individual spinal lesion level correlations, but this does not provide the entire picture as one level alone has not been found to be essential to the behavioral deficits. We are currently processing these animals to also provide NeuN numbers from laminae I-IV, V-VIII and IX.
Minor comments:
__ Figure 1A: if lesions are bilateral, it would be nice to illustrate this on the schematic.__
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This has been fixed. Figure 1B-D: scale bars are missing
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This has been fixed. Figure 3H: What represents the y-axis? % of completion or number of completion?
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This has been fixed. Figure 4 Table: Please specific what the acronym stands for: pLDA.
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This has been clarified in the figure legend. Figure 6 A: scale bars are missing
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This will be fixed when the data for the analysis is finished and the figure is redone. Figure 6B/C/D: please add the spinal level analyzed directly on the graphs. This will ease the comprehension.
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This has been adjusted. Figure 7 and Figure 8: While it is quite convincing that the model is purely a grey matter injury (panel C and D), the data are very much spread out for the number of motoneurons per mice (see major comments above). We would suggest to plot those data to present the number of neurons (interneurons in layer I-IV, V-VII and motoneurons) control vs KA.
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Thank you for the suggestion. We will plan on presenting the additional neuronal quantification data mentioned above by comparing Controls and KA animals.
Dots are missing on those figures (probably superimposed on top of each other). This should be changed to see all data points
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Thank you for the observation. They were superimposed but we have fixed this. Figure 8E,F: the number of motoneurons is very low also in controls. How is this explained?
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Depending on where the section was taken at each spinal level, there is variation in the number of motoneuron columns innervating targeted muscles (Mohan et al., 2015), Figure 6). Therefore, it is not surprising to see a range of motoneurons. In addition, we would like to clarify that these motoneuron counts are taken from only three sections across the lesion (from the three lesion injection epicenters), not the whole lumbar section. Often the motoneuron number in the KA group was equal to or greater than the Control group, indicating more often variation than motoneuron loss. Regardless motoneuron numbers do not correlate with the observed behavioral deficits.
__Reviewer #1 (Significance (Required)):
This paper by Kuehn and colleagues reports on the functional impairments that follow intermediate gray matter lesions using kainic acid. This work is largely confirmatory of previous studies (Magnuson et al., 1999; Hadi et al., 2000) with modern behavioral evaluation. After revision, it would provide a description of the functional impairments following those specific lesions. The paper would be informative for a specific audience in particular scientists in the field of spinal cord injury and spinal interneuron. Our field of expertise is spinal cord injury, inflammation, behavior and axon outgrowth.__
__Reviewer #2 (Evidence, reproducibility and clarity (Required)):
This manuscript reports on a pair of well-designed and well-carried out studies investigating a Kainic Acid (KA)-mediated gray matter lesion in the lumbar enlargement of adult female SD rats. The investigators demonstrate, using NeuN immunohistochemistry, that the KA lesion reduces NeuN positive cells along the length of the lumbar spinal cord from rostral to L2 to slightly caudal to L4 following 6 separate injections made on the right and left sides of the spinal cord at L2, L3 and L4. The investigators made significant efforts to avoid depleting neurons in the dorsal and ventral horns, and the evidence provided suggests they were successful. The methodology described is sound and sufficient details are provided to allow the reader to fully understand the studies. It is outstanding that the study was done while following all of the PREPARE and ARRIVE guidelines. A second major component of the work is the use of multiple outcome measures and efforts (using a Forest analysis) to develop a relatively quick, accurate and efficient system to screen or classify the injuries in individual animals within 2 weeks of the injury so that subsequent treatments could be done on animals which received injuries of sufficient severity (within a relatively narrow range) and with balanced experimental and groups. Again, with this effort the investigators were largely successful. The KA lesion results in persistent locomotor and sensorimotor deficits, that plateau early without substantial sensory dysfunction.__
Major Comments:
__ Introduction: Overall, the rationale presented and the review of the pertinent literature is solid, with the following exception: The authors state that their model should allow them to thoroughly investigate the behavioral readout of premotor IN loss. It is generally accepted that the designation of premotor interneurons refer to those directly connected to motor neurons, and while the chosen KA lesion certainly targets some premotor neurons, it also targets many other interneurons that do not directly contact motoneurons. Please revise how the lesions are referred to. In the very next paragraph the targets are defined somewhat differently as "INs and propriospinal INs in laminae V-VII in spinal levels L2-L4".__
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We agree that our wording does cause confusion to the reader and to avoid this we have now made the change from premotor INs to SpINs (pages 3-5).
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On a side note, we would like to state these are adult female Fischer rats and not adult female SD rats, also described in the methods.
Spared white matter. In many (but not all) labs, spared white matter at the epicenter is an important measurement because it presumably represents all the spared axons, such that any/all rostrocaudal communication is represented. Thus, it is the single point (or section, in this case) that has the smallest number of axons represented as stained white matter. So, to indicate that you assessed "three epicenters per spinal cord" doesn't make sense in this context, Even if you are referring to three separate KA injection sites (L2, L3 and L4). Thus, averaging three sections also doesn't really make sense because the actual epicenter should be represented by the single cross section that has the smallest area of stained white matter. Also related to spared white matter, in many labs they calculate %SWM based on a section from a control animal, and this should reduce variability because some cords shrink (injured gray matter) more than others after the injury, whether it be a contusion or mild excitotoxic injury. Please either re-calculate your SWM or provide additional justification for your current method.
- We agree with the reviewer that normally only the epicenter of the lesion needs to be examined for white matter damage as once the connection is severed it does not matter what is rostral or caudal to this site. However, in our case we do not find any significant differences in white matter between the Controls and the KA groups. To be certain we looked at all three lesion epicenters where the damage occurred. If you examine the graphs below, you will notice that in fact the KA animals have a higher % white matter of the CSA than the Controls. Given how this analysis is done we are looking at % white matter of the cross sectional area (CSA). In the KA animals the loss of gray matter causes a collapse that makes it appear as though the white matter covers more of the CSA area than it normally does. Even if we were to normalize to the Controls you would see the same as what you already observe in these graphs.
For this reason, we have compared the average area of white matter at the three lesion epicenters between the Control and KA groups and did not find significant differences (new Figure 7C). We also evaluated average area of white matter at the individual spinal levels (L2-L4) and did not find significant differences between the two groups and therefore averaged them. This indicates that we are not seeing any white matter alterations with our lesion model.
Results: Within the results (and elsewhere) there are a number of un-supported statements that should be removed, softened or supported. For example, on page 18 the authors talk about how the CatWalk "further investigates the role of propriospinal INs connecting the cervical and lumbar enlargements" and no reference is provided.
- The requested references have now been added.
It is important to note that two animals were not included overall because they were unable to perform the CatWalk assessment. Additional information about these animals might be helpful to further characterize the KA lesions, for example, when they are too large.
- Yes, we have looked into this. Lesion size appears to play a role (Figure 2C) but does not appear to be the only determining factor as two animals (KA#6, KA#7) with and without weight support had the same lesion length (10,325um). We predict this is due to the amount of neuronal loss; KA#7 had greater neuronal loss in all three levels compared to KA#6.
Figure 6 brings up a number of questions including how the three "epicenters" were determined and how some KA lesioned spinal cords appear to have more than 100% the number of neurons in the control spinal cords. Yes, there is variability in normal animals, but still this seems unlikely. Is it possible that the KA injection sites were not accurate in these animals? I know it is unlikely, however, the large number of neurons in some animals at L2 is bothersome. Did the investigators always inject L2, L3 and L4 in that order? Pipettes tend to wick up liquid thus diluting the drug/cells/whatever at the tip.
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We understand your concern of being greater than 100%, therefore we have changed the normalization to the greatest control value vs the average of controls (except for lesion size which is done to largest lesion size overall, new Supplemental Figure 3 and Figures 6 and 7 will be altered once our new analysis is finished).
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Animal KA #1 that you are referring to could have been a technical error due to injections but it is hard to say at this point as we have found nothing from our surgery records that indicate why this animal would be different from others. Yes, bilateral injections were always performed in the same order (L2, L3, L4). However, we think it is unlikely that this created a significant drug dilution problem as we see animals with more damage in L4 than L3 or L2 (KA #3, #6 and #7 in new Supplemental Figure 3). But clearly L2 in animal KA 1 is not significantly damaged.
Also for Figure 6, I am not convinced that the color coding is really very useful here. I think what might be more useful would be some higher magnification images of the intermediate gray matter. This figure also appears to show pipette tracks in some sections suggesting that the KA was leaking up the track either during injection or when the pipette was withdrawn. This is not a serious issue, but might be worth mentioning as a confound.
- First, we would like to clarify that Figure 6 is already a higher magnification image of only laminae V-VII not the entire gray matter (please see figure legend). Figure 1 is a lower magnification but here in Figure 6 we wanted to highlight the region of interest that was analyzed for neuronal loss. Pipette tracks were also observed in the Controls and not thought to be due to KA leakage, as we don’t see neuronal damage beyond the injection tracts in the dorsal horns. With the new figure we will see if the color coding will be added or not dependent on the space available.
Finally, for Figure 6, the correlations shown are quite poor, and would be even worse of control animals were not included. Too much strength is given to these findings.
These issues with Figure 6 become even more serious as we move to Figure 7. Here, looking at the correlation to loss of MNs is weak because this reviewer is not convinced that looking at the "three epicenters" is a valid approach. Were the epicenters identified by particular criteria? Also, I think images showing how MNs were identified and counted would be important, in particular since you did not use ChAT staining but relied on NeuN and size.
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These epicenters were chosen after reviewing all coronal sections in a 1:7 series of the lumbar cord (T12-L5). The three epicenters were the three coronal slices with the greatest neuronal loss (methods, page 12). This is supported by the inflammatory response in these sections (not shown).
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Please see the schematic below that explains the motoneuron analysis that is also performed in our work which is detailed in the methods. Briefly, the cell soma area of NeuN+ cells in lamina IX were measured in Image J. NeuN+ cells with an area greater than 916µm2 were used for the motoneuron analysis (Wen et al, 2015).
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We agree that in Figure 6 the correlations for each spinal level although significant are moderate but this is due to the fact that one given spinal level was not found to be responsible for the behavioral deficits. This is supported by our work on correlation with lesion length, the lesion must span multiple levels to produce the behavioral deficit. Finally, the correlations may change when we add in lamina VIII, but we won’t know until the analysis is finished.
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As for Figure 7, we agree that we do not see correlations and our argument is that motoneuron and white matter area are not responsible for the behavioral deficits we observe (new Figure 7). Therefore, you are reading those correctly, these are not significant correlations.
Discussion Yes, interneurons in the intermediate gray matter throughout the lumbar enlargement "regulate lower motoneurons" but they also do other things, most notably communicating both intra and intersegmentally (short and long propriospinals). Please adjust this statement.
- We appreciate this detailed feedback, we have adjusted this statement to the following:
“Damage to this area, which includes regulation of lower motoneurons leads not only to gross motor deficits (BBB score), but rhythmic and skilled walking (even and uneven horizontal ladders), coordination (BBB subscore), balance (inclined beam) and gait deficits (CatWalk), as well.” (page 25)
On page 25, you talk again about premotor SpINs. I understand that you are using this term/nomenclature to distinguish these INs from motoneurons, but this is problematic because many if not most of your readers will assume the premotor SpINs synapse directly onto MNs, which of course many of the INs that are eliminated by KA do not. Calling them simply SpINs would be sufficient and still distinguish them from MNs.
- We have adjusted this to the term “SpIN and premotor circuitry” on pages 26 and 27.
On page 27 you talk about the RI, and while there is a statistically significant drop in RI, it must be admitted that the RI remains above 90% (0.9) which means that 9 out of 10 steps use a normal sequence. Thus, I think it is misleading to indicate that this indicates a difference for the KA animals. In fact, I think it is more important to consider how these animals were able to maintain an RI in excess of 90% despite the loss of substantial numbers of INs.
- Thank you for the comment, we have adjusted this in the discussion:
“In addition to gait rhythm changes, we also saw significant differences in pattern generation. The regularity index (RI) measures correctly sequenced footsteps and is used to analyze recovery in mild to moderate injuries and coordination (Koopmans et al., 2005; Kuerzi et al., 2010; Shepard et al., 2021). While KA-animals have a significantly lower RI in comparison to the controls, the RI remains above 90% which is still relatively high given the amount of neuronal loss. However, we would argue that a single parameter is not the defining factor of gait/coordination, but a combination of parameters and tests provides a more comprehensive picture, as we have seen with our pLDA analysis and Random Forest classification approaches.” (Pages 28-29)
The rationale for determining classification prior to histological analysis is somewhat weak, and I think it would be worthwhile strengthening this rationale at the beginning of this paragraph...it becomes more obvious later why this classification is important. Is the variability of the KA model greater than an NYU or IH contusion model? If so, why? The early functional plateau is key to this argument.
- We postulate that less severe SCIs and our milder KA lesion tend to have more variability than more severe SCI models. In the contusion models this is due to the delayed natural compensatory functional recovery plateau that can last up to 5-6 weeks. However with the KA model, variability arises from titrating down KA and adding multiple injection sites increasing variable success rate per injection. In the KA model, the early functional plateau at two weeks allows for correctly excluding or classifying animals into equally lesioned groups prior to treatment with our Random Forest Eco model. We agree that we need to clarify this reasoning in the results and have now done so on page 22. “To test the efficacy of experimental SCI therapies, it is important to effectively evaluate recovery performance through the combination of behavioral tests. In addition to carefully classifying groups at the end of the study, there is a need to provide exclusion criteria and equal sorting of variability between groups prior to treatment (after deficits have stabilized at two weeks).” (page 22)
Minor Comments:
__ Heatmap Analysis: The term "lesion size" is insufficiently accurate to be used in this context. Do you mean lesion length?__
- This term has now been adjusted to lesion length throughout the manuscript and figures.
Kainic Acid injuries are known to be accompanied by cell division and neurogenesis in the brain, and if that kind of thing is happening in the presented model, it could be an interesting confound/addition to the alluded to cellular replacement __therapies.____
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- KA has been shown to be accompanied by cell division and neurogenesis in the brain, however from our own work and previous work with KA in the spinal cord if this occurs it is not at a level that is relevant to functional recovery as evidenced in our long-term study. A previous study by Magnuson et al compared E14 cerebral rat precursor cell transplantation 40 minutes and 4 weeks post-KA injury and did not find significant differences in cell survival/division (Magnuson et al., 2001). Therefore, we do not believe this would hamper or confound our future work with cellular replacement therapies. In addition, cell transplantation would take place 2 weeks post-KA injury when KA would no longer be able to hamper the transplanted cells.
__Reviewer #2 (Significance (Required)):
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__ Overall, this is a well-designed and performed set of studies that takes the KA lesion model into new territory, well set-up to perform delayed (sub-acute or early chronic) neuron replacement studies. The work characterizes a multi-segment but mild KA injury model that demonstrates persistent dysfunction that plateaus early, and a rapid and efficient system to classify the injury with a high predictability of long-term dysfunction by 2 weeks post-injury.
This model should be of interest because it focuses on gray-matter specific tissue loss and functional deficits that should be amenable to neuron replacement strategies without the complications of white-matter dependent functional losses.
My expertise: I have been using a variety of spinal cord injury models, in rats, for many years including contusions, lacerations and excitotoxic (KA) lesions. I have a lot of experience with locomotor, motor and sensory outcome measures. However, I have very limited experience with the Random Forest analysis employed and am not an expert in statistics.__
__References: __
Hadi, B., Zhang, Y. P., Burke, D. A., Shields, C. B., & Magnuson, D. S. (2000). Lasting paraplegia caused by loss of lumbar spinal cord interneurons in rats: no direct correlation with motor neuron loss. J Neurosurg, 93(2 Suppl), 266-275. https://doi.org/10.3171/spi.2000.93.2.0266
Koopmans, G. C., Deumens, R., Honig, W. M., Hamers, F. P., Steinbusch, H. W., & Joosten, E. A. (2005). The assessment of locomotor function in spinal cord injured rats: the importance of objective analysis of coordination. J Neurotrauma, 22(2), 214-225. https://doi.org/10.1089/neu.2005.22.214
Kuerzi, J., Brown, E. H., Shum-Siu, A., Siu, A., Burke, D., Morehouse, J., Smith, R. R., & Magnuson, D. S. (2010). Task-specificity vs. ceiling effect: step-training in shallow water after spinal cord injury. Exp Neurol, 224(1), 178-187. https://doi.org/10.1016/j.expneurol.2010.03.008
Mohan, R., Tosolini, A. P., & Morris, R. (2015). Segmental Distribution of the Motor Neuron Columns That Supply the Rat Hindlimb: A Muscle/Motor Neuron Tract-Tracing Analysis Targeting the Motor End Plates. Neuroscience, 307, 98-108. https://doi.org/10.1016/j.neuroscience.2015.08.030
Nicolopoulos-Stournaras, S., & Iles, J. F. (1983). Motor neuron columns in the lumbar spinal cord of the rat. J Comp Neurol, 217(1), 75-85. https://doi.org/10.1002/cne.902170107
Pitzer, C., Kurpiers, B., & Eltokhi, A. (2021). Gait performance of adolescent mice assessed by the CatWalk XT depends on age, strain and sex and correlates with speed and body weight. Sci Rep, 11(1), 21372. https://doi.org/10.1038/s41598-021-00625-8
Shepard, C. T., Pocratsky, A. M., Brown, B. L., Van Rijswijck, M. A., Zalla, R. M., Burke, D. A., Morehouse, J. R., Riegler, A. S., Whittemore, S. R., & Magnuson, D. S. (2021). Silencing long ascending propriospinal neurons after spinal cord injury improves hindlimb stepping in the adult rat. Elife, 10. https://doi.org/10.7554/eLife.70058
Wen, J., Sun, D., Tan, J., & Young, W. (2015). A consistent, quantifiable, and graded rat lumbosacral spinal cord injury model. J Neurotrauma, 32(12), 875-892. https://doi.org/10.1089/neu.2013.3321
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Referee #2
Evidence, reproducibility and clarity
This manuscript reports on a pair of well-designed and well-carried out studies investigating a Kainic Acid (KA)-mediated gray matter lesion in the lumbar enlargement of adult female SD rats. The investigators demonstrate, using NeuN immunohistochemistry, that the KA lesion reduces NeuN positive cells along the length of the lumbar spinal cord from rostral to L2 to slightly caudal to L4 following 6 separate injections made on the right and left sides of the spinal cord at L2, L3 and L4. The investigators made significant efforts to avoid depleting neurons in the dorsal and ventral horns, and the evidence provided suggests they were successful. The methodology described is sound and sufficient details are provided to allow the reader to fully understand the studies. It is outstanding that the study was done while following all of the PREPARE and ARRIVE guidelines. A second major component of the work is the use of multiple outcome measures and efforts (using a Forest analysis) to develop a relatively quick, accurate and efficient system to screen or classify the injuries in individual animals within 2 weeks of the injury so that subsequent treatments could be done on animals which received injuries of sufficient severity (within a relatively narrow range) and with balanced experimental and groups. Again, with this effort the investigators were largely successful. The KA lesion results in persistent locomotor and sensorimotor deficits, that plateau early without substantial sensory dysfunction.
Major Comments:
Introduction: Overall, the rationale presented and the review of the pertinent literature is solid, with the following exception: The authors state that their model should allow them to thoroughly investigate the behavioral readout of premotor IN loss. It is generally accepted that the designation of premotor interneurons refer to those directly connected to motor neurons, and while the chosen KA lesion certainly targets some premotor neurons, it also targets many other interneurons that do not directly contact motoneurons. Please revise how the lesions are referred to. In the very next paragraph the targets are defined somewhat differently as "INs and propriospinal INs in laminae V-VII in spinal levels L2-L4".
Spared white matter. In many (but not all) labs, spared white matter at the epicenter is an important measurement because it presumably represents all the spared axons, such that any/all rostrocaudal communication is represented. Thus, it is the single point (or section, in this case) that has the smallest number of axons represented as stained white matter. So, to indicate that you assessed "three epicenters per spinal cord" doesn't make sense in this context, Even if you are referring to three separate KA injection sites (L2, L3 and L4). Thus, averaging three sections also doesn't really make sense because the actual epicenter should be represented by the single cross section that has the smallest area of stained white matter. Also related to spared white matter, in many labs they calculate %SWM based on a section from a control animal, and this should reduce variability because some cords shrink (injured gray matter) more than others after the injury, whether it be a contusion or mild excitotoxic injury. Please either re-calculate your SWM or provide additional justification for your current method.
Results: Within the results (and elsewhere) there are a number of un-supported statements that should be removed, softened or supported. For example, on page 18 the authors talk about how the CatWalk "further investigates the role of propriospinal INs connecting the cervical and lumbar enlargements" and no reference is provided.
It is important to note that two animals were not included overall because they were unable to perform the CatWalk assessment. Additional information about these animals might be helpful to further characterize the KA lesions, for example, when they are too large.
Figure 6 brings up a number of questions including how the three "epicenters" were determined and how some KA lesioned spinal cords appear to have more than 100% the number of neurons in the control spinal cords. Yes, there is variability in normal animals, but still this seems unlikely. Is it possible that the KA injection sites were not accurate in these animals? I know it is unlikely, however, the large number of neurons in some animals at L2 is bothersome. Did the investigators always inject L2, L3 and L4 in that order? Pipettes tend to wick up liquid thus diluting the drug/cells/whatever at the tip.
Also for Figure 6, I am not convinced that the color coding is really very useful here. I think what might be more useful would be some higher magnification images of the intermediate gray matter. This figure also appears to show pipette tracks in some sections suggesting that the KA was leaking up the track either during injection or when the pipette was withdrawn. This is not a serious issue, but might be worth mentioning as a confound.
Finally, for Figure 6, the correlations shown are quite poor, and would be even worse of control animals were not included. Too much strength is given to these findings.
These issues with Figure 6 become even more serious as we move to Figure 7. Here, looking at the correlation to loss of MNs is weak because this reviewer is not convinced that looking at the "three epicenters" is a valid approach. Were the epicenters identified by particular criteria? Also, I think images showing how MNs were identified and counted would be important, in particular since you did not use ChAT staining but relied on NeuN and size.
Discussion Yes, interneurons in the intermediate gray matter throughout the lumbar enlargement "regulate lower motoneurons" but they also do other things, most notably communicating both intra and intersegmentally (short and long propriospinals). Please adjust this statement.
On page 25, you talk again about premotor SpINs. I understand that you are using this term/nomenclature to distinguish these INs from motoneurons, but this is problematic because many if not most of your readers will assume the premotor SpINs synapse directly onto MNs, which of course many of the INs that are eliminated by KA do not. Calling them simply SpINs would be sufficient and still distinguish them from MNs.
On page 27 you talk about the RI, and while there is a statistically significant drop in RI, it must be admitted that the RI remains above 90% (0.9) which means that 9 out of 10 steps use a normal sequence. Thus, I think it is misleading to indicate that this indicates a difference for the KA animals. In fact, I think it is more important to consider how these animals were able to maintain an RI in excess of 90% despite the loss of substantial numbers of INs.
The rationale for determining classification prior to histological analysis is somewhat weak, and I think it would be worthwhile strengthening this rationale at the beginning of this paragraph...it becomes more obvious later why this classification is important. Is the variability of the KA model greater than an NYU or IH contusion model? If so, why? The early functional plateau is key to this argument.
Minor Comments:
Heatmap Analysis: The term "lesion size" is insufficiently accurate to be used in this context. Do you mean lesion length?
Kainic Acid injuries are known to be accompanied by cell division and neurogenesis in the brain, and if that kind of thing is happening in the presented model, it could be an interesting confound/addition to the alluded to cellular replacement therapies.
Significance
Overall, this is a well-designed and performed set of studies that takes the KA lesion model into new territory, well set-up to perform delayed (sub-acute or early chronic) neuron replacement studies. The work characterizes a multi-segment but mild KA injury model that demonstrates persistent dysfunction that plateaus early, and a rapid and efficient system to classify the injury with a high predictability of long-term dysfunction by 2 weeks post-injury.
This model should be of interest because it focuses on gray-matter specific tissue loss and functional deficits that should be amenable to neuron replacement strategies without the complications of white-matter dependent functional losses.
My expertise: I have been using a variety of spinal cord injury models, in rats, for many years including contusions, lacerations and excitotoxic (KA) lesions. I have a lot of experience with locomotor, motor and sensory outcome measures. However, I have very limited experience with the Random Forest analysis employed and am not an expert in statistics.
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Referee #1
Evidence, reproducibility and clarity
In this paper, Kuehn and colleagues report on the analysis of functional impairments following intermediate gray matter lesion with kainic acid. The image convincingly show that mostly purely grey matter lesion can be achieved throughout the paper. The authors took care to do a battery of well-designed behavioral tests and sophisticated analysis in order to access functional impairment. They then correlate their behavioral assessment to lesion size, the number of NeuN positive cells in layers V-VII epicenters as well motoneuron numbers and the percentage of white matter. Overall, the manuscript is well written, nicely framed in the existing literature, very clear and the experiments are simple but well designed. The behavioral testing and evaluations including random forest ranking are well performed. The methodology is complete and would allow reproducing the experiments. Statistics are used appropriately. We have however some reserves and comments on some of the results and interpretations. Addressing these comments would not involve new experiments but new re-analysis of the existing datasets.
Major comments:
While the claims that grey matter lesions trigger major behavioral impairments is convincing in particular with the refine behavioral experiments performed, the key claim that only interneuron loss in layer V-VII mediates those deficits is currently not supported by the presented data. In particular, we would suggest that the lesions performed, in contrast to the claims, are not purely and selectively impacting layer V-VII but might also impact layers VIII-IX. We think that presenting neuronal counts based on NeuN staining separately for layer I-IV, V-VII, VIII-IX and comparing control vs KA is necessary. Only with these data can conclusions be supported either in the direction suggested by the authors or otherwise.. Another claim relative to the lack of involvement of motoneurons in the related behavioral deficits is also difficult to resolve with the current data. Motoneurons have been identified based on NeuN staining and size. While this is not the state of the art (ChAT staining would have been preferable), it remains acceptable. However, the data presented figures 7 and 8 show a very wide range in the motoneuron count (15 to 50) indicating either motoneuron loss or a count performed at different lumbar levels in the animals. This raises questions on the model (is it really involving only layers V-VII?) or on the interpretation of the data. Therefore we believe that motoneurons counts need to be presented separately (see above) in control vs KA groups and data need to be discussed in this perspective. Authors should also tone down the specificity of the model and involvement of motoneurons accordingly (page 20 for example). Most of the conclusions rely on correlations that include control animals (injected with saline hence with no lesions and no behavioral deficits; Fig 6 and 7). This artificially skews the correlations as those animals show no lesions and good performance in the behavioral tests. These correlations need to be performed only with KA injected animals to determine the respective involvements of interneurons and motoneurons.<br /> The long-term study (Fig 8) is performed with very few animals and hence, drawing conclusions from these animal numbers is difficult. All correlations are performed including control animals which is even more of a problem here as in Figure 6 and 7 due to the low number of animals. The authors should either add animals or remove the figure. When control animals (injected with saline) are removed (as they do not show any lesion and perform accurately in the behavior), one would actually see a correlation between the number of motoneurons and the behavioral performance (Fig. 8E,F) but not with the lesion size (Fig.8C,D).
Minor comments:
Figure 1A: if lesions are bilateral, it would be nice to illustrate this on the schematic.
Figure 1B-D: scale bars are missing
Figure 3H: What represents the y-axis? % of completion or number of completion?
Figure 4 Table: Please specific what the acronym stands for: pLDA.
Figure 6 A: scale bars are missing
Figure 6B/C/D: please add the spinal level analyzed directly on the graphs. This will ease the comprehension.
Figure 7 and Figure 8: While it is quite convincing that the model is purely a grey matter injury (panel C and D), the data are very much spread out for the number of motoneurons per mice (see major comments above). We would suggest to plot those data to present the number of neurons (interneurons in layer I-IV, V-VII and motoneurons) control vs KA.
Dots are missing on those figures (probably superimposed on top of each other). This should be changed to see all data points
Figure 8E,F: the number of motoneurons is very low also in controls. How is this explained?
Significance
This paper by Kuehn and colleagues reports on the functional impairments that follow intermediate gray matter lesions using kainic acid. This work is largely confirmatory of previous studies (Magnuson et al., 1999; Hadi et al., 2000) with modern behavioral evaluation. After revision, it would provide a description of the functional impairments following those specific lesions. The paper would be informative for a specific audience in particular scientists in the field of spinal cord injury and spinal interneuron.
Our field of expertise is spinal cord injury, inflammation, behavior and axon outgrowth.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
*Randhawa and co-authors have studied various aspects of the regulation of lignocellulose degradation by the filamentous ascomycete fungus Penicillium funiculosum. Over-expression of the well-known transcription factor clr2 (which regulates cellulase gene expression in Neurospora and other ascomycetes) in a delta-mig1 strain did not result in an increase in cellulase activity. However, when combined with an increased Ca2+ concentration the cellulase activity in the medium did increase. Using RNA-Seq, the authors have identified a candidate regulator: Snf1. Indeed, a knockout confirms that this gene is involved in the posttranscriptional regulation of cellulase production, specifically by regulating the secretion of the cellulases. *
Major comments:
In general, the topic and results are interesting. There are a few issues that need to be addressed, however. The manuscript would benefit from some careful proofreading. For example, articles ('the', 'a') are frequently missing. Very informal language is sometimes used ('zilch effect'). Put a space between '1000bp', etc. It is 'kDa', not 'kD', etc.
Response – Thank you very much for the encouraging remarks. We have thoroughly checked the manuscript and have added the articles at appropriate places. We have also improved the manuscript’s language and removed any informal language used.
I am a bit puzzled by the choice of calcium source: CaCO3, up to 10 g/L. Calcium carbonate does not efficiently dissolve in water unless the pH is low. Fungi generally acidify their culture medium during growth. As such, calcium carbonate likely has a pH buffering effect. Therefore, the described effects may also be attributed to a more neutral pH of the medium, and not necessarily to an increase in calcium ions.
Response – We completely agree with the reviewer and had the same thought that the pH buffering effect of CaCO3 could be the reason for increased cellulase production. We ruled out this by using 50 mg/l CaCl2 solely in rest of the experiments performed in Fig. 3 and afterwards. We have also mentioned the same in the manuscript (lines 175-178).
The authors have performed RNA-Seq, but as far as I can tell the data has not been made publicly available. At least, the raw reads should be deposited in the Short Read Archive of NCBI (or a similar repository), and preferably also the expression values in GEO of NCBI (or a similar repository).
Response – We will comply and deposit the raw reads in the short read archive of NCBI. We will also be providing the differential analysis of transcription factors expressed under glucose and Avicel in NCIM1228 and ∆Mig1 in the supplementary information.
P21. Very little information is provided in the M&M regarding the gene expression analysis. Provide references to all the tools, as well as the version numbers. Were any non-default parameters used?
Response – We have added the complete information on tools and procedures used for RNA-seq data analysis. For differential expression profiling, all FPKM values were normalized to the library size using the R package, Edge R. The expression value for the transcript was calculated using the reads aligned & normalised it on library size (Total sequencing reads generated) & transcript length giving us FPKM value (Fragments Per Kilobase of transcript per Million mapped reads), and TPM value (Transcript per million reads), which is regarded as normalized expression value for a particular transcript. We have taken the number of reads which got aligned to the conserved transcripts (Present in both the comparison group i.e Wild Type Glu & Cellulose samples (S1, S2, S7 & S8) Vs MIG1 glu & Cellulose sample (S3, S4, S5 & S6) and performed the differential gene expression between the two groups. The excel sheet having differential expression profiling of transcription factors is available as supplementary data.
The authors claim that SSP1 CaMKK phosphorylates SNF1 AMPK (last title of the Results section). I don't see any evidence for a direct interaction between these two proteins. I will believe that they are in the same pathway, but if the authors want to claim a direct interaction then additional experiments will be required. E.g. Y2H.
Response – Ssp1 is known to phosphorylate SNF1 during nutritional stress in S. pombe and they were found to interact directly by Co-IP studies. Based on the literature, we planned to over-express Ssp1 in P. funiculosum.
Minor comments:
- Please add line numbers to the manuscript, this facilitates the review process.*
Response - Line numbers have been added.
*P14 "in all yeasts and filamentous fungi". I doubt that all fungi have been tested. *
Response - The phrase has been modified.
P18. "in diverse yeasts and fungi". Yeasts are also fungi.
Response - The phrase has been modified.
P16. "solves dual purpose". I think this is meant: "serves a dual purpose"?
Response - The phrase has been modified.
*P17, first paragraph: this seems very speculative to me, so it should probably be labeled as such. *
Response - The phrase has been modified.
P21. What reference genome is used? Please cite the paper.
Response - We have our own reference genome in lab which is yet to be published.
Fig 1B. These are reported as volcano plots, but to me it looks like an empty graph (no data points), only a number of genes.
Response - The pictures have been changed.
Fig 1D. What do the colors on the right represent? The colors on the right represents k-means clustering of the genes of transcription factors.
Response - The same has been added to the figure legend also.
On various places in the manuscript the term "three times in triplicate" is used. What is meant here, three technical replicates of each of the three biological replicates?
Response - Yes we mean the same and the phrase has been modified.
P46. "We aimed to sought"
Response - The phrase has been modified.
Abstract: The sentence "Further, Ca2+-signaling" should be rewritten, because currently is seems to suggest that SSP1 downregulates the phospho-HOG1 levels.
Response – As suggested by the Western blot in the Fig.4b, Snf1 gets phosphorylated only when dual signal of calcium and cellulose are present. Since we observed upregulated Ssp1 expression in Avicel (Fig. 4a), and increased Ssp1 expression could increase the phosphorylated Snf1 in the cell (Fig. 7i), our data suggests that Ssp1 phosphorylates Snf1 in a Ca2+-dependent manner. Further Hog1 was found in hyperphosphorylated state in ∆Snf1 (Fig 6e), thus we believe Snf1 AMPK downregulates phospho-Hog1 levels.
Reviewer #1 (Significance (Required)):
*In general, the topic and results are interesting. There are a few issues that need to be addressed, however. The manuscript would benefit from some careful proofreading. *
Response – We highly appreciate the encouraging words of the reviewer. We have addressed all the issues raised by the reviewer. The major ones included the language and readability of the text, which has been improvised. We have replaced the volcano plot figures, and will be uploading the RNA-seq data to the SRA database of NCBI and excel sheet of differential expression analysis of transcription factor will be added as a supplementary file to the manuscript.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
- Randhawa et al. study the effect of loss of function of Snf1 kinase and calcium on the production of enzymes related to cellulose degradation in the fungus Penicillium funiculosum. *
- The manuscript is well structured and the researchers have done an enormous amount of work in constructing a number of mutant strains in this fungus. *
- Transcriptomics and proteomics support the conclusions reached with the strains generated.*
Response - Thank you very much for showing confidence in our research work, we are highly obliged by positive remarks on the manuscript.
The manuscript is long and suffers from an excess of results presented in figures. My main criticism focuses on the presentation of data on the cellular distribution of the ER and Golgi apparatus. The micrographs are inconclusive and it is not really clear what the authors are trying to show in these experiments. These results are not really necessary for the article and I suggest that they be removed from the article.
Response – We agree with the reviewers comments on data on the cellular distribution of the ER and Golgi apparatus. We have removed the micrograph data on the cellular distribution of the ER and Golgi apparatus (earlier Figure 3j and Figure 4r).
Reviewer #2 (Significance (Required)):
The authors have done an excellent job in producing a large number of strains carrying null alleles. In addition, they have used two broad analysis techniques that allow them to establish coherent hypotheses and corroborate them with the results.
Response – Thank you very much for the positive comments
The manuscript is difficult to understand in some sections because of the excessive amount of data and panels in the figures. The names designating each strain and given in full length in the graphs do not help either.
Response – Thank you very much for the valuable suggestion. We have reduced the number of graphs by including all enzymes assays in one concise graph in Figure 4. We have also shortened the names of strains and enzymes, in all the figures.
This work is of interest to all researchers interested in the integrity of signaling and regulatory pathways on extracellular enzymes of biotechnological interest.
*My interests focus on the cell biology of filamentous fungi, in particular on the molecular mechanisms and subcellular localization of elements involved in intracellular transport, signaling against environmental stresses and changes in transcriptional regulatory patterns. *
Response – Thank you once again for the encouraging remarks.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The manuscript submitted by Randhawa et al focus on the mechanism of cellulases secretion, the very important and basal question in the filamentous fungi, particularly for cellulases biotechnology. As the author said the molecular basis of cellulases production previously study mainly focuses on regulation mechanism at transcription level, the study of molecular mechanism of cellulases translation and secretion are much rare. Therefore the submitted work is very impressive me on the progress of this area. What they presented shown the Ca2+ is critical for the regulation of cellulases secretion by SNF-1, SSP1 and HOG1. The regulation might be caused by affecting the protein trafficking in ER and Golgi, the manuscript found the development of ER and Golgi shown changes by staining by ER-tracker and Bodipy under different conditions and mutants. The manuscript constructed a model about regulatory mechanism of Ca2+ on cellulases translation and secretion level. The present study is close to make significant progress in the cellulases regulation area.
Response – We appreciate the positive comments of the reviewer.
Major comments: I am really impressive for the great work in the manuscript, however, I think the more work do need for give the conclusion of paper.
1.In terms of dynamics development of ER and Golgi of strains, the very critical data for the conclusion of the paper, the current data is only by chemical staining. It is not robust, it will be needed by other methods, for example, GFP-labeling the marker of ER or Golgi.
Response – The manuscript focuses on the signaling events governing cellulase production, and secretion. Since ER and Golgi are the sites of protein production and secretion, we hypothesized, if the Ca2+ signaling affects post-transcriptional events, it must have had some impact on the dynamics of these organelles; and microscopy experiments suggested us the same. In the next set of experiments, we proved our hypothesis with the proteomics and functional analysis of Snf1, Ssp1, and Hog1 MAPK. Hog1 MAPK pathway is known to regulate protein trafficking and secretion in yeast. We here showed that Ca2+- dependent regulation of Hog1 MAPK and its downregulation by Snf1 AMPK is crucial to cellulase secretion.
2.Also the author try to suggest the cellulases were detained in the ER, not went into Golgi, therefore the secretome protein decreased. It is very much possibly but the evidence is not robust either, to trafficking the GFP-labelled CBH1 might be a good experiment to make it clear.
Response – Thank you very much for raising the query. The manuscript majorly focuses on the role of calcium signaling on cellulase translation and secretion. Further, we have studied two signaling proteins, Snf1 AMPK and Hog1 MAPK which are downstream to calcium signaling, and we found their crosstalk vital to cellulase secretion. We have not talked about cellulases being detained in the ER or Golgi, rather we focused on the signaling events regulating cellulase production and transport.
Since we had already ruled out the role of calcium in cellulase transcriptional activation, and ER and Golgi being major site of protein production in the cell; we performed microscopy experiments to see if the calcium signaling modifies ER and Golgi morphology during carbon stress. We found under-developed Golgi in the absence of calcium in wild type. This experiment helped us to build a hypothesis that calcium signaling might have role in downstream events like protein translation, and secretion. The hypothesis was proved by functional analysis of signaling proteins, Western blot and proteomics experiments. Further, microscopy experiments further strengthened our observation that Snf1 AMPK is downstream target of calcium signaling and has no role in the cellulase translation, but cellulase secretion.
Considering that we are not focusing on the protein trafficking of cellulase, the confocal microscopy experiments are not decisive, rather build supporting evidence for our hypothesis, as suggested by the second reviewer. We have proved our hypothesis of Ca2+-dependent post-transcriptional regulation of cellulase by proteomics, and other biochemical experiments. Nevertheless, we plan to perform the confocal experiments again to achieve pictures with higher resolution.
1.On page 9, please indicate the fold changes of the kinases genes talked about, snf1 and so on.
Response – We have added the Fold change in the expression of Snf1 and Ssp1 (line number 221).
2.The quality of microscopic figure is not good, should have one with higher resolution, even consider to present the electron microscope picture to give the er and Golgi dynamics changes the manuscript talked about(optional).
Response: We agree with the reviewer’s suggestion to add high resolution confocal images of mycelia in Fig 3j and Fig. 4o. We are in the process of repeating the confocal microscopy experiment. We will update the manuscript with improved microscopic pictures.
*3. The quality of Western plot need to be improved, particularly figure 4f,figure 7i, it is hard to give the conclusion based on the picture presented *
Response – We have replaced the pictures of western blots (Fig 4f, and Fig 7i) with high resolution images.
Reviewer #3 (Significance (Required)):
The manuscript submitted by Randhawa et al focus on the mechanism of cellulases secretion, the very important and basal question in the filamentous fungi, particularly for cellulases biotechnology. As the author said the molecular basis of cellulases production previously study mainly focuses on regulation mechanism at transcription level, the study of molecular mechanism of cellulases translation and secretion are much rare. Therefore the submitted work is very impressive me on the progress of this area. What they presented shown the Ca2+ is critical for the regulation of cellulases secretion by SNF-1, SSP1 and HOG1. The regulation might caused by affecting the protein trafficking in ER and Golgi, the manuscript found the development of ER and Golgi shown changes by staining by ER-tracker and Bodipy under different conditions and mutants. The manuscript constructed a model about regulatory mechanism of Ca2+ on cellulases translation and secretion level. The present study is close to make significant progress in the cellulases regulation area.
Response - Thank you for the positive comments on the manuscript.
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Referee #3
Evidence, reproducibility and clarity
The manuscript submitted by Randhawa et al focus on the mechanism of cellulases secretion, the very important and basal question in the filamentous fungi, particularly for cellulases biotechnology. As the author said the molecular basis of cellulases production previously study mainly focuses on regulation mechanism at transcription level, the study of molecular mechanism of cellulases translation and secretion are much rare. Therefore the submitted work is very impressive me on the progress of this area. What they presented shown the Ca2+ is critical for the regulation of cellulases secretion by SNF-1, SSP1 and HOG1. The regulation might caused by affecting the protein trafficking in ER and Golgi, the manuscript found the development of ER and Golgi shown changes by staining by ER-tracker and Bodipy under different conditions and mutants. The manuscript constructed a model about regulatory mechanism of Ca2+ on cellulases translation and secretion level. The present study is close to make significant progress in the cellulases regulation area.
Major comments
I am really impressive for the great work in the manuscript, however, I think the more work do need for give the conclusion of paper.
1.In terms of dynamics development of ER and Golgi of strains, the very critical data for the conclusion of the paper, the current data is only by chemical staining. It is not robust, it will be needed by other methods, for example, GFP-labeling the marker of ER or Golgi 2.Also the author try to suggest the cellulases were detained in the ER, not went into Golgi,therefore the secretome protein decreased. It is very much possibly but the evidence is not robust either, to trafficking the GFP-labelled CBH1 might be a good experiment to make it clear
Minors
1.On page 9, please indicate the fold changes of the kinases genes talked about, snf1 and so on. 2.The quality of microscopic figure is not good, should have one with higher resolution, even consider to present the electronmicroscope picture to give the er and Golgi dynamics changes the manuscript talked about(optional) . 3.The quality of western plot need to be improved, particularly figure 4f,figure 7i, it is hard to give the conclusion based on the picture presented
Significance
The manuscript submitted by Randhawa et al focus on the mechanism of cellulases secretion, the very important and basal question in the filamentous fungi, particularly for cellulases biotechnology. As the author said the molecular basis of cellulases production previously study mainly focuses on regulation mechanism at transcription level, the study of molecular mechanism of cellulases translation and secretion are much rare. Therefore the submitted work is very impressive me on the progress of this area. What they presented shown the Ca2+ is critical for the regulation of cellulases secretion by SNF-1, SSP1 and HOG1. The regulation might caused by affecting the protein trafficking in ER and Golgi, the manuscript found the development of ER and Golgi shown changes by staining by ER-tracker and Bodipy under different conditions and mutants. The manuscript constructed a model about regulatory mechanism of Ca2+ on cellulases translation and secretion level. The present study is close to make significant progress in the cellulases regulation area.
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Referee #2
Evidence, reproducibility and clarity
Randhawa et al. study the effect of loss of function of snf1 kinase and calcium on the production of enzymes related to cellulose degradation in the fungus Penicillium funiculosum. The manuscript is well structured and the researchers have done an enormous amount of work in constructing a number of mutant strains in this fungus. Transcriptomics and proteomics support the conclusions reached with the strains generated. The manuscript is long and suffers from an excess of results presented in figures. My main criticism focuses on the presentation of data on the cellular distribution of the ER and Golgi apparatus. The micrographs are inconclusive and it is not really clear what the authors are trying to show in these experiments. These results are not really necessary for the article and I suggest that they be removed from the article.
Significance
The authors have done an excellent job in producing a large number of strains carrying null alleles. In addition, they have used two broad analysis techniques that allow them to establish coherent hypotheses and corroborate them with the results. The manuscript is difficult to understand in some sections because of the excessive amount of data and panels in the figures. The names designating each strain and given in full length in the graphs do not help either. This work is of interest to all researchers interested in the integrity of signalling and regulatory pathways on extracellular enzymes of biotechnological interest.
My interests focus on the cell biology of filamentous fungi, in particular on the molecular mechanisms and subcellular localisation of elements involved in intracellular transport, signalling against environmental stresses and changes in transcriptional regulatory patterns.
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Referee #1
Evidence, reproducibility and clarity
Randhawa and co-authors have studied various aspects of the regulation of lignocellulose degradation by the filamentous ascomycete fungus Penicillium funiculosum. Over-expression of the well-known transcription factor clr2 (which regulates cellulase gene expression in Neurospora and other ascomycetes) in a delta-mig1 strain did not result in an increase in cellulase activity. However, when combined with an increased Ca2+ concentration the cellulase activity in the medium did increase. Using RNA-Seq, the authors have identified a candidate regulator: Snf1. Indeed, a knockout confirms that this gene is involved in the posttranscriptional regulation of cellulase production, specifically by regulating the secretion of the cellulases.
Major comments:
In general, the topic and results are interesting. There are a few issues that need to be addressed, however. The manuscript would benefit from some careful proofreading. For example, articles ('the', 'a') are frequently missing. Very informal language is sometimes used ('zilch effect'). Put a space between '1000bp', etc. It is 'kDa', not 'kD', etc.
I am a bit puzzled by the choice of calcium source: CaCO3, up to 10 g/L. Calcium carbonate does not efficiently dissolve in water unless the pH is low. Fungi generally acidify their culture medium during growth. As such, calcium carbonate likely has a pH buffering effect. Therefore, the described effects may also be attributed to a more neutral pH of the medium, and not necessarily to an increase in calcium ions. The authors have performed RNA-Seq, but as far as I can tell the data has not been made publicly available. At least, the raw reads should be deposited in the Short Read Archive of NCBI (or a similar repository), and preferably also the expression values in GEO of NCBI (or a similar repository). P21. Very little information is provided in the M&M regarding the gene expression analysis. Provide references to all the tools, as well as the version numbers. Were any non-default parameters used? The authors claim that SSP1 CaMKK phosphorylates SNF1 AMPK (last title of the Results section). I don't see any evidence for a direct interaction between these two proteins. I will believe that they are in the same pathway, but if the authors want to claim a direct interaction then additional experiments will be required. Eg Y2H.
Minor comments:
Please add line numbers to the manuscript, this facilitates the review process.
P14 "in all yeasts and filamentous fungi". I doubt that all fungi have been tested.
P18. "in diverse yeasts and fungi". Yeasts are also fungi.
P16. "solves dual purpose". I think this is meant: "serves a dual purpose"?
P17, first paragraph: this seems very speculative to me, so it should probably be labeled as such.
P21. What reference genome is used? Please cite the paper.
Fig 1B. These are reported as volcano plots, but to me it looks like an empty graph (no data points), only a number of genes.
Fig 1D. What do the colors on the right represent?
On various places in the manuscript the term "three times in triplicate" is used. What is meant here, three technical replicates of each of the three biological replicates?
P46. "We aimed to sought"
Abstract: The sentence "Further, Ca2+-signaling" should be rewritten, because currently is seems to suggest that SSP1 downregulates the phosphor-HOG1 levels.
Significance
In general, the topic and results are interesting. There are a few issues that need to be addressed, however. The manuscript would benefit from some careful proofreading.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
* Negreira et al. have studied aneuploidy in Leishmania selected using a "flash selection" with SbIII or miltefosine (MF). They provided evidence for the SbIII arm that a few parasites in the population with a specific genotype were enriched during drug selection, and these selected parasites with continuous drug pressure further present modifications in their ploidy. For MF selection they show a different scenario where first a minor population with a mutation in the MT gene is selected and with further passages with drugs, parasites with changes in ploidy are further enriched.*
* Here are some comments that hopefully will be helpful for the authors.*
* The plasticity of the Leishmania genome is fascinating. It is remarkable that these parasites can tolerate so many and frequent changes in ploidy. Either these changes are stochastic and serendipitous or as convey by the authors are part of the parasite arsenal to respond to a changing environment. They cleverly used single cell sequencing and bar-coded parasites in this well designed and well conducted study to assess the role of ploidy in parasite biology.*
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Drugs are not inducing any of the changes observed, instead the drugs are selecting for parasites with different genotypes (e.g. polyploidy of chromosome 23 for SbIII or parasites with mutations in MT). This is an important conceptual difference and the authors need to change their text throughout starting at line 28.
R: We agree with the reviewer and adapted the text. These changes were introduced as follow:
Line 27 (line 19 in the new version):
“____we revealed that ____antimony-induced aneuploidy changes ____under antimony pressure____ result from the polyclonal selection of pre-existing karyotypes”
Line 201 (line 187 in the new version):
“____This approach revealed that____ the flash selection with SbIII ____induced led to____ a fourfold reduction in lineage diversity that stabilized between passages 3 to 4, leaving between 101 to 131 of detectable lineages”
Line 354 (line 381 in the new version)
“____The flash selection performed with miltefosine revealed a contrasting scenario where aneuploidy remained unchanged ____even after a stronger bottleneck induced by associated with the drug at passage 1, 25 µM and illustrated by the strong decrease in barcode diversity (from 453 to 7 lineages).”
- Line 170. Its is probably expected that no cells have increased copy of chromosome 23, 27 and 31 after single cell genomics. None of the first passages of the four SePOP are polyploid for chromosome 27. One possibility is that a subpopulation of cells with increased copy of chr. 23 (because of MRPA?) and 31 (because of ?) are first selected and in subsequent passages cells triploid for 27 are selected. Of note the ploidy of chr. 27 appears to decrease from passage 4 to 5 in SePOP1 which is unusual if the drug pressure is maintained.*
R: We agree with the reviewer that the aneuploidy changes seen in the SePOP1-4 can be explained by the initial selection of subpopulations of cells with a beneficial pre-existing dosage increase in one or two chromosomes (e.g., chromosome 23 and 31) followed by the selection of additional cumulative modifications emerging in subsequent time points. This conclusion was previously stated throughout the text and is also depicted by the minimum spanning tree in figure 1C, but we made some alterations in the text in order to better state this conclusion:
Line 100 (line 87 in new version):
“____Using single-cell genome sequencing, we could uncover the evolutionary paths that might have led to the emergence of such aneuploidy changes,____ which involved ____indicating a process of ____selection of pre-existing karyotypes complemented by further ____de novo cumulative ____alterations in chromosome copy number along evolution”
Line 168 (line 156 in new version):
“However, none of the sequenced promastigotes showed amplification of chromosomes 23, 27 and 31 concomitantly, and no pre-existing karyotype was identified with a pentasomy in chromosome 23 as observed in the SePOP3, suggesting that some of the aneuploidy ____modifications were generated along adaptation to SbIII changes seen in SePOP1-4 happened after initial exposure to SbIII.____”
Line 191 (line 177 in new version):
“Altogether, our single-cell data suggest that (i) aneuploidy changes observed in the SbIII-exposed populations are explained by the selection of pre-existing aneuploid cells, complemented by additional somy changes generated de novo during the experiment and initial selection of subpopulations bearing ____pre-existing chromosomal amplifications followed by the further selection of cumulative karyotypic modifications emerging in subsequent time points____ and (ii) that the aneuploidy changes seen in SePOP1-4 would have a polyclonal origin.”
Regarding the decrease of chr.27 in SePOP1 from passage 4 to 5, we believe this decrease is not very significant as its somy value (2.71) indicates that the majority of cells still display a trisomy for this chromosome. Moreover, this decrease coincides with the moment where a dosage increase (from ~3 to ~10 copies per haploid genome) in the MRPA locus happens exclusively in that population and in that passage (see supplementary figure S2B), which likely has a stronger impact in SbIII tolerance compared to the trisomy of chr27.
- Lane 194. I agree with the concept of the selection of pre-existing aneuploid cells but the additional somy changes observed are, in my opinion, just selected because these changes occur continuously.** *
R: The changes mentioned above starting at line 191 were also done in response to this comment.
Their barcoded strategy was interesting but it would appear that different lineages are enriched in the 4 SePOP. It would be of interest to test whether those lineages have similar ploidy at the onset. I am unclear of why they have to amplify the barcode prior sequencing. Could they just not get this info from the SePOP data; it is my understanding that the drug selection was done with the barcoded population. This would have facilitated the correlation barcode-specific ploidy.
R: We agree that it would have been interesting to integrate the single-cell genomics and the barcode data in order to determine if the selected lineages had similar karyotypes at the onset of the experiment. However, although the genome coverage of individual cells in the single-cell genomics method used in our study is enough to determine differences in chromosome copy number, it is not enough to evaluate, at sequence level, individual genomic loci such as the lineage barcodes. This is because the genome coverage per cell is too low (in our case 0,8x) meaning that most genomic loci are mapped by just a single sequence read or not mapped at all (10X Genomics, 2020). Thus, it was not possible to determine the lineage barcode of individual cells from the single-cell data.
Regarding the need for amplifying the barcodes: in contrast to WGS, a targeted amplification of the barcodes enabled us to obtain millions of reads covering the barcodes. This, in turn allowed quantifying accurately the frequency of each barcoded lineage.
This is now mentioned in the text starting in line 514 (548 in the new version):
“____Barcode amplification was done using the same DNA samples used for bulk whole genome sequencing. Targeted amplification of the barcodes is needed as the number of reads containing a lineage barcode (~50 pair end reads per sample on average in our case) in the whole genome sequencing data is insufficient for the determination of the frequency of each barcoded lineage in the parasite pool.____”
- The MF screen was harsh and the parasites selected (derived from few clones within the population when considering the time needed to expand) contained SNPs in MT. Difficult to compare the two screens. Passages with higher MF concentration led to major changes in ploidy but with few common features between the MePOP lines.*
R: The screen of the BPK282 strain under SbIII or miltefosine pressure provides two contrasting models and this is one of the interests of the present study. The BPK282 strain belongs to a population of L. donovani parasites from the lowlands of the Indian subcontinent, where parasites were exposed to strong SbIII pressure for decades, even more since these parasites are transmitted from human to human. This population is characterized by strong genomic variations affecting SbIII susceptibility, of which the intra-chromosomal amplification of MRPA is a well-known driver of SbIII pre-adaptation. BPK282 has this intrachromosomal amplification of MRPA and thus it is strongly pre-adapted to SbIII. In contrast, at the time of isolation of BPK282, miltefosine was not yet implemented in clinical practice in the Indian sub-continent (ISC). BPK282 is considered highly susceptible to miltefosine and pre-adaptation to this drug was not, until the present study, identified in this strain and in the ISC population it was isolated from. We performed the flash selection with both drugs to investigate if aneuploidy modulations would follow similar patterns in these two contrasting environments, one where the strain is pre-adapted, and another where it is highly susceptible.
We state this starting in line 242 (line 230 in the new version):
“The results described above demonstrated the importance of aneuploidy for parasite adaptation to high SbIII pressure together with the polyclonality of corresponding molecular adaptations. We aimed here to verify if the same features would be observed with another anti-leishmania drug, miltefosine. In contrast to SbIII, there was – at least before present study – no pre-adaptation known to miltefosine in the BPK282 strain, which is considered very susceptible to the drug (23).”
We also added two sentences in the discussion reiterating this contrast between SbIII and MF in BPK282:
Starting in line 353 (377 in the new version):
__“Finally, we assessed the role and dynamics of aneuploidy under strong pressure of another drug, miltefosine. _Noteworthy, BPK282 was isolated from the population endemic in the Gangetic plain, before miltefosine was implemented in the region (in sharp contrast to SbIII). Hence different results were expected for the scenario of genomic adaptation and clonal dynamics._” __
In addition, we believe that the results of the miltefosine flash selection further corroborate the notion that aneuploidy modulations seen in these drug selection experiments can happen de novo along adaptation to the drug. This was not well stressed in the manuscript and thus we included the following statement during in the discussion:
Starting at line 360 (line 387 in the new version):
“__This demonstrated that the strong bottleneck associated with initial exposure to miltefosine in the first passage did not impair the potential for aneuploidy modulations in later passages, and that these modifications depend on the strength of the stress caused by the drug. These observations are also in agreement with the notion of aneuploidy modulations happening de novo during adaptation to the drug as the aneuploidy profiles seen at passage 9 in the MePOPs exposed to 100 µM are also very different from the pre-existing karyotypes identified in the single-cell data of BPK282____.” __
- I am not asking for extra work but as a suggestion to help in linking ploidy with phenotype it would have been very interesting to look at 5 passages without drug (SbIII or miltefosine) to see whether a decrease in ploidy is correlated to a decrease in resistance.*
R: Unfortunately, we do not have access to the selected populations anymore, but we agree that characterizing these selected populations after keeping them for a few passages without drug would further strengthen the understanding of the relationship between aneuploidy modulations and SbIII tolerance.
Minor points
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The environment studied (high drug pressure) is unlikely to occur in nature. The authors may wish to comment on how this may translate in the sand fly or in animals.
First of all, the population of L. donovani from which strain BPK282 originated has been naturally under high drug pressure since decades, given the anthroponotic nature of transmission in the Indian sub-continent and the absence of reported animal reservoir. An additional pressure came from the strong pollution with Arsenic, that is present in the lowlands where BPK282 was isolated (Perry et al., 2011). The same authors showed that chronic exposure to arsenic in drinking water can lead to resistance to antimonial drugs (cross resistance) in a mouse model of visceral leishmaniasis and concluded that arsenic contamination in the Gangetic plain may have played a significant role in the development of Leishmania antimonial resistance (Perry et al., 2013). This might explain why antimony resistance drivers like amplification of MRPA were already present in the populations even before antimony was implemented in the region (Imamura et al., 2016).
This is now mentioned in the text starting at line 311 (320 in the new version)
__ “_This pre-adaptation likely comes from the combination of high antimony pressure for decades, highly endemic pollution with arsenic – which can cause cross-resistance to antimonials (33, 34) – and anthroponotic transmission without animal reservoir_.”__
Secondly, in current study, we pushed further the parasite and experimentally exposed it to even higher drug pressure. Our flash selection approach was done as a general model to investigate the mechanisms that Leishmania exploits in order to adapt to sudden and strong environmental stresses, with a focus on aneuploidy changes. This is stated in the manuscript.
Starting at line 93 (line 79 in the new version):
“____In the present study we aimed to address these questions using a reproducible in vitro evolutionary model to study aneuploidy modulations and karyotype evolution in the context of adaptation to sudden environmental stresses, invoked here by the direct exposure to high concentrations of 2 drugs, trivalent antimonial (SbIII) or miltefosine (further called ‘flash selection’).”
In addition, for miltefosine, the concentrations used in our flash selection are lower than the concentrations found in the blood of treated patients or inside macrophages. Thus, for miltefosine, parasites are likely to be exposed to similar or even higher concentrations than those used in our study. We now highlight this in the discussion of the manuscript:
Starting at line 291 (line 290 in new version):
“This abrupt change in environments is also a characteristic of drug treatment. In the case of antimonials, measures made in patients treated for visceral leishmaniasis estimate a peak of 10 mg/L or ~82 µM of Sb in the blood after only 2 hours post drug administration (26). For miltefosine, blood concentrations can be as high as 70 µg/ml, or 172 µM after 72h (27). Moreover, bone marrow-derived macrophages exposed to 10 µM of miltefosine in vitro display intracellular concentrations of the drug as high as 323 µM after 72h (28). This illustrates that Leishmania parasites are directly exposed to sharp increases in drug concentrations – in the case of miltefosine, even higher than the concentrations used in this study – in patients upon drug administration.”
With respect to the importance of sand flies or animals in the environmental pressure, (i) animals play a negligible role given that transmission of L. donovani in the ISC is anthroponotic, without animal reservoir and (ii) the sand fly hosts the parasite for a short period of time (max 10 days), during which the parasite is not exposed to drugs.
- In Fig. S2 MRPA in SePOP1 is a signature of extrachromosomal amplification. *Was that studied?
R: We previously showed that amplification of MRPA in L. donovani encountered in the Indian sub-continent was intrachromosomal (Imamura et al., 2016); further amplification of that specific gene could occur by intrachromosomal expansion/contraction or indeed by episomal amplification. However, one of the core messages of present paper is that increased somy of chr23 automatically leads to increased dosage of the intra-chromosomal MRPA amplicon. We adapted the text in order to acknowledge the possibility of episomal amplification:
Starting at line 140 (line 127 in the new version):
“The BPK282 strain already contains a natural intra-chromosomal amplification of the MRPA gene that may bring a pre-adaptation to SbIII (____14____), and the locus might be subject to further ____intrachromosomal ____expansion ____or____,____ contraction____, or episomal amplification____.”
- For Chromosome 31 in the Sb screen, it would appear that the proximal (left) part is of lower copy number than the distal (right) portion of the chromosome. How could this have happened? Deletion of a portion of chromosome 31 for one allele? This has been described before (Mukherjee et al., 2013) in SbIII resistant lines as one telomeric end of Chr. 31 encodes AQP1, the route of entry of SbIII.*
R: The figures 1A and 2F and 3A do not indicate the copy number of intra-chromosomal segments as they reflect a single numeric value representing the somy of each chromosome at different time points (the x axis of the graphs). Thus, there is no information on differences between distal or proximal copy numbers inside a chromosome in those figures. The only figure showing read depth along the chromosome is fig S2B and corresponds to chr23 and not 31. It is indeed possible that there are telomeric deletions affecting AQP1 but this was not the scope of our study, since we were interested in understanding the reasons and possible drivers of increased gene dosage of chr31.
Reviewer #1 (Significance (Required)):
* The plasticity of the Leishmania genome is fascinating. It is remarkable that these parasites can tolerate so many and frequent changes in ploidy. Either these changes are stochastic and serendipitous or as convey by the authors are part of the parasite arsenal to respond to a changing environment. They cleverly used single cell sequencing and bar-coded parasites in this well designed and well conducted study to assess the role of ploidy in parasite biology.*
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
* Negreira et al. present a study that aims to understand the early evolution of aneuploidy. They use Leishmania, a protozoon parasite known for its genome plasticity, as model, and two drugs as stress inducers. In this work, they use single-cell genomics and lineage tracing to detect changes in chromosome copy numbers. They conclude that, although parasites tend to have genomes with unusual plasticity, aneuploidy dynamics depend on the stressor more than the organism.
* Further experiments:
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Lines 121-124: I believe the authors should corroborate the statement that expansion of lineages that were fitter prior to drug exposure is stochastically by doing a statistical test comparing their obtained data and randomly generated simulated values. Given that there is still a considerable proportion of lineages with higher fitness and found in more than one passage, I believe this experiment/test would add strength to the conclusion.
R: We believe that the stochasticity per se is not the relevant aspect of our results, but the fact that the expansion of different lineages in different populations is followed by the emergence of the same somy changes in a set of chromosomes (23, 27, and 31), thus showing a process of convergent evolution. Therefore, we decided to reduce the emphasis on the stochasticity itself and adapted the text to highlight this process of convergence. This was done in the following parts of the manuscript:
Starting at line 98 (line 84 in new version):
“we revealed that changes in aneuploidy under ____SbIII____ pressure have a polyclonal origin, arising from the reproducible survival of a specific subset of lineages, which further expand stochastically differentially between independent replicates but converge to similar aneuploidy modifications”.
Starting at line 220 (line 205 in new version):
“____Moreover____, ____most of the positively affected lineages were enriched in only one of the SePOPs ____(Fig. 2C and fig. S3B)____ (figure 2C and supplementary figure S3B).____, suggesting that____. Altogether, these data indicate that____ (i) a subset of lineages was fitter to SbIII prior the drug exposure and (ii)____ their ____the further____ expansion ____of these surviving lineages was ____stochastically driven. divergent between independent replicates.____”
Starting at line 344 (line 366 in the new version):
“From 453 different traceable lineages, 303 consistently disappeared during SbIII exposure and 60 showed an increased frequency in at least one replicate. Most of these positively affected lineages were enriched in only one of the SePOP replicates, suggesting (i) higher tolerance to SbIII in a subset of lineages that reproducibly survived the flash selection and (ii) further expansion of these surviving lineages being stochastically driven. , including lineages which were dominating the population at the onset of the experiment (figure 2F), thus indicating that these lineages had a fitness disadvantage to SbIII compared to the other lineages. Among the surviving lineages, 60 could further expand in at least one of the SePOPs, leading to different clonal compositions in each population. Interestingly, changes in clonal composition in each SePOP coincide with the moments where changes in aneuploidy are observed in these populations, suggesting that these aneuploidy changes are due to the emergence of subsets of fitter lineages. Moreover, the observation that the same set of 3 chromosomes displayed dosage increases in all SePOP despite the fact that different lineages dominated each SePOP points to a process of convergent evolution, which further supports the notion of these chromosomes being under positive selection.”
Minor issues:
Fig. 1B: Add label to top horizontal axis, showing frequency of each karyotype.
R: A label stating ‘Number of Cells’ was added at figure 1B.
Lines 92-96: Could the authors postulate how and why pre-existing aneuploid cells seem to be selected upon SbIII exposure?
R: We believe that some aneuploidy changes, like the dosage increase of chromosome 23 (from 3 to 4 copies) offer an adaptive advantage to the cells bearing it by over-expressing genes related to SbIII tolerance. This was discussed in the manuscript.
starting at line 304 (314 in the new text):
“____Chromosome 23 bears the MRPA genes which encode an ABC-thiol transporter involved in the sequestration of Sb-thiol conjugates into intracellular vesicles (28). Amplification of MRPA genes through extra-or intra-chromosomal amplification is a well-known driver of experimental SbIII resistance. The line here used (BPK282) is remarkably pre-adapted to SbIII (18) – like other strains of the Gangetic plain – thanks to a pre-existing intra-chromosomal amplification of MRPA genes encountered in 200 sequenced L. donovani isolates of that region (13). The recurrent dosage increase of chromosome 23 observed here under SbIII pressure is a rapid way to further amplify the MRPA gene and this mechanism was likely selected instead of further amplifying MRPA genes intra-chromosomally.”
Fig. 3: Are panels B and C swapped in the figure or the reference swapped in the text? Fig. 3C seems to refer to the mutation (lines 173-179), whereas Fig. 3B seems to relate to the surviving lineages (lines 183-186).
R: Indeed, figures 3B and 3C were erroneously positioned in the panel. This is now fixed in the new version.
Lines 94-97: Could the authors comment on the advantages and disadvantages of such an aggressive selection method? I am not surprised with such a drastic decrease in lineage diversity in this context.
R: We now added a section at the beginning of the discussion commenting this:
starting at line 291 (line 281 in the new version):
“____Historically, adaptation in Leishmania was mainly addressed using a ‘gentle’ stepwise approach where parasite populations are exposed to progressively increasing drug concentrations in vitro over the course of months, allowing these populations to adapt to each concentration before proceeding to the next increment (19, 23-25). This approach is useful to reveal mechanisms promoting full resistance against that drug which emerge at the later time points where drug concentration is high, but it precludes the evaluation of mechanisms allowing parasites to cope with sudden and strong environmental changes as initial concentrations are often too permissive. Importantly, in nature, changes in environmental pressures are often abrupt rather than gradual, and therefore, demand for mechanisms which allow parasite populations to quickly adapt to the new environment.____”
And then on line 300 in the new version:
“____In____ the present study, we investigated the mechanisms governing the early adaptation of Leishmania promastigote populations to a direct exposure to high concentrations of two drugs – SbIII and miltefosine – as models of sudden environmental stresses.____”
Could the authors elaborate on what is different in chromosome 31 that makes it so prone to change?
R: We improved our discussion about the potential drivers of dosage increases for the other 2 chromosomes (chr 27 and chr 31) which, apart from chr23, are also consistently amplified under SbIII exposure.
Starting at line 320 (line 331 in the new version):
“_Regarding the other 2 chromosomes, chromosome 31 also bears a gene involved in antimony resistance, the sodium stibogluconate resistance protein gene (LdBPK310951.1). Interestingly, the ortholog of this gene displayed an increased copy number in L. braziliensis promastigotes experimentally selected for antimony resistance in vitro compared to non-selected lines (31). Moreover, this same study found a 50 kb intrachromosomal amplification affecting 23 genes (out of a total of 31 amplified genes) in chromosome 27 in the SbIII resistant line, with many of these genes displaying a copy number more than 10 times higher compared to the SbIII sensitive line (31). Among these genes, a WW domain/Zinc finger C-x8-C-x5-C-x3-H type - protein gene (LdBPK_270130.1 ortholog in L. donovani) was also the gene with the most upregulated expression compared to the SbIII-sensitive line. Importantly, CCCH type zinc finger proteins are known targets of antimony (32), and therefore, a higher expression of this gene might mitigate its inactivation by the drug.____” __
And for chromosome 31, we also discussed further its potential role in general response against drug-induced stresses.
Starting at line 360 (line 394 in new version):
“____At 100 µM, aneuploidy changes were specific to each of the 4 MePOP replicates, with the exception of chromosome 31 that consistently showed a higher somy than the control. The fact that an increase in copy number of chromosome 31 was observed under strong SbIII and miltefosine pressure, as well as under pressure of other drugs (24) might indicate that the dosage increase in this chromosome has also a general role against multiple types of stresses. ____Noteworthy, there are several ABC transporters in that chromosome (ABCC4-7 and ABCD3) which could play a role in drug efflux (36). Moreover, ontology analysis of chromosome 31 in L. braziliensis have demonstrated an enrichment of genes involved in iron metabolism which could play a role in general adaptation to oxidative stresses (37), but empirical evidence is still lacking.____”
Reviewer #2 (Significance (Required)):
* Aneuploidy can be well-tolerated, beneficial, or deleterious. Particularly, they can confer resistance against environment stresses, including drug pressures. This study aims to understand how aneuploidy arises. The authors approach this question using a model organism, Leishmania donovani, and two distinct drugs as environmental stressors. Using single-cell DNA sequencing and lineage tracing, the authors find that the appearance of aneuploidy is dependent on the drug used, which makes it dependent on the environmental stressor, rather than pre-determined. Importantly, they present a new barcoding method that may be useful to the field of experimental genome evolution.*
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
* This interesting, well written paper uses cutting edge technologies to address the evolutionary dynamics of changes in Leishmania donovani genomes in response to high drug pressure. Using single-cell genome sequencing and lineage tracing with a newly adapted cell barcoding system, the authors were able to follow aneuploid changes and lineage selection following exposures to high concentrations of either antimony or miltefosine. The main conclusions drawn from the careful bioinformatic analyses and methodic representation of 864 single cell genomes and 453 different traceable lineages were that for each drug exposure there was polyclonal selection of pre-adapted parasites complemented by de novo adaptions. Consistent changes in aneuploidy were associated with the populations selected by antimony, while miltefosine selected for populations that had a point mutation in a miltefosine transporter gene. These conclusions are well supported by the data.*
* Reviewer #3 (Significance (Required)):*
*3 comments, 3 responses *
Comment 1
*One general comment is that the contribution of pre-adapted lineages to the emergence of drug resistant populations under conditions of natural exposure is apt to be overstated from the current analysis. As the authors discuss, the L. donovani line used is already pre-adapted to resist antimony due, at least in part, to the amplification of the MRPA gene on chromosome 23. So it is expected that lineages adapted to strong antimony pressure will pre-exist in this line. It seems possible that the de novo adaptions that were observed, involving further copy number amplification of chromosome 23 and other chromosomes (e.g., chr 31), might be facilitated by their pre-existing aneuploides. Thus, the evolutionary dynamics observed might be very particular to these sorts of pre-conditioned cells. *
R: Although BPK282 is indeed pre-adapted to antimony due to an amplification of the MRPA locus, this strain is a clone, so this intra-chromosomal amplification is shared among all cells in the population. Thus, it is probable that this intra-chromosomal amplification alone is not the only reason why some lineages are better adapted to antimony than others, but its combination with variations in aneuploidy affecting chromosome 23. We agree that de novo adaptations were likely facilitated by the presence of pre-existing aneuploidies. This was already commented in answers to comments 2 and 3 of reviewer 1.
Comment 2
It should also be discussed that the culture condtions themselves may pre-condition the parasites for antimony resistance (and possibly other drugs). Continuous passage of L. donovani in axenic culture produced consistent patterns of aneuploid changes, including amplification of Chr 23 (Barja et al., Nat Ecol evol, 2017). Thus a potential caveat of the use of cultured promastigotes is that their culture adaptions might involve genes on the same chromosomes that confer drug resistance.
R: Indeed, and we are aware of the work of Barja et al 2017. However, the flash selection models characterize a competition assay between (sub)clonal lineages which are exactly in the same environment (lineages within each SePOP were in the same culture flasks). Thus, although culture adaptation might indeed lead to pre-conditioning against SbIII due to amplification of chr23, this pre-conditioning should affect the entire population and does not explain the differences in susceptibility to SbIII between the lineages within each SePOP. Moreover, the controls (maintenance in the same culture medium but without drug pressure) did not show any change in their aneuploidy, while SePOP showed an increase in somy of several chromosomes, including chromosome 23 (see fig.1A).
Comment 3
For the miltefosine selection, of the 7 lineages surviving in at least one of the MePOP replicates, only lineage 302 is represented more than once. What is the evidence that the adaptive mutations in the other 6 lineages were pre-existing and did not arise de novo?
R: We agree that evidence for pre-existing mutations is only present for lineage 302 and changed that in the text.
At line 29 (line 22 in the new version):
“In the case of miltefosine, early parasite adaptation was associated with independent pre-existing point mutations in a miltefosine transporter gene.”
Figs 3b and 3c are incorrectly referenced in the text.
R: Fixed in new version.
Discussion p. 8 - "Interestingly, the Gly160Asp mutation also correlated with the frequency of a specific lineage (lineage 27) and appeared in 3 of the 4 MePOPs, indicating that this was a pre-existing mutation found in that lineage." Lineage 302 would appear to be the correct lineage, not 27. Please clarify.
R: Indeed, the correct is lineage 302. This has now been fixed in the new version.
Additional modifications in the manuscript:
1) The mutation in the LdMT gene affecting the codon of amino acid 1016 was described as a Glutamate to stop codon mutation (Glu1016Stop), while in fact the original amino acid is a Serine (Ser1016Stop). This was corrected in the new version.
References
10X Genomics, 2020. How much of a single cell’s genome is amplified? [WWW Document]. 10X Genomics. URL https://kb.10xgenomics.com/hc/en-us/articles/360005108931-How-much-of-a-single-cell-s-genome-is-amplified- (accessed 4.3.23).
Imamura, H., Downing, T., Van den Broeck, F., Sanders, M.J., Rijal, S., Sundar, S., Mannaert, A., Vanaerschot, M., Berg, M., De Muylder, G., Dumetz, F., Cuypers, B., Maes, I., Domagalska, M., Decuypere, S., Rai, K., Uranw, S., Bhattarai, N.R., Khanal, B., Prajapati, V.K., Sharma, S., Stark, O., Schönian, G., De Koning, H.P., Settimo, L., Vanhollebeke, B., Roy, S., Ostyn, B., Boelaert, M., Maes, L., Berriman, M., Dujardin, J.-C., Cotton, J.A., 2016. Evolutionary genomics of epidemic visceral leishmaniasis in the Indian subcontinent. eLife 5, e12613. https://doi.org/10.7554/eLife.12613
Perry, M.R., Wyllie, S., Prajapati, V.K., Feldmann, J., Sundar, S., Boelaert, M., Fairlamb, A.H., 2011. Visceral Leishmaniasis and Arsenic: An Ancient Poison Contributing to Antimonial Treatment Failure in the Indian Subcontinent? PLoS Negl. Trop. Dis. 5, e1227. https://doi.org/10.1371/journal.pntd.0001227
Perry, M.R., Wyllie, S., Raab, A., Feldmann, J., Fairlamb, A.H., 2013. Chronic exposure to arsenic in drinking water can lead to resistance to antimonial drugs in a mouse model of visceral leishmaniasis. Proc. Natl. Acad. Sci. 110, 19932–19937. https://doi.org/10.1073/pnas.1311535110
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Referee #3
Evidence, reproducibility and clarity
This interesting, well written paper uses cutting edge technologies to address the evolutionary dynamics of changes in Leishmania donovani genomes in response to high drug pressure. Using single-cell genome sequencing and lineage tracing with a newly adapted cell barcoding system, the authors were able to follow aneuploid changes and lineage selection following exposures to high concentrations of either antimony or miltefosine. The main conclusions drawn from the careful bioinformatic analyses and methodic representation of 864 single cell genomes and 453 different traceable lineages were that for each drug exposure there was polyclonal selection of pre-adapted parasites complemented by de novo adaptions. Consistent changes in aneuploidy were associated with the populations selected by antimony, while miltefosine selected for populations that had a point mutation in a miltefosine transporter gene. These conclusions are well supported by the data.
Significance
One general comment is that the contribution of pre-adapted lineages to the emergence of drug resistant populations under conditions of natural exposure is apt to be overstated from the current analysis. As the authors discuss, the L. donovani line used is already pre-adapted to resist antimony due, at least in part, to the amplification of the MRPA gene on chromosome 23. So it is expected that lineages adapted to strong antimony pressure will pre-exist in this line. It seems possible that the de novo adaptions that were observed, involving further copy number amplification of chromosome 23 and other chromosomes (eg chr 31), might be facilitated by their pre-existing aneuploides. Thus the evolutionary dynamics observed might be very particular to these sorts of pre-conditioned cells. It should also be discussed that the culture condtions themselves may pre-condition the parasites for antimony resistance (and possibly other drugs). Continuous passage of L. donovani in axenic culture produced consistent patterns of aneuploid changes, including amplification of Chr 23 (Barja et al., Nat Ecol evol, 2017). Thus a potential caveat of the use of cultured promastigotes is that their culture adaptions might involve genes on the same chromosomes that confer drug resistance.<br /> For the miltefosine selection, of the 7 lineages surviving in at least one of the MePOP replicates, only lineage 302 is represented more than once. What is the evidence that the adaptive mutations in the other 6 lineages were pre-existing and did not arise de novo?
Figs 3b and 3c are incorrectly referenced in the text.
Discussion p. 8 - "Interestingly, the Gly160Asp mutation also correlated with the frequency of a specific lineage (lineage 27) and appeared in 3 of the 4 MePOPs, indicating that this was a pre-existing mutation found in that lineage." Lineage 302 would appear to be the correct lineage, not 27. Please clarify.
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Referee #2
Evidence, reproducibility and clarity
Negreira et al. present a study that aims to understand the early evolution of aneuploidy. They use Leishmania, a protozoon parasite known for its genome plasticity, as model, and two drugs as stress inducers. In this work, they use single-cell genomics and lineage tracing to detect changes in chromosome copy numbers. They conclude that, although parasites tend to have genomes with unusual plasticity, aneuploidy dynamics depend on the stressor more than the organism.
Further experiments:
Lines 121-124: I believe the authors should corroborate the statement that expansion of lineages that were fitter prior to drug exposure is stochastically by doing a statistical test comparing their obtained data and randomly generated simulated values. Given that there is still a considerable proportion of lineages with higher fitness and found in more than one passage, I believe this experiment/test would add strength to the conclusion.
Minor issues:
Fig. 1B: Add label to top horizontal axis, showing frequency of each karyotype. Lines 92-96: Could the authors postulate how and why pre-existing aneuploid cells seem to be selected upon SbIII exposure? Fig. 3: Are panels B and C swapped in the figure or the reference swapped in the text? Fig. 3C seems to refer to the mutation (lines 173-179), whereas Fig. 3B seems to relate to the surviving lineages (lines 183-186). Lines 94-97: Could the authors comment on the advantages and disadvantages of such an aggressive selection method? I am not surprised with such a drastic decrease in lineage diversity in this context.
Could the authors elaborate on what is different in chromosome 31 that makes it so prone to change?
Significance
Aneuploidy can be well-tolerated, beneficial, or deleterious. Particularly, they can confer resistance against environment stresses, including drug pressures. This study aims to understand how aneuploidy arises. The authors approach this question using a model organism, Leishmania donovani, and two distinct drugs as environmental stressors. Using single-cell DNA sequencing and lineage tracing, the authors find that the appearance of aneuploidy is dependent on the drug used, which makes it dependent on the environmental stressor, rather than pre-determined. Importantly, they present a new barcoding method that may be useful to the field of experimental genome evolution.
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Referee #1
Evidence, reproducibility and clarity
Negreira et al. have studied aneuploidy in Leishmania selected using a "flash selection" with SbIII or miltefosine (MF). They provided evidence for the SbIII arm that a few parasites in the population with a specific genotype were enriched during drug selection, and these selected parasites with continuous drug pressure further present modifications in their ploidy. For MF selection they show a different scenario where first a minor population with a mutation in the MT gene is selected and with further passages with drugs, parasites with changes in ploidy are further enriched.
Here are some comments that hopefully will be helpful for the authors.
The plasticity of the Leishmania genome is fascinating. It is remarkable that these parasites can tolerate so many and frequent changes in ploidy. Either these changes are stochastic and serendipitous or as convey by the authors are part of the parasite arsenal to respond to a changing environment. They cleverly used single cell sequencing and bar-coded parasites in this well designed and well conducted study to assess the role of ploidy in parasite biology.
- Drugs are not inducing any of the changes observed, instead the drugs are selecting for parasites with different genotypes (e.g. polyploidy of chromosome 23 for SbIII or parasites with mutations in MT). This is an important conceptual difference and the authors need to change their text throughout starting at line 28.
- Line 170. Its is probably expected that no cells have increased copy of chromosome 23, 27 and 31 after single cell genomics. None of the first passages of the four SePOP are polyploid for chromosome 27. One possibility is that a subpopulation of cells with increased copy of chr. 23 (because of MRPA?) and 31 (because of ?) are first selected and in subsequent passages cells triploid for 27 are selected. Of note the ploidy of chr. 27 appears to decrease from passage 4 to 5 in SePOP1 which is unusual if the drug pressure is maintained.
- Lane 194. I agree with the concept of the selection of pre-existing aneuploid cells but the additional somy changes observed are, in my opinion, just selected because these changes occur continuously.
- Their barcoded strategy was interesting but it would appear that different lineages are enriched in the 4 SePOP. It would be of interest to test whether those lineages have similar ploidy at the onset. I am unclear of why they have to amplify the barcode prior sequencing. Could they just not get this info from the SePOP data; it is my understanding that the drug selection was done with the barcoded population. This would have facilitated the correlation barcode-specific ploidy.
- The MF screen was harsh and the parasites selected (derived from few clones within the population when considering the time needed to expand) contained SNPs in MT. Difficult to compare the two screens. Passages with higher MF concentration led to major changes in ploidy but with few common features between the MePOP lines.
- I am not asking for extra work but as a suggestion to help in linking ploidy with phenotype it would have been very interesting to look at 5 passages without drug (SbIII or miltefosine) to see whether a decrease in ploidy is correlated to a decrease in resistance.
Minor points
- The environment studied (high drug pressure) is unlikely to occur in nature. The authors may wish to comment on how this may translate in the sand fly or in animals.
- In Fig. S2 MRPA in SePOP1 is a signature of extrachromosomal amplification. Was that studied?
- For Chromosome 31 in the Sb screen, it would appear that the proximal (left) part is of lower copy number than the distal (right) portion of the chromosome. How could this have happened? Deletion of a portion of chromosome 31 for one allele? This has been described before (Mukherjee et al., 2013) in SbIII resistant lines as one telomeric end of Chr. 31 encodes AQP1, the route of entry of SbIII.
Significance
The plasticity of the Leishmania genome is fascinating. It is remarkable that these parasites can tolerate so many and frequent changes in ploidy. Either these changes are stochastic and serendipitous or as convey by the authors are part of the parasite arsenal to respond to a changing environment. They cleverly used single cell sequencing and bar-coded parasites in this well designed and well conducted study to assess the role of ploidy in parasite biology.
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Reply to the reviewers
We thank all reviewers for their comments and suggestions. The revised manuscript included new experiments they suggested and extensive text edits. Our point-by-point response is shown in bold.
Point-by-point description of the revisions
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Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary
In this manuscript, Blank et al. propose a link between cell-cycle dependent changes in metabolic flux and corresponding changes in TORC1 activity in yeast cells. Based on their findings, the authors propose that Bat1-dependent leucine synthesis from glucose increases as cells progress through G1 and that this activates TORC1 to drive cell cycle progression. Although the existence of cell-cycle dependent synthesis of leucine is a novel and exciting finding, several aspects of the proposed model are not sufficiently supported by experimental evidence, in particular the fact that the increase in Leu synthesis is causing the increase in TORC1 activity in late G1.
Major comments:
- To show that the increase in Leu biosynthesis in S-phase is activating TOR, one would ideally want to blunt this increase in biosynthesis and assay TORC1 activity. Admittedly, this is difficult. So, instead, the authors study bat1- cells which have strongly impaired synthesis of BCAA including Leucine. The relevance of these bat1- cells to the proposed cell-cycle dependent model, however, is questionable for two reasons: 1) Although the authors state that "exogenous supplementation of BCAAs in all combinations suppressed the growth defect of bat1- cells, especially when valine was present", the spot assays in Figure 3 show visible rescues only when valine is present either alone or in combination, while supplementation of leucine or isoleucine does not seem to have any effect. Hence it appears that the bat1- phenotype is mainly due to limiting valine levels, not leucine levels. 2) The relevance of these results for understanding TORC1 regulation are questionable, since valine does not typically activate TORC1. Does addition of Leu to bat1- cells increase TORC1 activity ? RESPONSE: The reviewer’s comments were very valuable. We performed the suggested experiments (adding not only Leu but also Ile and Val) to bat1 cells and measuring phosphorylation of Rps6 (see new Figure 4D) and the DNA content of those cells (see new Figure 3C). We found that Leu weakly promotes cell cycle progression, compared to the addition of Val, which also leads to pronounced activation of TORC1 (>10-fold activation; see Figure 4D). We discuss these findings in the revised text.
We also note, as published by others and now discussed in the text, that in WT cells, exogenous addition of Leu (or any other BCAA) does not lead to sustained activation of TORC1 (see new Figure 4D). This is not surprising. As reported by the Hall lab (see PMID: 25063813, which we now cite), the Gtr-dependent activation of TORC1 by BCAAs mentioned by the reviewer is very transient. Hence, our new data, showing sustained TORC1 activation and cell cycle effects upon Val addition in bat1 cells, is exciting. They argue that bat1 cells serve as a highly sensitized background of low TORC1 activity, enabling the display of effects that are difficult to measure in WT cells.
TORC1 activity is known to depend on steady-state leucine concentrations in the cell rather than on leucine flux. Although the authors observe that the synthesis rate of leucine increases during G1 progression, this does not necessarily translate into increased leucine concentrations in the cell. To support the claim that the increase in TORC1 activity during G1 progression depends on leucine, the authors would need to show that, not only leucine synthesis, but also overall leucine levels in the cell increase during G1 progression.
RESPONSE: We did this experiment and now report the data (see new Figure EV2), using the Edman degradation-based assay. We found that changes in the steady-state levels of BCAAs had a similar pattern, and those changes were most significant for valine (rising 30-40% from late G1 to G2/M). Nonetheless, we note also that the kinetics of amino acid synthesis measured by our isotope tracing experiment need not match the steady-state levels of amino acids. Steady-state levels are affected by a multitude of parameters, only one of which is the rate of synthesis, as we now discuss in detail in the manuscript.
To test whether the increase in Leu biosynthesis in S-phase activates TORC1, a few different approaches could be tested: 1) Since leucine activates TORC1 through the Gtr proteins, the authors could test whether rendering TORC1 resistant to low leucine through expression of constitutively active Gtrs abolishes the cell-cycle dependence in TORC1 activity. 2) Leu could be added to the medium of wildtype cells in G1 to the amount necessary to cause an increase in intracellular Leu levels similar to those seen in S-phase to test whether this increases TORC1 activity.
RESPONSE: We did the suggested experiments, which are now shown in the new Figure 5. Leucine and valine accelerated the rise in TORC1 activity in G1. However, there were no noticeable downstream consequences in the kinetics of cell cycle progression. As we discuss in the text:
“A small acceleration of the rise in the levels of phosphorylated Rps6 was evident in both the leucine- and valine supplemented cells (Figure 5A,B). Nonetheless, there were no noticeable downstream consequences in the kinetics of cell cycle progression, in either the rate the cells increased in size or their critical size (Figure 5A; see values above the corresponding blots), consistent with the notion that TORC1 activity already is at a maximal level in these conditions…”
In Fig 2B one sees that Leu biosynthesis peaks at 150min and then drops again. The p-RpS6 blot in Fig. 5D, however, only goes up to 140 min and shows that TORC1 activity increases up to 140 min, but it doesn't show timepoints beyond 150 min when Leu biosynthesis drops again, and hence one would expect TORC1 activity to drop. If TORC1 activity were to drop from 150min onwards, this would strengthen the correlation between Leu biosynthesis and TORC1 activity.
RESPONSE: The reason for the drop in Figure 2 is trivial and does not affect the interpretation. As seen in Figure 1 (the experiment from which the data in Figure 2 are shown), by 180 min, the cells were entering a new cell cycle, evidenced by a reduction in cell size (Figure 1B) and in the fraction of budded cells (Figure 2B). At that point, there is a mix of mothers and daughters with very poor synchrony, making it impossible to conclude much about the drop in Leu synthesis (i.e., does it arise from the lack of new synthesis in mothers, daughters, or both?). In the experiment in Figure 5, the reviewer mentions (now those figures have moved to File S8 because we added more experiments in the figure) the experiment terminated when peak budding was reached, which was 140 min, within one cell cycle. Lastly, it is important to stress that every elutriation experiment is different. While the times are close, comparing various experiments on a time basis alone is inaccurate. Instead, the metric used in the field to compare different experiments is usually cell size, which we use in all other Figures except Figure 1 because, in that case, the experiment was a time-based, pulse-chase one.
Minor concerns:
- In Figure EV4, the authors should highlight some of the metabolites that are significantly changed, in particular the BCAA. The figure is not very informative as currently presented. __RESPONSE: We have now labeled the BCAAs, and a few more metabolites as suggested (note the Figure is now EV5). __
Fig 2 - are "expressed ratios" the best term for metabolite levels? Unlike genes, where such heat maps are often used, the metabolites are not 'expressed'. How about 'relative metabolite level' instead?
RESPONSE: Good point. The axis now reads “relative abundance”.
Page 8: "We also measured the MID values from the media of the same cultures used to prepare the cell extracts." Where are these data? We don't see them in File S2?
RESPONSE: The data are in File S2 (there are many ‘sheets’ in the file). In sheets 3,4 are the MID values and the analysis from metabolites in the media.
Fig 4B - the x-axis labeling is missing for the bat1- cells
RESPONSE: Corrected. Note that new DNA content measurements are now shown in Figure 3C.
Although the authors state repeatedly that they show "for the first time in any system" that TORC1 activity is dynamic in the cell cycle, similar observations have already been made before, for instance showing high mTORC1 activity in the G1/S transition in the Drosophila wing disc or low mTORC1 activity during mitosis in mammalian cells (see PMIDs 28829944, 28829945, and 31733992). The text should be amended accordingly.
RESPONSE: Thank you. Corrected.
There are two entries for valine in File S1/Sheet8. Why?
RESPONSE: The reason is that they were detected in both analytical pipelines (primary metabolites and biogenic amines; primary metabolites were measured with GC-TOF MS, while biogenic amines with HILIC-QTOF MS/MS), which were combined in the Table. We did not describe it adequately in the previous version. We do now, in the Methods. We also note that the raw data from each method are shown in the corresponding supplemental files. We combined them in the Table used in the Figure for display purposes. We also note that the amino acids were also measured by another method (PTH-based HPLC). Hopefully, the new edits in the Methods clarify these points.
Reviewer #1 (Significance (Required)):
Significance
Despite the well-known effects of pharmacological or genetic manipulations of TORC1/mTORC1 on cell cycle progression, whether and how mTORC1 activity itself is physiologically coupled to cell cycle progression is still an insufficiently studied aspect. Hence this study provides an interesting link between cell-cycle dependent regulation of amino acid biosynthesis and TORC1 regulation. Importantly, the results of this study rely on centrifugal elutriation to obtain cell cycle synchronization, thus ruling out potential metabolic artifacts due to pharmacological methods. The observed changes in metabolic flux are therefore likely genuine and represent the major strength of the study. The major limitation is the lack of strong evidence supporting the notion that the increase in Leu biosynthesis at late G1 or S-phase is causing the increase in TORC1 activity.
The major advance is conceptual - that amino acid biosynthesis rates are cell-cycle dependent.
These results will be of interest to a broad audience of people studying the cell cycle, cell growth, TORC1 activity, cell metabolism and cancer.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
This paper provides evidence that branched chain amino acid (BCAA) in the G1 phase of the cell cycle, fueled by pyruvate generated by glucose catabolism activates cell growth and allows cells to reach the critical size required for entry into S phase by activation of TORC1 signaling. Previous work had indicated that Leucine supplementation of a bat1 bat2 mutant, lacking both enzymes that catalyze BCAA from the alpha-keto acid precursors and starved on minimal medium, led to TORC1 activation. This work is significant in suggesting that BCAA synthesis from glucose is responsible for a cyclic activation of TORC1 necessary for a normal rate of cell growth in the G1 phase of the cell cycle.
The study employs metabolic flux analysis of metabolites derived from glucose following a pulse-chase with different isotopes of glucose in synchronized early G1 cells (obtained by elutriation) throughout one cell cycle. They claim that the only compelling changes in metabolites observed as the cell cycle proceeds was a decline in pyruvate containing only one heavy 13C carbon atom and a corresponding increase in Leu (M6) with 6 heavy carbon atoms, which is interpreted to indicate Leu synthesis from pyruvate that begins in early G1 and peaks at mitosis. They show that a bat1 mutant exhibits a slow-growth phenotype that can be mitigated only by valine (although they infer similar effects for Leu and Ile that I find unconvincing) and they observed reductions in all three BCAAs in different experiments that measure steady amino acid levels in different ways (although the results are compelling only for Val). They go on to show evidence that the bat1 mutation reduces birth and mean cell size and leads to an increased proportion of G1 cells in asynchronous cultures, and they claim that bat1 cells take much longer than WT to achieve the same size found when a synchronized WT culture reaches 50% budding (although they don't show the data for this last point.) Interestingly, they find that deleting BAT1 suppresses sensitivity to the TORC1 inhibitor rapamycin (Rap), consistent with the idea that the bat1 mutation impairs TORC1 activity in the same manner as Rap and that BCAA are required to activate TORC1 in WT cells to the level that can be impaired by Rap, as summarized in the model in Fig. 5F. Consistent with this, they present evidence that the bat1 mutation reduces TORC1 signaling as judged by diminished Rps6 phosphorylation (although it was not shown that this effect could be reversed by Val addition). They also show that TORC1 signaling/Rps6-P increases as the cell cycle progresses using elutriated early G1 cells, suggesting that TORC1 activity is periodic in the cell cycle (although they don't establish this periodicity through a second cell cycle).
General critique:
The conclusion that BCAA synthesis from glucose is responsible for a cyclic activation of TORC1 necessary for a normal rate of cell growth in the G1 phase of the cell cycle is potentially of considerable significance. There are however a number of puzzling aspects of the data that seem to weaken this conclusion. As described in greater detail below, it is difficult to explain why only Leu is synthesized from glucose during the cell cycle, and why only Val shows a marked reduction in the bat1 mutant that appears to be responsible for the slow-growth phenotype. In addition, there are important controls lacking of showing that a Val supplement can suppress the G1 delay and reduction in TORC1 signaling in the bat1 mutant. In addition, the evidence that TORC1 activity is periodic in the cell cycle is lacking and it needs to be shown that Rps6-P levels are periodic through at least a second cell cycle.
Major comments:
-Why don't they observe synthesis of Ile and particularly Val in the metabolic flux experiment of Fig. 1, especially considering that only Val appears to be critically required for normal cell growth in the bat1 mutant based on the results in Fig. 3B?
RESPONSE: We now show the actual plots and the errors of all the measurements in Figure 2 (instead of a heatmap we had shown before). Valine (M5) levels show a very similar trend to leucine (M6). The variance in the measurements was higher, though, and statistically, the valine changes were less significant. Hence, it was more appropriate to highlight the leucine changes. Lastly, the new DNA content data (Figure 3C) show an effect upon the addition of leucine, albeit less significant than that of valine addition.
-The data in Fig. 3B do not show a convincing increase in growth of the bat1 mutant with addition of Leu and Ile; and the stimulation by Val alone seems identical to that seen with Val in combination with Leu and Ile. Thus, it appears that the slow-growth of the bat1 mutant results only from reduced Val levels, not all 3 BCAAs, which is at odds with their interpretation of the data.
__RESPONSE. As mentioned above, the effect of valine is more pronounced than leucine's, but leucine does have consequences, best shown in the DNA content analysis (new Figure 3C). We also note that valine alone is insufficient to suppress the growth and cell cycle defects of bat1 cells. The latest data we have added (see Figures 3 and 5) are consistent with the interpretation that at least some de novo synthesis of BCAAs in the cell may be needed, explaining why exogenous BCAAs, including valine, are unable to correct the defects of bat1 cells fully. __
-they claim to see reductions in all three BCAAs in the bat1 mutant; however, no significant reduction was found for Leu in Fig. EV3, and only Val was altered by the 1.5-fold cut-off imposed on the MS metabolomics data in Fig. EV4 (which could be appreciated only by an in-depth examination of the supplementary data in File S1-the Val, Leu, and Ile dots should be labeled in Fig. EV4). In addition, the reductions in Ala and Gly showin in Fig. EV3 were not found in the MS analysis of Fig. EV4. It needs to be acknowledged that the metabolomics data show a marked reduction in the bat1 mutant only for Valine with little or no change in Leucine levels. This result is difficult to explain with the simple models shown in Fig. 3A and 5F, which requires additional comment. The authors should acknowledge the much greater effect of the bat1 mutation on Val levels versus Leu and Ile, revealed both by measuring the levels of BCAAs in the mutant and comparing the BCAAs for rescuing the slow-growth of the mutant, and explain how this can be reconciled with the results in Fig. 2 where only Leu and not Val or Ile synthesis was detected.
__RESPONSE. The perceived discrepancy in the steady-state measurements could easily arise from the different analytical methods used in each case. The differences are less substantial than the reviewer implies. For steady-state measurements in BAT1 vs. bat1 cells, we used the PTH-based method (which only detects amino acids) and two different MS-based pipelines (which detect various metabolites). From the MS-based analyses, the drop for all BCAAs was statistically significant. Although the magnitude of the drop was greater for valine (about 60% for valine vs. ~30% for isoleucine and leucine). Why is this a problem? __
As for the valine changes in the isotope tracing experiments, as we mentioned above, the trend for valine (M5) was similar to that of leucine (M6) (now, hopefully, that data is shown better in Figure 2). Furthermore, as we commented above (see response to Reviewer 1) and now stated in the text, our isotope tracing experiments measure only the rate of synthesis, which need not match the steady-state abundances. The latter are affected by a multitude of variables, including the turnover of proteins and amino acids, not to mention their partition into distinct intracellular pools.
__Lastly, please note that we have now added PTH-based measurements of amino acid levels in the cell cycle of wild type cells (new Figure EV2). As mentioned in our response to Reviewer 1, we found that changes in the steady-state levels of BCAAs had a similar pattern, and those changes were most significant for valine (rising 30-40% from late G1 to G2/M). __
-They need to add the data indicating that the bat1 mutant requires longer than WT cells to reach the ~35 fL volume at which 50% of WT cells are budded.
__RESPONSE: We added all that data (new Figure EV6) and discussed it better in the text. Note that our elutriation analyses allow accurate estimates of the G1 duration, which is at least 2x longer in bat1 vs. BAT1 cells. __
-It seems important to show that Val supplementation can suppress the overabundance of G1 cells in bat1 mutant cells shown in Fig. 4C; and can restore sensitivity to Rap and Rps6-P accumulation in bat1 mutant cells (in Fig.s 5A & B).
__RESPONSE: Excellent suggestions. We now present the requested experiments. The DNA content data are in Figure 3C, and the phospho-Rps6 data in the new Figure 4D are discussed in the text. Briefly, exogenous valine, and to a lesser extent leucine, suppressed the G1 accumulation, but not to wild type levels. Exogenous valine also substantially increased TORC1 activity (>10-fold). __
-It seems important to show that Rps6-P will decline in M phase and increase during a second cell cycle to establish that TORC1 activity actually fluctuates in the cell cycle instead of just by reduced by the manipulations involved in collecting young G1 cells by elutriation.
RESPONSE: The second cycle comment is not pertinent to our elutriation setup. The two-cycle approach should be used in arrest-and-release synchronizations to minimize arrest-related artifacts when cells continue to grow in size. This is why we used elutriation in the first place, as described in the text, to avoid such artifacts. In elutriations it is the first cycle, exclusively of daughter cells, that can be meaningfully scored. After that, the cells lose synchrony very fast because you have mothers (which grow in size very little) and daughters (which need to double in size until mitosis). Hence, the second cycle will be meaningless and impossible to interpret.
Reviewer #2 (Significance (Required)):
General Assessment:
Strengths: Evidence for BCAA biosynthesis from glucose in the G1 phase of the cell cycle, and evidence obtained from analyzing the bat1 mutant that BCAA synthesis underlies activation of TORC1 early in the cell cycle in a manner required to achieve the critical cell size necessary for G1 to S transition.
Weaknesses: Lack of evidence for Val biosynthesis in G1 despite evidence that Val limitation is more crucial than Leu limitation in the bat1 mutant; lack of confirmation that Val limitation underlies the delayed G1-S transition and reduced TORC1 signaling in the bat1 mutant; and lack of compelling evidence that TORC1 activity is periodic in WT cells.
Advance: This would be the first evidence that TORC1 activity varies through the cell cycle in a manner controlled by synthesis of BCAAs
Audience: This advance would be of great interest to a wide range of workers studying how the cell cycle is regulated and the role of TORC1 in controlling cell growth and division in normal cells and in human disease.
My expertise: Mechanisms of metabolic regulation of gene expression at the transcriptional and translational levels in budding yeast
**Referees cross-commenting**
Ref. #1's major comment 1 echoes my request for clarification about whether Leu, and not just Val, is limiting growth in the bat1 mutant, and also the need to determine which BCAA supplement to bat1 cells will restore TORC1 activity (which was also requested by Ref. #3).
I agree with this reviewer's request to provide evidence that Leu levels actually increase during G1 progression (comment #2). I also think the suggested experiments in Comment #3 are reasonable for their potential to provide stronger evidence that Leu production in the G1 phase of wild-type cells activates TORC1, as currently the argument is based on the finding of low TORC1 activation in bat1 cells (that seem to be limiting for Val vs. Leu). Comment #4 echoes similar requests made by both me and Ref. #3. Ref. #3's major comments 1 and 3 mirror two of my major comments. I wasn't convinced of the need to monitor Sch9 versus Rps6 phosphorylation as a read-out of TORC1 activity-does being a direct substrate truly matter? Regarding comment 5, I wasn't convinced of the need to include Rap-sensitive or -resistant control strains for the analysis in Fig. 5A. And regarding comment 4, while it would be interesting to examine if TORC1 regulates BCAA synthesis during cell cycle progression, this seems to be outside the scope of a demonstration that BCAA synthesis stimulates TORC1.
Thus, it seems we all agree on certain experiments that need to be carried out, and Ref. #1 has rightly proposed a few others with the potential to strengthen the evidence that Leu production during G1 phase mediates cyclic activation of TORC1
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In this manuscript, Blank and colleagues measure the synthesis of various metabolites from glucose during cell cycle progression and observe an increased synthesis of branched-chain amino acids (BCAA) from the early G1 to late G1 phase. Interestingly, they also found a gradual increase in TORC1 activity from the early G1 to the S phase which is proposed to be dependent on BCAA synthesis.
Major comments:
- The authors show that TORC1 activity increases from the early G1 to the S phase. TORC1 activity is sensitive to short-term starvations caused during changing media or centrifugations. Hence, the concern arises regarding the increased pattern of TORC1 activity during the cell cycle. Is it really a biological phenomenon or a cellular adaptation to experimental conditions? Can authors provide more support for this observation? Can authors monitor the cell cycle for the two cell cycles to confirm that TORC1 activity shows a wavy pattern? RESPONSE: The same point was also made by Reviewer #2. As we noted in our response above, “____The second cycle comment is not pertinent to our elutriation setup. The two-cycle approach should be used in arrest-and-release synchronizations to minimize arrest-related artifacts when cells continue to grow in size. This is why we used elutriation in the first place, as described in the text, to avoid such artifacts. In elutriations it is the first cycle, exclusively of daughter cells, that can be meaningfully scored. After that, the cells lose synchrony very fast because you have mothers (which grow in size very little) and daughters (which need to double in size until mitosis). Hence, the second cycle will be meaningless and impossible to interpret.____”
The authors use Rps6 phosphorylation as a read-out of TORC1 activity, which is not a direct substrate of TORC1. Analysis of the direct substrates of TORC1, such as phosphorylation of Sch9 will solidify the author's claim.
RESPONSE: The reviewers discussed this point (see their comments above). We agree with the opinion that Rps6 phosphorylation accurately reports on TORC1 activity (also used in the fly experiments we now cite, as requested by Reviewer 1). For all our experiments' objectives and conclusions, it doesn't matter if the phosphorylation of Rps6 lies more downstream than Sch9 phosphorylation.
Authors show that Bat1 lacking strain have reduced TORC1 activity. Can authors restimulate these cells with Leucin, Valine, and Isoleucine individually or in combination to identify the critical amino acid for the TORC1 activity?
RESPONSE: Yes, that is an excellent suggestion. We show the experiment in Figure 4D (see previous response). Valine showed pronounced activation (>10-fold).
The authors claim that increased BCAA synthesis is necessary for TORC1 activation. Since TORC1 is shown to be upstream of amino acid biosynthesis pathways, it will be interesting to check if TORC1 per se regulates BCAA synthesis during cell cycle progression. The authors could inhibit TORC1 by rapamycin treatment and monitor if the BCAA synthesis still shows cell cycle-dependent modulation.
RESPONSE: The reviewers also discussed this point (see their comments above). We agree with the view that it is a very substantial undertaking, well beyond the scope of this work.
In Figure 5A, the use of any rapamycin-sensitive and rapamycin-resistant strains as controls will strengthen their claim of TORC1 inhibition being epistatic to Bat1 deletion, since the rapamycin in minimal media might be less effective.
RESPONSE: Again, the reviewers also discussed this point (see their comments above). We agree that it will not add much to the conclusions in the context of all the data we show and the existing literature.
Minor comments:
- The data of metabolic labeling, especially various species M1, M2, M3, etc., of an individual metabolite is difficult to understand for the general readers. Hence, a schematic explaining various species might be helpful. RESPONSE: We added a new Figure (EV1) delineating the carbons from glucose to valine and leucine.
Please describe the elutriation approach in more detail with media conditions and buffer conditions to understand the overall experimental setup.
RESPONSE: We now added this information (see the second section of the Materials and Methods).
Reviewer #3 (Significance (Required)):
Significance:
Overall, this study presents an interesting observation to the researchers working in TORC1 and cell cycle regulation.
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Referee #3
Evidence, reproducibility and clarity
In this manuscript, Blank and colleagues measure the synthesis of various metabolites from glucose during cell cycle progression and observe an increased synthesis of branched-chain amino acids (BCAA) from the early G1 to late G1 phase. Interestingly, they also found a gradual increase in TORC1 activity from the early G1 to the S phase which is proposed to be dependent on BCAA synthesis.
Major comments:
- The authors show that TORC1 activity increases from the early G1 to the S phase. TORC1 activity is sensitive to short-term starvations caused during changing media or centrifugations. Hence, the concern arises regarding the increased pattern of TORC1 activity during the cell cycle. Is it really a biological phenomenon or a cellular adaptation to experimental conditions? Can authors provide more support for this observation? Can authors monitor the cell cycle for the two cell cycles to confirm that TORC1 activity shows a wavy pattern?
- The authors use Rps6 phosphorylation as a read-out of TORC1 activity, which is not a direct substrate of TORC1. Analysis of the direct substrates of TORC1, such as phosphorylation of Sch9 will solidify the author's claim.
- Authors show that Bat1 lacking strain have reduced TORC1 activity. Can authors restimulate these cells with Leucin, Valine, and Isoleucine individually or in combination to identify the critical amino acid for the TORC1 activity?
- The authors claim that increased BCAA synthesis is necessary for TORC1 activation. Since TORC1 is shown to be upstream of amino acid biosynthesis pathways, it will be interesting to check if TORC1 per se regulates BCAA synthesis during cell cycle progression. The authors could inhibit TORC1 by rapamycin treatment and monitor if the BCAA synthesis still shows cell cycle-dependent modulation.
- In Figure 5A, the use of any rapamycin-sensitive and rapamycin-resistant strains as controls will strengthen their claim of TORC1 inhibition being epistatic to Bat1 deletion, since the rapamycin in minimal media might be less effective.
Minor comments:
- The data of metabolic labeling, especially various species M1, M2, M3, etc., of an individual metabolite is difficult to understand for the general readers. Hence, a schematic explaining various species might be helpful.
- Please describe the elutriation approach in more detail with media conditions and buffer conditions to understand the overall experimental setup.
Significance
Overall, this study presents an interesting observation to the researchers working in TORC1 and cell cycle regulation.
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Referee #2
Evidence, reproducibility and clarity
This paper provides evidence that branched chain amino acid (BCAA) in the G1 phase of the cell cycle, fueled by pyruvate generated by glucose catabolism activates cell growth and allows cells to reach the critical size required for entry into S phase by activation of TORC1 signaling. Previous work had indicated that Leucine supplementation of a bat1 bat2 mutant, lacking both enzymes that catalyze BCAA from the alpha-keto acid precursors and starved on minimal medium, led to TORC1 activation. This work is significant in suggesting that BCAA synthesis from glucose is responsible for a cyclic activation of TORC1 necessary for a normal rate of cell growth in the G1 phase of the cell cycle.
The study employs metabolic flux analysis of metabolites derived from glucose following a pulse-chase with different isotopes of glucose in synchronized early G1 cells (obtained by elutriation) throughout one cell cycle. They claim that the only compelling changes in metabolites observed as the cell cycle proceeds was a decline in pyruvate containing only one heavy 13C carbon atom and a corresponding increase in Leu (M6) with 6 heavy carbon atoms, which is interpreted to indicate Leu synthesis from pyruvate that begins in early G1 and peaks at mitosis. They show that a bat1 mutant exhibits a slow-growth phenotype that can be mitigated only by valine (although they infer similar effects for Leu and Ile that I find unconvincing) and they observed reductions in all three BCAAs in different experiments that measure steady amino acid levels in different ways (although the results are compelling only for Val). They go on to show evidence that the bat1 mutation reduces birth and mean cell size and leads to an increased proportion of G1 cells in asynchronous cultures, and they claim that bat1 cells take much longer than WT to achieve the same size found when a synchronized WT culture reaches 50% budding (although they don't show the data for this last point.) Interestingly, they find that deleting BAT1 suppresses sensitivity to the TORC1 inhibitor rapamycin (Rap), consistent with the idea that the bat1 mutation impairs TORC1 activity in the same manner as Rap and that BCAA are required to activate TORC1 in WT cells to the level that can be impaired by Rap, as summarized in the model in Fig. 5F. Consistent with this, they present evidence that the bat1 mutation reduces TORC1 signaling as judged by diminished Rps6 phosphorylation (although it was not shown that this effect could be reversed by Val addition). They also show that TORC1 signaling/Rps6-P increases as the cell cycle progresses using elutriated early G1 cells, suggesting that TORC1 activity is periodic in the cell cycle (although they don't establish this periodicity through a second cell cycle).
General critique:
The conclusion that BCAA synthesis from glucose is responsible for a cyclic activation of TORC1 necessary for a normal rate of cell growth in the G1 phase of the cell cycle is potentially of considerable significance. There are however a number of puzzling aspects of the data that seem to weaken this conclusion. As described in greater detail below, it is difficult to explain why only Leu is synthesized from glucose during the cell cycle, and why only Val shows a marked reduction in the bat1 mutant that appears to be responsible for the slow-growth phenotype. In addition, there are important controls lacking of showing that a Val supplement can suppress the G1 delay and reduction in TORC1 signaling in the bat1 mutant. In addition, the evidence that TORC1 activity is periodic in the cell cycle is lacking and it needs to be shown that Rps6-P levels are periodic through at least a second cell cycle.
Major comments:
- Why don't they observe synthesis of Ile and particularly Val in the metabolic flux experiment of Fig. 1, especially considering that only Val appears to be critically required for normal cell growth in the bat1 mutant based on the results in Fig. 3B?
- The data in Fig. 3B do not show a convincing increase in growth of the bat1 mutant with addition of Leu and Ile; and the stimulation by Val alone seems identical to that seen with Val in combination with Leu and Ile. Thus, it appears that the slow-growth of the bat1 mutant results only from reduced Val levels, not all 3 BCAAs, which is at odds with their interpretation of the data.
- they claim to see reductions in all three BCAAs in the bat1 mutant; however, no significant reduction was found for Leu in Fig. EV2, and only Val was altered by the 1.5-fold cut-off imposed on the MS metabolomics data in Fig. EV3 (which could be appreciated only by an in-depth examination of the supplementary data in File S1-the Val, Leu, and Ile dots should be labeled in Fig. EV3). In addition, the reductions in Ala and Gly showin in Fig. EV2 were not found in the MS analysis of Fig. EV3. It needs to be acknowledged that the metabolomics data show a marked reduction in the bat1 mutant only for Valine with little or no change in Leucine levels. This result is difficult to explain with the simple models shown in Fig. 3A and 5F, which requires additional comment. The authors should acknowledge the much greater effect of the bat1 mutation on Val levels versus Leu and Ile, revealed both by measuring the levels of BCAAs in the mutant and comparing the BCAAs for rescuing the slow-growth of the mutant, and explain how this can be reconciled with the results in Fig. 2 where only Leu and not Val or Ile synthesis was detected.
- They need to add the data indicating that the bat1 mutant requires longer than WT cells to reach the ~35 fL volume at which 50% of WT cells are budded.
- It seems important to show that Val supplementation can suppress the overabundance of G1 cells in bat1 mutant cells shown in Fig. 4C; and can restore sensitivity to Rap and Rps6-P accumulation in bat1 mutant cells (in Fig.s 5A & B).
- It seems important to show that Rps6-P will decline in M phase and increase during a second cell cycle to establish that TORC1 activity actually fluctuates in the cell cycle instead of just by reduced by the manipulations involved in collecting young G1 cells by elutriation.
Referees cross-commenting
Ref. #1's major comment 1 echoes my request for clarification about whether Leu, and not just Val, is limiting growth in the bat1 mutant, and also the need to determine which BCAA supplement to bat1 cells will restore TORC1 activity (which was also requested by Ref. #3). I agree with this reviewer's request to provide evidence that Leu levels actually increase during G1 progression (comment #2). I also think the suggested experiments in Comment #3 are reasonable for their potential to provide stronger evidence that Leu production in the G1 phase of wild-type cells activates TORC1, as currently the argument is based on the finding of low TORC1 activation in bat1 cells (that seem to be limiting for Val vs. Leu). Comment #4 echoes similar requests made by both me and Ref. #3. Ref. #3's major comments 1 and 3 mirror two of my major comments. I wasn't convinced of the need to monitor Sch9 versus Rps6 phosphorylation as a read-out of TORC1 activity-does being a direct substrate truly matter? Regarding comment 5, I wasn't convinced of the need to include Rap-sensitive or -resistant control strains for the analysis in Fig. 5A. And regarding comment 4, while it would be interesting to examine if TORC1 regulates BCAA synthesis during cell cycle progression, this seems to be outside the scope of a demonstration that BCAA synthesis stimulates TORC1.
Thus, it seems we all agree on certain experiments that need to be carried out, and Ref. #1 has rightly proposed a few others with the potential to strengthen the evidence that Leu production during G1 phase mediates cyclic activation of TORC1
Significance
General Assessment:
Strengths: Evidence for BCAA biosynthesis from glucose in the G1 phase of the cell cycle, and evidence obtained from analyzing the bat1 mutant that BCAA synthesis underlies activation of TORC1 early in the cell cycle in a manner required to achieve the critical cell size necessary for G1 to S transition.
Weaknesses: Lack of evidence for Val biosynthesis in G1 despite evidence that Val limitation is more crucial than Leu limitation in the bat1 mutant; lack of confirmation that Val limitation underlies the delayed G1-S transition and reduced TORC1 signaling in the bat1 mutant; and lack of compelling evidence that TORC1 activity is periodic in WT cells.
Advance: This would be the first evidence that TORC1 activity varies through the cell cycle in a manner controlled by synthesis of BCAAs
Audience: This advance would be of great interest to a wide range of workers studying how the cell cycle is regulated and the role of TORC1 in controlling cell growth and division in normal cells and in human disease.
My expertise: Mechanisms of metabolic regulation of gene expression at the transcriptional and translational levels in budding yeast
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Referee #1
Evidence, reproducibility and clarity
Summary
In this manuscript, Blank et al. propose a link between cell-cycle dependent changes in metabolic flux and corresponding changes in TORC1 activity in yeast cells. Based on their findings, the authors propose that Bat1-dependent leucine synthesis from glucose increases as cells progress through G1 and that this activates TORC1 to drive cell cycle progression. Although the existence of cell-cycle dependent synthesis of leucine is a novel and exciting finding, several aspects of the proposed model are not sufficiently supported by experimental evidence, in particular the fact that the increase in Leu synthesis is causing the increase in TORC1 activity in late G1.
Major comments:
- To show that the increase in Leu biosynthesis in S-phase is activating TOR, one would ideally want to blunt this increase in biosynthesis and assay TORC1 activity. Admittedly, this is difficult. So, instead, the authors study bat1- cells which have strongly impaired synthesis of BCAA including Leucine. The relevance of these bat1- cells to the proposed cell-cycle dependent model, however, is questionable for two reasons: 1) Although the authors state that "exogenous supplementation of BCAAs in all combinations suppressed the growth defect of bat1- cells, especially when valine was present", the spot assays in Figure 3 show visible rescues only when valine is present either alone or in combination, while supplementation of leucine or isoleucine does not seem to have any effect. Hence it appears that the bat1- phenotype is mainly due to limiting valine levels, not leucine levels. 2) The relevance of these results for understanding TORC1 regulation are questionable, since valine does not typically activate TORC1. Does additionn of Leu to bat1- cells increase TORC1 activity ?
- TORC1 activity is known to depend on steady-state leucine concentrations in the cell rather than on leucine flux. Although the authors observe that the synthesis rate of leucine increases during G1 progression, this does not necessarily translate innto increased leucine concentrations in the cell. To support the claim that the increase in TORC1 activity during G1 progression depends on leucine, the authors would need to show that, not only leucine synthesis, but also overall leucine levels in the cell increase during G1 progression.
- To test whether the increase in Leu biosynthesis in S-phase activates TORC1, a few different approaches could be tested: 1) Since leucine activates TORC1 through the Gtr proteins, the authors could test whether rendering TORC1 resistant to low leucine through expression of constitutively active Gtrs abolishes the cell-cycle dependence in TORC1 activity. 2) Leu could be added to the medium of wildtype cells in G1 to the amount necessary to cause an increase in intracellular Leu levels similar to those seen in S-phase to test whether this increases TORC1 activity.
- In Fig 2B one sees that Leu biosynthesis peaks at 150min and then drops again. The p-RpS6 blot in Fig. 5D, however, only goes up to 140 min and shows that TORC1 activity increases up to 140 min, but it doesn't show timepoints beyond 150 min when Leu biosynthesis drops again, and hence one would expect TORC1 activity to drop. If TORC1 activity were to drop from 150min onwards, this would strengthen the correlation between Leu biosynthesis and TORC1 activity.
Minor concerns:
- In Figure EV3, the authors should highlight some of the metabolites that are significantly changed, in particular the BCAA. The figure is not very informative as currently presented.
- Fig 2 - are "expressed ratios" the best term for metabolite levels? Unlike genes, where such heat maps are often used, the metabolites are not 'expressed'. How about 'relative metabolite level' instead?
- Page 8: "We also measured the MID values from the media of the same cultures used to prepare the cell extracts." Where are these data? We don't see them in File S2?
- Fig 4B - the x-axis labeling is missing for the bat1- cells
- Although the authors state repeatedly that they show "for the first time in any system" that TORC1 activity is dynamic in the cell cycle, similar observations have already been made before, for instance showing high mTORC1 activity in the G1/S transition in the Drosophila wing disc or low mTORC1 activity during mitosis in mammalian cells (see PMIDs 28829944, 28829945, and 31733992). The text should be amended accordingly.
- There are two entries for valine in File S1/Sheet8. Why?
Significance
Despite the well-known effects of pharmacological or genetic manipulations of TORC1/mTORC1 on cell cycle progression, whether and how mTORC1 activity itself is physiologically coupled to cell cycle progression is still an insufficiently studied aspect. Hence this study provides an interesting link between cell-cycle dependent regulation of amino acid biosynthesis and TORC1 regulation. Importantly, the results of this study rely on centrifugal elutriation to obtain cell cycle synchronization, thus ruling out potential metabolic artifacts due to pharmacological methods. The observed changes in metabolic flux are therefore likely genuine and represent the major strength of the study. The major limitation is the lack of strong evidence supporting the notion that the increase in Leu biosynthesis at late G1 or S-phase is causing the increase in TORC1 activity.
The major advance is conceptual - that amino acid biosynthesis rates are cell-cycle dependent.
These results will be of interest to a broad audience of people studying the cell cycle, cell growth, TORC1 activity, cell metabolism and cancer.
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Reply to the reviewers
General Statement
We thank the reviewers for a thorough review that will help us to improve the manuscript in the revision process. In our opinion, all three reviewers found the manuscript interesting, novel, and relevant for a broader readership. The reviewers suggested performing additional analyses of cell quantification from existing brain tissue or from newly generated tissue. All reviewers identified several shared concerns that we are happy to address by additional experiments and analyses to improve our manuscript. The reviewers suggested including the Control Diet + LiPR treatment group to further characterize the effects of LiPR on adult neurogenesis outside the context of the High Fat Diet. Also, the reviewers suggested including built upon the analysis of tanycytes and their proliferation. Some of these analyses will require generating new experimental animals, however, most analyses can be performed from already available brain tissue or previously collected confocal microscope images. Because we had anticipated some of the possible concerns, we have placed mice in the experiment already in February 2023. These mice are in the 4-month treatment group of Control Diet + LiPR. We will collect the brain tissue at the end of May 2023 and will analyze it in June and July 2023. In April and May 2023, we will work on analyses from existing tissue or images as described in detail below. We estimate that the suggested analyses are all feasible and should be manageable in 3 months. In fact, we are pleasantly surprised by the favorable nature of the reviews, especially from the reviewer 1 and 3, which allowed us to address around 50% of comments already as demonstrated in this revision plan (see section 3). Therefore, we are confident that we will be able to address the remaining concerns to full satisfaction of all relevant reviewers’ comments.
Reviewer 1
In this manuscript, Jorgensen and colleagues describe their findings on the action of a palmitoylated form of prolactin-release peptide (LiPR) on neural stem cells (NSC) in the adult mouse hypothalamus and adult mouse hippocampus. Their main conclusion is that LiPR can counteract the effects of high-fat diet (HFD) and rescue some of the adverse effects of HFD. Specifically, the authors provide evidence that: - Exposure to HFD reduces the number of presumptive adult neural stem cells (NSCs) in the adult hypothalamus, whereas exposure to LiPR reverses this trend. - The results suggest that LiPR reduces the proliferation of alpha-tanycytes and/or their progeny in the hypothalamus in the context of HFD, with Liraglutide acting similarly. In contrast, while LiPR also suppresses proliferation in the SGZ, Liraglutide works there in the opposite direction. - LiPR also helps the survival of adult-born hypothalamic neurons. - Reduction of proliferation by LiPR suggests a model where LiPR increases the number of NSCs presumably by reducing their rate of activation. - The results suggest that LiPR promotes expression of PrRP receptors in the hypothalamic neurons, suggesting that PrRP may act directly on such neurons (and tanycytes?) in vivo. - The authors also show that HFD and LiPR alter gene expression profiles of the MBH cells, with HFD, but not LiPR, inducing myelination-related genes. - Finally, they show that PrRP stimulates an increase in Ca2+ in in vitro-derived human hypothalamic neurons. - The authors conclude that LiPR may be reducing activation and proliferation of the hypothalamic stem cells and thereby preserve their pool from exhaustion, which was stimulated by HFD. The manuscript presents interesting data and is clearly written. There are several comments, mainly editorial.
RESPONSE: We thank the reviewer for the favorable and positive assessment of our manuscript and for finding our study to be interesting to a broad audience and well written, with most comments described by the reviewer as “editiorial”. Below, we address the reviewer’s concerns in a detailed revision plan.
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- It is unclear why most of the experiments do not include the control+LiPR group. Even though the focus of the study was the action of LiPR in the context of HFD, questions remain regarding the action of LiPR per se. Is LiPR (or Liraglutide, for that matter) completely inactive on the normal diet background, with respect to neurogenesis in the hypothalamus and the hippocampus? Whether the Response is positive or negative, it would give a much better understanding of the action of LiPR - does it regulate neurogenesis in various physiological contexts, or does it only kick in with a particular type of diet? In fact, this was examined (see Supplementary figures), but only for the cells in culture and, when performed with animals, was limited to 7 and 21 days, rather than 4 months, which would have been much more informative.* RESPONSE: We thank the reviewer for this suggestion. We agree that including the Control Diet + LiPR group for the 4-month HFD group would complement the results from the 7 and 21 days. We will generate this treatment group for the 4-month HFD group and analyze the effect of LiPR on aNSC and adult-generated neurons. These mice in the 4-month treatment are in the experiment already from February 2023 and we plan to analyze their brain sections in June and July 2023.
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The question above is also relevant when considering the conclusions on the potential depletion of the stem cell pool (again, whether in the hypothalamus or the hippocampus), particularly at the 4-month time point. The mice are ~6 months old by that time, and neurogenesis in both regions is expected to decrease by that time. Are LiPR or Liraglutide able to suppress or exacerbate this decrease? Can they be used to mitigate this decrease when mice are on a regular diet?*
RESPONSE: This concern will be addressed by analyzing the Control + LiPR mice for the 4-month HFD group (see our response to the point 1 above). We will analyze neural stem cells in the Hypothalamic Ventricular Zone and neural progenitors in the Median Eminence of these mice to address whether LiPR treatment changes the time-dependent decrease in both cell populations.
- A somewhat related issue is that, in most cases, only the percentage or the density of cells are shown on the graphs, rather than the absolute numbers (at least for some cases). This sometimes complicates the comparisons; for instance, does the surface of the hypothalamus change between 2 and 6 months of age? The tanycytes' number stays, apparently, the same (e.g., Fig. 2) but the production of new neurons is supposed to fall dramatically.*
RESPONSE: We thank the reviewer for this comment. We agree that the quantification of absolute number of cells is the preferable approach that we have used in our previous publications on subventricular (SVZ) or subgranular (SGZ) neurogenesis. However, hypothalamic adult neurogenesis is dispersed over much larger volume of tissue than neurogenesis in the SVZ or SGZ, which is confined to narrow tissue compartments. As we do not have access to a confocal microscope with stereological software, absolute quantification in entire MBH is not feasible. Nevertheless, we believe that our quantification of cell density provides an unbiased and informative approach that allowed us to compare the effects of LiPR and diet on the neurogenic process.
- The authors write "LiPR may prevent stem cells from exhaustion, induced by HFD" - but it is not clear that HFD indeed leads to exhaustion - there is no statistically significant difference in the number of the stem cells (alpha-tanycytes) between the control and HFD or between HFD at 1, 3, or 12 weeks.*
RESPONSE: We thank the reviewers for their insights. We adjusted the interpretation to better reflect our results. On line 442, we replaced the original statement “The lower cell activation may protect the stem cell pool from exhaustion elicited by the HFD“ with a new one, “The lower cell activation may protect the stem cell pool from exhaustion elicited by the HFD“.
- Numerous papers show that the rate of production of new adult hypothalamic neurons (mainly those derived from beta-tanycytes) drops drastically within the first several weeks of mouse life. Does HFD accelerate, and LiPR mitigate, this decrease? Perhaps one can calculate the numbers from the graphs, but it would help if this is explained in the text of the manuscript. Also, it is not always clear whether specific experiments were performed with the zones of the hypothalamic wall that only contain alpha-tanycytes.*
RESPONSE: Our results show that LiPR rescues the HFD-induced reduction in adult-generated hypothalamic neurons only in the context of 4-month HFD but not in the 7- and 21-day HFD. In the methods (line 877), we specify that “the Region of Interest (ROI) quantified included the MBH parenchyma with the Arcuate (Arc), DMN and Ventromedial (VMN) Nuclei and the Medial Eminence (ME)”. In the results of the revised manuscript (lines 301-303), we highlighted the areas of the ROI. Upon the request of Reviewer 3 (comment 14), we included new data on quantification of BrdU+ neurons in the Arcuate Nucleus (S.Fig.5O). This data show that 21d HFD increases the number of new neurons in ArcN, which is reversed by LiPR or Liraglutide (text added to results and discussion on lines 309-313 and 468-474, respectively). Finally, in the discussion (lines 464-488), it is stated that HFD and/or LiPR had no effect on number of new hypothalamic neurons or cells in the MBH parenchyma in the 7- and 21-day groups and this is discussed in the context of relevant literature.
- A sharp increase in PCNA+ cells in the hippocampus at the 21-day time point, both in the control and in the HFD and HFD/LiPR groups (Fig. S2f) is a little puzzling because neither the Dcx+ nor the Ki67+ cells show this increase.*
RESPONSE: We agree with the reviewer that this increase in the number of PCNA+ cells is puzzling. We quantified the number of PCNA+ cells twice by two different people, always getting the same result. Given that this is a minor result in a supplementary figure, we would prefer not analyzing this again, unless the reviewer would insist on it.
- The study deals with several agents and several processes; a simple scheme that summarizes authors' conclusions might help to better understand the relationships between those agents and processes.*
RESPONSE: We thank the reviewer for this useful suggestion. We included a summarizing schematic in the revised manuscript as the new Figure 6. We will update the schematic for the final revised manuscript, when we will incorporate the new analyses.
***Referee cross-commenting**
I agree, the lack of the LiPR group complicates the interpretation of the results. I also agree that the experiments with vimentin staining, calcium increase, and even with neurospheres do not add much to the main questions that this study attempts to Response, and I'd rather see a more thorough analysis of the activation and differentiation data. I also want to reiterate that the concept of LiPR/PrRP preventing the exhaustion of the hypothalamic stem cell pool is not clear, because it is not shown that this pool does actually get exhausted under normal or HFD conditions. This latter issue again requires the LiPR-alone group. Also, as a clarification - I wrote about 1 month required to compete the revision assuming that the authors actually have the data on the Control+LipR group or at least the specimens available, mainly because the supplementary material shows results with this group, at least with the neurospheres. If this group is fully missing, then the effort will obviously take a longer time.
Reviewer #1 (Significance (Required)):
The provided evidence suggests, for the first time, that PrRP prevents the loss of the neural stem cells population in the adult hypothalamus that was diminished by obesity and HFD. This finding might be interesting to a broad audience.
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Reviewer 2
*The authors examine the effect of an anorexigenic drug, LiPR in the context of treatment with high fat diet (HFD) and with a special focus on hypothalamic neural stem/progenitor cells and neurogenesis. The work is mostly based on mice and a barrage of different techniques (confocal imaging, cell cultures with time lapse, gene expression...) are used. The results are interesting because they address the yet-poorly understood implication of hypothalamic neurogenesis in food intake and energy balance. The results point at complex effects at different levels (neural stem cells, neurons, division, survival...). The experimental approach is sometimes thorough in the treatment of details on the one hand, it also lacks of consistency on the other, and as a result the conclusions lack strength. There is a number of experiments that sometimes seem unrelated and this hurts the comprehension of the manuscript, specially in lieu of the complexity of the results obtained.
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RESPONSE: We thank the reviewer for finding our results interesting and relevant. We will strive to improve the consistency of our results in the revised manuscript to satisfy the reviewer’s concerns.
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A major issue is the lack of a LiPR-only group, which would much facilitate the interpretation of the results. The effect of LiPR alone is however tested, but only in comparison with the Control in one of the in vitro experiments (S.Fig. 3) RESPONSE: We agree with the reviewer that expanding on the LiPR-only effect would facilitate the interpretation of the results (see concern 1 and 2 of reviewer 2). We want to emphasize, however, that we analyzed the HFD-independent LiPR effects not only in vitro but also in vivo by quantifying the number of BrdU+ cells and neurons in the MBH of mice exposed to 21-day HFD (S.Fig. 5 O-Q) and by including the Control Diet + LiPR in the RNAseq experiment (Fig.5C). Nevertheless, we will analyze the number of alpha tanycytes and proliferating cells for the 21-day Control Diet + LiPR treatment group. And we will generate mice treated with Control Diet + LiPR to complement the 4-month group. In this Control Diet + LiPR group, we will quantify the number of tanycytes and number of BrdU+ cells and neurons.
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As plotted, in Fig 1B is difficult to interpret the effect of HFD and LiPR, might be using percentage and noting the statistical differences as in the other would help. It looks like HFD has no effect compared to control on weight and only at the end LiPR could have an effect. On the other hand, after 4 months, HFD mice are clearly above the controls and it is then, albeit when weight gain has reached a plateau, that LiPR has an effect. The election of these arbitrary paradigms and their drawbacks has to be better explained.*
RESPONSE: We thank the reviewer for the comment. We analyzed the effect of HFD and/or LiPR on the body weight for the 21-day group (Fig.1B) in the original manuscript (lines 111-115). The two-way, repeated measure ANOVA revealed no effect of the treatment on the body weight in the 7-day group, however, it revealed the effect of the duration of treatment on the body weight in the 21-day group. As suggested by the reviewer, we included the Control Diet + LiPR in the 21-day group (Fig.1B). We analyzed the data with ANOVA and found that the treatment has a statistically significant effect on the body weight, however, without any statistical difference between treatment groups (lines 112-116 in the revised manuscript). In addition, we will include the Control Diet + LiPR in the 4-month group.
Why was the proportion of GPR10+BrdU+MAP2+ cells only assessed in control mice and no in the experimental groups if its expression in overall neurons changes? This suggests that the receptor is expressed in neurons. Interestingly, exposure to 21d HFD reduced density of GPR10, which was rescued by LiPR administration (Fig.1L). Why was this time point chosen and not the longer-term one? What is the consequence of the alterations in the potential number of GPR10, specially in relation to the administration of LiPR? This clarification is important because a 14-day treatment was chosen for the in vitro experiments in which LiPR, but not HFD, seems to have an effect on cell proliferation. Might be it would have been more useful to use a paradigm in which HFD has an effect to better compare with in vivo work and for the rationale of the work. "Besides GPR10, we co-localized neuronal cytoskeleton structures with NPFFR2 in the MBH (Fig.1O-P)..." Why were not GPR10 and NPFF2 analyzed in a similar and consistent manner ? It is confusing.
RESPONSE: The proportion of GPR10+BrdU+Map2+ neurons was quantified to address whether new neurons express the PrRP receptor. We chose to analyze the proportion of GPR10+BrdU+Map2+ neurons at the 21d time-point because we had the most robust data for this or related time points in vitro and in vivo. We will emphasize this in the text. But we prefer not to analyze the effect of LiPR on the density or expression of GPR10 or NPFF2 for all time points. We consider this to be beyond the scope and focus of the manuscript.
The number of GFAP+ α-tanycytes is not significantly changed by HFD therefore LiPR does not rescue, but rather increases the number of GFAP+ α-tanycytes in the 7-day setting. There are no differences among groups later, the effect is lost by 21 days, therefore there is a transient excess of GFAP+ α-tanycytes which later "disappear" in the LiPR group. The authors state that LiPR rescues the decrease in "htNSCs", but after 21 days the number of the GFAP+ α-tanycytes is the same in all groups without the need of LiPR. There is no experimental follow up (addressing proliferation and survival of these cells) and the conclusions stated in the text (results and discussion) are not really supported by the data. The in vitro experiments could be a complement, but are no substitute for the missing in vivo exploration.
RESPONSE: We thank the reviewer for this comment. We agree that we did not correctly interpret the data. On line 158, we replaced the original statement “This suggests that short LiPR rescues HFD-induced reduction in the number of htNSCs” with a new one that reflects of date correctly, “This suggests that short LiPR increases the number of htNSCs. In our revision plan, we will quantify the number of proliferating tanycytes to complement our in vitro results.
- The fact that cell division is "rarely found" (Rax GFAP) experiments also push for further investigation. It is difficult to see that relevance of the inclusion of the vimentin staining experiment if there is no further exploration. The effect of LiPR is only transient, in the 7-day paradigm and as the parameter evaluated is the proportion of vimentin+ tanycytes among GFAP+ tanycytes it could only be reflecting increased expression of the filament. "Nevertheless, we did not observe a statistically different change in the area occupied by Rax+ tanycytes (Fig.2H)." Why did the authors use Rax only for this experiment if "GFAP+ α-tanycytes which are considered the putative htNSCs?" What is the justification for not seeing changes in relation to the results reported in Fig 2D-F? "Because Vimentin is associated with nutrient transport in cells and with metabolic response to HFD 52-54, we quantified the proportion of GFAP+ tanycytes expressing Vimentin (Fig.2F)." It is difficult to see that relevance of the inclusion of the vimentin staining experiment if there is no further exploration. The effect of LiPR is only transient, in the 7-day paradigm and as the parameter evaluated is the proportion of vimentin+ tanycytes among GFAP+ tanicytes it could only be reflecting increased expression of the filament.*
RESPONSE: Because Vimentin is a marker of neural stem cells and alpha tanycytes, we quantified the number of GFAP+Vimentin+ tanycytes to complement the quantification of GFAP+ alpha tanycytes. We are sorry that this was not clear, and we highlighted this connection in the revised manuscript (line 165). Because Rax is expressed in alpha tanycytes, we expected that LiPR will increase Rax in the Hypothalamic Ventricular Zone (HVZ). We agree with the reviewer that further investigation may be useful, and we will quantify the number of alpha tanycytes positive for Rax instead of determining only the volume of Rax+ tissue. We will quantify Rax+GFAP+ neural stem cells in the HVZ and Rax+GFAP+ neural progenitors (so-called beta tanycytes) in the Median Eminence to improve characterization of the cell dynamics in vivo.
- Why there is no Ki67 experiment in the 7-day paradigm if that is the timepoint in which changes in the number or proportion of GFAP+ tanycytes are observed? PCNA was then used but only in the 21-day paradigm. What is the interpretation and relevance of these data? What are the non-htNSCs proliferating cells, whose dynamics are different from the changes in the number or proportion of htNSCs that could be potentially related to changes in mitosis? Again, I think it would be much useful for the work to explore in detail the changes in the putative htNSCs than investing in experiments that only add confusion.*
__RESPONSE: __We apologize if the data presentation is confusing. We will include the quantification of the Ki67+ cells for the 7-day time point. In the MBH, many cell types undergo mitosis, including the oligodendrocyte precursor cells, microglia, astrocytes, and infiltrating macrophages. However, characterizing the identify of all these different cell types in response to the HFD and/or LiPR is beyond the scope of this study. To resolve whether HFD and/or LiPR influence proliferating aNSCs, we will quantify the proliferating cells in the HVZ, which will allow us to separate the proliferating aNSCs from all other proliferating cell types in the MBH.
- The inclusion of Liraglutide + HFD, (not Liraglutide alone) only in some of the experiments is pointless if there is no direct comparison with LiPR and a timepoint is missing. In S.Fig 3, Fig. 5 and S.Fig 7 LFD (low fat diet?) is used in several occasions as in: "on reducing number of PCNA+ cells in 21d protocol (one-way ANOVA (OWA), F(2,12) = 16.66, p = 0.0003) when compared to both LFD and HFD groups". Is this the control diet?*
RESPONSE: We apologize for the confusion caused by labelling the conditions of the Control Diet inconsistently. In some figures (e.g., Fig.2, S.Fig.3, Fig.4), we labelled the Control Diet as “Control”, whereas in some other figures (e.g., Fig.5, S.Fig.7) we labelled the Control Diet as “LFD” (Low Fat Diet). In all experiments and figures, the used Control Diet was identical. We unified the labelling of the Control Diet in all figures and in the text of the revised manuscript. Respectfully, we do not agree that including the Liraglutide data is pointless. We included the Liraglutide in the context of the HFD as a direct comparison with the HFD + LiPR group to demonstrate that the two anti-obesity compounds exert differential effects on adult neurogenesis. Such comparison has not been done before in analyzing adult neurogenesis and is valuable for better understanding of functions of these anti-obesity compounds.
- The final experiment shows that application of hPrRP31, a variation of LiPR, causes an immediate calcium increase in human induced pluripotent stem cell-derived hypothalamic nucleus. This finding is interesting in itself because it brings light about the function of the receptor/s. It would have been very useful to test what other receptors mentioned to bind LiPR is mediating the effect. In any case, the focus of the work are the neural stem/progenitor cells responsible for neurogenesis and the changes in their properties because of HFD and LiPR, therefore I would trade these experiments for a more thorough and detailed dissection of these effects.*
RESPONSE: We thank the reviewer for recognizing the relevance of the experiments with the hiPSC-derived neurons. As described in the comments above, we will conduct additional experiments to address the effect of LiPR on aNSCs and proliferation to more thoroughly as suggested by the reviewer.
Minor points: __ A.__ Introduce "GLP-1RA"
__RESPONSE: __We thank the reviewer for identifying this omission. We introduced the term in the revised manusript (line 50).
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- "HFD-induced inflammation and astrogliosis in the hypothalamus 45,46, whereas the long (4mo) protocol leads to DIO" Are these notions exclusive?* __RESPONSE: __This statement emphasized that HFD-induced inflammation and astrogliosis precede obesity. We prefer to leave the statement as it is.
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- LiPR displays no effects on astrocytes" "Displays" is not the correct term.* RESPONSE: We replaced the term “display” with the word “show” in the revised manuscript (line 342).
***Referee cross-commenting**
I think we all referees agree for the most part. The main concern stated by all of us is the lack of a LiPR-alone group. The rest of the concerns are also related or complementary. In my opinion the mostly common view by the referees is reasuring.
Reviewer #2 (Significance (Required)):
The strengths of the work are its novelty in the field and the variety of techniques employed. The work has the potential of unveiling mechanistic insight into the regulation of neural stem/progenitor cells and neurogenesis. The main audience of this work would be the community working on this field. The lack of experiments testing that the changes observed actually participate in food intake prevent the work from being of relevance for a broader audience (food intake, energy balance, obesity...). The limitations are the descriptive nature of the work and the lack of a consistent and systematic experimental design that would allow to extract solid conclusions upon to which build upon future research.
*
Reviewer 3
The work of Jörgensen et al describes the effect of a lipidized analogue of the prolactin releasing peptide (LiPR) on the mouse metabolism in response to high fat diet (HFD) and on hypothalamic and subgranular zone (SGZ) neurogenesis. They conclude that LiPR reduces body weight and improves metabolic parameters affected by HFD as well as it concomitantly stimulates neurogenesis in both niches the SGZ and the hypothalamus. The link between both effects is not demonstrated. The work is well conducted, the hypothesis is interesting and the experimental approach is adequate. The scope is wide and results are interesting, however a few aspects need to be further clarified. The manuscript is well written although the modification of some aspects would facilitate the reading such as the use of non described abbreviations for example.
RESPONSE: We thank the reviewer for the positive assessment of our manuscript and for recognizing its novelty and importance for the research in neurogenesis, endocrinology, and metabolism. We will strive to clarify and facilitate our conclusions to improve the manuscript.
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- One concern in this study is the experimental groups. Authors analyze three groups control,HFD and HFD treated with LiPR. Authors conclude that the effects of LiPR are diet independent. However, given the results obtained by the authors on the effect of LiPR, the main question that arises in here is whether LiPR would have an effect on control mice. It seems tha a group is missing in the experimental design in which control ,mice are treated with LiPR during 7, 21 and the last two weeks of the 4 months. Author must include this information or at least argue the election of the experimental design.* RESPONSE: We thank the reviewer for this insight. We agree that including the Control Diet + LiPR in some of our analyses would improve the revised manuscript as also noted by Reviewer 2 (comment 1 and 2) and by Reviewer 2 (comment 1 and 2). In the original manuscript, we included the quantification of BrdU+ cells in the MBH for the Control Diet + LiPR in the 21-day group. To expand on these results, we will quantify the effects of LiPR on alpha tanycytes in the 21-day group. In addition, we will generate Control Diet + LiPR mice for the 4-month group to complement the HFD and HFD + LiPR data.
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Body weight is found reduced by LiPR as well as other metabolic parameters in mice treated with LiPR during the last two weeks of the 4 Mo HFD. However, no effects on hypothalamic or SGZ neurogenesis are not observed in this experimental group. How do authors explain this results?*
__RESPONSE: __The 4-month group contains animals that are over 6-month-old, which display very low levels of cell proliferation and differentiation in comparison with the 7 and 21-day groups that contain mice that are 2 and 2.5 months old, respectively. It is possible that these low levels of neurogenesis did not allow us to detect any pro-neurogenic effects of LiPR. Alternatively, the low neurogenesis in older animals precludes us from detecting the adverse effects of the HFD, which are rescued by LiPR in younger animals.
- In figure 1 I-K images are not clear and better resolution images would help.*
RESPONSE: We provided images with higher resolution for Figure 1I-K of the revised manuscript.
- Authors conclude that LiPR is increasing the number of NSC by reducing their activation. However, authors show an induced increase in htNSC only in mice fed HFD for 7 days and not in the 21 day fed mice or the 4 mo fed mice (fig 2 d-f). In addition, authors test for the number of cells expressing Ki67 (fig 2 L), however, the number of Ki67+ alpha tanicytes is not shown.*
RESPONSE: We thank the reviewer for this insight. In the revised manuscript (line 158), we corrected the inaccurate statement that LiPR increased the number of aNSCs and did not rescue their number, which was also noted by Reviewer 1 (comment 5) and by Reviewer 2 (comment 4). In addition, we will quantify the number of Ki67+ cells in the Hypothalmic Ventricular Zone (HVZ), which will address whether LiPR affects proliferation of aNSCs. This concern parallels comment 6 of Reviewer 2.
- On figure 2B it seems that is alpha 2 tanicytes that are missing in response to HFD.*
RESPONSE: Indeed, the panel in Figure 2B shows that the HFD reduces the number of alpha tanycytes, including the alpha 2 tanycytes. This representative image supports our quantification results in Figure 2D-E.
- Are Fig 2 A-C images representative of mice fed HFD for 7 days?*
__RESPONSE: __Yes, the representative images in panels of Fig. 2A-C are from the 7-day group. However, the legend states that these images are from the 21-day group. This is an error that we corrected in the revised manuscript in the legend of Figure 2 (line 572). We apologize for this and thank the reviewer for double-checking.
- By looking at figure 2B it seems like the proportion of alpha tanicytes is higher in HFD since no or very few tanicytes are observed and almost all of them are alpha tanicytes.*
RESPONSE: Indeed, 7 days of HFD reduced the number of alpha 2 tanycytes, which occupy the ventral-lateral aspect of the 3rd ventricle. This reduction of alpha 2 tanycytes drives the lover proportion of GFAP+ alpha-tanycytes out of all GFAP+ tanycytes. We emphasized this in the text of the revised manuscript (line 435-437).
- In fig 2 d-f, an increase in the number of GFAP+ alpha tanicytes and its proportion as well as labelled with vimentin is observed in control mice fed with normal diet for 7 days compared with mice fed normal diet for 21 days. How do authors explain this difference?*
RESPONSE: There is no difference in the number of GFAP+ alpha tanycytes or proportion of GFAP+ alpha tanycytes between 7-day and 21-day Control Diet mice. We used the two-way, repeated measure ANOVA with the Bonferroni’s pots-hoc test and did not observe any statistical difference between these 2 quantifications for the Control Diet mice at 7 and 21 days. There is a statistical difference between 7-day and 21-day Control Diet mice in the proportion of GFAP+Vimentin+ tanycytes. This could be due to expansion of the Vimentin+ tanycytes in relatively young adult mice. Given that this is not a major point, we prefer not expanding its discussion in the manuscript.
- In fig 2 Why are the differences in RAX, KI67 and PCNA only present in mice fed HFD for 21 days?*
RESPONSE: We thank the reviewer for this question, which reflects a similar comment 6 of Reviewer 2. To improve consistency of the presented data, we will quantify the proliferating cells also for the 7-day time point. In addition, we will quantify the number of proliferating cells in the HVZ, which will allow us to address whether HFD and/or LiPR alter proliferation of tanycytes.
- Authors test for adult hippocampal neurogenesis in the three groups. DO images in fig S2 correspond to the 21 day treatment group?*
RESPONSE: Yes, the representative images in the Supplementary Figure 2 are from the 21-day group. This is stated in the figure legend.
- On fig S2 C, it seems that in HFD fed mice treated with LiPR newly generated neuroblasts are more differentiated have authors looked at DCX+ cell morphology?*
RESPONSE: We thank the reviewer for this observation. We have not analyzed the morphology of DCX+ cells or DCX+ neuroblasts in the SGZ. As the manuscript focuses on the hypothalamic and not hippocampal neurogenesis, we prefer not to analyze the morphology in the revised manuscript.
- In this same figure, it seems like the number of DCX+ neuroblasts and the number of newly generated neurons is reduced in mice of the 21 d group compared to the 7 day group. Is this statistically significant?*
RESPONSE: We used the two-way, repeated measure ANOVA with the Bonferroni’s pots-hoc test to analyze the DCX+ neuroblasts and neurons. We observed a statistically very significant effect of LiPR treatment on the number of DCX+ neuroblasts and neurons (page 10 of the original manuscript). However, the Bonferroni’s test did not reveal any difference between 7-day and 21-day treatment groups.
- There is a large reduction in the number of DCX+ cells from control 21 d treated mice to control 4 month treated mice. Is this statistically significat? How do authors explain this dramatic reduction?*
RESPONSE: Yes, there is statistically significant reduction in the number of DCX+ cells and DCX+ neurons in the SGZ between the 21-day and 4-month group S.Fig.2). This reduction is most likely a result of aging. The mice of the 21-day group were around 2.5 months of age when culled, whereas the 4-month group month mice were over 6.5-month-old. The decline in SGZ neurogenesis with age is well documented. Because this decrease in DCX+ cells in the SGZ is an obvious consequence of the animals’ age and because the hippocampal neurogenesis is not the primary focus of this manuscript, we prefer not to discuss this feature in the manuscript.
- Authors do not show the effect of HFD on BrdU+ neurons in the Arcuate. However, all data need to be shown.
*
RESPONSE: We stated (on page 12 of the original manuscript) that in the Arcuate Nucleus of the 21-day group, there was “a statistically significant increase of BrdU+ neurons by HFD compared to Control (data not shown)”. To satisfy reviewer’s comment, we incorporated this data in the S.Fig.5 as the new panel S.Fig.5O and added the following text (lines 309-313) to the revised manuscript: “However, in the ArcN, the primary nutrient and hormone sensing neuronal nucleus of MBH 4, there was a statistically significant difference in number of BrdU+ neurons due to treatment (OWA, F(3,15) = 3.97, p = 0.0029). Exposure to 21d HFD significantly increased the number of BrdU+ neurons in the ArcN, which was reversed by co-administration of LiPR or Liraglutide (S.Fig.5O).” In addition, we adjusted the relevant discussion (lines 468-472): “Our results show that the short and intermediate exposure to HFD does not change the number of newly generated, BrdU+ cells, neurons, or astrocytes in the MBH parenchyma, however, it increases the number of BrdU+ neurons in the primary sensing ArcN, which is reversed by the con-current administration of LiPR or Liraglutide” and (lines 474-476): “In addition, our results show that while LiPR does not change the number of new cells in the MBH parenchyma, it can rescue the increased production of new neurons in the ArcN in the context of the intermediate HFD exposure.”
*Reviewer #3 (Significance (Required)):
In general the manuscript includes a great amount of work to demonstrate the effect of LiPR on neurogenesis (hippocampal and hypothalamic). The scope is wide, and the hypothesis is really interesting. Authors may need to solve some issues in order to completely demonstrate their claims and conclusions, but once the work is done, it will be very valuable to understand the effect of pharmacological agents used in the field of endocrinology to treat metabolic disorders such as type 2 diabetes di type 2 diabetes. So far, no studies have been done in which the effect of this molecules have been described on SGZ and hypothalamic neurogenesis. Both the field of endocrinology and metabolism as well as the field of adult neurogenesis may benefit of a study of this type.*
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Referee #3
Evidence, reproducibility and clarity
The work of Jörgensen et al describes the effect of a lipidized analogue of the prolactin releasing peptide (LiPR) on the mouse metabolism in response to high fat diet (HFD) and on hypothalamic and subgranular zone (SGZ) neurogenesis. They conclude that LiPR reduces body weight and improves metabolic parameters affected by HFD as well as it concomitantly stimulates neurogenesis in both niches the SGZ and the hypothalamus. The link between both effects is not demonstrated. The work is well conducted, the hypothesis is interesting and the experimental approach is adequate. The scope is wide and results are interesting, however a few aspects need to be further clarified. The manuscript is well written although the modification of some aspects would facilitate the reading such as the use of non described abbreviations for example.
Major comments:
- One concern in this study is the experimental groups. Authors analyze three groups control,HFD and HFD treated with LiPR. Authors conclude that the effects of LiPR are diet independent. However, given the results obtained by the authors on the effect of LiPR, the main question that arises in here is whether LiPR would have an effect on control mice. It seems tha a group is missing in the experimental design in which control ,mice are treated with LiPR during 7, 21 and the last two weeks of the 4 months. Author must include this information or at least argue the election of the experimental design.
- Body weight is found reduced by LiPR as well as other metabolic parameters in mice treated with LiPR during the last two weeks of the 4 Mo HFD. However, no effects on hypothalamic or SGZ neurogenesis are not observed in this experimental group. How do authors explain this results?
- In figure 1 I-K images are not clear and better resolution images would help.
- Authors conclude that LiPR is increasing the number of NSC by reducing their activation. However, authors show an induced increase in htNSC only in mice fed HFD for 7 days and not in the 21 day fed mice or the 4 mo fed mice (fig 2 d-f). In addition, authors test for the number of cells expressing Ki67 (fig 2 L), however, the number of Ki67+ alpha tanicytes is not shown.
- On figure 2B it seems that is alpha 2 tanicytes that are missing in response to HFD.
- Are Fig 2 A-C images representative of mice fed HFD for 7 days?
- By looking at figure 2B it seems like the proportion of alpha tanicytes is higher in HFD since no or very few tanicytes are observed and almost all of them are alpha tanicytes.
- In fig 2 d-f, an increase in the number of GFAP+ alpha tanicytes and its proportion as well as labelled with vimentin is observed in control mice fed with normal diet for 7 days compared with mice fed normal diet for 21 days. How do authors explain this difference?
- In fig 2 Why are the differences in RAX, KI67 and PCNA only present in mice fed HFD for 21 days?
- Authors test for adult hippocampal neurogenesis in the three groups. DO images in fig S2 correspond to the 21 day treatment group?
- On fig S2 C, it seems that in HFD fed mice treated with LiPR newly generated neuroblasts are more differentiated have authors looked at DCX+ cell morphology?
- In this same figure, it seems like the number of DCX+ neuroblasts and the number of newly generated neurons is reduced in mice of the 21 d group compared to the 7 day group. Is this statistically significant?
- There is a large reduction in the number of DCX+ cells from control 21 d treated mice to control 4 month treated mice. Is this statistically significat? How do authors explain this dramatic reduction?
- Authors do not show the effect of HFD on BrdU+ neurons in the Arcuate. However, all data need to be shown.
Significance
In general the manuscript includes a great amount of work to demonstrate the effect of LiPR on neurogenesis (hippocampal and hypothalamic). The scope is wide, and the hypothesis is really interesting. Authors may need to solve some issues in order to completely demonstrate their claims and conclusions, but once the work is done, it will be very valuable to understand the effect of pharmacological agents used in the field of endocrinology to treat metabolic disorders such as type 2 diabetes di type 2 diabetes.
So far, no studies have been done in which the effect of this molecules have been described on SGZ and hypothalamic neurogenesis. Both the field of endocrinology and metabolism as well as the field of adult neurogenesis may benefit of a study of this type.
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
The authors examine the effect of an anorexigenic drug, LiPR in the context of treatment with high fat diet (HFD) and with a special focus on hypothalamic neural stem/progenitor cells and neurogenesis. The work is mostly based on mice and a barrage of different techniques (confocal imaging, cell cultures with time lapse, gene expression...) are used.
The results are interesting because they address the yet-poorly understood implication of hypothalamic neurogenesis in food intake and energy balance. The results point at complex effects at different levels (neural stem cells, neurons, division, survival...). The experimental approach is sometimes thorough in the treatment of details on the one hand, it also lacks of consistency on the other, and as a result the conclusions lack strength. There is a number of experiments that sometimes seem unrelated and this hurts the comprehension of the manuscript, specially in lieu of the complexity of the results obtained.
These are the detailed comments:
A major issue is the lack of a LiPR-only group, which would much facilitate the interpretation of the results. The effect of LiPR alone is however tested, but only in comparison with the Control in one of the in vitro experiments (S.Fig. 3)
As plotted, in Fig 1B is difficult to interpret the effect of HFD and LiPR, might be using percentage and noting the statistical differences as in the other would help. It looks like HFD has no effect compared to control on weight and only at the end LiPR could have an effect. On the other hand, after 4 months, HFD mice are clearly above the controls and it is then, albeit when weight gain has reached a plateau, that LiPR has an effect. The election of these arbitrary paradigms and their drawbacks has to be better explained.
Why was the proportion of GPR10+BrdU+MAP2+ cells only assessed in control mice and no in the experimental groups if its expression in overall neurons changes?
This suggests that the receptor is expressed in neurons. Interestingly, exposure to 21d HFD reduced density of GPR10, which was rescued by LiPR administration (Fig.1L). Why was this time point chosen and not the longer-term one? What is the consequence of the alterations in the potential number of GPR10, specially in relation to the administration of LiPR?
This clarification is important because a 14-day treatment was chosen for the in vitro experiments in which LiPR, but not HFD, seems to have an effect on cell proliferation. Might be it would have been more useful to use a paradigm in which HFD has an effect to better compare with in vivo work and for the rationale of the work.
"Besides GPR10, we co-localized neuronal cytoskeleton structures with NPFFR2 in the MBH (Fig.1O-P)..." Why were not GPR10 and NPFF2 analyzed in a similar and consistent manner ? It is confusing.
The number of GFAP+ α-tanycytes is not significantly changed by HFD therefore LiPR does not rescue, but rather increases the number of GFAP+ α-tanycytes in the 7-day setting. There are no differences among groups later, the effect is lost by 21 days, therefore there is a transient excess of GFAP+ α-tanycytes which later "disappear" in the LiPR group. The authors state that LiPR rescues the decrease in "htNSCs", but after 21 days the number of the GFAP+ α-tanycytes is the same in all groups without the need of LiPR. There is no experimental follow up (addressing proliferation and survival of these cells) and the conclusions stated in the text (results and discussion) are not really supported by the data. The in vitro experiments could be a complement, but are no substitute for the missing in vivo exploration.
The fact that cell division is "rarely found" (Rax GFAP) experiments also push for further investigation.
It is difficult to see that relevance of the inclusion of the vimentin staining experiment if there is no further exploration. The effect of LiPR is only transient, in the 7-day paradigm and as the parameter evaluated is the proportion of vimentin+ tanycytes among GFAP+ tanycytes it could only be reflecting increased expression of the filament. "Nevertheless, we did not observe a statistically different change in the area occupied by Rax+ tanycytes (Fig.2H)."
Why did the authors use Rax only for this experiment if "GFAP+ α-tanycytes which are considered the putative htNSCs?" What is the justification for not seeing changes in relation to the results reported in Fig 2D-F?
"Because Vimentin is associated with nutrient transport in cells and with metabolic response to HFD 52-54, we quantified the proportion of GFAP+ tanycytes expressing Vimentin (Fig.2F)." It is difficult to see that relevance of the inclusion of the vimentin staining experiment if there is no further exploration. The effect of LiPR is only transient, in the 7-day paradigm and as the parameter evaluated is the proportion of vimentin+ tanycytes among GFAP+ tanicytes it could only be reflecting increased expression of the filament.
Why there is no Ki67 experiment in the 7-day paradigm if that is the timepoint in which changes in the number or proportion of GFAP+ tanycytes are observed? PCNA was then used but only in the 21-day paradigm. What is the interpretation and relevance of these data? What are the non-htNSCs proliferating cells, whose dynamics are different from the changes in the number or proportion of htNSCs that could be potentially related to changes in mitosis? Again, I think it would be much useful for the work to explore in detail the changes in the putative htNSCs than investing in experiments that only add confusion.
The inclusion of Liraglutide + HFD, (not Liraglutide alone) only in some of the experiments is pointless if there is no direct comparison with LiPR and a timepoint is missing. In S.Fig 3, Fig. 5 and S.Fig 7 LFD (low fat diet?) is used in several occasions as in: "on reducing number of PCNA+ cells in 21d protocol (one-way ANOVA (OWA), F(2,12) = 16.66, p = 0.0003) when compared to both LFD and HFD groups". Is this the control diet?
The final experiment shows that application of hPrRP31, a variation of LiPR, causes an immediate calcium increase in human induced pluripotent stem cell-derived hypothalamic nucleus. This finding is interesting in itself because it brings light about the function of the receptor/s. It would have been very useful to test what other receptors mentioned to bind LiPR is mediating the effect. In any case, the focus of the work are the neural stem/progenitor cells responsible for neurogenesis and the changes in their properties because of HFD and LiPR, therefore I would trade these experiments for a more thorough and detailed dissection of these effects.
Minor points:
Introduce "GLP-1RA"
"HFD-induced inflammation and astrogliosis in the hypothalamus 45,46, whereas the long (4mo) protocol leads to DIO" Are these notions exclusive?
"LiPR displays no effects on astrocytes" "Displays" is not the correct term.
Referee cross-commenting
I think we all referees agree for the most part. The main concern stated by all of us is the lack of a LiPR-alone group. The rest of the concerns are also related or complementary. In my opinion the mostly common view by the referees is reasuring.
Significance
The strengths of the work are its novelty in the field and the variety of techniques employed. The work has the potential of unveiling mechanistic insight into the regulation of neural stem/progenitor cells and neurogenesis. The main audience of this work would be the community working on this field. The lack of experiments testing that the changes observed actually participate in food intake prevent the work from being of relevance for a broader audience (food intake, energy balance, obesity...).
The limitations are the descriptive nature of the work and the lack of a consistent and systematic experimental design that would allow to extract solid conclusions upon to which build upon future research.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, Jorgensen and colleagues describe their findings on the action of a palmitoylated form of prolactin-release peptide (LiPR) on neural stem cells (NSC) in the adult mouse hypothalamus and adult mouse hippocampus. Their main conclusion is that LiPR can counteract the effects of high-fat diet (HFD) and rescue some of the adverse effects of HFD. Specifically, the authors provide evidence that:
- Exposure to HFD reduces the number of presumptive adult neural stem cells (NSCs) in the adult hypothalamus, whereas exposure to LiPR reverses this trend.
- The results suggest that LiPR reduces the proliferation of alpha-tanycytes and/or their progeny in the hypothalamus in the context of HFD, with Liraglutide acting similarly. In contrast, while LiPR also suppresses proliferation in the SGZ, Liraglutide works there in the opposite direction.
- LiPR also helps the survival of adult-born hypothalamic neurons.
- Reduction of proliferation by LiPR suggests a model where LiPR increases the number of NSCs presumably by reducing their rate of activation.
- The results suggest that LiPR promotes expression of PrRP receptors in the hypothalamic neurons, suggesting that PrRP may act directly on such neurons (and tanycytes?) in vivo.
- The authors also show that HFD and LiPR alter gene expression profiles of the MBH cells, with HFD, but not LiPR, inducing myelination-related genes.
- Finally, they show that PrRP stimulates an increase in Ca2+ in in vitro-derived human hypothalamic neurons.
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The authors conclude that LiPR may be reducing activation and proliferation of the hypothalamic stem cells and thereby preserve their pool from exhaustion, which was stimulated by HFD. The manuscript presents interesting data and is clearly written. There are several comments, mainly editorial.
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It is unclear why most of the experiments do not include the control+LiPR group. Even though the focus of the study was the action of LiPR in the context of HFD, questions remain regarding the action of LiPR per se. Is LiPR (or Liraglutide, for that matter) completely inactive on the normal diet background, with respect to neurogenesis in the hypothalamus and the hippocampus? Whether the answer is positive or negative, it would give a much better understanding of the action of LiPR - does it regulate neurogenesis in various physiological contexts, or does it only kick in with a particular type of diet? In fact, this was examined (see Supplementary figures), but only for the cells in culture and, when performed with animals, was limited to 7 and 21 days, rather than 4 months, which would have been much more informative.
- The question above is also relevant when considering the conclusions on the potential depletion of the stem cell pool (again, whether in the hypothalamus or the hippocampus), particularly at the 4-months time point. The mice are ~6 months old by that time, and neurogenesis in both regions is expected to decrease by that time. Are LiPR or Liraglutide able to suppress or exacerbate this decrease? Can they be used to mitigate this decrease when mice are on a regular diet?
- A somewhat related issue is that, in most cases, only the percentage or the density of cells are shown on the graphs, rather than the absolute numbers (at least for some cases). This sometimes complicates the comparisons; for instance, does the surface of the hypothalamus change between 2 and 6 months of age? The tanycytes' number stays, apparently, the same (e.g., Fig. 2) but the production of new neurons is supposed to fall dramatically.
- The authors write "LiPR may prevent stem cells from exhaustion, induced by HFD" - but it is not clear that HFD indeed leads to exhaustion - there is no statistically significant difference in the number of the stem cells (alpha-tanycytes) between the control and HFD or between HFD at 1, 3, or 12 weeks.
- Numerous papers show that the rate of production of new adult hypothalamic neurons (mainly those derived from beta-tanycytes) drops drastically within the first several weeks of mouse life. Does HFD accelerate, and LiPR mitigate, this decrease? Perhaps one can calculate the numbers from the graphs, but it would help if this is explained in the text of the manuscript. Also, it is not always clear whether specific experiments were performed with the zones of the hypothalamic wall that only contain alpha-tanycytes.
- A sharp increase in PCNA+ cells in the hippocampus at the 21-day time point, both in the control and in the HFD and HFD/LiPR groups (Fig. S2f) is a little puzzling because neither the Dcx+ nor the Ki67+ cells show this increase.
- The study deals with several agents and several processes; a simple scheme that summarizes authors' conclusions might help to better understand the relationships between those agents and processes.
Referee cross-commenting
I agree, the lack of the LiPR group complicates the interpretation of the results. I also agree that the experiments with vimentin staining, calcium increase, and even with neurospheres do not add much to the main questions that this study attempts to answer, and I'd rather see a more thorough analysis of the activation and differentiation data. I also want to reiterate that the concept of LiPR/PrRP preventing the exhaustion of the hypothalamic stem cell pool is not clear, because it is not shown that this pool does actually get exhausted under normal or HFD conditions. This latter issue again requires the LiPR-alone group. Also, as a clarification - I wrote about 1 month required to compete the revision assuming that the authors actually have the data on the Control+LipR group or at least the specimens available, mainly because the supplementary material shows results with this group, at least with the neurospheres. If this group is fully missing, then the effort will obviously take a longer time.
Significance
The provided evidence suggests, for the first time, that PrRP prevents the loss of the neural stem cells population in the adult hypothalamus that was diminished by obesity and HFD. This finding might be interesting to a broad audience.
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Reply to the reviewers
We thank both the reviewers for the positive comments, insightful suggestions, and constructive criticisms. We have added new calculations, analyzed new data, added new figures in the main text and the supplementary material, revised the main text and the supplementary text to address the reviewer’s comments. We believe the modifications have improved the quality of the manuscript. Below we append our point-by-point response to the reviewers’ comments.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): * Summary: The paper by Rajakaruna, Desai, and Das develops a multiscale computational model (PASCAR) to study design of features of CAR-T cells. Their ODE-based model captures cell-cell interactions using equilibrium receptor-ligand binding relations and a simplified representation of intracellular signaling. The cellular-scale model feeds into a population model including populations of CAR-T cells, healthy cells, and target cells. The model accounts for CAR-T cells with varying numbers of CARs; it accounts for target/healthy cells with varying numbers of ligands. The authors use published cytometry and cytotoxicity data to parameterize the model, which they show captures experimental trends well when they use a kinetic proofreading model to phenomenologically represent intracellular signaling. They then use an optimization approach to characterize features of the CAR-T cell design space that maximize killing of target cells while minimizing the destruction of healthy cells. Their conclusions are consistent with physical intuition and provide quantitative and generalizable predictions about biophysical parameters (including equilibrium binding constants, kinetic rates, etc.).
Major comments:
- In general, the paper is logically laid out and easy to follow.*
Thank you for the positive comment.
However, some of the underlying mechanisms were not clear to me: * * (A) - In Figure 3A, it is not clear why the rate of lysis is greater for populations with an intermediate range of CAR abundances. I understand the authors' statement that "this is because the smaller number of CAR-T cells present in [higher or lower CAR expression groups]..." However, it is not clear why intermediate-level CAR-T cell populations are largest, noting that populations with higher receptor levels have larger proliferation rates. Is this simply reflecting the initial size of the populations, or is another mechanism at play? I think the paper would benefit from discussion/quantification of this.
We thank the reviewer for the insightful comment.
We have edited the main text (pages 8-9) and added a supplementary figure (Fig. S4) to address the above comment. The proliferation rate (ρRHUH) for a subpopulation of size TR increases almost linearly with R since ρRH ∝ R when CAR and HER2 interact with high affinity, i.e., KD≪ R and KD≪H. The distribution of CAR abundances at t=0 estimated by our method follows a lognormal distribution, i.e., the CAR T cell subpopulation size at an intermediate value of R is larger than that at larger values of R. However, given the estimated values for ρRHUH (RHUH decreases with time as the number of target cells are lysed by the CAR T cells. Therefore, the peak of the population remains at intermediate values of R values at later times, and both the initial distribution and the relatively smaller values of the estimated proliferation rate are responsible for the behavior.
*(B) - In Figure 2, C_N plateaus at HER2 density between 10^3 and 10^4. However, % lysis does not plateau until a density closer to 10^5. What is the underlying mechanism? I think the paper would benefit from its exploration.
*
Thank you for the comment.
We have modified the Figure 2 to show the percentage lysis at intermediate values of the HER2 density. The percentage lysis plateaus at similar HER2 concentrations as CN which is expected as the lysis and proliferation rates are proportional to CN. We have modified the text to explain the behavior.
- It is likely that CAR-T cells would encounter various ratios of target and healthy cells depending on patient, microenvironment, in vitro experimental design, etc. My understanding is that the optimization was done with equal numbers of healthy and target cells. It would be useful to explore how sensitive the optimization is to the ratio of target and healthy cells. This could provide useful design guidance to experimentalists.
*
Thank you for the comment.
We have carried out our Pareto front calculations at different healthy and tumor cell ratios namely, 1:4 and 4:1. The Pareto fronts show similar behavior as that shown for the 1:1 ratio in Figure 4 with small vertical and horizontal shifts in the curves compared to the 1:1. We have shown these additional results in the main text (page 11) and the Figure S8 in the supplementary material.
- Two assumptions of the population model initially surprised me. However, given the strong performance of the model, they seem to be well justified. Could the authors address the following with brief discussion?
(A) - The model essentially assumes a well-mixed population of cells, treating lysis and proliferation as second-order "reactions." However, individual cells likely encounter relatively few cells on the time scale of simulations. *
This is an excellent point.
We have added a supplementary text (Supplementary Text 3) and the text below in the Discussion section (page 14) to address the above comment.
PASCAR also assumes that the target and the T cells are well mixed. In vitro cytotoxicity experiments are carried out in culture wells and for the experiments in Hernandez-Lopez et al.6 Our estimates show that 99.8% of the T cells were partnered with target cells (details in Supplementary Text 3). However, depending on the number of target and T cells, the number of target cells in the immediate vicinity of a T cell is likely to be varied (details in Supplementary Text 3), therefore, a weighted sum for the target and T cells in Eq. (3)-(4) would be more appropriate. We plan to include that in a future study.
(B) - The model doesn't include "mixing" of CAR-T cell populations upon proliferation (i.e., a cell with R receptors can't divide and result in cell with a different number of receptors). Is this justified by the biology?
We thank the reviewer for raising this excellent point.
We have added the text below in the Discussion section (page 14) to address the above comment.
PASCAR assumes that the CAR abundances in single CD8+ T cells do not mix as they divide, i.e., daughter cells have the same CAR abundances as the mother cell. However, proteins in human cells (e.g., H1299 non-small cell lung carcinoma cell line) have been observed to mix due to cell division (Sigal et al., 2006) in time scales longer than two cell generations. It is unclear if the CARs follow the similar pattern as the CD8+ T cells proliferate. The doubling time scale for the faster proliferating CD8+ T cells in our model is ~1.7 days and the mean doubling time of the CD8+ T cell population is ~3 days, therefore, there will a negligible amount of mixing in the system due to cell proliferation if a similar mixing time scale as in Sigal et al. (Sigal et al., 2006) occurs for the CAR CD8+ T cells.
*Minor comments
- A couple of figures appear to be mis-referenced in the paper: Figure 2D (end of paragraph, page 7) should presumably be Figure 2E, and Figure S3 should be S2 (end of page 7).*
Done.
- I don't know what "conv." stands for in the figures (I couldn't find the abbreviation in the captions or main text). *
We have changed all the “conv” abbreviations to “const.” indicating constitutive CAR T cells.
- Last pargraph of page 9: "However, decreasing K_D further starts decreasing lysis..." Given the previous sentences, this should presumably say "...increasing K_D further..."*
Done.
- I was initially confused by the second sentence of the last paragraph of Results. Based on the previous paragraph, I expected the sentence to read "when K_D increased" (not decreased) because of the statement "similar to constitutive CAR-T cells..." However, I think the underlying argument/conclusion is the same.*
Done.
- It is not completely clear to me what is being plotted in Figures 2D, 4B, and S1. Where do each of the points come from? Why do there appear to be sets of 4 points when there are more experimental data points in 2C?*
Thank you for the comment.
We have edited the figures and the captions to address the comment.
- What were the values of $\Delta_R$ and $\Delta_H$? (Or, alternatively, how many bins were chosen?) *
We have shown the ΔH and ΔR values in Figures S10-11 in the supplementary material.
7. It would be useful to define $\mu$ and $\sigma$ in the main text before they are introduced in Table 1.
Done.
*Reviewer #1 (Significance (Required)):
The paper addresses an important and timely problem, given the strong interest in designing CAR-T cells for cancer therapy. This paper adds to existing computational approaches (clearly summarized in the intro) by introducing a multiscale framework that includes cellular-level properties - like CAR binding affinities, etc. - with a population model that is important for capturing collective behavior of many cells. It is parameterized by experimental data and provides a framework for optimizing cells to maximize target cell killing while minimizing off-target killing of healthy cells. This will be of interest to computational groups in the field, can be extended to incorporate additional biology and/or data, and has the potential to provide useful guidance to experimental design of CAR-T cells. It could be highly impactful if combined with experiments in the future.*
We appreciate the positive comment.
Reviewer #2 (Evidence, reproducibility and clarity (Required)): * Summary :
In this study, Rajakaruna et al. propose a mathematical modeling framework called PASCAR to simulate the response of T cells engineered to express chimeric antigen receptors (CAR) against the oncogenic marker HER2 on target cells. The authors propose that the degree of T cell activation is given by a simple CAR occupancy model in the presence or absence of additional kinetic proofreading steps. A population-level ODE model is then used to describe proliferation and death of both target cells and T cells on longer time-scales as a function of the degree of T cell activation.
The model results are compared with recent experiments by Fernandez-Lopez et al. 2021 (ref. 6). showing that T cells respond to HER2 abundance on target cells in an ultrasensitive manner when using a circuit where a low-affinity synthetic Notch receptor (synNotch) for HER2 controls the expression of a high-affinity CAR for HER2. With this synNotch-CAR circuit, T cells are able to kill tumor cells with high HER2 abundance while sparing healthy cells with 100 fold less HER2.
The authors first fit model parameters in the situation where T cells constitutively express CARs of either low (Kd=210nM) or high (Kd=17.6nM) affinity and suggest that 7 kinetic proofreading steps are needed to account for the experimental data. For the situation where T cells are endowed with the synNotch-CAR circuit, the authors implicitly account for ultrasensitivity by assuming that CAR abundance is proportionnal to a Hill function of HER2 abundance on target cells. Using this asumption, they fit model parameters to experimental data. The authors use the model to predict the response (%lysis in target cells) for different initial numbers of T cells not used in the fitting procedure and conclude that the PASCAR model can generalize well to unseen situations.
The authors finally perform pareto optimization to investigate how optimization of lysis of tumor cell with high HER2 abundance and sparing of healthy cells with low HER2 can be performed simultaneously. They conclude by suggesting parameters values of the synNotch-CAR circuit optimizing the discrimination between healthy and tumor cells. * Major comments :
1(A) - In Figure 2A, the error bars are not properly drawn : the whiskers are not horizontal, not aligned and seem to have been placed manually. Some points and error bars are found outside plot limits. This is intriguing and suggests that this figure was edited manually. Error bars do not seem to agree with the original experimental data.
Thank you for pointing this out. We have modified Figure 2A. The extracted experimental data from Hernandez-Lopez et al.6 and the corresponding error bars are also provided in in an excel data file ”Error_bars_%lysis_&Predictions” available at the GitHub link.
*(B) The lines corresponding to the model results should be drawn using many more points(as compared to experimental results) to better illustrate the model behavior over the range of HER2 abundance values represented. Here, the representation of the model result is misleading (it suggests a linear increase of the %lysis between the 10^3 and 10^5 HER2 molecules/cell). *
Done. Reviewer 1 also pointed to this in Major comment #1B. We have modified Figures 2A-D,G and Figures 4A,D,F to address this. Please refer to our response to Reviewer #1 for details.
(C)The number of target and CAR T cells should be modified to correspond to those used in the original experiment (100000 target cells and 15000 CAR T cells for the model versus 20000 target cells and 10000 CAR T cells in the experiments).
The numbers (20000 of target cells and 10000 CAR T cells) we used in our model are taken from Hernandez-Lopez (see figure caption of Fig. 2 (page 2) in Hernandez-Lopez et al.). In addition, we reached out to Dr. Hernandez-Lopez and Dr. Wendell Lim to confirm the numbers of target cells and CAR T cells used in the experiments.
2 - An error is found in the expression of CN in the KP model. Indeed, Kd_tilde should be equal to Kd. Given that the authors do not provide the details of their calculation, it is not clear where the error comes from. A potential source of error could be the absence of the dissociation reaction of the CN complex in Fig.1 (see minor comments). The authors should correct the error and re-run the model with the correct expression for CN.
Thank you for raising this point.
The expressions shown in Eqs. 1 and 2 in our original manuscript is correct, however, it can be further simplified to get an expression where Kd_tilde is equal to K_d. We have included a detailed derivation of the equations in the supplementary material (Supplementary Text 1).
3(A) - The conversion scheme used to convert the association rate k_on (and also of the dissociation Kd) from units 1/(nM . s) to units 1/(molecules per cell . s) is not appropriate. Indeed, association rates depend on the diffusion of molecules which greatly differs between soluble (SPR measurements) and membrane-bound molecules. These different diffusion properties should be taken into account for the conversion.
We thank the reviewer for raising this point.
We have modified the main text (page 7) and added additional calculations (Supplementary Text 2) and a figure (Figure S1) in the supplementary material to address the comment. Briefly, we evaluated the role of diffusion in modifying the binding (k_on) and unbinding (k_off) rates following the approach developed by Eigen, Bell, Keizer, and others and found that for the rates used in Hernandez-Lopez et al, the changes in the rates are less than 20%, which does not lead to appreciable changes in in CN (Fig. S1). Therefore, including the effect of diffusion will affect the percentage lysis negligibly in this case.
*(B) Moreover, the conversion formula was found to give a Kd of 3.2 molecules/cell for the high affinity CARs and of 39 molecules/cell for the low affinity CARs. This information is important to interpret the results and should appear in the main text. As such, these Kd estimates are far below the typical number of CARs on T cells (10^3) and of HER2 ligands (from 10^3 to 10^6) on target cells. In this situation, the number of HER2:CAR complexes is entirely determined by the limiting component (HER2 or CAR) and does not depend on Kd (as shown in Fig.2B). Estimates of Kd in the 10^3 molecules/cell range would produce T cell responses that depend on Kd and potentially provide a good agreement between the NKP model and the experimental results shown in Fig.2A. The authors should therefore re-evaluate the performances of the NKP model. *
We agree with the reviewer regarding the above comment.
We have moved the conversion of K_D to the unit of molecules/cell. As we point out in our response to the previous comment, including the effect of diffusion in the reactions does not change the K_d appreciably and therefore, the NKP model would be unable to fit the results (% Lysis) shown in Fig 2A.
4(A) - KP model : The authors make a confusion about the performance of the KP model when stating : "The estimated value of the phosphorylation rate, kp (≈ 0.007 s -1 ) is larger than the ligand unbinding rate koff (≈ 10^-4 s^-1 ) indicating that the kinetic proofreading scheme is active in separating CAR-T cell responses across high and low affinity CARs". KP ligand discrimination is efficient when kp is much smaller than koff which is not the case here. To compensate for this inefficient discrimination, a large number N of proofreading steps is needed.
Thank you for the comment.
We have edited the sentence to address the comment (bottom of page 9 in the main text).
(B) The rate kp=7e-3 s^-1 sets a time-scale 1/kp = 2.5 min. The typical time scale for activation would then be N/kp = 17.5min which is much larger than the time-scale at which the KP mechanism operates during normal TCR signaling following pMHC-TCR engagement. Indeed, during TCR signaling, KP operates within a few tens of seconds as recently illustrated in a study by Mc Affee et al. (https://doi.org/10.1038/s41467-022-35093-9*) showing that LAT condensates appear typically 20 to 30 seconds following TCR engagement. *
Thank you for the comment and the reference.
We have edited the discussion to incorporate the above comment (last paragraph in page 12 in the main text).
5 - The authors should modify Fig.2D to produce a separate graph for each variable ("%lysis", "mean" and "var"). Indeed, differences are potentially hidden by plotting variables with different scales on the same graph. For the comparison of the % lysis between data and model, it would be helpful to have colors and shapes as in Fig.2A and Fig.2C. The authors should also represent the experimental and theoretical distributions of CAR molecules / T cell for the different experimental conditions (different abundance of HER2/target cell).
Done.
We have included Figures 2E and 4C in the main text to show comparisons between the means and variances.
6 - The "Cost" function in the methods section seems to be defined for only one experimental condition (corresponding to a given HER2 abundance). Please indicate that it is the sum over all experimental conditions that is minimized. Author show in Fig.2A the variable (%lysis) used in the cost function. Importantly, the other variables (mean and variance of CAR abundance at day 3) should also be plotted to help the reader appreciate the agreement between model and data.
Done.
We have edited the equation in page 15 in the main text to reflect the sum in the cost function.
We have included figures (Figs. 2F, 2H, 4B) in the main text and the supplementary material (Fig. S2A ) in the supplementary material quantifying comparisons between the data and our model.
7 - The author should quantify the goodness of the fit and analyze the sensitivity of the model results (the "Cost" function) with respect to parameter values. An investigation of the sensitivity of the model output as of function of all pairs of parameters would certainly highlight the fact that the estimates of parameters kp and N are correlated.
Done.
We have calculated correlations between the estimated parameters to address this. The results are shown in the main text (pages 10 and 17) and in Fig. S5 in the supplementary material.
8 - To model the ultrasensitive synNotch-CAR circuit, the authors assume that CAR expression is a Hill function of HER2 abundance on target cells. The parameters of this Hill function are estimated by fitting both the % lysis and CAR expression at day 3. The authors should evaluate the agreement between model results and experimental values by plotting CAR expression at day 3 (using CAR expression data from Supplementary Figure 1C in ref.6).
Done.
We have included the comparisons in Figure S12 in the supplementary material and mentioned those in the figure legend for Fig. 4 in the main text.
9 - In Figure 4C, for 12000 and 15000 T cells, experimental results show a non-ultrasensitive response (also Supp.Fig.S4E in ref 6) which does not agree well with the model results. Hence, the authors claim that the agreement is good does not seem to be supported. The model should also be tested using experimental data where synNotch and CAR receptors with different affinities are used (in particular Supp.Fig.S4D in ref.6 where a Hill coefficent of 0.6 is estimated for the med-low circuit). It will also be of interest to show that the model can reproduce results from Supp.Fig.S5A in ref.6 where cells with high and low CAR expression are used.
Thank you for the comment.
We have calculated the goodness of the fit R2 for our predictions of Fig. S4E in ref. 6 and our R2 = 0.97 suggest excellent agreement with the data. However, we agree that the data for E:T= 0.75 or E:T=0.6 in Fig. S4E in ref. 6 can be interpreted as a gradual increase, however, additional experiments at HER2 abundances 104 molecules/cell probably would be able to help distinguish a ultrasensitive response vs a gradual response at these E:T ratios.
We have tested model predictions for synNotch CAR T cells for higher affinity CAR (Fig. S4D, top panel, in ref. 6) which shows excellent agreement (Fig. 4F in our revised manuscript). We were unable to generate any prediction for the med-low synNotch circuit (Fig. S4D, bottom panel, in ref. 6) as the CAR expressions for the med-low synNotch circuit are not available in the manuscript. However, we have tested new model predictions (Figs. 2G-H) for constitutive CAR T cells (Fig. S5A in ref. 6) for high and low CAR expressions at different E:T ratios. The agreement between the data and the predictions is reasonable (R2 = 0.90) . Therefore, we believe we have confronted our model with responses generated by several types of CAR T cells and the excellent to reasonable agreements of the PASCAR model with the data provide confidence in the utility of our framework to investigate CAR T cell responses in vitro.
Minor comments :
*Figure 1 : left : The schematic of the CAR receptor is inaccurate. CD3z domains should be shown within the intra-cytoplasmic part of the receptor, and not as separate proteins. In addition to the CD3z domain, the 41BB domain should also be represented (see ref 6 by Fernadez-Lopez at al.). The arrow correspond to the dissociation of the complex C_N is missing. Without this reaction in the KP model, the steady state solution leads to C_i = 0 for i in [0, N-1]. All receptor-ligand complexes eventually reach and stay in the C_N state. *
We thank the reviewer for catching this.
We have made changes in the schematic figure to include the changes suggested above.
middle: In the schematic, add labels "lysis of target cell" and "proliferation" next to the corresponding parameters. The arrows should point from the label ("cancer cell" and "CAR-T cell") to the cell not to the other way around.
Done.
Right : this schematic is not useful and should either be removed or completed to provide useful information to the reader.
Done.
*Figure 2 : A - A reference to the article with the original data should be added in the legend. In line with the original article, "conv." should be replaced by "const." as an abbreviation for "constitutive". B and E - Please use a log scale for the y-axis. Have the authors represented an average of C0 and CN across the population at day 3? If so, that information should appear in the figure legend. *
Done.
Figure 3. To help the reader interpret these graphs, the authors should also show T_R(t) and U_H(t) on separate graphs. It would also be useful to show C_N as a function of R for H=10^6.2 both for high and low affinity CAR.
Done.
Figure 4. A - the number of target cells and CAR T cells do not correspond to those used in the original experiment (see major comment 1).
Done. Please check our response to comment #1(B) for Reviewer #2.
*B - Same comments as for Fig.2D. The legend appears to be incorrect ("% lysis" should be blue open circle and orange open squares). *
Done.
*C - Use more points to plot the model results. *
These figures have all the points plotted. However, some points are overlapping with some other.
Reviewer #2 (Significance (Required)):
The modeling framework is minimal but appropriate to describe CAR T cell activation and subsequent proliferation and lysis of target cells. The advantage of the simplicity of the model formulation is to allow a direct interpretation of the impact of the different parameters on the model output.
Thank you for the positive remark.
*However, the authors seldom discuss how the behavior of the model is controlled by the parameters and their values. Accordingly, the analysis of the theoretical results needs to be further developed. The authors should also quantify the goodness of fit and analyze the sensitivity of model results to parameter values. This will allow to evaluate how the experimental data constrain model parameters and to compare the performances of the different models. *
We have provided further explanation for some of the results obtain using our model (please refer to responses to comments # 1A, 3A, and 2B) for Reviewer 1), added a correlation analysis for the estimated parameters (Fig. S5 in the supplementary material), and included goodness of the fit (R2 values) for the fits and the model predictions. We believe these new results address the reviewers’ comments.
The authors should also assess the biological significance of their results by confronting their parameter estimates to related parameter estimates used in other models of T cell activation. The model should further be tested in other situations with different receptor affinities and cell numbers.
Thank you for the comment.
We have now tested new predictions for a highest affinity synN-CAR (Figure 4F) and for increasing and decreasing CAR abundances at different E:T ratios (Figure 2G-H). There are few models of CAR T cells (e.g., Rohrs et al. iScience, 2020) which use more detailed signaling models. Therefore, it will be difficult to compare the estimated values of parameters in our model and with those models. The time scales of signaling can also depend on the specifics of the CAR construct. Therefore, though it will be useful to compare different models and their parameter values developed so far, we believe this is outside the scope of this manuscript. We have included some potential directions for extending our current framework in the Discussion section (pages 12-14). If the editor and the reviewer strongly feel the need for including this in the current manuscript, we can do that.
This research should be of interest to readers specialized in the field of mathematical modeling of biological systems and in CAR-T cell immunotherapies.
Thank you for the positive comment.
*Fields of expertise of the reviewer : biophysics, mathematical modeling of biological systems, molecular mechanisms of T cell signaling and activation. *
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Referee #2
Evidence, reproducibility and clarity
Summary:
In this study, Rajakaruna et al. propose a mathematical modeling framework called PASCAR to simulate the response of T cells engineered to express chimeric antigen receptors (CAR) against the oncogenic marker HER2 on target cells. The authors propose that the degree of T cell activation is given by a simple CAR occupancy model in the presence or absence of additional kinetic proofreading steps. A population-level ODE model is then used to describe proliferation and death of both target cells and T cells on longer time-scales as a function of the degree of T cell activation.
The model results are compared with recent experiments by Fernandez-Lopez et al. 2021 (ref. 6). showing that T cells respond to HER2 abundance on target cells in an ultrasensitive manner when using a circuit where a low-affinity synthetic Notch receptor (synNotch) for HER2 controls the expression of a high-affinity CAR for HER2. With this synNotch-CAR circuit, T cells are able to kill tumor cells with high HER2 abundance while sparing healthy cells with 100 fold less HER2.
The authors first fit model parameters in the situation where T cells constitutively express CARs of either low (Kd=210nM) or high (Kd=17.6nM) affinity and suggest that 7 kinetic proofreading steps are needed to account for the experimental data. For the situation where T cells are endowed with the synNotch-CAR circuit, the authors implicitly account for ultrasensitivity by assuming that CAR abundance is proportionnal to a Hill function of HER2 abundance on target cells. Using this asumption, they fit model parameters to experimental data. The authors use the model to predict the response (%lysis in target cells) for different initial numbers of T cells not used in the fitting procedure and conclude that the PASCAR model can generalize well to unseen situations.
The authors finally perform pareto optimization to investigate how optimization of lysis of tumor cell with high HER2 abundance and sparing of healthy cells with low HER2 can be performed simultaneously. They conclude by suggesting parameters values of the synNotch-CAR circuit optimizing the discrimination between healthy and tumor cells.
Major comments:
- In Figure 2A, the error bars are not properly drawn : the whiskers are not horizontal, not aligned and seem to have been placed manually. Some points and error bars are found outside plot limits. This is intriguing and suggests that this figure was edited manually. Error bars do not seem to agree with the original experimental data. The lines corresponding to the model results should be drawn using many more points(as compared to experimental results) to better illustrate the model behavior over the range of HER2 abundance values represented. Here, the representation of the model result is misleading (it suggests a linear increase of the %lysis between the 10^3 and 10^5 HER2 molecules/cell). The number of target and CAR T cells should be modified to correspond to those used in the original experiment (100000 target cells and 15000 CAR T cells for the model versus 20000 target cells and 10000 CAR T cells in the experiments).
- An error is found in the expression of CN in the KP model. Indeed, Kd_tilde should be equal to Kd. Given that the authors do not provide the details of their calculation, it is not clear where the error comes from. A potential source of error could be the absence of the dissociation reaction of the CN complex in Fig.1 (see minor comments). The authors should correct the error and re-run the model with the correct expression for CN.
- The conversion scheme used to convert the association rate k_on (and also of the dissociation Kd) from units 1/(nM . s) to units 1/(molecules per cell . s) is not appropriate. Indeed, association rates depend on the diffusion of molecules which greatly differs between soluble (SPR measurements) and membrane-bound molecules. These different diffusion properties should be taken into account for the conversion.
Moreover, the conversion formula was found to give a Kd of 3.2 molecules/cell for the high affinity CARs and of 39 molecules/cell for the low affinity CARs. This information is important to interpret the results and should appear in the main text. As such, these Kd estimates are far below the typical number of CARs on T cells (10^3) and of HER2 ligands (from 10^3 to 10^6) on target cells. In this situation, the number of HER2:CAR complexes is entirely determined by the limiting component (HER2 or CAR) and does not depend on Kd (as shown in Fig.2B). Estimates of Kd in the 10^3 molecules/cell range would produce T cell responses that depend on Kd and potentially provide a good agreement between the NKP model and the experimental results shown in Fig.2A. The authors should therefore re-evaluate the performances of the NKP model. 4. KP model : The authors make a confusion about the performance of the KP model when stating : "The estimated value of the phosphorylation rate, kp (≈ 0.007 s -1 ) is larger than the ligand unbinding rate koff (≈ 10^-4 s^-1 ) indicating that the kinetic proofreading scheme is active in separating CAR-T cell responses across high and low affinity CARs". KP ligand discrimination is efficient when kp is much smaller than koff which is not the case here. To compensate for this inefficient discrimination, a large number N of proofreading steps is needed.
The rate kp=7e-3 s^-1 sets a time-scale 1/kp = 2.5 min. The typical time scale for activation would then be N/kp = 17.5min which is much larger than the time-scale at which the KP mechanism operates during normal TCR signaling following pMHC-TCR engagement. Indeed, during TCR signaling, KP operates within a few tens of seconds as recently illustrated in a study by Mc Affee et al. (https://doi.org/10.1038/s41467-022-35093-9) showing that LAT condensates appear typically 20 to 30 seconds following TCR engagement. 5. The authors should modify Fig.2D to produce a separate graph for each variable ("%lysis", "mean" and "var"). Indeed, differences are potentially hidden by plotting variables with different scales on the same graph. For the comparison of the % lysis between data and model, it would be helpful to have colors and shapes as in Fig.2A and Fig.2C. The authors should also represent the experimental and theoretical distributions of CAR molecules / T cell for the different experimental conditions (different abundance of HER2/target cell). 6. The "Cost" function in the methods section seems to be defined for only one experimental condition (corresponding to a given HER2 abundance). Please indicate that it is the sum over all experimental conditions that is minimized. Author show in Fig.2A the variable (%lysis) used in the cost function. Importantly, the other variables (mean and variance of CAR abundance at day 3) should also be plotted to help the reader appreciate the agreement between model and data. 7. The author should quantify the goodness of the fit and analyze the sensitivity of the model results (the "Cost" function) with respect to parameter values. An investigation of the sensitivity of the model output as of function of all pairs of parameters would certainly highlight the fact that the estimates of parameters kp and N are correlated. 8. To model the ultrasensitive synNotch-CAR circuit, the authors assume that CAR expression is a Hill function of HER2 abundance on target cells. The parameters of this Hill function are estimated by fitting both the % lysis and CAR expression at day 3. The authors should evaluate the agreement between model results and experimental values by plotting CAR expression at day 3 (using CAR expression data from Supplementary Figure 1C in ref.6). 9. In Figure 4C, for 12000 and 15000 T cells, experimental results show a non-ultrasensitive response (also Supp.Fig.S4E in ref 6) which does not agree well with the model results. Hence, the authors claim that the agreement is good does not seem to be supported. The model should also be tested using experimental data where synNotch and CAR receptors with different affinities are used (in particular Supp.Fig.S4D in ref.6 where a Hill coefficent of 0.6 is estimated for the med-low circuit). It will also be of interest to show that the model can reproduce results from Supp.Fig.S5A in ref.6 where cells with high and low CAR expression are used.
Minor comments:
Figure 1 : left : The schematic of the CAR receptor is inaccurate. CD3z domains should be shown within the intra-cytoplasmic part of the receptor, and not as separate proteins. In addition to the CD3z domain, the 41BB domain should also be represented (see ref 6 by Fernadez-Lopez at al.). The arrow correspond to the dissociation of the complex C_N is missing. Without this reaction in the KP model, the steady state solution leads to C_i = 0 for i in [0, N-1]. All receptor-ligand complexes eventually reach and stay in the C_N state.
middle: In the schematic, add labels "lysis of target cell" and "proliferation" next to the corresponding parameters. The arrows should point from the label ("cancer cell" and "CAR-T cell") to the cell not to the other way around.
Right : this schematic is not useful and should either be removed or completed to provide useful information to the reader.
Figure 2 : A - A reference to the article with the original data should be added in the legend. In line with the original article, "conv." should be replaced by "const." as an abbreviation for "constitutive". B and E - Please use a log scale for the y-axis. Have the authors represented an average of C0 and CN across the population at day 3? If so, that information should appear in the figure legend.
Figure 3. To help the reader interpret these graphs, the authors should also show T_R(t) and U_H(t) on separate graphs. It would also be useful to show C_N as a function of R for H=10^6.2 both for high and low affinity CAR.
Figure 4. A - the number of target cells and CAR T cells do not correspond to those used in the original experiment (see major comment 1). B - Same comments as for Fig.2D. The legend appears to be incorrect ("% lysis" should be blue open circle and orange open squares). C - Use more points to plot the model results.
Significance
The modeling framework is minimal but appropriate to describe CAR T cell activation and subsequent proliferation and lysis of target cells. The advantage of the simplicity of the model formulation is to allow a direct interpretation of the impact of the different parameters on the model output. However, the authors seldom discuss how the behavior of the model is controlled by the parameters and their values. Accordingly, the analysis of the theoretical results needs to be further developed. The authors should also quantify the goodness of fit and analyze the sensitivity of model results to parameter values. This will allow to evaluate how the experimental data constrain model parameters and to compare the performances of the different models. The authors should also assess the biological significance of their results by confronting their parameter estimates to related parameter estimates used in other models of T cell activation. The model should further be tested in other situations with different receptor affinities and cell numbers.
This research should be of interest to readers specialized in the field of mathematical modeling of biological systems and in CAR-T cell immunotherapies.
Fields of expertise of the reviewer: biophysics, mathematical modeling of biological systems, molecular mechanisms of T cell signaling and activation.
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Referee #1
Evidence, reproducibility and clarity
Summary: The paper by Rajakaruna, Desai, and Das develops a multiscale computational model (PASCAR) to study design of features of CAR-T cells. Their ODE-based model captures cell-cell interactions using equilibrium receptor-ligand binding relations and a simplified representation of intracellular signaling. The cellular-scale model feeds into a population model including populations of CAR-T cells, healthy cells, and target cells. The model accounts for CAR-T cells with varying numbers of CARs; it accounts for target/healthy cells with varying numbers of ligands. The authors use published cytometry and cytotoxicity data to parameterize the model, which they show captures experimental trends well when they use a kinetic proofreading model to phenomenologically represent intracellular signaling. They then use an optimization approach to characterize features of the CAR-T cell design space that maximize killing of target cells while minimizing the destruction of healthy cells. Their conclusions are consistent with physical intuition and provide quantitative and generalizable predictions about biophysical parameters (including equilibrium binding constants, kinetic rates, etc.).
Major comments:
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In general, the paper is logically laid out and easy to follow. However, some of the underlying mechanisms were not clear to me:
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In Figure 3A, it is not clear why the rate of lysis is greater for populations with an intermediate range of CAR abundances. I understand the authors' statement that "this is because the smaller number of CAR-T cells present in [higher or lower CAR expression groups]..." However, it is not clear why intermediate-level CAR-T cell populations are largest, noting that populations with higher receptor levels have larger proliferation rates. Is this simply reflecting the initial size of the populations, or is another mechanism at play? I think the paper would benefit from discussion/quantification of this.
- In Figure 2, C_N plateaus at HER2 density between 10^3 and 10^4. However, % lysis does not plateau until a density closer to 10^5. What is the underlying mechanism? I think the paper would benefit from its exploration.
- It is likely that CAR-T cells would encounter various ratios of target and healthy cells depending on patient, microenvironment, in vitro experimental design, etc. My understanding is that the optimization was done with equal numbers of healthy and target cells. It would be useful to explore how sensitive the optimization is to the ratio of target and healthy cells. This could provide useful design guidance to experimentalists.
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Two assumptions of the population model initially surprised me. However, given the strong performance of the model, they seem to be well justified. Could the authors address the following with brief discussion?
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The model essentially assumes a well-mixed population of cells, treating lysis and proliferation as second-order "reactions." However, individual cells likely encounter relatively few cells on the time scale of simulations.
- The model doesn't include "mixing" of CAR-T cell populations upon proliferation (i.e., a cell with R receptors can't divide and result in cell with a different number of receptors). Is this justified by the biology?
Minor comments
- A couple of figures appear to be mis-referenced in the paper: Figure 2D (end of paragraph, page 7) should presumably be Figure 2E, and Figure S3 should be S2 (end of page 7).
- I don't know what "conv." stands for in the figures (I couldn't find the abbreviation in the captions or main text).
- Last pargraph of page 9: "However, decreasing K_D further starts decreasing lysis..." Given the previous sentences, this should presumably say "...increasing K_D further..."
- I was initially confused by the second sentence of the last paragraph of Results. Based on the previous paragraph, I expected the sentence to read "when K_D increased" (not decreased) because of the statement "similar to constitutive CAR-T cells..." However, I think the underlying argument/conclusion is the same.
- It is not completely clear to me what is being plotted in Figures 2D, 4B, and S1. Where do each of the points come from? Why do there appear to be sets of 4 points when there are more experimental data points in 2C?
- What were the values of $\Delta_R$ and $\Delta_H$? (Or, alternatively, how many bins were chosen?)
- It would be useful to define $\mu$ and $\sigma$ in the main text before they are introduced in Table 1.
Significance
The paper addresses an important and timely problem, given the strong interest in designing CAR-T cells for cancer therapy. This paper adds to existing computational approaches (clearly summarized in the intro) by introducing a multiscale framework that includes cellular-level properties - like CAR binding affinities, etc. - with a population model that is important for capturing collective behavior of many cells. It is parameterized by experimental data and provides a framework for optimizing cells to maximize target cell killing while minimizing off-target killing of healthy cells. This will be of interest to computational groups in the field, can be extended to incorporate additional biology and/or data, and has the potential to provide useful guidance to experimental design of CAR-T cells. It could be highly impactful if combined with experiments in the future.
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Reply to the reviewers
We would like to thank all reviewers for their time and effort invested into reviewing our manuscript.
Please find our responses to your comments, criticisms and suggestions below in blue.
__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __
Summary:
The manuscript by Vishwanatha et al. presents findings on the fission yeast transcription factor Cbf11, which is involved in regulating lipid synthesis. Changes in lipid metabolism often have detrimental effects on nuclear division (evidenced by the high percentage of cut phenotypes among strains with altered lipid content). Here the authors show that cbf11 deletion strains produce additional phenotypes such as changes to cohesion dynamics and altered chromatin modification within centromeric regions, in turn perhaps affecting microtubule attachment and proper chromosome distributions. This hypothesis is supported by the authors' finding of epistatic effects between cbf11 and cohesin loading and unloading.
Major comments:
While the evidence presented supports the hypothesis of altered cohesin loading as a major driver of observed mitotic defects, changes in the NE surface area are likely to also contribute to the phenotypes even in pre-anaphase stages.
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This is an interesting notion. We are only aware of NE overproduction and nuclear “flares” observed upon the Lipin phosphatase dysregulation (PMID 23873576).
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However, in our case we rather expect NE membrane shortage, not overproduction. Accordingly, we do see that the nuclear cross section area (thus likely also NE surface area) is smaller in cbf11KO compared to WT (see boxplots below). Is this what you are referring to? We are not sure how this would affect the pre-anaphase stages of mitosis.
Did the authors test any double deletions with regulators involved in decreasing lipid content (e.g. spo7, nem1, ned1) to counteract the role of Cbf11? This could be useful in assessing the relative contribution of cohesion dynamics and histone modifications.
- We previously published (PMID: 27687771) that cut6/ACC overexpression can indeed partially suppress the cut phenotype in the cbf11KO background. So lipid metabolism does play a role and does contribute to mitotic fidelity. In the current manuscript, we are showing that other factors contribute as well and that defects arise already prior to anaphase, which is not consistent with the simple notion of shortage of membrane building blocks during anaphase. We appreciate your suggestion on testing the relative contributions of these various factors to mitotic fidelity, but we have not tested any of the suggested double mutants.
A possible role of physical constraints dictated by the NE was already mentioned by the authors in the context of spindle bending and decreased elongation rates and some preliminary experimental data on this would be appreciated. Generation of strains, acquisition of some timelapses, and quantification of spindle elongation rate/buckling frequency should be feasible in a reasonable time frame.
- Assaying spindle parameters in Lipin-related mutants would indeed be interesting, but again, these are anaphase phenotypes. We are not sure how this is relevant for the pre-anaphase findings we report? Also, we unfortunately no longer have the personnel and capacity to carry out the suggested experiments.
The authors report mRNA levels of the centromere flanking genes per1 and sdh1 to be increased by 1.5x and decreased by 2x in comparison to WT. Could the authors elaborate on whether this is an expected trend? Kaufmann et al., 2010 reported low transcription of per1 when the surrounding regions are predominantly acetylated. Fig. 4A suggests a slight increase of H3K9ac at per1 and a decrease of transcription would be conceivable.
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We do not have any particular expectations regarding the expression levels of per1 and sdh1 in our system. We simply note that their expression changes in cbf11KO (in different directions) and this is accompanied by changes in H3K9 acetylation patterns.
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The increased histone acetylation at the per1 locus that you mention (Kaufmann et al., 2010) was only shown for H4K12ac, while we measured H3K9ac (these marks are deposited by different enzymes). The authors actually report that “The levels of histone H3 at per1 did not change significantly between the two growth conditions and strains”, so we do not think that paper is relevant for our study.
Fig. 3B indicates a catastrophic mitosis percentage of roughly 9.5% in cbf11∆ while in Fig. 1C 4% of all cells, or ˜31% of all mitotic events, is noted as abnormal. Could the authors clarify this discrepancy? Since Fig. 1 utilises time course data of 333 cells (please specify the number of analysed cells also in the legend), would the authors expect this data to be more trustworthy when compared to images of fixed cells? What were the criteria to assign divisions as catastrophic in fixed cells and which features were utilised to identify the 400 cells as mitotic?
- We typically do see higher proportions of cut cells in fixed samples than in live-cell imaging. We believe this has to do with the different fluorescence readouts for live vs fixed cells. We have added the following explanations to the methods:
“Please note that the observed frequencies of mitotic defects are not directly comparable between live and fixed cells. Following catastrophic mitosis, the dead cells rapidly lose histone-GFP fluorescence (imaging of live cells), but their DNA can still be visualized with DAPI for a much longer period (imaging of fixed cells), resulting in higher apparent defect frequencies in fixed cells.”
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Importantly, we always compared cbf11KO to WT grown and processed under the same conditions, and that is how we determined the significance of any defects.
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Mitotic defects were classified based on nuclear morphology both in live cells (histone signal) and in fixed cells (DAPI): Cells having the cut phenotype, or mis-segregated nucleus = 2 nuclei of different sizes, or septated cells with only one daughter cell having a nucleus, respectively.
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We have analyzed images of at least 400 cells *in total* from asynchronous populations (interphase + mitotic >= 400). We have modified the figure legend to make this fact more clear. In our experience, this is the standard way of reporting the frequency of mitotic defects in asynchronous yeast cell populations.
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We have specified the number of cells analyzed in Fig. 1C.
Minor comments:
Previous literature is, to the best of our knowledge, sufficiently referenced. The text is largely clear (some exceptions within the methods section will be elaborated on below). The figures, however, would benefit from graph titles and some minor formatting changes.
- Figures:
o Fig. 1: Specify the number of cells analysed in C within the legend as well. For B, please use colourblind-friendly schemes - especially since images are shown as merges only. The example of the "cut" phenotype appears small and crowded by surrounding cells. Especially the latter might affect mitotic fidelity. Under the assumption that this did not affect quantifications (WT seem fine) a less crowded cell would present a nicer example.
- We have changed Fig. 1 as requested.
o Fig. 3: Images shown in A add little benefit in their current form. What is the takeaway for the reader?
- We hope that the reader gets concrete information on cellular and nuclear morphology of the investigated strains, which would be otherwise difficult to reproduce by textual description.
Indicating that images represent DAPI staining and pointing out cells of interest with arrows/symbols would be helpful.
- Done.
The example shown for cbf11 appears to be dimmer in comparison and cell morphology is hard to interpret.
- The cbf11KO cells stain fainter with DAPI than cells of other strains. We do not know why. To increase the clarity of the image, we have now adjusted the brightness and contrast of the cbf11KO panel (and indicated this adjustment in the figure legend).
C feels misplaced in this figure and a title could improve readability.
- We have added a title and moved the panel to Fig. 4 (4D).
o Fig. 4: Graph titles needed, figure might work better in portrait
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We have added the required graph titles.
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We have recreated all ChIP-seq related figures to incorporate new data and to (hopefully) better highlight the differences between genotypes.
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Text:
o Mention median duration of mitosis in cbf11∆ (Fig. 2E) in text since WT is already noted;
- Done.
o Discussion, third paragraph: "TBZ [REF] and are prone to chromosome loss [...]". I assume this referred to minichromosome loss or have changes in ploidy/chromosome segregation been quantified?
- Changes in ploidy were indeed not quantified. We have changed the wording to “__mini__chromosome loss”. But please note that the Ch16 minichromosome is derived from regular Chromosome III and is a real chromosome, albeit a small one.
o Methods, Microscopy and image analysis:
How were fixed cells imaged (glass bottom dishes, plated on lectin, mounted on slides)?
Specify the CellR as widefield and provide details of the objective used (immersion and NA)
- We have added the following information to the relevant Methods section:
“Cells were applied on glass slides coated with soybean lectin, covered with a glass cover slip, and imaged using the 60X objective of the Olympus CellR widefield microscope with oil immersion (NA 1.4)”
Elaborate on "manual evaluation of microscopic images"
- We have extended the description of cell scoring:
“The frequency of catastrophic mitosis occurrence was determined by manual evaluation of microscopic images using the counter function of ImageJ software, version 1.52p (Schneider et al., 2012). At least 400 cells from the asynchronous populations were analyzed per sample and mitotic defects were scored based on nuclear morphology and septum presence/position. ”
For live cell microscopy, what was the estimated final density of cells within the 5 µl resuspension?
- Our estimate is 4-8 x 10^6 cells in 5 ul. We have added this information into the Methods.
What is meant by measuring the maximum section of plotted profiles? Is this the maximum distance of Hht1 signals within the entire time-lapse?
- We have changed the description:
“The nuclear distance was measured by using Hht2–GFP signals and converting the green channel images to binary, measuring the maximum distance between the Hht2-GFP signals using plot profile function in imageJ.”
Was spindle length quantified the same way?
- We have added the description:
“Spindle length was quantified by drawing a line along the length of the spindle (using mCherry-Atb2 signals) at each timepoint and measuring the length of the line using imageJ.”
Methods, ChIP-qPCR:
It is not clear which strains were used, this can only be guessed by the use of a GFP antibody suggesting GFP tagged chromatin to be precipitated. For people with expertise outside of ChIP assays, this should be specified
- We have listed the used strains in the ChIP-qPCR methods section.
Reviewer #1 (Significance (Required)):
Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
This manuscript presents a novel role for a transcription factor, one typically implicated in lipid metabolism, in chromatin modification and cohesin dynamics, with the possibility of this representing a more conserved process across ascomycetes. The mechanism of cbf11 regulation remains to be determined.
Place the work in the context of the existing literature (provide references, where appropriate).
This work helps link two bodies of work related to cell division that are usually considered in isolation, the regulation of lipid dynamics and the control of chromatin dynamics and cohesion. Some comparisons to phenotypes in closely related species would have helped provide a broader context (such as Yam et al., 2011, where the spindle morphologies in S. japonicus and response to cerulenin treatment might be of relevance to the work presented here).
- We now briefly discuss the semi-open mitosis of Sch. japonicus and the Yam et al. 2011 paper at the beginning of the Discussion.
State what audience might be interested in and influenced by the reported findings.
Molecular and cellular biologists with interests in nuclear remodelling, lipid metabolism, kinetochore assembly.
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.
Fission yeast biology, nuclear remodelling, microscopy. We are not qualified to make in-depth comments on the soundness of ChIP-Seq and ChIP-qPCR experiments.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
This manuscript describes detailed mechanisms by which the cbf11 deletion showed the phenotype. They found that the cbf11 deletion altered pericentromeric chromatin states such as the level of cohesin and hypermethylation.
In general, their results are interesting and provide important insights into the relationship between lipid metabolism and chromosome segregation. The presented data are valuable for the community, but the authors should carefully re-assess their data.
Major comments:
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Statistical analyses in some of the Fig.3B, 3C, 4B and S2 seem to be somewhat weird because p-values are too small for such a small number of experiments (three independent experiments) with large standard deviations. Please show all the data points in Fig. 2C-E, and provide raw values as a supplementary table for assessment of the data.
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We now show individual data points for all barplots and boxplots and provide all source numerical data as supplementary tables. The details of the used statistical tests are given in the respective figure legends.
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Pages 5-6: As for Fig. 4, the data is difficult to interpret because the trends of the ChIP-seq pattern of H3K9me2 between replicates look different: replicate 2 shows an increase of H3K9me2 signal, while replicate 1 shows almost no difference or weak if any. In such a case, the authors should repeat ChIP-seq one more time and confirm hypermethylation at these regions or confirm it by ChIP-qPCR.
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We do not agree with this statement. It is true that the exact histone modification patterns are not identical between the two replicates, but this is likely due to the differences in chromatin extract preparation in replicate 1 vs replicate 2 (see Methods). Importantly, both replicates show pronounced differences in H3K9me2 patterns between WT and cbf11KO. We have changed the visualization style to better highlight the differences between WT and mutant (Fig. 4A, Fig. S2B, S3)).
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Also, we have added one more biological replicate for the H3K9me2 ChIP-seq (Fig. S3) and performed the H3K9me2 ChIP-seq also in the Pcut6MUT strain with ~50% decreased expression of the cut6 gene (Cut6/ACC is the rate-limiting enzyme of fatty acid synthesis; cut6 is target of Cbf11) as 3 biological replicates (Fig. 4A and Fig. S3). Importantly, all replicates of both mutant strains show hypermethylated regions in the centromeres compared to WT.
Assuming that the pericentromeric regions are hypermethylated by cbf11 deletion, it is still unclear why the transcription from only dh, but not dg, regions increased although their ChIP-seq data indicated both dh/dg regions were hypermethylated. A similar question arises to the expression of per1 and sdh1. Both K9Ac and K9me2 modifications seem to unchange at both per1 and sdh1 loci, whereas the expression levels of these loci changed in the opposite direction. These results suggest that the transcription levels of the centromeric region are independent of their histone modification states.
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We do not know why dh expression differs from dg. But note that these are multi-copy repeats and it is very difficult to study individual copies separately. Our expression data, and partly also the ChIP-seq data represent “average” values across all the dh and dg copies present in the genome.
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Importantly, Figure 4A (and Fig. S2B, S3) show a large piece of the fission yeast chromosome (~57 kbp) and this scale does not allow making informed judgements about the state of histone modifications at a particular promoter locus.
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When we zoom in, we do see increased and decreased H3K9ac around the TSS of per1 and sdh1, respectively (2 replicates shown).
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A key question of this study is to understand the relationship between lipid metabolism and chromosome structures. However, the results presented are not enough to address this question. I request to distinguish whether the defects on pericentromeric regions are mediated by lipid metabolism or direct effect by cbf11 deletion. Cbf11 is a transcription factor and can directly bind to DNA, thereby there is a possibility that Cbf11 directly modulates the pericentromeric chromatin state without regulating lipid metabolism. This question can probably be addressed. As the authors have shown in their previous study (Prevorovsky et al., 2016), overexpression of cut6, which encodes acetyl coenzyme A carboxylase and is a target of cbf11, can bypass nuclear defects. If the overexpression of cut6 restores alteration on pericentromeric regions such as cohesin enrichment and hypermethylation, it suggests the defects are a secondary effect of the decrease of phospholipid biosynthesis.
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We agree that any rescue effects can be direct or indirect. And distinguishing between these two alternatives is unfortunately not straightforward.
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Our Cbf11 ChIP-seq data do not show Cbf11 binding to centromeres (PMID 19101542), suggesting that any impact of Cbf11 on centromeric chromatin is most likely indirect and mediated by some other, downstream, players.
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Instead of assaying cut6OE, we now show data that decreased cut6/ACC (a target of Cbf11) expression also leads to changes in histone methylation, similar to cbf11KO (Fig. 4A, Fig. S3). This suggests that lipid metabolism indeed can affect chromatin state (and the chromatin defects in cbf11KO are likely also lipid-related).
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We have recently shown (Princová et al., 2023, PMID: 36626368) that decreased fatty acid synthesis leads to changes in acetylation and expression of specific stress-response genes in S. pombe, and the whole process involves the histone acetyltransferases Gcn5 and Mst1. Therefore, instead of implicating membrane phospholipids, we rather suggest that lipid metabolism can affect chromatin acetylation/methylation and structure via HATs, potentially through acetyl-CoA, the common substrate of both FA synthesis and HATs. We now mention the Princová et al., 2023 paper in the Discussion section.
Minor comments:
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Figure 3C: The legend says, "Values represent means + SD from 3 independent experiments". It meant "means {plus minus} SD"?
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Corrected. Thank you for spotting this.
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The relationship between phospholipid synthesis and mitotic fidelity is now discussed in the bioRxiv paper (https://doi.org/10.1101/2022.06.01.494365). It would be nice to discuss this paper.
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Thank you for pointing out this reference. We now briefly mention this paper as a note that dysregulation of membrane phospholipid synthesis leads to mitotic phenotypes similar to cbf11KO.
Reviewer #2 (Significance (Required)):
Faithful chromosome segregation into daughter cells is crucial for cell proliferation. The authors previously reported that the deletion of cbf11, a transcription factor that regulates lipid metabolism genes, causes "cut (cell untimely torn)" phenotype (Prevorovsky et al., 2015; Prevorovsky et al., 2016). In this report, they examined detailed mechanisms by which the cbf11 deletion showed the phenotype, and found that the cbf11 deletion altered pericentromeric chromatin states such as the level of cohesin and hypermethylation. In general, their results are interesting and provide important insights into the relationship between lipid metabolism and chromosome segregation. The presented data are valuable for the community of basic science in the fields of chromosome biology and cell biology.
We are cell biologists working on chromosomes and the cell nucleus.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The Vishwanatha et al. manuscript examined the nature of the mitotic defect in cbf11 deletion cells. cbf11+ encodes a CSL transcription factor that regulates lipid metabolism genes in S. pombe. Loss of cbf11+ was previously shown to have a "cut" phenotype presumably due in part to aberrant regulation of its target gene cut6+ which encodes-acetyl CoA/biotin carboxylase involved in fatty acid biosynthesis (Zach et al. 2018). The authors hypothesized that the mitotic defect exhibited as chromosome missegregation in cbf11 deletion cells may be caused by alterations in cohesin occupancy and H3K9 methylation in centromeres. Cohesin occupancy was slightly higher in centromeric dh and dg repeats in the cbf11 mutant and loss of the cohesin-loader gene wpl1+ appeared to suppress the mitotic defect. The authors also showed by ChIP-Seq that H3K9 methylation was higher in the centromeric regions, as well as increased minichromosomal loss in the cbf11 mutant.
The discovery of increased cohesin occupancy and H3K9 hypermethylation in the centromeric regions of cbf11 deletion cells is novel and interesting. However, the main deficiency of the manuscript is that this discovery is underdeveloped. For example, the evidence linking the mitotic defect phenotype to these two processes was not well supported.
- We believe that the links have already been well established in the literature. The integrity of centromeric heterochromatin (H3K9me2) is known to be required for mitotic fidelity (eg. Clr4/HMT and Clr6/HDAC mutants with H3K9me2 deficiency have high minichromosome loss and/or show lagging chromosomes during mitosis - PMID: 19556509, PMID: 8937982, PMID: 9755190). Moreover, we stress the known interconnections and provide relevant citations in the Discussion:
“It is also important to note that heterochromatin, kinetochore function, cohesin occupancy, and gene expression are all interconnected and actually interdependent (Bernard et al., 2001; Folco et al., 2019, 5; Grewal and Jia, 2007; Gullerova and Proudfoot, 2008; Nonaka et al., 2002; Volpe et al., 2002)”
- We show in the manuscript altered cohesin occupancy in cbf11KO and show that mutations in cohesin loading factors do affect mitotic fidelity of cbf11KO. While we do agree that this connection can be developed further, we believe this is beyond the scope of our current project.
Moreover, there was no investigation in whether/how Cbf11 regulates cohesin occupancy or H3K9 methylation at the centromeres.
- This is true. But again, we believe this is beyond the scope of our current project.
Finally, the title and abstract provided an impression that lipid metabolism may influence cohesin occupancy and histone H3 hypermethylation at the centromeres, but this was not directly studied in the manuscript.
- We now provide H3K9me2 ChIP-seq data on the Pcut6MUT mutant deficient in fatty acid synthesis to show that lipid metabolism indeed can affect histone methylation at the centromeres (Fig. 4A, Fig. S3).
Centromeres are regions where sister chromatid cohesion is abolished last in mitosis. The observed higher levels of cohesin occupancy in the centromeric dh and dg repeats of cbf11 deletion cells could be the cause of chromosome missegregation, presumably because there is a delay or hinderance of cohesin removal from sister chromatids in mitosis. However, cohesin occupancy was carry out in asynchronous wild type and cbf11 deletion cultures, so it is unknown whether there is a delay of cohesion abolishment in mitosis. A cdc25-22 block and release experiment could better address this hypothesis.
- We acknowledge these limitations of our findings regarding cohesin occupancy in the paper:
“ Notably, centromeres are the regions where sister chromatin cohesion is abolished last during mitosis (Peters et al., 2008). Since cbf11Δ cells show altered cell-cycle and pre-anaphase mitotic duration compared to WT (Fig. 2), the observed difference in cohesin occupancy might merely reflect these changes in the timing of cell cycle progression. Alternatively, altered cohesin dynamics could play a role in the cbf11Δ mitotic defects.”
- We agree the issue could be addressed better using synchronous cell populations. However, the cdc25 or cdc10 block-release does not work well in cbf11KO (PMID: 27687771), and we currently do not have the capacity to perform less disruptive forms of cell cycle synchronization.
The observation that the spindle assembly checkpoint did not influence the mitotic catastrophe phenotype of cbf11 deletion cells suggests that the chromosome missegregation may not be mediated by defects in cohesin dynamics. How does Cbf11 influence cohesin dynamics in mitosis?
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There are clearly multiple contributors to the mitotic defects observed in the cbf11KO strain and we state this explicitly throughout the manuscript.
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We agree that it would be interesting in future to know more details about the link between Cbf11 and cohesin, but this is beyond the scope of our current project.
Does Cbf11 regulate transcription of cohesin genes or indirectly through defects in the centromere or condensins?
- Expression levels of cohesin and condensin genes are not affected by deletion of cbf11 (PMID: 26366556). We now mention these findings in the Results section.
There was no direct evidence that H3K9 hypermethylation at the centromeres contributes to the mitotic catastrophe phenotype of cbf11 deletion cells.
- This is true. However, the importance of H3K9me2 for mitotic fidelity has already been established in the literature (as we mention above).
It is also not clear whether Cbf11 directly or indirectly influences histone methylation at the centromeres of affect centromere function.
- When the Cbf11 protein is missing, centromeric histone methylation is different from normal (WT), and centromere function is not normal either - dh repeats are less expressed, minichromosome derived from ChrIII (so has a normal centromere) is 9x more frequently lost. So Cbf11 does affect these processes. The question remains, whether Cbf11 does this directly or indirectly. We favor the indirect route, as we have recently shown that H3K9 acetylation or methylation can be affected by shifting the balance between fatty acid synthesis (which is regulated by Cbf11) and histone acetyltransferase activity. We now mention these findings in the Discussion (Princová et al., 2023).
Based on a substantial number of protein-protein interactions of Cbf11 and gene products that affect chromatin function/silencing at the centromeres from the Pancaldi et al. 2012 study (e.g. HIR complex, Hrp1-Hrp3, Cnp1, Ino80 complex), I am surprised that these candidates were not mentioned in this study or investigated.
- Unfortunately, no DNase treatment was used during the affinity purification of Cbf11 in the study you mention. Therefore, the list of potential interactors is likely contaminated by irrelevant, DNA-mediated interactions with proteins sitting at nearby loci. This is why we have not pursued these candidates.
Also, it would be more comprehensive to examine defects in transcriptional silencing in the centromeric regions using an ade6+ or ura4+/FOA marker system rather than measuring expression of per1+ and sdh1+.
- We agree. We actually tried the ura4/FOA reporter system, but had problems constructing the reporter strains in the cbf11KO background. The resulting clones showed variable levels of FOA sensitivity (see figure of clones OC5-9 below), so we could not get a conclusive answer from this experiment and resorted to measuring the expression of pericentromeric genes.
Figure 1A shows that the "cut" and nuclear displacement phenotypes are independent. However, cut mutants can also generate a nuclear displacement phenotype [Samejima et al. (1993) J. Cell Sci. 105: 135-143]. Therefore, I am not sure whether the latter phenotype can be treated as entirely independent from "cut" mutants.
- We have made clarifications to Fig. 1A accordingly.
Reviewer #3 (Significance (Required)):
The discovery of increased cohesin occupancy and H3K9 hypermethylation in the
centromeric regions of cbf11 deletion cells is novel and interesting. However, the main deficiency of the manuscript is that this discovery is underdeveloped.
The results of this manuscript would be of considerable interest in the area of cell cycle research, transcription and chromatin structure and function.
Reviewer #4 (Evidence, reproducibility and clarity (Required)):
Summary
In this paper Vishwanatha et al. analyze the mitotic phenotypes of cells lacking a regulator of lipid metabolism Cbf11. They propose that sister chromatid cohesion abnormalities and altered chromatin marks may contribute to the increased incidence of catastrophic mitosis. Additional experiments are required to improve the study and strengthen the authors' conclusions.
Major Comments
Both histone and alpha-tubulin tagging are known to aggravate mitotic errors in S. pombe. Before using these markers for live imaging, the authors should quantitate mitotic phenotypes in untagged cbf11∆ cells, as compared to the wild type. Using DAPI and Calcofluor staining (and ideally, also visualizing microtubules using anti- alpha-tubulin antibodies) the authors should measure the percentage of cells in mitosis and the percentage of cells that are going, or just went, through catastrophic mitosis, in asynchronous early-mid-exponential cell populations.
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We agree that tagging can affect protein function in numerous ways.
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The tagged versions of tubulin (mCherry-Atb2) and H3 (Hht2-GFP) used in our paper have been obtained from Phong Tran’s lab. These tagged alleles had been published (Nature Communications, PMID: 26031557) and used successfully to monitor mitotic defects including chromosome segregation errors and the cut phenotype.
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The analyses of mitotic and septation defects of asynchronous untagged cbf11KO cells that you suggest (except for the spindle visualization) were already done by us (PMID: 19101542, PMID: 26366556) and are in agreement with our present study. In brief, we showed that cbf11KO populations contain ~10-30% of cells with mitotic defects (eg. cut), depending on the cultivation conditions. They also show septation defects and altered cell morphology and shorter cell length.
In analyzing the dynamic of nuclear division, the authors claim that the interval between spindle formation and anaphase onset is "longer" and "more variable" in cbf11∆ cells compared to WT cells. The authors should provide proper statistical analysis of both differences to show that these differences are significant.
- We now show the required data and statistical testing as Fig. 2H.
The same goes for the authors' claim that mitotic duration is "more variable" in cbf11∆ cells compared to WT cells.
- The spread of values for both WT and cbf11KO is given in Fig. 2G.
As mentioned above, alternative estimates of possible perturbations of mitotic dynamics could be obtained by measuring the percentage of cells in different mitotic phases in asynchronous untagged cell populations, in order to avoid possible artifacts given by tagging histones and alpha-tubulin.
- As you mention above, to estimate their cell cycle stage, untagged cells would need to be fixed and stained to visualize the nucleus and septum. However, using fixed cbf11KO cells is not optimal for this purpose. cbf11KO have septation and cell separation defects (PMID: 19101542, PMID: 26366556). This results in increased numbers of cells having a (persistent) septum in the asynchronous population, which obscures any estimates of cell cycle stages, and this is why we observed live cells during a timecourse.
The fact that inactivation of SAC does not change the incidence of catastrophic mitoses shows that SAC is not involved and that there are likely no problems with kinetochore-microtubule attachments. Therefore, the authors' statement "These results suggest that SAC activity only plays a minor role (if any) in the mitotic defects observed in cbf11Δ cells" should be changed.
- We have changed the sentence to:
“These results suggest that SAC activity only plays a minor role (if any) in the mitotic defects observed in cbf11Δ cells, or that the defects are not caused by problems with kinetochore-microtubule attachment.”
Also, the authors' statement in the conclusion that "This indicates that proper microtubule attachment to kinetochores might be compromised and takes longer to achieve in cbf11Δ cells, possibly triggering the SAC" should be changed accordingly or further proof should be provided.
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This is probably a misunderstanding. We do not conclude that failed microtubule attachment to kinetochores is surely the cause of mitotic defects in cbf11KO. We merely describe our reasoning about structuring the project during its execution. We have rephrased the problematic sentence to improve clarity.
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We already state in the Discussion that the mitotic defects of cbf11KO may be caused by something completely different from microtubule attachment.
As pointed out by the authors, cohesion occupancy is affected by the cell cycle phases duration. Therefore, the authors should correct their data (Fig.3C) for the different duration of mitosis or measure cohesion occupancy in mitotically synchronized populations. If this is not possible, I suggest removing this piece of data altogether.
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We agree (and acknowledge in the paper) that the measurement of cohesin occupancy can be affected by duration of mitotic phases. However we do not see a straightforward way of normalizing for mitotic duration, as cohesin occupancy changes differentially at particular chromosomal loci.
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The suggested experiment of measuring cohesin occupancy in synchronized mitotic cells would likely help. However, as mentioned in our response to Reviewer 3 above, the cdc25 or cdc10 block-release does not work well in cbf11KO (PMID: 27687771), and the heat shock or drugs (eg. spindle poisons) would introduce confounding issues themselves. Unfortunately, we currently do not have the capacity to perform less disruptive forms of cell cycle synchronization.
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Since we show that mutations in cohesin loading factors can rescue mitotic fidelity of cbf11KO cells (Fig. 3B), we consider the data shown in Fig. 3C relevant. Therefore, we opt to keep Fig. 3C in the paper, and we do point out the potential limitations of these results in the Results section.
In Fig. 3A it is not clear what the authors mean by "morphological" differences between WT and cbf11∆ cells or between cbf11∆ cells and cbf11∆wpl1∆ cells. The authors should provide clearer images and indicate for each image which cells show morphological defects as an example.
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We now use arrows to highlight cells with nuclear defects in Fig. 3A.
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We now state examples of the cbf11KO-associated morphological defects in the text, together with a reference to the paper describing these defects in detail.
In Fig. 3A many cells in single or double cbf11∆ mutants show increased size typical of diploid cells. The authors should perform flow cytometry to test for possible diploidization in their mutants, as that would clearly affect any conclusions on mitotic defects rescue or enhancement.
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We previously published that cbf11KO cells show increased tendency for spontaneous diploidization (PMID: 19101542). When constructing cbf11KO strains, we always take care (including flow cytometry tests of DNA content) to exclude purely diploid clones, but the process of spurious diploidization is continuous and there are always diploid cells present in the cbf11KO culture.
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We mention diploidization as a possible mitotic outcome in cbf11KO cells in the first section of the Results.
As correctly pointed out by the authors, it is not clear if the increase in mitotic defects in cbf11∆ cells is entirely due to the perturbed lipid metabolism or to other factors being affected by Cbf11. A possible approach to prove this point, as suggested by the authors too, would be to test if the mitotic defects identified in cbf11∆ are common to other mutants of lipid metabolism that also show an increase in catastrophic mitotic events.
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We now show ChIP-seq data showing that centromeric H3K9 shows aberrant methylation patterns also in a hypomorphic cut6/ACC mutant (Pcut6MUT) (Fig. 4A, Fig. S3).
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We previously showed that the Pcut6MUT mutation predisposes fission yeast cells to catastrophic mitosis, and the defects manifest when Cut6 function is further weakened by limiting the supply of biotin (cofactor of Cut6) (PMID: 27687771).
Also, the authors' statement in the conclusion: "we have demonstrated several novel factors, not directly related to lipid metabolism, that affect mitotic fidelity in cells with perturbed lipid homeostasis" should be modified as it was not proven that these effects are not due to altered lipid metabolism.
- We agree that “it was not proven that these effects are not due to altered lipid metabolism”. However, the emphasis here is on the word “directly”. H3K9me2 and cohesin dynamics are not directly related to the metabolism of lipids. We have changed the phrasing to improve clarity.
Minor comments
The initial distinction (Fig. 1A) between "cut" and "nuclear displacement" phenotypes is somewhat confusing, especially since the authors are not investigating the different outcomes of a catastrophic mitosis. The two outcomes should be grouped together under the definition of "catastrophic mitosis" as it is done in the rest of the paper.
- We have changed Fig. 1A accordingly.
I do not think I understand the statement that "SAC abolition might actually suppress the mitotic defects of the cbf11∆ cells". The lack of SAC might aggravate defects in kinetochore-microtubule attachment or other aspects of spindle assembly. If the authors know of specific examples where the deletion of mad2 or the genes encoding other SAC components rescued the mitotic defects, they should cite those papers. Either way, this point needs clarification.
- We already provide an example in the Discussion:
“Intriguingly, SAC inactivation has been shown to suppress the temperature sensitivity of the cut9-665 APC/C mutant, which is also prone to catastrophic mitosis (Elmore et al., 2014)”
- We have now included this reference and explanation also at the point in the text that you are referring to.
Brightfield images in Fig. 1 would be clearer without the overlap of the fluorescence channels. The authors could also change the contrast of the images to highlight the septum.
- We have changed Fig. 1B as requested.
The length of spindle (shown in Fig. S1) is a more informative measurement for mitotic dynamics and should be used instead of the "nuclear distance" presented in Fig. 2.
- This might be true for a successful mitosis. But in case of defects (such as spindle detachment from the chromosomes, regressive merger of the daughter nuclei), these parameters become partially uncoupled and both are informative. We have therefore included the data from Fig. S1 in new Fig. 2C-D.
Generally, the authors could improve the data visualization by including in all the plots the single data points distribution along with the mean/median and error bars like it was done in Fig.2 C,D,E.
- Done.
Reviewer #4 (Significance (Required)):
The paper expands the knowledge on Cbf11, a still poorly characterized regulator of lipid metabolism. The idea that in addition to nuclear membrane limitation, perturbations of lipid metabolism might cause mitotic chromosome dynamics defects (for instance, through changing the protein acetylation levels), is interesting, but the authors should strengthen their conclusions by performing controls and further experiments.
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Referee #4
Evidence, reproducibility and clarity
Summary
In this paper Vishwanatha et al. analyze the mitotic phenotypes of cells lacking a regulator of lipid metabolism Cbf11. They propose that sister chromatid cohesion abnormalities and altered chromatin marks may contribute to the increased incidence of catastrophic mitosis. Additional experiments are required to improve the study and strengthen the authors' conclusions.
Major Comments
Both histone and alpha-tubulin tagging are known to aggravate mitotic errors in S. pombe. Before using these markers for live imaging, the authors should quantitate mitotic phenotypes in untagged cbf11∆ cells, as compared to the wild type. Using DAPI and Calcofluor staining (and ideally, also visualizing microtubules using anti- alpha-tubulin antibodies) the authors should measure the percentage of cells in mitosis and the percentage of cells that are going, or just went, through catastrophic mitosis, in asynchronous early-mid-exponential cell populations.
In analyzing the dynamic of nuclear division, the authors claim that the interval between spindle formation and anaphase onset is "longer" and "more variable" in cbf11∆ cells compared to WT cells. The authors should provide proper statistical analysis of both differences to show that these differences are significant. The same goes for the authors' claim that mitotic duration is "more variable" in cbf11∆ cells compared to WT cells. As mentioned above, alternative estimates of possible perturbations of mitotic dynamics could be obtained by measuring the percentage of cells in different mitotic phases in asynchronous untagged cell populations, in order to avoid possible artifacts given by tagging histones and alpha-tubulin.
The fact that inactivation of SAC does not change the incidence of catastrophic mitoses shows that SAC is not involved and that there are likely no problems with kinetochore-microtubule attachments. Therefore, the authors' statement "These results suggest that SAC activity only plays a minor role (if any) in the mitotic defects observed in cbf11Δ cells" should be changed. Also, the authors' statement in the conclusion that "This indicates that proper microtubule attachment to kinetochores might be compromised and takes longer to achieve in cbf11Δ cells, possibly triggering the SAC" should be changed accordingly or further proof should be provided.
As pointed out by the authors, cohesion occupancy is affected by the cell cycle phases duration. Therefore, the authors should correct their data (Fig.3C) for the different duration of mitosis or measure cohesion occupancy in mitotically synchronized populations. If this is not possible, I suggest removing this piece of data altogether.
In Fig. 3A it is not clear what the authors mean by "morphological" differences between WT and cbf11∆ cells or between cbf11∆ cells and cbf11∆wpl1∆ cells. The authors should provide clearer images and indicate for each image which cells show morphological defects as an example.
In Fig. 3A many cells in single or double cbf11∆ mutants show increased size typical of diploid cells. The authors should perform flow cytometry to test for possible diploidization in their mutants, as that would clearly affect any conclusions on mitotic defects rescue or enhancement.
As correctly pointed out by the authors, it is not clear if the increase in mitotic defects in cbf11∆ cells is entirely due to the perturbed lipid metabolism or to other factors being affected by Cbf11. A possible approach to prove this point, as suggested by the authors too, would be to test if the mitotic defects identified in cbf11∆ are common to other mutants of lipid metabolism that also show an increase in catastrophic mitotic events. Also, the authors' statement in the conclusion: "we have demonstrated several novel factors, not directly related to lipid metabolism, that affect mitotic fidelity in cells with perturbed lipid homeostasis" should be modified as it was not proven that these effects are not due to altered lipid metabolism.
Minor comments
The initial distinction (Fig. 1A) between "cut" and "nuclear displacement" phenotypes is somewhat confusing, especially since the authors are not investigating the different outcomes of a catastrophic mitosis. The two outcomes should be grouped together under the definition of "catastrophic mitosis" as it is done in the rest of the paper.
I do not think I understand the statement that "SAC abolition might actually suppress the mitotic defects of the cbf11∆ cells". The lack of SAC might aggravate defects in kinetochore-microtubule attachment or other aspects of spindle assembly. If the authors know of specific examples where the deletion of mad2 or the genes encoding other SAC components rescued the mitotic defects, they should cite those papers. Either way, this point needs clarification.
Brightfield images in Fig. 1 would be clearer without the overlap of the fluorescence channels. The authors could also change the contrast of the images to highlight the septum.
The length of spindle (shown in Fig. S1) is a more informative measurement for mitotic dynamics and should be used instead of the "nuclear distance" presented in Fig. 2.
Generally, the authors could improve the data visualization by including in all the plots the single data points distribution along with the mean/median and error bars like it was done in Fig.2 C,D,E.
Significance
The paper expands the knowledge on Cbf11, a still poorly characterized regulator of lipid metabolism. The idea that in addition to nuclear membrane limitation, perturbations of lipid metabolism might cause mitotic chromosome dynamics defects (for instance, through changing the protein acetylation levels), is interesting, but the authors should strengthen their conclusions by performing controls and further experiments.
-
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Referee #3
Evidence, reproducibility and clarity
The Vishwanatha et al. manuscript examined the nature of the mitotic defect in cbf11 deletion cells. cbf11+ encodes a CSL transcription factor that regulates lipid metabolism genes in S. pombe. Loss of cbf11+ was previously shown to have a "cut" phenotype presumably due in part to aberrant regulation of its target gene cut6+ which encodes-acetyl CoA/biotin carboxylase involved in fatty acid biosynthesis (Zach et al. 2018). The authors hypothesized that the mitotic defect exhibited as chromosome missegregation in cbf11 deletion cells may be caused by alterations in cohesin occupancy and H3K9 methylation in centromeres. Cohesin occupancy was slightly higher in centromeric dh and dg repeats in the cbf11 mutant and loss of the cohesin-loader gene wpl1+ appeared to suppress the mitotic defect. The authors also showed by ChIP-Seq that H3K9 methylation was higher in the centromeric regions, as well as increased minichromosomal loss in the cbf11 mutant.
The discovery of increased cohesin occupancy and H3K9 hypermethylation in the centromeric regions of cbf11 deletion cells is novel and interesting. However, the main deficiency of the manuscript is that this discovery is underdeveloped. For example, the evidence linking the mitotic defect phenotype to these two processes was not well supported. Moreover, there was no investigation in whether/how Cbf11 regulates cohesin occupancy or H3K9 methylation at the centromeres. Finally, the title and abstract provided an impression that lipid metabolism may influence cohesin occupancy and histone H3 hypermethylation at the centromeres, but this was not directly studied in the manuscript.
Centromeres are regions where sister chromatid cohesion is abolished last in mitosis. The observed higher levels of cohesin occupancy in the centromeric dh and dg repeats of cbf11 deletion cells could be the cause of chromosome missegregation, presumably because there is a delay or hinderance of cohesin removal from sister chromatids in mitosis. However, cohesin occupancy was carry out in asynchronous wild type and cbf11 deletion cultures, so it is unknown whether there is a delay of cohesion abolishment in mitosis. A cdc25-22 block and release experiment could better address this hypothesis. The observation that the spindle assembly checkpoint did not influence the mitotic catastrophe phenotype of cbf11 deletion cells suggests that the chromosome missegregation may not be mediated by defects in cohesin dynamics. How does Cbf11 influence cohesin dynamics in mitosis? Does Cbf11 regulate transcription of cohesin genes or indirectly through defects in the centromere or condensins?
There was no direct evidence that H3K9 hypermethylation at the centromeres contributes to the mitotic catastrophe phenotype of cbf11 deletion cells. It is also not clear whether Cbf11 directly or indirectly influences histone methylation at the centromeres of affect centromere function. Based on a substantial number of protein-protein interactions of Cbf11 and gene products that affect chromatin function/silencing at the centromeres from the Pancaldi et al. 2012 study (e.g. HIR complex, Hrp1-Hrp3, Cnp1, Ino80 complex), I am surprised that these candidates were not mentioned in this study or investigated. Also, it would be more comprehensive to examine defects in transcriptional silencing in the centromeric regions using an ade6+ or ura4+/FOA marker system rather than measuring expression of per1+ and sdh1+.
Figure 1A shows that the "cut" and nuclear displacement phenotypes are independent. However, cut mutants can also generate a nuclear displacement phenotype [Samejima et al. (1993) J. Cell Sci. 105: 135-143]. Therefore, I am not sure whether the latter phenotype can be treated as entirely independent from "cut" mutants.
Significance
The discovery of increased cohesin occupancy and H3K9 hypermethylation in the centromeric regions of cbf11 deletion cells is novel and interesting. However, the main deficiency of the manuscript is that this discovery is underdeveloped.
The results of this manuscript would be of considerable interest in the area of cell cycle research, transcription and chromatin structure and function.
-
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Referee #2
Evidence, reproducibility and clarity
This manuscript describes detailed mechanisms by which the cbf11 deletion showed the phenotype. They found that the cbf11 deletion altered pericentromeric chromatin states such as the level of cohesin and hypermethylation.
In general, their results are interesting and provide important insights into the relationship between lipid metabolism and chromosome segregation. The presented data are valuable for the community, but the authors should carefully re-assess their data.
Major comments:
- Statistical analyses in some of the Fig.3B, 3C, 4B and S2 seem to be somewhat weird because p-values are too small for such a small number of experiments (three independent experiments) with large standard deviations. Please show all the data points in Fig. 2C-E, and provide raw values as a supplementary table for assessment of the data.
- Pages 5-6: As for Fig. 4, the data is difficult to interpret because the trends of the ChIP-seq pattern of H3K9me2 between replicates look different: replicate 2 shows an increase of H3K9me2 signal, while replicate 1 shows almost no difference or weak if any. In such a case, the authors should repeat ChIP-seq one more time and confirm hypermethylation at these regions or confirm it by ChIP-qPCR. Assuming that the pericentromeric regions are hypermethylated by cbf11 deletion, it is still unclear why the transcription from only dh, but not dg, regions increased although their ChIP-seq data indicated both dh/dg regions were hypermethylated. A similar question arises to the expression of per1 and sdh1. Both K9Ac and K9me2 modifications seem to unchange at both per1 and sdh1 loci, whereas the expression levels of these loci changed in the opposite direction. These results suggest that the transcription levels of the centromeric region are independent of their histone modification states.
- A key question of this study is to understand the relationship between lipid metabolism and chromosome structures. However, the results presented are not enough to address this question. I request to distinguish whether the defects on pericentromeric regions are mediated by lipid metabolism or direct effect by cbf11 deletion. Cbf11 is a transcription factor and can directly bind to DNA, thereby there is a possibility that Cbf11 directly modulates the pericentromeric chromatin state without regulating lipid metabolism. This question can probably be addressed. As the authors have shown in their previous study (Prevorovsky et al., 2016), overexpression of cut6, which encodes acetyl coenzyme A carboxylase and is a target of cbf11, can bypass nuclear defects. If the overexpression of cut6 restores alteration on pericentromeric regions such as cohesin enrichment and hypermethylation, it suggests the defects are a secondary effect of the decrease of phospholipid biosynthesis.
Minor comments:
- Figure 3C: The legend says, "Values represent means + SD from 3 independent experiments". It meant "means {plus minus} SD"?
- The relationship between phospholipid synthesis and mitotic fidelity is now discussed in the bioRxiv paper (https://doi.org/10.1101/2022.06.01.494365). It would be nice to discuss this paper.
Significance
Faithful chromosome segregation into daughter cells is crucial for cell proliferation. The authors previously reported that the deletion of cbf11, a transcription factor that regulates lipid metabolism genes, causes "cut (cell untimely torn)" phenotype (Prevorovsky et al., 2015; Prevorovsky et al., 2016). In this report, they examined detailed mechanisms by which the cbf11 deletion showed the phenotype, and found that the cbf11 deletion altered pericentromeric chromatin states such as the level of cohesin and hypermethylation. In general, their results are interesting and provide important insights into the relationship between lipid metabolism and chromosome segregation. The presented data are valuable for the community of basic science in the fields of chromosome biology and cell biology.
We are cell biologists working on chromosomes and the cell nucleus.
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Referee #1
Evidence, reproducibility and clarity
Summary:
The manuscript by Vishwanatha et al. presents findings on the fission yeast transcription factor Cbf11, which is involved in regulating lipid synthesis. Changes in lipid metabolism often have detrimental effects on nuclear division (evidenced by the high percentage of cut phenotypes among strains with altered lipid content). Here the authors show that cbf11 deletion strains produce additional phenotypes such as changes to cohesion dynamics and altered chromatin modification within centromeric regions, in turn perhaps affecting microtubule attachment and proper chromosome distributions. This hypothesis is supported by the authors' finding of epistatic effects between cbf11 and cohesin loading and unloading.
Major comments:
While the evidence presented supports the hypothesis of altered cohesin loading as a major driver of observed mitotic defects, changes in the NE surface area are likely to also contribute to the phenotypes even in pre-anaphase stages. Did the authors test any double deletions with regulators involved in decreasing lipid content (e.g. spo7, nem1, ned1) to counteract the role of Cbf11? This could be useful in assessing the relative contribution of cohesion dynamics and histone modifications.
A possible role of physical constraints dictated by the NE was already mentioned by the authors in the context of spindle bending and decreased elongation rates and some preliminary experimental data on this would be appreciated. Generation of strains, acquisition of some timelapses, and quantification of spindle elongation rate/buckling frequency should be feasible in a reasonable time frame.
The authors report mRNA levels of the centromere flanking genes per1 and sdh1 to be increased by 1.5x and decreased by 2x in comparison to WT. Could the authors elaborate on whether this is an expected trend? Kaufmann et al., 2010 reported low transcription of per1 when the surrounding regions are predominantly acetylated. Fig. 4A suggests a slight increase of H3K9ac at per1 and a decrease of transcription would be conceivable.
Fig. 3B indicates a catastrophic mitosis percentage of roughly 9.5% in cbf11∆ while in Fig. 1C 4% of all cells, or ˜31% of all mitotic events, is noted as abnormal. Could the authors clarify this discrepancy? Since Fig. 1 utilises time course data of 333 cells (please specify the number of analysed cells also in the legend), would the authors expect this data to be more trustworthy when compared to images of fixed cells? What were the criteria to assign divisions as catastrophic in fixed cells and which features were utilised to identify the 400 cells as mitotic?
Minor comments: Previous literature is, to the best of our knowledge, sufficiently referenced. The text is largely clear (some exceptions within the methods section will be elaborated on below). The figures, however, would benefit from graph titles and some minor formatting changes.
- Figures:
- Fig. 1: Specify the number of cells analysed in C within the legend as well. For B, please use colourblind-friendly schemes - especially since images are shown as merges only. The example of the "cut" phenotype appears small and crowded by surrounding cells. Especially the latter might affect mitotic fidelity. Under the assumption that this did not affect quantifications (WT seem fine) a less crowded cell would present a nicer example.
- Fig. 3: Images shown in A add little benefit in their current form. What is the takeaway for the reader? Indicating that images represent DAPI staining and pointing out cells of interest with arrows/symbols would be helpful. The example shown for cbf11 appears to be dimmer in comparison and cell morphology is hard to interpret. C feels misplaced in this figure and a title could improve readability.
- Fig. 4: Graph titles needed, figure might work better in portrait
- Text:
- Mention median duration of mitosis in cbf11∆ (Fig. 2E) in text since WT is already noted;
- Discussion, third paragraph: "TBZ [REF] and are prone to chromosome loss [...]". I assume this referred to minichromosome loss or have changes in ploidy/chromosome segregation been quantified?
- Methods, Microscopy and image analysis: How were fixed cells imaged (glass bottom dishes, plated on lectin, mounted on slides)? Specify the CellR as widefield and provide details of the objective used (immersion and NA) Elaborate on "manual evaluation of microscopic images" For live cell microscopy, what was the estimated final density of cells within the 5 µl resuspension? What is meant by measuring the maximum section of plotted profiles? Is this the maximum distance of Hht1 signals within the entire time-lapse? Was spindle length quantified the same way?
Methods, ChIP-qPCR:
It is not clear which strains were used, this can only be guessed by the use of a GFP antibody suggesting GFP tagged chromatin to be precipitated. For people with expertise outside of ChIP assays, this should be specified
Significance
Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
This manuscript presents a novel role for a transcription factor, one typically implicated in lipid metabolism, in chromatin modification and cohesin dynamics, with the possibility of this representing a more conserved process across ascomycetes. The mechanism of cbf11 regulation remains to be determined.
Place the work in the context of the existing literature (provide references, where appropriate).
This work helps link two bodies of work related to cell division that are usually considered in isolation, the regulation of lipid dynamics and the control of chromatin dynamics and cohesion. Some comparisons to phenotypes in closely related species would have helped provide a broader context (such as Yam et al., 2011, where the spindle morphologies in S. japonicus and response to cerulenin treatment might be of relevance to the work presented here).
State what audience might be interested in and influenced by the reported findings. Molecular and cellular biologists with interests in nuclear remodelling, lipid metabolism, kinetochore assembly.
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.
Fission yeast biology, nuclear remodelling, microscopy. We are not qualified to make in-depth comments on the soundness of ChIP-Seq and ChIP-qPCR experiments.
- Figures:
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
In this paper, the authors present convincing experimental proof on why the BH3-only protein PUMA resists displacement by BH3-mimetics, while others such as tBID do not. Using a SMAC-mCherry based MOMP assay on isolated mitochondria, FRET in the presence of liposomes with a phospholipid composition similar to that of mitochondria as well as quantitative fast fluorescence lifetime imaging microscopy (F__�__rster resonance energy transfer - qF3) they show that the C-terminal region of PUMA (CTS), together with its BH3-domain, effectively "double-bolt" locks its interaction with BCL-XL and BCL-2 to resist displacement by the BCL-XL-specific BH3-mimetic A-1155463 or the BCL-2/BCL-XL inhibitor ABT-263 and AZD-4320. Although a similar mechanism has previously been published for BIM, the novel C-terminal binding sequence in PUMA is unrelated to that in the CTS of BIM and functions independent of PUMA binding to membranes. First, in contrast to BIM, PUMA contains multiple prolines and charged residues, and an unusually short span of hydrophobic amino acids, secondly, full length PUMA was more resistant to BH3-mimetic displacement than a PUMA mutant lacking the CTS (PUMA-d26) even in solution suggesting that the CTS of PUMA contributes to BH3-mimetic resistance even in the absence of membranes.<br /> The second, quite unexpected finding of this paper is that, in contrast to previous publications, the CTS of PUMA does not target the protein to mitochondria but to the ER. The authors show this by FLIM-FRET imaging and confocal microscopy, and they created mutants to identify the CTS residues (I175 and P180) that mediate binding to ER membranes.
The authors did an excellent job to show the mechanism of displacement resistance of PUMA from BCL-2 survival factors from different angles (in vitro, on isolated mitochondria, liposomes and inside living cells), generating respective BH3 and CTS mutants and also domain swaps with other BH3-only proteins such as tBID. Also, the unexpected finding that PUMA primarily localizes to the ER has been extensively scrutinized and the data presented are convincing.
Response:
We appreciate the favourable comments and that the reviewer found the data presented convincing.
Major comments:
I have only three questions which I like the authors to address before this MS can be published.
1) How can PUMA perform its pro-apoptotic action on MOMP from its site on the ER? Does PUMA eventually localize to MAMs (mitochondrial/ER contact sites)? Is it possible to co-IP PUMA with BCL-XL or BCL-2 from ER membranes or show such an interaction inside cells with PLA?
Response:
The reviewer raises an important point. One of the main conclusions from this paper is that the primary localization of exogenously expressed PUMA is at the ER. Our intent was to highlight the inherent specificity of the PUMA CTS sequence. However, we agree that identifying the localization of PUMA-BCL-XL complexes would add significantly to the manuscript. We carefully considered using co-IP or a proximity ligation assay (PLA) in order to investigate the localization of PUMA-BCL-XL complexes. In our experience the use of co-IP is very difficult to interpret due to the well characterized detergent-induced artifacts previously shown for BCL-2 family protein interactions (PMID: 9553144, PMID: 33794146). Moreover, PLAs are a proximity assay with a detection range of ~>20nm, and are difficult to quantify beyond enumerating frequency (ie counting spots). In contrast, the detection of FRET by fluorescence lifetime imaging microscopy (FLIM) is very sensitive to distance with a maximum that is <10nm, and the results can be interpreted quantitatively as apparent dissociation constants (manuscript Figures 2-3). Therefore we elected to use FLIM-FRET to address this question. We examined PUMA-specific interactions with BCL-XL at the ER and mitochondria by differentially segmenting the FLIM-FRET image data based on the signal from a mCherry-fused landmark expressed at the ER (mCherry-Cb5) or mitochondria (mCherry-ActA). This approach has similar spatial resolution to PLA yet retains more rigorous requirement for proximity and the quantitative interpretability of FLIM-FRET.
For these experiments we used a recently described the method of mitochondrial image segmentation using hyperspectral image data collected during FLIM-FRET imaging (Osterlund et al., 2023). In this approach, a watershed segmentation algorithm was used to identify mitochondria areas from mCherry-ActA images collected simultaneously with the FLIM data. The ER was identified in separate samples using the same approach with mCherry-Cb5 image data. Simultaneous collection of the images ensures that the data are not affected by movement within the cells. Example images showing the segmentation results for each organelle have been added to the manuscript as Figure 4 - Figure Supplement 2A.
The results of this FLIM-FRET experiment described in the text lines 581-598, revealed that VPUMA interacts with CBCL-XL within both ER and mitochondria-segmented ROIs (new Figure 4 - Figure Supplement 2B). These results can be explained by the fact that VPUMA is targeted to the ER, and BCL-XL is known to localize to the ER and mitochondria when bound to BH3 proteins in cells (Kale et al., 2018, PMID: 29149100). This result is similar to what we reported for BIK, another ER-localized BH3 protein that exerts its pro-apoptotic function from ER membranes (PMID: 11884414 and PMID: 15809295). Our recent data for ER localized BIK binding to mitochondria-targeted BCL-XL (Osterlund et al., 2023), suggests that, as the referee suggested, binding to occurs via a membrane-spanning interaction at MAMs (ER-mitochondia contact sites) and/or via relocalization of BIK and/or BCL-XL in response to their co-expression (Osterlund et al., 2023). Consistent with these interpretations, when expression of endogenous PUMA was upregulated in response to stress (Figure 4- figure supplement 3A-B), the amount of PUMA increased at both ER and mitochondria (Figure 4- figure supplement 3C). We have presented this data and interpretation on lines 599-621 and discussed the localization results and the similarity to BIK in the manuscript discussion, lines 1029-1035.
2) Since PUMA seems to be "double-bolt" locked to BCL-2 or BCL-XL via its BH3-domain and CTS, how can it act as a pro-apoptotic inducer? Is its main function to act as an inhibitor of BCL-2 and BCL-XL rather than a direct BAX/BAK activator? And if it acts as a BAX/BAK activator, how can it be released from BCL-2/ BCL-XL, for example by another BH3-only protein which is induced by apoptosis stimulation? Or would in this case PUMA remain bound to BCL-2/ BCL-XL in order to activate BAX/BAK (which would be a kind of new activation mechanism)?
Response:
We appreciate the reviewers queries and have clarified the text to indicate that our interpretation is that by binding to BCL-XL, PUMA releases active BAX that is sequestered by BCL-XL (as shown in Figure 1A for purified proteins). Double bolt locking increases both affinity and avidity of PUMA for BCL-XL enabling competition to favor PUMA binding and displacement of sequestered BAX. To further address the reviewers point we added two additional experiments now shown in figure supplements to Figure 1. The data shown in new Figure 1 – figure supplement 1A (described on lines 182-191 of the revised manuscript) demontrates that PUMA kills HCT116 and BMK cells but not HEK293 cells. New Figure 1 – figure supplement 1B shows that inhibition of BCL-XL and MCL-1 using BH3 mimetics is sufficient to kill HCT116 and BMK cells while HEK293 cells are not killed by even high concentrations of these BH3 mimetics. To kill HEK293 cells requires activation of BAX (described on lines 191-201). Together this data indicates that the primary pro-apoptotic function of PUMA is inhbiting BCL-XL and MCL-1 rather than by activating BAX. This data fits very well with PUMA double-bolt locking resulting in very tight binding of PUMA to BCL-XL and likely MCL-1 as the primary mode of PUMA mediated induction of cell death, at least in the three cell lines investigated here. The importance and role of PUMA mediated BAX activation is an interesting area of active investigation that is beyond the purview of the current paper.
3) Is PUMA still bound to the ER when it is transcriptionally induced by genotoxic stress. In this case, the extra amount of PUMA produced is supposed to directly activate BAX/BAK. Does it do this on the ER or on mitochondria?
Response:
The referee raises a very interesting point.
Interestingly, Zheng et al., 2022 highlighted a P53-dependent death response to genotoxic stress, which results in the extension of peripheral, tubular ER and promotes the formation of ER-mitochondria contact sites (PMID: 30030520). Furthermore, PUMA is transcriptionally activated by P53 (PMID: 17360476). Therefore, we hypothesized the induction of PUMA would increase the fraction of PUMA at ER membranes and MAMs. As the latter resemble mitochondria in micrographs of cells we anticipated an increase in apparent mitochondrial localization. To address this question experimentally, we treated MCF-7 cells with genotoxic stress and ER stressors and tracked the expression of endogenous PUMA by immunofluorescence. The results are described in the manuscript (line 603-613, page 28) and shown in Figure 4 figure supplement 3.
The immunofluorescence data confirmed that PUMA protein levels increase after genotoxic stress, as expected (Reference 39, 40 in the manuscript) and to a lessor but still significant extent after ER stress (Figure 4 figure supplements 3A and B). In response to stress the amount of PUMA increased at both ER and mitochondria, however, in unstressed cells the endogenous Puma co-localized more to the mitochondria than to the ER (Figure 4- figure supplement 3C). This suggests that similar to BIK localization of PUMA is dynamic. In particular, the abundance and localization of PUMA binding partners such as BCL-XL also affects PUMA localization (the new data are described on pages 27-28, Lines 591-621). As described above, the extra PUMA induced by genotoxic stress can indirectly activate BAX by binding BCL-XL and displacing sequestered activated BAX. Our FLIM-FRET data suggest PUMA can bind BCL-XL at both the mitochondria and the ER. Moreover, given the expansion of ER-mitochondrial contact sites that occurs during stress we cannot rule out the possibility that ER-localized PUMA can inhibit mitochondria-localized anti-apoptotic proteins (both BCL-XL and MCL-1) at the ER (for BCL-XL)and MAMs for both proteins.
Reviewer #1 (Significance):
Very significant contribution to the field. Quite novel
Reviewer #2 (Evidence, reproducibility and clarity):
This study by Pemberton and colleagues investigates interactions of pro-apoptotic PUMA with anti-apoptotic BCL-2 proteins, employing a variety of BH3-mimetics. The authors demonstrate that the PUMA/aa BCL-2 interactions are mediated not only via BH3-domain/groove interactions, but also dependent on a C-terminal sequence of PUMA. This mirrors (with distinct differences) what the authors have previously reported for BIM. They then, reveal that unexpectedly PUMA is often localising to the ER (as opposed to mitochondria), though this localisation is not important for the resistance of PUMA/BCL-2 complexes to BH3-mimetic treatment, authors speculate that ER localised PUMA may have a day job.
In my opinion, the study is important for several reasons, not least it strongly argues that BH3-mimetics are not optimal (in themselves) to promote apoptosis dependent on PUMA, and that approaches to disrupt the "double-lock" mechanisms should be sought - this has clear clinical importance, but equally important is it adds a new layer of complexity to how BCL-2 family members "work", how the double-lock mechanism is overcome in physiological apoptosis remains an open question, for instance. The data support the authors' conclusions, I have a few points that could be addressed.
Response:
The positive comments from the reviewer are greatly appreciated.
1 - The authors data in cells is consistent with a membrane recruitment effect of the PUMA CTS making a contribution to the resistance of PUMA/aa BCL-2 complexes to BH3-mimetics. What I found really intriguing, is that the CTS also influences affinity in the absence of membranes (Figure 1) - could the authors speculate why they think CTS may be affecting PUMA/aaBCL-2 binding in the absence of membranes ?
Response:
We agree with the reviewer that membrane binding contributes to BH3 mimetic resistant binding of PUMA to BCL-XL consistent with elegant data presented previously (Pécot et al., 2016; PMID: 28009301). However, we show in Figure 5D that mutants of VPUMA-d26 with restored membrane binding (VPUMA-d26-ER1 and VPUMA-d26-ER2) remain sensitive to BH3-mimetic displacement, indicating that membrane binding alone is not sufficient to confer resistance to BH3-mimetics. Furthermore, as the reviewer pointed out BH3 mimetic resistant binding is observed in the absence of membranes (Figure 1).
The data using purified proteins strongly suggests that the CTS of PUMA binds to BCL-XL and is directly involved in the protein-protein interaction. The fact that PUMA with the C-terminal fusion to the fluorescent protein Venus (PUMAV) still localizes to membranes in live cells (Figure 4 D,E) suggests that the C-terminus of PUMA does not span the membrane bilayer. Instead, we hypothesize that the C-terminus of PUMA binds peripherally to the membrane making it available to physically contribute to a protein interaction with anti-apoptotic proteins. This interpretation is consistent with the low hydrophobicity and high proline content (6 of 28 residues) of the amino acid sequence of the PUMA CTS as shown in Figure 6 and compared to the transmembrane tail anchor sequences of other proteins, including the BH3-protein BIK, in Figure 5 supplement 1. Binding of Bcl-XL by both the BH3 region and CTS of PUMA would increase both the affinity and avidity of the interaction. The presentation of this data has been revised to add clarity on pages Page 8, lines 215-223 and in the discussion (Lines 988-997 and 1044-1050).
2 - A minor point for clarification, are the mitochondria used in Fig 1A from BAX/BAK DKO cells ? - I had presumed so given exogenous BAX was added, but didn't note this in the text.
We indeed use mitochondria from BAX/BAK DKO cells and exogenous recombinant BAX in Figure 1A. This has now been added to the text on lines 166-180.
Reviewer #2 (Significance):
detailed in report above
Reviewer #3 (Evidence, reproducibility and clarity):
In this paper, Pemberton et al show that PUMA resists BH3-mimetic mediated displacement from BCL-XL via a novel binding site within its C-terminus of PUMA termed CTS (the last 26aa). Interestingly, the CTS of PUMA directs the protein to the ER membrane and residues I175 and P180 within the CTS are required for both ER localization and BH3-mimetic resistance.
Specific comments:<br /> 1 - BH3-mimetics kill cells by displacing sequestered pro-apoptotic proteins to initiate apoptosis. However, PUMA resists BH3-mimetic mediated displacement, and PUMA-d26 and PUMA I175A/P180A (CTS) do not. Thus, are these mutants sensitive to BH3-mimetics cell killing? In other words, do BH3-mimetics kill PUMA-/- cells that express either PUMA-d26 or PUMA I175A/P180A but not PUMA-/- cells that express wild type PUMA?
Response:
The reviewer raises a very interesting question that unfortunately we have been unable to address unambiguously. To answer this question requires separating the effects of PUMA on anti-apoptosis proteins and on activation of BAX and BAK as exogenous expression of express either PUMA-d26 or PUMA I175A/P180A is sufficient to kill PUMA-/- cells without the addition of a BH3 mimetic. To date we have been unable to identify mutants that inhibit anti-apoptotic proteins but that do not activate BAX and BAK as both PUMA-d26 and PUMA I175A/P180A have impaired BAX-activation function. This is additionally complicated by PUMA mediated inhibition of MCL-1, BCL-2 and BCL-W. Further, it isn’t possible to separate the function(s) using BAX/BAK knock-out cells because then PUMA induced cell death is completely abrogated. Understanding the direct activation of BAX by PUMA is an area of current investigation that is out of the scope of this paper as here we are focused on the interaction(s) of PUMA with anti-apoptotic proteins.
2 - The authors elegantly demonstrate using microscopic analysis that over expressed PUMA mostly localizes to the ER membrane. Since this is a major conclusion in the paper which is different than previously reported, the authors should confirm these findings using sub-cellular fractions followed by Western blot analysis. They should demonstrate that endogenous and over-expressed PUMA are mainly localized to the ER membrane and that the PUMA-d26 and PUMA I175A/P180A are mainly localized to the cytoplasm.
Response:
We appreciate that the reviewer found the microscopic analysis convincing. We also tested the idea of sub-cellular fractionation proposed by the reviewer.However, we have found it to be very difficult to separate mitochondria and MAMs. To address the question raised we instead performed new co-localization experiments,in addition to those reported for PUMA-d26 and the point mutants in Figure 6 (images in Figure 6 - figure supplement 3). The new experiments areforendogenous PUMA at steady state and with increased expressed in response to stress. These immunofluorescence experiments are reported in Figure 4 -figure supplements 3. We also added FLIM-FRET experiments in which ROIs were derived from areas of the cell enriched in either ER or mitochondria(Figure 4 - figure supplement 2). The results of these experiments indicate that PUMA localization is dynamic and are described in detail above in response to reviewer 1 question 3 and in the manuscript from line 579 to 621 and discussed on lines 1029-1036.
Reviewer #3 (Significance):
The advance in this paper is significant and the paper should be published once the specific comments are adequately addressed
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Referee #3
Evidence, reproducibility and clarity
In this paper, Pemberton et al show that PUMA resists BH3-mimetic mediated displacement from BCL-XL via a novel binding site within its C-terminus of PUMA termed CTS (the last 26aa). Interestingly, the CTS of PUMA directs the protein to the ER membrane and residues I175 and P180 within the CTS are required for both ER localization and BH3-mimetic resistance.
Specific comments:
- BH3-mimetics kill cells by displacing sequestered pro-apoptotic proteins to initiate apoptosis. However, PUMA resists BH3-mimetic mediated displacement, and PUMA-d26 and PUMA I175A/P180A (CTS) do not. Thus, are these mutants sensitive to BH3-mimetics cell killing? In other words, do BH3-mimetics kill PUMA-/- cells that express either PUMA-d26 or PUMA I175A/P180A but not PUMA-/- cells that express wild type PUMA?
- The authors elegantly demonstrate using microscopic analysis that over expressed PUMA mostly localizes to the ER membrane. Since this is a major conclusion in the paper which is different than previously reported, the authors should confirm these findings using sub-cellular fractions followed by Western blot analysis. They should demonstrate that endogenous and over-expressed PUMA are mainly localized to the ER membrane and that the PUMA-d26 and PUMA I175A/P180A are mainly localized to the cytoplasm.
Significance
The advance in this paper is significant and the paper should be published once the specific comments are adequately addressed
-
Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.
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Referee #2
Evidence, reproducibility and clarity
This study by Pemberton and colleagues investigates interactions of pro-apoptotic PUMA with anti-apoptotic BCL-2 proteins, employing a variety of BH3-mimetics. The authors demonstrate that the PUMA/aa BCL-2 interactions are mediated not only via BH3-domain/groove interactions, but also dependent on a C-terminal sequence of PUMA. This mirrors (with distinct differences) what the authors have previously reported for BIM. They then, reveal that unexpectedly PUMA is often localising to the ER (as opposed to mitochondria), though this localisation is not important for the resistance of PUMA/BCL-2 complexes to BH3-mimetic treatment, authors speculate that ER localised PUMA may have a day job.
In my opinion, the study is important for several reasons, not least it strongly argues that BH3-mimetics are not optimal (in themselves) to promote apoptosis dependent on PUMA, and that approaches to disrupt the "double-lock" mechanisms should be sought - this has clear clinical importance, but equally important is it adds a new layer of complexity to how BCL-2 family members "work", how the double-lock mechanism is overcome in physiological apoptosis remains an open question, for instance. The data support the authors' conclusions, I have a few points that could be addressed.
- The authors data in cells is consistent with a membrane recruitment effect of the PUMA CTS making a contribution to the resistance of PUMA/aa BCL-2 complexes to BH3-mimetics. What I found really intriguing, is that the CTS also influences affinity in the absence of membranes (Figure 1) - could the authors speculate why they think CTS may be affecting PUMA/aaBCL-2 binding in the absence of membranes ?
- A minor point for clarification, are the mitochondria used in Fig 1A from BAX/BAK DKO cells ? - I had presumed so given exogenous BAX was added, but didn't note this in the text.
Significance
detailed in report above
-
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Referee #1
Evidence, reproducibility and clarity
In this paper, the authors present convincing experimental proof on why the BH3-only protein PUMA resists displacement by BH3-mimetics, while others such as tBID do not. Using a SMAC-mCherry based MOMP assay on isolated mitochondria, FRET in the presence of liposomes with a phospholipid composition similar to that of mitochondria as well as quantitative fast fluorescence lifetime imaging microscopy (Förster resonance energy transfer - qF3) they show that the C-terminal region of PUMA (CTS), together with its BH3-domain, effectively "double-bolt" locks its interaction with BCL-XL and BCL-2 to resist displacement by the BCL-XL-specific BH3-mimetic A-1155463 or the BCL-2/BCL-XL inhibitor ABT-263 and AZD-4320. Although a similar mechanism has previously been published for BIM, the novel C-terminal binding sequence in PUMA is unrelated to that in the CTS of BIM and functions independent of PUMA binding to membranes. First, in contrast to BIM, PUMA contains multiple prolines and charged residues, and an unusually short span of hydrophobic amino acids, secondly, full length PUMA was more resistant to BH3-mimetic displacement than a PUMA mutant lacking the CTS (PUMA-d26) even in solution suggesting that the CTS of PUMA contributes to BH3-mimetic resistance even in the absence of membranes.
The second, quite unexpected finding of this paper is that, in contrast to previous publications, the CTS of PUMA does not target the protein to mitochondria but to the ER. The authors show this by FLIM-FRET imaging and confocal microscopy, and they created mutants to identify the CTS residues (I175 and P180) that mediate binding to ER membranes.
The authors did an excellent job to show the mechanism of displacement resistance of PUMA from BCL-2 survival factors from different angles (in vitro, on isolated mitochondria, liposomes and inside living cells), generating respective BH3 and CTS mutants and also domain swaps with other BH3-only proteins such as tBID. Also, the unexpected finding that PUMA primarily localizes to the ER has been extensively scrutinized and the data presented are convincing.
Major comments:
I have only three questions which I like the authors to address before this MS can be published.
- How can PUMA perform its pro-apoptotic action on MOMP from its site on the ER? Does PUMA eventually localize to MAMs (mitochondrial/ER contact sites)? Is it possible to co-IP PUMA with BCL-XL or BCL-2 from ER membranes or show such an interaction inside cells with PLA?
- Since PUMA seems to be "double-bolt" locked to BCL-2 or BCL-XL via its BH3-domain and CTS, how can it act as a pro-apoptotic inducer? Is its main function to act as an inhibitor of BCL-2 and BCL-XL rather than a direct BAX/BAK activator. And if it acts as a BAX/BAK activator, how can it be released from BCL-2/ BCL-XL, for example by another BH3-only protein which is induced by apoptosis stimulation? Or would in this case PUMA remain bound to BCL-2/ BCL-XL in order to activate BAX/BAK (which would be a kind of new activation mechanism)?
- Is PUMA still bound to the ER when it is transcriptionally induced by genotoxic stress. In this case, the extra amount of PUMA produced is supposed to directly activate BAX/BAK. Does it do this on the ER or on mitochondria?
Significance
Very significant contribution to the field. Quite novel
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Reply to the reviewers
We are very pleased that our manuscript was well-received by each of the three reviewers. Reviewer #1 found our study to be “interesting”, “clear” and “convincing”. Reviewer #2 found our study to be “unprecedented” and of “considerable interest to cell biologists in the vision community and likely to the broader cell biology community”. Reviewer #3 believed that we reported “novel and significant findings into an important cell biological problem” and that our study “should be of broad interest to cell biologists and vision scientists”. This reviewer also stated that “it is strongly recommended for publication”.
Reviewer #1:
The paper of Lewis et al. presents an interesting study describing new information about the morphology of nascent discs and the role of peripherin in determining disc and incisure structure. I have only a few comments mostly about presentation.
We are happy that the reviewer liked our study.
- Because this study employs both frog and mouse, the authors should be careful to give the species when describing their results. The naming of the species would be particularly important in the first paragraph of the Results section and the legend to the first data figure, Fig. 2.
We have clarified the text and figure legends to allow the reader to better follow which species each result came from.
- It is unclear what Movie 1 adds to Fig. 3. This movie could perhaps be omitted.
We prefer to include the source data that the image in Figure 3 is derived from, particularly to stress that the pattern shown in a single z-section in this figure can be seen throughout the entire tomogram. We hope that the reviewer would agree.
- Movies 3 and 5 either don't work or consist of single frames, which would be better illustrated as figures in the text rather than as supplementary movies.
We appreciate the reviewer catching that there were some technical issues with video playback. We have recompressed these videos and ensured that they will now play appropriately across a wide variety of computer specifications and video player applications.
- The incisures in Fig. 4 will be difficult for many readers to visualize. My experience was that once I saw one of them, I began to see the others. The incisures in Fig. 5 are, on the other hand, very easy to see. If Fig. 5 had come before Fig. 4, I would have had no problem. The authors may wish to exchange these two figures or to supply a cartoon for one of the rods in Fig. 4, so that the reader can more easily understand what he or she should be trying to see.
We thank the reviewer for pointing out that some readers may have difficulties in fully appreciating the structure of incisures in this figure. We made two changes to improve the presentation of these images. First, we pseudo-colored several examples of enclosed discs in Figure 3, which highlights the structure of incisures. We also indicated one example of an incisure in these images with an arrowhead. Second, we pseudo-colored the example shown in Figure 4A to illustrate the same point, while still allowing the reader to view the three remaining examples in Figure 4 without any overlaid modifications.
- It is unclear to me why the authors are so fond of their untested theory that incisures "likely serve to protect the flat lamellar disc membranes from undesirable deformations" but seem skeptical of the notion that incisures are present and especially numerous in rods of large diameter to aid longitudinal diffusion. The later notion is supported not only by theoretical calculations but also by common sense.
We appreciate this comment and, in fact, feel agnostic about both of these not mutually exclusive ideas. We removed the statement that the deposition of peripherin-2 in incisures likely serves to protect the flat lamellar disc membranes from undesirable deformations from the Introduction and rephrased the text in Discussion to stress that both functions are plausible and not mutually exclusive.
This manuscript presents a clear and convincing description of disc formation and the role of the protein peripherin in the formation of disc incisures.
Thank you for your kind comment.
Reviewer #2:
Summary: The manuscript by Lewis et al. focuses on the potential mechanisms underlying formation of incisures in rod photoreceptors. Incisures refer to the indentations that occur on the rim of the photoreceptor disc membranes. The presence of incisures has been noted for decades and have been identified across a number of species. The role of incisures is not entirely clear and the mechanisms governing their formation have largely been inferred from early transmission electron microscopy studies 40-60 years ago. More recent ultrastructural studies of rod outer segment discs from mice carrying mutant alleles of rhodopsin or periperhin-2 described changes in the length or presence of incisures, suggesting that these proteins likely play a fundamental role in incisure formation in mouse. The authors take advantage of advances in electron tomography to provide unprecedented analyses of incisure formation, size, and structural complexity in stacked discs within mouse photoreceptors. They also use genetic models to explore how rhodopsin and peripherin-2 contribute to incisure formation and length. The authors find that new discs are highly irregular in shape and do not contain incisures during disc formation. Incisures are only formed are discs are enclosed. They find that the incisures in adjacent discs always align adjacent to the ciliary axoneme. Intriguingly, they find evidence of physical connections on opposing sides of the incisure. Critically, they find that elevated levels of peripherin-2 increase incisure size and complexity while low levels of peripherin-2 prevent incisure formation. In contrast, reduced molar ratios of rhodopsin lead to smaller disc surface area but increased incisure complexity. These results lead the authors to conclude that incisure formation is mechanistically linked to the relative molar ratio of peripherin-2 to rhodopsin and that rods make a slight excess of peripherin-2 in order to drive proper disc closure. The excess peripherin-2 within the disc rim forces formation of an incisure.
We are happy that the reviewer liked our study.
Major comments<br /> 1. Line 145-146: the location of the incisure adjacent to the ciliary axoneme is an interesting observation indeed. As frogs have a number of incisures, is this a similar observation in species with multiple incisures or more exclusive to those species with a single incisure?
Indeed, we did observe that one of the many incisures in a frog disc is aligned with the ciliary axoneme. We have now included Supplementary Figure S2 to highlight this observation using an example of two adjacent cells.
- While the presence of non-axonemal microtubules aligned with incisures in frog rods may provide an explanation for the number of incisures, the correlation with peripherin and rhodopsin content was lacking. In other words, do frog rods have considerably more peripherin-2 per disc than mouse rods?
This is a great question and one that we are interested in pursuing in the future. However, adapting the mass spectrometry-based protein quantification approach that we used to determine the absolute numbers of peripherin-2, ROM1 and rhodopsin molecules per disc was a significant undertaking that took several years (Skiba et al., PMID: 36711880). This approach is currently applicable to only a particular set of outer segment proteins in the mouse and cannot be automatically re-purposed to quantification of proteins in other species that have different amino acid sequences. Thus, designing, validating and employing this quantification protocol to all peripherin-2 and ROM1 isoforms along with rhodopsin in the frog would be a major undertaking that cannot be completed in the context of this revision. Nonetheless, we are very appreciative for the reviewer’s enthusiasm for this topic and plan to address this question in the future.
Minor comments<br /> 1. The location of the incisures are difficult to see in Figure 4. The arrowhead is pointing to a very low contrast area of the disc and the thin incisure can be seen, but it's difficult. If it is possible to pseudocolor the image in some way to highlight the disc vs the extramembrane space, it would be helpful.
We thank the reviewer for noticing this issue, which was also commented by another reviewer. As described above, we pseudo-colored several examples in Figures 3 and 4.
- Line 138-142: As with any descriptive narrative of cell structures, it is important to ensure the reader can fully understand and appreciate the interpretation of the authors. The shape of the newly forming discs can be difficult to appreciate in Figure 4. The authors are strongly encouraged to perhaps take 1-2 examples and provide a drawing or schematic of the image that can be more clearly annotated to assist readers in finding the outline of the discs and incisures.
We appreciate this point and pseudo-colored the surfaces of new forming discs in the examples shown in Figure 4A. We feel that pseudo-coloring helps the reader better visualize not only the structure of incisures, but also the irregular shape of the newly forming discs as in this specific example.
Overall, the paper is well-written and organized logically. The figures are generally easy to interpret although some additional annotations would help readers identify incisures in some low-contrast images (see comments). The authors utilized state-of-the-art electron tomographic data and mouse genetics to address a fundamental question. This will be of considerable interest to cell biologists in the vision community and likely to the broader cell biology community on how peripheral/rim proteins can shape membrane.
It is needless to say that we are very pleased by these comments and that the reviewer found our study to be of considerable interest to the broader cell biology community.
The authors provide a well-reasoned model for how incisures form in mouse rod photoreceptors: a relative excess of peripherin-2 drives incisure formation. This agrees with their mass-spectrometry data and molar ratios of peripherin-2 and rhodopsin._ _The main concern and outstanding question is whether these results are specific to mouse photoreceptors? The experiments in Xenopus were limited and only found that a CRISPR knockout of one peripherin-2 ortholog prevented incisure formation. While this result agreed with the general model and how molar ratios of peripherin-2 contribute, the knockout phenotypes are different than that of mouse. Some hypotheses are mentioned to explain this, but none were tested. The authors provide a model that agrees with mouse data, but is this generalizable? The model should permit several predictions for incisure formation beyond that of mouse rods. It would be most helpful to look in a species with multiple incisures and calculate the molar ratios of rhodopsin and peripherin-2. Do Xenopus require significantly more peripherin-2 to form multiple incisures? Alternatively, is it possible for the authors to mine publically available proteomics studies to assess rhodopsin and peripherin-2 content from other species (e.g. human, non-human primates, rats, etc...) and correlate to incisure number and/or length? The study overall is interesting and thought-provoking, but the overall impact would be greatly enhanced if additional evidence was provided that their model is broadly generalizable given the variety in incisure number and photoreceptor disc morphology (e.g. surface area, diameter) across species.
Related to a comment above, we are interested in pursuing each of these directions in frogs and other species in future studies, although it is not feasible to accomplish the required body of work in the context of manuscript revision. There are three other photoreceptor tetraspanins homologous to peripherin-2 that remain to be quantified and knocked out in frogs, alone and in combinations (the xrds36 and xrds35 isoforms and the peripherin-2-like protein). Testing the function of each of these in incisure formation would be an endeavor spanning several years of work. Additionally, there are no publicly available proteomic datasets that would contain information allowing an accurate quantification of rhodopsin and these homologous tetraspanins in other species. This question would require us to adapt our protein quantification approach, which would indeed be valuable, but would take significant time to complete.
Reviewer #3:
Summary. This work explores the formation of incisures in rod outer-segment (OS) disks. The visual pigment rhodopsin is the major lamellar protein in rod OS disks, while peripherin is the major structural protein of the disk rim. The authors used wild-type, Rho+/- and Rds+/- mice to vary the ratio of rhodopsin to peripherin in vivo, and compared these ratios to incisure length and complexity in rod OS.
Comments. This study presents several new findings. The authors convincingly show by EM tomography that incisures only form after each OS disk has reached maturity (fully separated from the plasma membrane). This new finding corrects an earlier published observation. Next, they examined disk morphology in Rds+/- heterozygous null-mutant mice and showed that an ~50% reduction in peripherin levels resulted in rod OS disks with no incisures. They performed a similar study on Rho+/- heterozygotes mutants. This time they observed that an ~50% reduction in rhodopsin levels resulted in OS disks with excessively long incisures. MS analysis of rod OS proteins and quantitative analysis of the EM images showed that incisure length varies with the ratio of peripherin to rhodopsin. They further showed that wild-type rods contain a small excess of peripherin over the amount required to form mature disks with normal incisures. Finally, the authors examined the effects of peripherin levels in rods from Xenopus tropicalis, an animal containing large OS disks with multiple incisures and three homologs of peripherin. They used gene editing to generate Xenopus tropicalis with a null mutation in the xrds35 gene, which is most like mammalian peripherin. OS disks from xrds35-/- frogs contained no incisures by EM tomography, further supporting their hypothesis.
Thank you for this nice summary of our study.
Another protein in the rims of rod OS disks is ABCA4, an ATP-driven flippase that translocates PE conjugated to retinaldehyde from the lumenal to cytoplasmic leaflets of the disk membrane. Retinaldehyde is a toxic photoproduct of rhodopsin bleaching. It has been suggested that the large number of incisures in frog disks is due to the larger diameter of frog versus mouse rod OS, and hence the greater number of rhodopsins per disk. This relationship is thought to ensure sufficient ABCA4 flippase activity to process the larger flux of retinaldehyde released by rhodopsin in these wide disks during light exposure, and possibly to minimize the diffusion distance of retinaldehyde from the disk lamella to the rim. The authors' findings seem in conflict with this explanation. They may wish to comment on this facet of their results.
We agree that it is possible for incisures to promote the encounter rate between retinaldehyde and ABCA4 in the disc. We do not find this idea to conflict with any of our interpretations; rather, this may be a complementary function of incisures. However, we failed to find any place in the literature where this hypothesis has been explicitly proposed and feel uneasy to present it as a new idea of our own in discussion. Fortunately, these reviews are public and truly interested readers could appreciate this idea. It is also worth noting that the correlation between incisure number and disc diameter is not perfect. For example, owl monkey discs appear to have a large number of incisures despite having a similar diameter to the mouse (Kroll and Machemer, PMID: 4970987).
Significance. The manuscript presents novel and significant findings into an important cell biological problem, development of the rod OS. It is clearly written and the data are of high quality. The manuscript should be of broad interest to cell biologists and vision scientists. It is strongly recommended for publication.
We are glad that the reviewer found our study to be of broad interest.
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Referee #3
Evidence, reproducibility and clarity
Summary. This work explores the formation of incisures in rod outer-segment (OS) disks. The visual pigment rhodopsin is the major lamellar protein in rod OS disks, while peripherin is the major structural protein of the disk rim. The authors used wild-type, Rho+/- and Rds+/- mice to vary the ratio of rhodopsin to peripherin in vivo, and compared these ratios to incisure length and complexity in rod OS.
Comments. This study presents several new findings. The authors convincingly show by EM tomography that incisures only form after each OS disk has reached maturity (fully separated from the plasma membrane). This new finding corrects an earlier published observation. Next, they examined disk morphology in Rds+/- heterozygous null-mutant mice and showed that an ~50% reduction in peripherin levels resulted in rod OS disks with no incisures. They performed a similar study on Rho+/- heterozygotes mutants. This time they observed that an ~50% reduction in rhodopsin levels resulted in OS disks with excessively long incisures. MS analysis of rod OS proteins and quantitative analysis of the EM images showed that incisure length varies with the ratio of peripherin to rhodopsin. They further showed that wild-type rods contain a small excess of peripherin over the amount required to form mature disks with normal incisures. Finally, the authors examined the effects of peripherin levels in rods from Xenopus tropicalis, an animal containing large OS disks with multiple incisures and three homologs of peripherin. They used gene editing to generate Xenopus tropicalis with a null mutation in the xrds35 gene, which is most like mammalian peripherin. OS disks from xrds35-/- frogs contained no incisures by EM tomography, further supporting their hypothesis.
Another protein in the rims of rod OS disks is ABCA4, an ATP-driven flippase that translocates PE conjugated to retinaldehyde from the lumenal to cytoplasmic leaflets of the disk membrane. Retinaldehyde is a toxic photoproduct of rhodopsin bleaching. It has been suggested that the large number of incisures in frog disks is due to the larger diameter of frog versus mouse rod OS, and hence the greater number of rhodopsins per disk. This relationship is thought to ensure sufficient ABCA4 flippase activity to process the larger flux of retinaldehyde released by rhodopsin in these wide disks during light exposure, and possibly to minimize the diffusion distance of retinaldehyde from the disk lamella to the rim. The authors' findings seem in conflict with this explanation. They may wish to comment on this facet of their results.
Significance
The manuscript presents novel and significant findings into an important cell biological problem, development of the rod OS. It is clearly written and the data are of high quality. The manuscript should be of broad interest to cell biologists and vision scientists. It is strongly recommended for publication.
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Referee #2
Evidence, reproducibility and clarity
Summary: The manuscript by Lewis et al. focuses on the potential mechanisms underlying formation of incisures in rod photoreceptors. Incisures refer to the indentations that occur on the rim of the photoreceptor disc membranes. The presence of incisures has been noted for decades and have been identified across a number of species. The role of incisures is not entirely clear and the mechanisms governing their formation have largely been inferred from early transmission electron microscopy studies 40-60 years ago. More recent ultrastructural studies of rod outer segment discs from mice carrying mutant alleles of rhodopsin or periperhin-2 described changes in the length or presence of incisures, suggesting that these proteins likely play a fundamental role in incisure formation in mouse. The authors take advantage of advances in electron tomography to provide unprecedented analyses of incisure formation, size, and structural complexity in stacked discs within mouse photoreceptors. They also use genetic models to explore how rhodopsin and peripherin-2 contribute to incisure formation and length. The authors find that new discs are highly irregular in shape and do not contain incisures during disc formation. Incisures are only formed are discs are enclosed. They find that the incisures in adjacent discs always align adjacent to the ciliary axoneme. Intriguingly, they find evidence of physical connections on opposing sides of the incisure. Critically, they find that elevated levels of peripherin-2 increase incisure size and complexity while low levels of peripherin-2 prevent incisure formation. In contrast, reduced molar ratios of rhodopsin lead to smaller disc surface area but increased incisure complexity. These results lead the authors to conclude that incisure formation is mechanistically linked to the relative molar ratio of peripherin-2 to rhodopsin and that rods make a slight excess of peripherin-2 in order to drive proper disc closure. The excess peripherin-2 within the disc rim forces formation of an incisure.
Major comments
- Line 145-146: the location of the incisure adjacent to the ciliary axoneme is an interesting observation indeed. As frogs have a number of incisures, is this a similar observation in species with multiple incisures or more exclusive to those species with a single incisure?
- While the presence of non-axonemal microtubules aligned with incisures in frog rods may provide an explanation for the number of incisures, the correlation with peripherin and rhodopsin content was lacking. In other words, do frog rods have considerably more peripherin-2 per disc than mouse rods?
Minor comments
- The location of the incisures are difficult to see in Figure 4. The arrowhead is pointing to a very low contrast area of the disc and the thin incisure can be seen, but it's difficult. If it is possible to pseudocolor the image in some way to highlight the disc vs the extramembrane space, it would be helpful.
- Line 138-142: As with any descriptive narrative of cell structures, it is important to ensure the reader can fully understand and appreciate the interpretation of the authors. The shape of the newly forming discs can be difficult to appreciate in Figure 4. The authors are strongly encouraged to perhaps take 1-2 examples and provide a drawing or schematic of the image that can be more clearly annotated to assist readers in finding the outline of the discs and incisures.
Significance
Overall, the paper is well-written and organized logically. The figures are generally easy to interpret although some additional annotations would help readers identify incisures in some low-contrast images (see comments). The authors utilized state-of-the-art electron tomographic data and mouse genetics to address a fundamental question. This will be of considerable interest to cell biologists in the vision community and likely to the broader cell biology community on how peripheral/rim proteins can shape membrane.
The authors provide a well-reasoned model for how incisures form in mouse rod photoreceptors: a relative excess of peripherin-2 drives incisure formation. This agrees with their mass-spectrometry data and molar ratios of peripherin-2 and rhodopsin. The main concern and outstanding question is whether these results are specific to mouse photoreceptors? The experiments in Xenopus were limited and only found that a CRISPR knockout of one peripherin-2 ortholog prevented incisure formation. While this result agreed with the general model and how molar ratios of peripherin-2 contribute, the knockout phenotypes are different than that of mouse. Some hypotheses are mentioned to explain this, but none were tested. The authors provide a model that agrees with mouse data, but is this generalizable? The model should permit several predictions for incisure formation beyond that of mouse rods. It would be most helpful to look in a species with multiple incisures and calculate the molar ratios of rhodopsin and peripherin-2. Do Xenopus require significantly more peripherin-2 to form multiple incisures? Alternatively, is it possible for the authors to mine publically available proteomics studies to assess rhodopsin and peripherin-2 content from other species (e.g. human, non-human primates, rats, etc...) and correlate to incisure number and/or length? The study overall is interesting and thought-provoking, but the overall impact would be greatly enhanced if additional evidence was provided that their model is broadly generalizable given the variety in incisure number and photoreceptor disc morphology (e.g. surface area, diameter) across species.
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Referee #1
Evidence, reproducibility and clarity
Review of Lewis et al. 2023
The paper of Lewis et al. presents an interesting study describing new information about the morphology of nascent discs and the role of peripherin in determining disc and incisure structure. I have only a few comments mostly about presentation.
- Because this study employs both frog and mouse, the authors should be careful to give the species when describing their results. The naming of the species would be particularly important in the first paragraph of the Results section and the legend to the first data figure, Fig. 2.
- It is unclear what Movie 1 adds to Fig. 3. This movie could perhaps be omitted.
- Movies 3 and 5 either don't work or consist of single frames, which would be better illustrated as figures in the text rather than as supplementary movies.
- The incisures in Fig. 4 will be difficult for many readers to visualize. My experience was that once I saw one of them, I began to see the others. The incisures in Fig. 5 are, on the other hand, very easy to see. If Fig. 5 had come before Fig. 4, I would have had no problem. The authors may wish to exchange these two figures or to supply a cartoon for one of the rods in Fig. 4, so that the reader can more easily understand what he or she should bel trying to see.
- It is unclear to me why the authors are so fond of their untested theory that incisures "likely serve to protect the flat lamellar disc membranes from undesirable deformations" but seem skeptical of the notion that incisures are present and especially numerous in rods of large diameter to aid longitudinal diffusion. The later notion is supported not only by theoretical calculations but also by common sense.
Significance
This manuscript presents a clear and convincing description of disc formation and the role of the protein peripherin in the formation of disc incisures.
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Reply to the reviewers
RC-2022-01805
We thank all reviewers for their careful analysis of our manuscript, constructive suggestions and support of our work.
Reviewer 1
The authors show that proximity of early mouse embryo blastomere chromosomes to the cell cortex activates the Polar Body Extrusion pathway to generate cell fragments. The authors use live cell imaging in control and Myo1C and dynein knockdown embryos to document accumulation of actin and myosin near chromosomes that come in close proximity to the cell cortex, which correlates with the increased fragmentation of the mutant blastomeres. The live imaging data are nicely presented and the results are well quantified. I have two major comments, and some minor comments on clarity, for the authors consideration in revising the manuscript.
Major comment:
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The authors imply that Myo1 and dynein knockdowns result in an increase in the number of cells where chromosomes come in close proximity to the cell cortex. Apparently the spindle anchoring defects are meant to indicate that such defects are responsible for the increased frequency of abnormal chromosome proximity to the cortex. But the authors never actually document whether chromosomes in fact do come into proximity to the cortex more often in the mutant than in control embryos. The authors should clarify if they think the spindle anchoring defect does result in abnormal chromosome distributions. Can the authors somehow quantify a defect in overall chromosome positioning in mutant vs control blastomeres? Presumably the movies the authors already have could be used to provide such quantification?
We thank the reviewer for this opportunity to correct our previous assumptions. Following the reviewer’s suggestion, we tracked the distance between the cell surface and the center of the chromosomes cluster throughout mitosis. We found little difference in this distance between control and Myo1cKO embryos (Fig S3a), unlike what we had initially implied. This distance seemed more variable in Myo1cKo embryos than in control ones, suggesting that chromosome movements may be more erratic but analysis of this variation for individual cells did not show consistent differences between control and Myo1cKO embryos either (Fig S3b). Therefore, we cannot explain the increased signaling with differences in proximity of the chromosomes to the cortex during mitosis.
Instead, as already hinted in our initial manuscript as an additional factor, we find that signaling from chromosomes to the cortex can occur for an extended time in embryos with impaired spindle anchoring.
We had already measured that mitotic spindles persisted for a longer time in Myo1cKO embryos than in control ones (Fig 2b), as well as in ciliobrevin treated embryos as compared to DMSO treated ones (Fig S2b). To strengthen this data, we performed additional experiments in which we injected mRNA encoding fluorescent lamin-associated protein 2b (Lap2b-GFP) to track the breakdown and reassembly of the nuclear envelope. Consistent with the mitotic spindle persisting for a longer time in Myo1cKO embryos than in control ones, it generally takes more time for Myo1cKO embryos to reassemble their nuclear envelope than for control embryos (50 min vs 70 min, n = 8 control and 15 Myo1cKO embryos, p = 0.0161, Fig S3c-d, Movie 5). Taken together, the nuclear envelope and spindle data indicate that, although chromosomes are not closer to the cortex in Myo1cKO embryos than in control ones, they spend more time outside of the nucleus. This should give chromosomes extended opportunities to signal to the cortex and explains how difficulties with chromosome separation can lead to the hyper-activation of the polar body extrusion pathway.
We have revised our manuscript accordingly.
Near the end of the paper, the authors discuss how cell with bent/un-anchored spindles are more prone to fragmentation, referring to Figure 2. But Figure 2 does not document a correlation between blastomeres with bent spindles and increased fragmentation. Rather it shows an increase in bent spindles and in fragmentation in mutant vs control, but does show that they occur together. The authors should more accurately describe their results or provide such a correlation with additional data.
We thank the referee for pointing out this missing information.
To support our conclusions, we now provide additional analyses of mitosis duration in non-fragmenting and fragmenting cells from Myo1cKO embryos. When cells fragment, their mitosis is consistently longer, as measured from the persistence of the mitotic spindle, than when not fragmenting (Fig 2c). This provides a direct correlation between spindle defects and fragmentation.
We now present these analyses in the revised manuscript.
Finally, in describing the data in Figure 3, the authors refer to persistence of the spindle and bending of the spindle as indicating problems with anchoring. It is not clear to me how either spindle persistence or bending relate to anchoring. The authors should explain how they are related if they are, and it would be better if the authors could document spindle displacement relative to the cell center or cortex to make their point more directly that anchoring is defective.
We apologize for not making this clearer in our initial manuscript. As others noted before (Kotak et al, 2012; Mangon et al, 2021), poorly anchored spindles show larger displacements or rotations during mitosis. Spindle persistence and bending may not be directly related to spindle anchoring defects but could reflect broader issues with spindle assembly and function caused by spindle anchoring defects. Since a previous in vitro study had identified that Myo1cKO is important for spindle anchoring (Mangon et al 2021) and that ciliobrevin, known for compromising spindle anchoring, phenocopied these aspects, we had initially focused on anchoring defects in our conclusions. We still stand by our conclusion that our data suggest spindle anchoring defects. Nevertheless, we agree that our observations report more general spindle defects and that anchoring may be only one of the defective aspects. Instead of “spindle anchoring defects”, we now simply mention “spindle defects” unless specifically discussing spindle straightness and rotation.
Minor comment.
The authors document in Figure 3 that Myo1C KO blastomeres have an enhanced response, with more myosin accumulating at the cortex in response to chromosomes. Why does knocking out one non-muscle myosin lead to enhanced accumulation of another? The authors note this effect but provide no discussion as to how it occurs. Some clarification might be helpful.
In our manuscript, we report that chromosome proximity to the cortex is associated with Cdc42 activation, which leads to cortical actin recruitment (Fig 4a-d). We also observe that non-muscle myosin II (Myh9) is recruited to the cortex when chromosomes come near (Fig 3d-f). Importantly, these phenomena occur in control embryos as well and not only in Myo1cKO embryos.
We propose that this recruitment is further increased in Myo1cKO embryos (Fig 3f) because chromosomes spend more time outside of the nuclear envelope (Fig 2). This leads to fragmentation and is not specific to Myo1cKO since the same occurs after ciliobrevin treatment (Fig S2).
The authors provide a significant advance in our understanding of why early mammalian embryos, especially early human embryos, are so prone to fragmentation. Their data strongly support their conclusion that increased proximity of chromosomes to the cortex does lead to activation of the PBE response, which is an interesting and well documented finding. However, unless the authors can address my major comments and provide more direct evidence for increased displacement of chromosomes being responsible for increased fragmentation, they should revise their manuscript to acknowledge that they have not directly quantified chromosome positioning and thus do not conclusively document that it is responsible for increased fragmentation in the mutant oocytes.
We thank the reviewer for their thorough analysis of our data and for giving us the opportunity to correct some of the aspects of our study.
Reviewer 2
The manuscript "Ectopic activation of the polar body extrusion pathway triggers cell fragmentation in preimplantation embryos" by Pelzer and colleagues is focused on mechanism of cell fragmentation in early preimplantation embryos. This is an important issue, since fragmentation, with subsequent cell loss, has significant impact on early development of human embryos in vitro.
To study the cell fragmentation within the embryo, authors used mouse model system. However, since during the mouse preimplantation development blastomere fragmentation is less frequent than in human embryos, they used knockout of unconventional myosin-Ic to induce fragmentation of embryonic blastomeres with higher frequency and a similar morphology, known from human embryos.
Using their Myo1c KO, authors confirmed previous observation that reduction of myosin-Ic impairs spindle anchoring and they further show that the defects in spindle anchoring are linked to cell fragmentation. And that similar defects could be induced by chemical inhibition of dynein. Importantly, the defects in anchoring, causing aberrant spindle movements, bring spindle and chromosomal DNA to the proximity of the cell cortex. This induces local changes in concentration and organization of actin and myosin IIA and leads into fragmentation. Authors show that this pathway shares similarity with mechanism of polar body extrusion (PBE) during meiosis, namely that it requires active Cdc42-mediated actin polymerization or Ect2 signaling. And also, that important role in cell fragmentation is played by cell surface tension. Based on their results, authors propose that cell fragmentation within the embryo is triggered either by hyperactivation of PBE pathway in cells with normal surface tension, or by PBE pathway activation in cells with higher contractility.
This manuscript brings important information about mechanism, which might contribute to the high incidence of blastomere fragmentation in human embryos. I have not identified any important issues with experimental work or conclusions and therefore I recommend this paper for publication. The results from the mouse model system however need to be verified by further studies in human or similar embryos, which naturally exhibit higher fragmentation.
We thank the reviewer for their careful examination of our manuscript and data.
We agree that it would be important to verify the validity of our findings in other species. We have considered performing experiments with human embryos.
Ideally, we would need embryos in their early cleavage stages (zygote to 4-cell stages) to be able study fragmentation without perturbing morphogenetic movements, which begin at the 8-cell stage. Such early embryos are particularly rare, which further requires careful experimental design.
Ideally, such carefully designed experiment would not cause additional fragmentation (as we have mostly done in the present study) but rather reduce this deleterious process. In light of our experiments shown in Fig 4c-d, inhibiting Cdc42 would be a good way to reduce polar body extrusion signaling. Injection of DNCdc42 mRNA would be embryo-consuming to setup. We tried a Cdc42 chemical inhibitor on mouse embryos with unreliable results. Therefore, we do not yet feel confident in using precious human embryos with our currently available options.
Another complication is administrative since this project was funded by the ERC, which does not allow experimentation with human embryos.
As for studying the phenomenon in species other than mouse or human, we currently have limited access to other mammalian species. Generally, other mammalian embryos are less well characterized and, in particular, the species-specific fragmentation behavior would need to be characterized before initiating any attempt to reduce it.
We hope that the reviewers will agree that the current manuscript, describing and dissecting a previously unknown mechanism, makes sufficient advances to be published without the need to assess its evolutionary conservation.
This study revealed important mechanism, which might be responsible for inducing fragmentation of blastomeres in early preimplantation embryos. Authors use mouse knockout model system and therefore the results should be verified in other species, in which the embryos show higher fragmentation naturally. The manuscript provides evidence that pathway, leading into PBE in oocytes, remains operational also in embryos and might contribute to blastomere fragmentation in case when spindle loses anchoring to the membrane. The results of this manuscript should be of interest not only to the researchers in reproduction, but also to the general audience.
Reviewer 3
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The manuscript discussed interesting and relevant topics in which the Authors addressed the effects of mouse Myo1C knock out on cell fragmentation and spindle anchoring defects. The authors found that fragmentation occurs in mitosis after ectopic activation of actomyosin contractility by signals emanating from DNA.
Reviewer #3 (Significance (Required)):
This is an excellent report dealing with significant technical methodologies. I find no fault in the methods, data analysis, or conclusions. I only have two comments. First, the authors should expand on the previous findings about the of the role of Myo1c during early preimplantation development. Second, the discussion should be expanded to compare the results of this study with those of previous/related studies (e.g., other factors involve in fragmentation and spindle anchoring). Finally, I was not able to open movie#2 and movie#8 so they may need to be re-uploaded.
We thank the reviewer for their careful assessment of our study.
We apologize for not discussing enough the previous research on Myo1c. To our knowledge, there is only one previous study reporting the effect of a point mutation on Myo1c on mouse ear physiology (Stauffer et al 2005). This is the first study on the role of Myo1c during mouse development. At this point, we would like to stress that our study, while partially based on the KO of Myo1c, is about cell fragmentation, which we induce experimentally in three independent ways: Myo1c KO, ciliobrevin treatment or Ect2 overexpression.
Regarding fragmentation, to our knowledge there is simply no convincing mechanism to explain this phenomenon. One study proposed that membrane threads connecting the cell surface to the zona pellucida could pull on cells and promote fragmentation (Derick et al 2017). However, fragmentation also occurs without zona pellucida, and hence without threads pulling on cells’ surfaces (Yumoto et al 2020). Other than that, fragmentation was associated with mitosis and general cytoskeleton defects, without no clear mechanism (Alikani 1999, Fujimoto et al 2011, Daughtry et al 2019).
We have now expanded these discussions.
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Referee #3
Evidence, reproducibility and clarity
The manuscript discussed interesting and relevant topics in which the Authors addressed the effects of mouse Myo1C knock out on cell fragmentation and spindle anchoring defects. The authors found that fragmentation occurs in mitosis after ectopic activation of actomyosin contractility by signals emanating from DNA.
Significance
This is an excellent report dealing with significant technical methodologies. I find no fault in the methods, data analysis, or conclusions. I only have two comments. First, the authors should expand on the previous findings about the of the role of Myo1c during early preimplantation development. Second, the discussion should be expanded to compare the results of this study with those of previous/related studies (e.g., other factors involve in fragmentation and spindle anchoring). Finally, I was not able to open movie#2 and movie#8 so they may need to be re-uploaded.
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Referee #2
Evidence, reproducibility and clarity
The manuscript "Ectopic activation of the polar body extrusion pathway triggers cell fragmentation in preimplantation embryos" by Pelzer and colleagues is focused on mechanism of cell fragmentation in early preimplantation embryos. This is an important issue, since fragmentation, with subsequent cell loss, has significant impact on early development of human embryos in vitro.
To study the cell fragmentation within the embryo, authors used mouse model system. However, since during the mouse preimplantation development blastomere fragmentation is less frequent than in human embryos, they used knockout of unconventional myosin-Ic to induce fragmentation of embryonic blastomeres with higher frequency and a similar morphology, known from human embryos.
Using their Myo1c KO, authors confirmed previous observation that reduction of myosin-Ic impairs spindle anchoring and they further show that the defects in spindle anchoring are linked to cell fragmentation. And that similar defects could be induced by chemical inhibition of dynein. Importantly, the defects in anchoring, causing aberrant spindle movements, bring spindle and chromosomal DNA to the proximity of the cell cortex. This induces local changes in concentration and organization of actin and myosin IIA and leads into fragmentation. Authors show that this pathway shares similarity with mechanism of polar body extrusion (PBE) during meiosis, namely that it requires active Cdc42-mediated actin polymerization or Ect2 signaling. And also, that important role in cell fragmentation is played by cell surface tension. Based on their results, authors propose that cell fragmentation within the embryo is triggered either by hyperactivation of PBE pathway in cells with normal surface tension, or by PBE pathway activation in cells with higher contractility.
This manuscript brings important information about mechanism, which might contribute to the high incidence of blastomere fragmentation in human embryos. I have not identified any important issues with experimental work or conclusions and therefore I recommend this paper for publication. The results from the mouse model system however need to be verified by further studies in human or similar embryos, which naturally exhibit higher fragmentation.
Significance
This study revealed important mechanism, which might be responsible for inducing fragmentation of blastomeres in early preimplantation embryos. Authors use mouse knockout model system and therefore the results should be verified in other species, in which the embryos show higher fragmentation naturally. The manuscript provides evidence that pathway, leading into PBE in oocytes, remains operational also in embryos and might contribute to blastomere fragmentation in case when spindle loses anchoring to the membrane. The results of this manuscript should be of interest not only to the researchers in reproduction, but also to the general audience.
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Referee #1
Evidence, reproducibility and clarity
The authors show that proximity of early mouse embryo blastomere chromosomes to the cell cortex activates the Polar Body Extrusion pathway to generate cell fragments. The authors use live cell imaging in control and Myo1C and dynein knockdown embryos to document accumulation of actin and myosin near chromosomes that come in close proximity to the cell cortex, which correlates with the increased fragmentation of the mutant blastomeres. The live imaging data are nicely presented and the results are well quantified. I have two major comments, and some minor comments on clarity, for the authors consideration in revising the manuscript.
Major comment:
- The authors imply that Myo1 and dynein knockdowns result in an increase in the number of cells where chromosomes come in close proximity to the cell cortex. Apparently the spindle anchoring defects are meant to indicate that such defects are responsible for the increased frequency of abnormal chromosome proximity to the cortex. But the authors never actually document whether chromosomes in fact do come into proximity to the cortex more often in the mutant than in control embryos. The authors should clarify if they think the spindle anchoring defect does result in abnormal chromosome distributions. Can the authors somehow quantify a defect in overall chromosome positioning in mutant vs control blastomeres? Presumably the movies the authors already have could be used to provide such quantification?
- Near the end of the paper, the authors discuss how cell with bent/un-anchored spindles are more prone to fragmentation, referring to Figure 2. But Figure 2 does not document a correlation between blastomeres with bent spindles and increased fragmentation. Rather it shows an increase in bent spindles and in fragmentation in mutant vs control, but does show that they occur together. The authors should more accurately describe their results or provide such a correlation with additional data.
- Finally, in describing the data in Figure 3, the authors refer to persistence of the spindle and bending of the spindle as indicating problems with anchoring. It is not clear to me how either spindle persistence or bending relate to anchoring. The authors should explain how they are related if they are, and it would be better if the authors could document spindle displacement relative to the cell center or cortex to make their point more directly that anchoring is defective.
Minor comment.
The authors document in Figure 3 that Myo1C KO blastomeres have an enhanced response, with more myosin accumulating at the cortex in response to chromosomes. Why does knocking out one non-muscle myosin lead to enhanced accumulation of another? The authors note this effect but provide no discussion as to how it occurs. Some clarification might be helpful.
Significance
The authors provide a significant advance in our understanding of why early mammalian embryos, especially early human embryos, are so prone to fragmentation. Their data strongly support their conclusion that increased proximity of chromosomes to the cortex does lead to activation of the PBE response, which is an interesting and well documented finding. However, unless the authors can address my major comments and provide more direct evidence for increased displacement of chromosomes being responsible for increased fragmentation, they should revise their manuscript to acknowledge that they have not directly quantified chromosome positioning and thus do not conclusively document that it is responsible for increased fragmentation in the mutant oocytes.
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Reply to the reviewers
We thank the reviewers for their constructive feedback on our manuscript. They did a very comprehensive and helpful job of laying out some key areas that could be improved. We were heartened by the fact that there was a fair amount of overlap between the two reviewers, and that comments were largely addressable without further experimentation.
Below, we provide a summary of how we have attempted to address the comments and concerns from both reviewers. We also provide the rationale and action items for our responses. Overlapping comments from both reviewers have been consolidated and responded to together.
Comment 1 (Reviewer #1, Minor Comment 1 & Reviewer #2, Significance)
Both reviewers raised concerns about our choice to focus on essential genes in our CRISPRi screen, which could potentially underestimate the role of non-essential factors contributing to Tae1 sensitivity or resistance.
Rationale: We agree with the reviewers that including non-essential genes could provide additional insights into the roles of non-essential factors in Tae1 sensitivity and resistance. We believe our focus on essential genes contributes a unique perspective to the field, as there already exists a body of work that interrogates non-essential genes in this space. Here are some citations that represent this body. We will highlight these better in the manuscript.
Lin, H.-H.; Yu, M.; Sriramoju, M. K.; Hsu, S.-T. D.; Liu, C.-T.; Lai, E.-M. A High-Throughput Interbacterial Competition Screen Identifies ClpAP in Enhancing Recipient Susceptibility to Type VI Secretion System-Mediated Attack by Agrobacterium Tumefaciens. Front Microbiol 2020, 10, 3077. https://doi.org/10.3389/fmicb.2019.03077.
Hersch, S. J.; Sejuty, R. T.; Manera, K.; Dong, T. G. High Throughput Identification of Genes Conferring Resistance or Sensitivity to Toxic Effectors Delivered by the Type VI Secretion System; preprint; Microbiology, 2021. https://doi.org/10.1101/2021.10.06.463450.
Additionally, our screen was experimentally optimized for essential genes using our approach. The knockdown strategy is useful specifically for essential genes because E.coli is phenotypically very sensitive to essential gene perturbations (see more here: https://doi.org/10.1128/mBio.02561-21). While it would have been ideal to include non-essential genes too, doing so would require a different additional optimization that we believe would have diluted our bandwidth for this study. We do thank the reviewers for recognizing how much effort went into this!
We do acknowledge this is a limitation and want to make sure the readership is aware of that. Ideally, one could do more rigorous side-by-side comparisons between studies if the approaches, set-up, and assays are the same. Unfortunately, due to differences in experimental set-up, we could not directly compare with the non-essential screens. We hope others will pick up where we left off. Here are some action items we can take to increase the odds of that:
In the Introduction, we will mention other studies and highlight the need to investigate essential genes side-by-side with non-essential. (Lines 64-7) In the Discussion, we will add a sentence that acknowledges the importance of exploring non-essential genes for a more comprehensive understanding of Tae1 sensitivity and resistance. (Lines 484-5)
Comment 2 (Reviewer #1, Minor Comment 5 & Reviewer #2, Major Comment)
Both reviewers mentioned that the dormancy state in msbA-KD cells is not well characterized and its relationship with Tae1 resistance is not convincingly shown.
Rationale: We agree that our manuscript does not clearly pin down whether Tae1 resistance is linked to a true dormancy state. There are some intriguing similarities between what we observe and what is classically known as “dormancy” or “persistence”, which have specific definitions. Although we don’t yet have a concrete reason to think it’s NOT those states, we also don’t have sufficient data to point to it clearly being the same at a mechanistic or cellular level. This is merely a hypothesis that our work suggests. We would love to see others follow up on this, as we suspect there are overlaps and potentially additional cellular states that have yet to be clearly defined in this field of bacterial physiology.
Here is how we propose to address this concern:
We simplified our language to be more descriptive and less loaded in terms of nomenclature around dormancy or persistence. Namely, we are referring to the cells in a more descriptive way with “slowed growth.” This allows us to clearly describe what we observe without attempting to ascribe mechanism or anything beyond that. It doesn’t fundamentally change the overarching interpretation of our study. (Lines 444, 490,497-9) In the Discussion, we will add text emphasizing the need for follow-up studies to fully address whether there is indeed a connection between Tae1 resistance and slowed growth. (Lines 491-3)
Comment 3 (Reviewer #2, Major Comment)
The reviewer asks if the degradation of the sugar backbone is also required for lysis or if it is just the crosslinking step that is important.
Rationale: This is an astute point. We acknowledge that the degradation of the sugar backbone may play a role in lysis, and it’s predicted that this may be why the Pae H1-T6SS delivers a second PG-degrading toxin (Tge1), a muramidase that targets the sugar backbone. The most parsimonious conclusion from past studies by us and others is that Tae1 is critical for lysis, but not sufficient in the absence of any backbone-targeting enzyme. Indeed, many T6SS-encoding bacterial species also encode >1 type of PG-degrading enzyme, which may speak precisely to the reviewer’s point. However, it should also be noted that there may be endogenous enzymes with activities that can be leveraged alongside these toxins for the same effect.
Action items:
In the Discussion, we will add a sentence addressing the potential role of sugar backbone degradation in the lysis process and the need for future research on this topic. (Lines 524-6)
Comment 4 (Reviewer #1, Minor Comment 2)
The reviewer asks why lptC-KD leads to sensitivity to Tae1, while msbA-KD leads to resistance, considering both genes are implicated in LPS export.
Rationale: We appreciate the reviewer's careful attention to the underlying biology. They are absolutely correct in pointing this difference out. Our interpretation is that the different phenotypes may indicate that although the LPS biosynthesis superpathway intersects with PG synthesis, lptC and msbA may intersect with PG synthesis in distinct ways. We can address this concern through the following:
We will add a sentence in the Discussion section providing our interpretation of the different phenotypes observed for lptC-KD and msbA-KD. (Lines 508-13)
Comment 5 (Reviewer #1, Minor Comment 4)
The reviewer notes that the contribution of msbA to Tae1 resistance appears minor based on the results in Figure 3d.
Rationale: There are actually two aspects to this concern, which we note below. We found it difficult to fully capture it in the manuscript, but our thoughts are as follows.
(1) Technical viewpoint:
Bacterial competition experiments are inherently noisy. The quantitative read-out is easily impacted by a number of parameters, including cellular density, input ratio between competitor cell types, growth stage, and possibly other environmental factors that are difficult to predict. In general, our view is that we should avoid over-indexing on the degree of the phenotype, focusing more on the direction of the phenotype (loss of statistically-significant Tae1 sensitivity) and the fact that it is reproducible in our hands. Furthermore, our argument is bolstered by clear validation of the loss of Tae1 sensitivity through orthogonal lysis assays (Fig. 4a-c).
(2) Biological viewpoint
It is challenging to isolate the specific interaction between Tae1 and individual genetic determinants, as we think it’s a complex system with multiple factors simultaneously at play. It is crucial to acknowledge that the unique contribution of Tae1 is only a part of the T6SS. There may be other compensatory actions that influence the outcomes observed, such as upregulation of non-Tae1 toxins, regulation of system activation/firing, timing and location of T6S injections, etc. We think these are exciting possibilities and that more groups should delve into the context-dependent dynamics of the system. Although outside the scope of our manuscript, we would be open to suggestions for how we can further emphasize this point.
Comment 6 (Reviewer #2, Minor Comment)
The reviewer recommends that we discuss whether our findings are specific to Tae1 or if they can be extrapolated to other toxins.
Rationale: We understand the reviewer's interest in understanding the broader implications of our findings. Although our study focuses specifically on Tae1, we believe that our findings may provide insights into the mechanisms of sensitivity and resistance to other toxins that target the cell wall. However, experimentally investigating this would fall outside the scope of our current manuscript.
Additional Minor Revisions
Table 1: I would label MsbA and LptC as "LPS transport" and not "LPS synthesis" (Reviewer 1) Rationale: We agree that using “LPS transport” to describe the gene functions for lptC and msbA is more specific to their functions.
Table 1 was updated to change the “pathway/process” categorizations for lptC and msbA from “LPS synthesis” to “LPS transport”. In line with this comment, we also changed the pathway/process categorization for murJ (Lipid II flippase) to “PG transport”. Figure 3 legend: "...deformed membranes .........are demarcated in (g) and (h)" (Reviewer 1) We thank the reviewer for pointing out the missing text in this figure legend.
We corrected the error by adding the missing text back in Figure 3. Line 339-341: Supp. Fig. 9 should be Supp. Fig. 8 (Reviewer 1) Referenced Supp. Fig. was corrected. * Second, (L422-425) the authors conclude that their data demonstrate a "reactive crosstalk between LPS and PG synthesis". I disagree. There is no information in the paper that this is the case. The authors can only suggest that cross talk may occur. (Reviewer 2) We agree. Line 421-2: replaced “demonstrate” with “suggest” to soften the argument. *
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Referee #2
Evidence, reproducibility and clarity
Summary:
This study reports the finding that lipopolysaccharide integrity modulates bacterial sensitivity to a Type-6-secreted bacterial toxin. The authors used the Tae1 amidase produced by the P. aeruginosa T6SS and Escherichia coli bacteria as prey cells as a model system to test the effect of knockdowns in essential gene expression of the prey. This was accomplished by constructing a library of knockdown (KD) genes based on Crispr/Cas9 and selecting for those targets where E. coli prey is not killed. The screen revealed, as expected, that KD genes encoding cell wall synthesis assembly (and bamA, involved in OM protein assembly) enhanced the sensitivity to Tae1. In contrast, KD targets in genes involved in lipid metabolism and lipopolysaccharide synthesis conferred resistant to the amidase toxin. The authors hypothesized that non-PG components of the cell envelope may shape Tae1 toxicity and undertook a more detailed analysis of the effects of knocking down one of these genes, msbA, using a various biochemical and imaging approaches. The MsbA protein is an ATPase permease that plays an essential role in flipping newly synthesized lipid A across the bacterial inner membrane. The authors show that resistance to Tae1 in msbA-KD is independent of cell wall hydrolysis (meaning that the Tae1 remains active), PG synthesis is suppressed (despite PG is still Tae1 sensitive), and that protein synthesis and growth is suppressed. This latter observation suggests that the E. coli prey enters a persistent (dormant) state that protects it from Tae1 toxicity. The authors conclude that Tae1 susceptibility in vivo is determined by cross talk between essential cell envelope pathways and the general growth state of the cell.
Major comments:
This is a nice study unravelling cellular off target factors that affect the killing in vivo by a T6SS toxin. In that sense the study is novel since the interplay of T6SS effectors in the context of the physiological state of the prey cell has not been directly investigated. so this study adds new information to the literature in the field.
I have several comments concerning the interpretation of the results.
First, it is interesting that Tae1, being an amidase, can be the sole responsible for PG degradation. The enzyme cleaved the peptide bridges but has no effect on the PG backbone. The study was not designed to pick up autolysins (since only essential genes were targeted) but one would assume that degradation of the sugar backbone must also be required for lysis.
Second, (L422-425) the authors conclude that their data demonstrate a "reactive crosstalk between LPS and PG synthesis". I disagree. There is no information in the paper that this is the case. The authors can only suggest that cross talk may occur.
Third, Tae1 maximal effect is present when new PG is made, which also begs the question about the location of this protein in the PG mesh. Like B-lactam and other PG-active antibiotics, the effect of Tae1 requires active cell growth. This is also consistent with the authors' finding that the msbA-KD bacterial cells enter a state of dormancy or persistence, which will make them capable of overcoming Tae1 toxicity.
Fourth, an important outcome of protein synthesis inhibition and PG synthesis is increased oxidation and lipid peroxidation. This could also influence the results obtained in this study. It would be consistent with the other targets observed, which compromise lipid metabolism and membrane trafficking and secretion.
Referees Cross-commenting
Based on my own review and that of Reviewer 1, I think we both agree that there are 2 major limitations in this work: (i) the KD library only targets essential genes and this would potentially miss non-essential genes that when targeted for mutated could lead to synthetic lethal phenotypes that could be more revaling than a general defect protein synthesis, etc. and (ii) the dormancy state is not well characterized.
Despite these points the study is very nicely done with a huge amount of work.
Significance
This is an important study addressing experimentally the complexities of bacteria-bacteria interactions in the context of predator-prey interplay. The T6SS effectors affecting PG appear to have the same characteristics as known antibiotics and bacteria use similar strategies to protect themselves from PG attack. This is not only to increase growth as an escape approach but also to reduce it to a point in which the target cell cannot be effectively killed despite the presence of the toxin.
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Referee #1
Evidence, reproducibility and clarity
Summary
The manuscript by Trotta and co-workers investigates functions that shape E. coli envelope when cells are targeted by the cell-wall degrading toxin Tae1. The experimental setting employed by the authors is well thought and is based on the competition engaged by P. aeruginosa (Pae) expressing the type 6 secretion system (T6SS) against E. coli cells. In this context, the authors used an arrayed library of chromosomally encoded CRISPRi strains targeting essential genes of E. coli (knockdowns, KDs) to identify functions that increase or decrease E coli fitness following interbacterial competition with Pae cells expressing Tae1. The majority of genes whose depletion makes E. coli cells more sensitive to the toxin are implicated in PG synthesis while depletion of genes implicated in other cell envelope processes can result in toxin sensitivity or resistance. Among genes whose depletion makes E. coli cells more resistant to the toxin the authors selected those implicated in LPS biogenesis (msbA-KD and lpxK-KD), to investigate the hypothesis that non-PG components of the cell envelope may also shape Tae1 toxicity. While resistance to lpxK-KD to Tae1 could not be validated in the reconstructed strain likely due to a polar effect, the reconstituted msbA-KD gained Tae1 specific resistance. Further characterization of the msbA-KD revealed that Tae1 resistance is independent of cell wall hydrolysis and PG dynamics. By showing that both slow growth and decreased protein synthesis is specifically linked to Tae1 resistance in msbA-KD cells the authors suggest that a persistent state, induced by block of LPS biogenesis, helps depleted msbA cells to resist the toxic activity of Tae1. Overall, the experimental approach is solid, the developed in vivo screen to identify genetic interaction between secreted Tae1 and E coli is smart and well thought. I also acknowledge the huge work performed by the authors to characterize selected KD strains.
My few comments to the manuscript are reported below.
Major Comments
There are no major comments
Minor Comments
- Why the authors limit the search of functions that help P. aeruginosa to antagonize E. coli cells only to essential genes? I understand that the available CRISPRi strains collection (developed by Carol Goss and co-workers) is only targeting essential genes, but the rationale for this choice should be discussed. This approach is inevitably underestimating the role of perhaps important non-essential factors contributing to Tae1 sensitivity/resistance.
- It is intriguing that in Table 1 lptC is listed among the genes whose depletion leads to sensitivity to Tae1 whereas msbA transcriptional down regulation leads to resistance. Both LptC and MsbA are implicated in LPS export to the cell surface, and one would expect that their down-regulation leads to similar output in competition experiments with P. aeruginosa. Can the authors comment on that?
- Based on results reported in Figure 3 d (fold change msbA-KD CFU) the contribution of MsbA to Tae1 resistance seems minor. Can the authors comment?
- Based on the observation that msbA-KD cells arrest growth, do not divide, and decrease protein synthesis, the authors suggest that these cells enter a persistent state which could protect against Tae1 activity by passive tolerance. In support of this hypothesis the authors refer to published work (Roghanian et al. PloSOne 2019) showing that CRISPRi KD in lpxA (the first gene of the LPS biosynthetic pathway) triggers a dormancy state to respond to imbalances in outer membrane biogenesis. In this manuscript Roghanian and co-workers show that CRISPRi KD in lptA (encoding the periplasmic component of the LPS export machinery) share the same phenotypes as lpxA. These observations bring me again to the comment n. 2 above. I think that the authors should comment on this. In my opinion this is the weakest part of the manuscript as it is not convincingly showed i) that msbA-Kd cells enter a dormancy state, ii) how this dormancy state is related to Tae1 resistance.
Table 1: I would label MsbA and LptC as "LPS transport" and not "LPS synthesis"
Minor points
Figure 3 legend: "...deformed membranes .........are demarcated in (g) and (h)"
Line 339 341: Supp. Fig. 9 should be Supp. Fig. 8
Significance
This study aims at understanding how Tae1, a PG-degrading toxin secreted by T6SS specifically aids P. aeruginosa in antagonizing E. coli cells in vivo. By exploiting a smart in vivo genetic screen, the authors want to understand at the molecular level the interplay between Tae1 and essential functions in E. coli. The study of interspecies competition offers the possibility to investigate and dissect complex physiological processes and the interactions between them. The work is solid and the experimental plan well-conceived. However, the in vivo genetic screen is limited to the search of essential functions implicated to sensitivity or resistance to the secreted toxin. Such an approach is inevitably underestimating the role of perhaps important non-essential factors contributing to Tae1 sensitivity/resistance. Also, as indicated above, I think that the authors did not convincingly show i) that msbA-Kd cells enter a dormancy state, ii) how this dormancy state is related to Tae1 resistance.
Audience Broad audience / basic research
Expertise in outer membrane biogenesis
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Reply to the reviewers
The authors would like to thank the reviewers for their valuable comments and suggestions. We have carefully considered all of the points raised and revised our manuscript accordingly. In the rebuttal letter below, we have extensively discussed all the different concerns and adjustments we made to our work. In what follows the reviewers’ comments are in blue and the authors’ responses are in black. The additions and changes to the main and supplementary text of the manuscript are highlighted in yellow.
*Reviewer #1 (Evidence, reproducibility and clarity (Required)): *
*In their paper entitled "CD38 promotes hematopoietic stem cell dormancy via c-Fos", Ibneeva et al., present a set of data predominantly from mouse HSCs where they explore the cell cycle kinetics and self-renewal capacity of LT-HSCs expressing (or not) CD38. They perform a series of sophisticated in vitro and in vivo experiments, including transplantations and single cell cultures and arrive at the conclusion that CD38 can fractionate LT-HSCs that are more deeply quiescent. Overall, it is an interesting question and would be of interest to experimental hematologists. That said, I had a number of issues that concerned me throughout the manuscript with regard to the robustness of the conclusions around CD38 and I have tried to detail these below.
Major concerns: *
*1) Novelty - It was unclear what the relationship of this CD38+ fraction had with other "segregators" of LT-HSCs - e.g., how does it compare with the Sca1 fractionation of Wilson et al, Cell Stem Cell 2015 or Gprc5c of Cabezas-Wallschied Cell 2017? Even if CD38 fractionated LT-HSCs, it was unclear what it would give beyond these two molecules (especially re: Sca-1 which is also a cell surface marker). *
Response:
We agree with the reviewer that further elaboration of this point with additional data would be helpful. We compared the expression of Sca-1 in the population of LT-HSCs (Lin- Kit+ Sca-1+ CD48- CD150+ CD34- CD201+) based on the gating strategy from the paper Wilson et al, Cell Stem Cell 2015. We found that all LT-HSCs (independent of CD38 expression) express Sca-1 at a high level and can be quantified as Sca-1hi (we have added these data in Fig. S2A). Thus, CD38 subfractionates LT-HSCs, and considering that we have shown that CD38+ are more quiescent (Fig. 3) and have higher repopulation capacity compared with CD38- LT-HSCs (Fig. 2E-G), we conclude that CD38 should be used in addition to Sca-1 to define dormant LT-HSCs.
We found that CD38+ dormant HSCs expressed Gprc5c mRNA at higher levels than CD38- LT-HSCs (Fig. 5D). Therefore, we cannot exclude that CD38+ and Gprc5c+ identify the same population of dormant HSCs. However, Cabezas-Wallscheid Cell 2017 used the reporter Gprc5c-EGFP mouse strain, which is not widely available. In contrast, we propose to use readily available antibodies against CD38 for efficient isolation of dormant HSCs. Moreover, to define CD38+ dormant HSCs, researchers do not need to use the CD38KO mice as a negative control, it would be sufficient to use total bone marrow cells to identify the CD38+ population for gating dHSCs (we have added this information to Fig. S2C and in the text: line 119-121: “We demonstrated that total bone marrow cells can be used to define the CD38+ fraction in the absence of CD38 knock-out mice (CD38KO) (Fig. S2C), providing the possibility of an internal positive control for easy identification of CD38+ cells”.
*Claims of CD38+ superiority in transplantation - I was surprised with the claim of CD38 negative cells being a less functional HSC when they are clearly still very strong in secondary transplantation assays. Both 38+ and 38- cells strongly repopulate secondary animals and only 5 mice were shown in the Figure. The legend suggests another experiment was undertaken, but these data are not presented. Did they substantially differ in their chimerism in primary and secondary animals? Was the magnitude of difference between the two fractions similar in both experiments? Is there a reason that the data could not be plotted on the same graph?
*
We have added the data from the second experiment to the graphs and changed the figure legend accordingly (Fig. 2D-H), now for primary transplantation n=8, for secondary transplantation n=6 vs 7. These data show the same trend of higher repopulation capacity of CD38+ LT-HSCs compared to CD38- LT-HSCs, although with the larger magnitude of difference in primary transplantation. We agree with the reviewer that CD38- LT-HSCs strongly repopulate secondary animals. However, the higher percentage of chimerism in peripheral blood and bone marrow for CD38+ LT-HSC progeny indicates their superior repopulation and self-renewal capacity compared to CD38- counterparts.
Also, the typical experiment to establish a quantitative difference in HSC production would be a limiting dilution analysis with a much larger number of recipient animals - without such data it is difficult to ascertain how different the two fractions really are.
While we appreciate the reviewer's suggestion to include additional data on the amount of repopulating HSCs, we respectfully disagree as we believe that this information is beyond the scope of the current study, which only aims to assess the functional superiority of CD38+ LT-HSCs over CD38- LT-HSCs in side-by-side comparisons. Assessment of donor-derived cells’ frequency in peripheral blood and bone marrow relative to the frequency of competitors after transplantation of the same amount of HSCs (so-called chimerism level) is a widely accepted assay in the field to demonstrate the difference in the functionality between two HSC fractions (Sanjuan-Pla et al., Nature 2013; Gekas C and Graf T, Blood 2015; Bernitz J.M et al. Cell 2016; and others, including papers cited by the reviewer: Wilson et al., Cell Stem Cell 2015 and Cabezas-Wallscheid et al., Cell 2017). A limiting dilution experiment will provide more detailed characteristics of two HSC fractions, namely the quantitative difference (how many cells from the sorted population can repopulate). However, this experiment will not significantly change our conclusion that the CD38+ LT-HSC fraction is superior in repopulation and self-renewal capacity compared to the CD38- LT-HSC fraction, as sufficiently demonstrated in Fig. 2E-G.
Furthermore the claim that CD38- HSCs do not ever produce CD38+ cells is a bit premature with so few mice and confusingly presented data (e.g., Fig 2I is 5 pooled mice in a single histogram plot - were these concatenated flow files? If so, how were they normalised? Did the other experiment look the same? And were all CD38+ HSCs capable of giving rise to both CD38+ and CD38- cells or was it a subfraction of mice/samples?).
The plot provided in Fig. 2I is a FACS analysis of pooled cells from mice transplanted with CD38+ or CD38- LT-HSCs (we added a detailed explanation in figure legend 2, lines 701-703). We provided data from the second experiment in Fig. S2G. All CD38+ LT-HSCs could give rise to both CD38+ and CD38- HSC; we added data in Fig. S2H.
Cell Cycle status differences and grades of quiescence - Ki67 and DAPI are really quite tricky for discerning G0 versus G1 and no flow cytometry plots are provided for the reader to assess how this has been done. Could another technique (e.g., Hoechst/Pyronin) be used to confirm the results? Perhaps more concerning is the variability of the assay in the authors own hands. If I am interpreting things correctly, the plots in 3G, 3H and 3I in the platelet depletion, pIpC and 5FU experiments are >10% higher in the CD38- control arm than the data in 3A which make me worried about the robustness of the cell cycle assay to distinguish G0 from G1.
Ki67 and DAPI staining is a widely accepted technique for distinguishing G0 from G1. We provide flow cytometry plots in Fig. S2F (original figures, S3B - updated figures), which the referee may have overlooked. We added a reference to the Fig. S3B to figure legend 3 to make it more transparent for the readers. We would like to clarify the reviewer’s concern regarding the slightly different frequency of CD38- cells in the G0 phase of the cell cycle at steady state in Fig. 3A (original figures). Fig. 3A compares the cell cycle stages between CD38- and CD38+ HSCs, while Fig. 3B compares the same parameters for CD38- vs CD38+ LT-HSCs, which are enriched for quiescent HSCs by using additional surface markers. Therefore, it is correct to compare the data for LT-HSCs under stress (Fig. 3G-I, original figures) with the data for LT-HSCs at steady state in figure 3B (original figures). To make it less confusing for the reader, since the entire Figure 3 is devoted to LT-HSCs, we have moved Figure 3A to the supplementary Figures (Fig. S3A).
All experiments for Fig. S3A&3A, 3F, 3G, and 3H (updated figures), were performed separately, and we did not compare mice from different experiments to avoid differences due to technical details. However, the groups of mice for each specific treatment (ctrl vs. treatment at different time points) were analyzed on the same day, using the same amount of cells, the same master mix of antibodies, and the same FACS machine and settings to compare ctrl vs. treated mice (we added this information in the Materials and Methods section, lines 388-391). In addition, we performed a BrdU incorporation assay and label retention assay using H2B-GFP mice, which support our finding that CD38+ LT-HSCs are more quiescent than CD38- cells in the steady state.
Minor points: Figure 3I was really confusing - it says it is the gating strategy for GFP retaining LT-HSCs, but only shows GFP versus cKit
We reformulated the figure legend for 3D: “Representative plot defining GFP+ cells in LT-HSCs.”
Figure 4B suggests that only 40% of CD38+ cells divide in the first 3 days - are there survival differences or are the cells sat there as single cells? It would be important to carry these further to see if cells eventually divide.
This is a relevant and crucial point addressed by the reviewer. We did not find any significant difference in the survival of cells. We have added this data to the supplementary data - Fig. S4Q-R.
Reviewer #1 (Significance (Required)):
I believe the study will be of interest to specialist readers in the HSC field, especially those working on quiescence and G0 exit. At present, I think the conclusion of a true subfractionation is a bit premature, but there are pieces of data that do look exciting and warrant further investigation. It was a little unclear how this would advance beyond Sca-1 or Gprc5c fractionation for finding more primitive HSCs, but having cleaner markers is always a useful advance for the field.
We thank the reviewer for his/her positive evaluation of our study. In our work, we compared several functional aspects of CD38+ and CD38- LT-HSCs:
- We used four techniques (Ki67 and DAPI staining, BrdU incorporation assay, label retention assay, single-cell division tracing assay) and showed that CD38+ LT-HSCs are more quiescent than CD38- cells.
- We performed a serial transplantation assay and found that although CD38- LT-HSCs have the long-term repopulation capacity, they repopulate significantly less effectively than CD38+ LT-HSCs.
- We used a combination of surface markers (Lin- Kit+ Sca-1+ CD48- CD150+ CD34- CD201+) to define LT-HSCs; all of which belong to the Sca-1hi population according to Wilson et al, 2015. We further separated Sca-1hi LT-HSCs into CD38+ and CD38- cells and found that they differ in the repopulation capacity and quiescence in steady state and upon hematological stress. We conclude that CD38 surface staining should be used on top of Sca-1 to sort dormant LT-HSCs.
- We found that CD38+ dormant LT-HSCs differ from CD38- cells in gene expression and response to CD38 and c-Fos inhibitors. CD38+ LT-HSCs are characterized by higher cytoplasmic Ca2+ and cell cycle inhibitor p57 levels than CD38- LT-HSCs. Thus, we demonstrated that CD38 is not only a marker but also has a functional role in mediating HSC dormancy. We discovered that CD38/cADPR/Ca2+/c-Fos/p57 axis regulates CD38+ HSC dormancy. Taken together, our findings demonstrate that CD38+ LT-HSCs have superior properties compared to CD38- LT-HSCs and can be classified as dHSCs, providing a simple approach for their isolation and further study. Moreover, we uncovered the CD38-mediated molecular mechanism regulating HSCs dormancy.
Regarding my own expertise - I have spent ~20 years in the field undertaking single cell assays of normal and malignant mouse and human HSCs, including many of the core functional assays described in this paper and consider myself very familiar with the topic area.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Although the experiments were well done and supported their testing hypothesis, but the overall novelty of the whole work is not that strong and this is because:
-the use of CD38 to identify/select and to test mouse LT-HSCs' function in vivo (although not commonly used nowadays) was demonstrated a few times more than 20 years ago (Randall, et al., 1996: PMID: 8639761 and Tajima et al., 2001; PMID: 11313250); in fact, the authors didn't even reference/acknowledge these papers which they should have done so; hence, most of the results in Fig.2 were already known (despite this current work gave a more detailed/better analysis);
We agree with the reviewer that the previous findings using CD38 to separate HSPCs should be appreciated; however, we would like to point out that while the studies by Randall, et al., 1996: PMID: 8639761 and Tajima et al., 2001; PMID: 11313250 employ only 3 markers to discriminate HSPC (Lin- Sca-1+ Kit+), in our study, we performed for the first time a very detailed characterization of CD38+ cells using surface markers that were not available 20 years ago. We analyzed not only the HSC compartment but also different populations of multipotent progenitors. Modern surface marker combinations for the LT-HSC isolation allow us to show that both populations: CD38- and CD38+, can be classified as LT-HSCs in contrast to the data of Randall et al, where the authors did not find any long-term repopulating activity in the CD38- KLS compartment. Moreover, we showed the hierarchical relationships between these two populations. We appreciate the previous findings and recommendations of the reviewer, and have added citations (Randall, et al., 1996: PMID: 8639761 and Tajima et al., 2001; PMID: 11313250) and comment in the discussion section, lines 267-271:
In contrast to previous studies reporting that only CD38+ HSPC compartment from adult mice contains LT-HSCs (42, 43), in our study we demonstrated using modern surface marker combinations for the isolation of LT-HSCs that while both populations: CD38- and CD38+, can be classified as LT-HSCs, only CD38+ LT-HSCs display characteristics of dormant HSCs (4).’’
-it is known the generic roles of CD38 in producing cADPR, ADPR, etc and these can induce Ca2+ oscillation in cells; despite that, it was nicely demonstrated here that in mouse HSCs cADPR was the main signalling mediator;
We thank the reviewer for pointing this out; indeed, it has not been shown before how Ca2+ is regulated in HSCs.
the roles of cADPR in human CD34+ were demonstrated (Podesta et al., 2023; PMID: 12475890: when CD34+ HSPCs were primed in vitro with cADPR it resulted in enhanced short-term while maintaining long-term (secondary transplant) engraftment in NOD/SCID mice, probably (mechanisms were not determined at that time) inducing cycling/expansion of human CD34+CD38+ progenitors while inhibiting cycling (hence, better long-term maintenance) of CD34+CD38- HSPCs); on this note; the data presented in Fig.4 K and S5 should be eliminated as it adds little to their story and it can be quite confusing when comparing to mouse data unless the authors wish to explore in a more detailed way the human part.
We appreciate the reviewer’s valuable suggestion. However, we respectfully disagree with their interpretation because we do not believe that the technical aspects of the cited paper (Podesta et al., 2003; PMID: 12475890) are robust enough to support their conclusions. Podesta et al. concluded that in vivo and in vitro treatment with a high dose of cADPR (25-fold higher than the physiological dose, according to the authors' estimation) stimulates the expansion of HSC and progenitor cells. At the same time, they did not use any surface markers to define populations and studied total mononuclear cord blood cells, so no conclusions can be drawn regarding CD34+ CD38+ and CD34+ CD38- dynamics. Unfortunately, we cannot confirm the reliability of the HSC engraftment data presented by Podesta et al. This is because they did not analyze the chimerism of human cells in peripheral blood and bone marrow for sixteen weeks post-transplantation, which is considered a standard time period for assessing long-term engraftment of human HSCs in the field (Brehm M.A. et al., Blood 2012, Cosgun K.N. et al., Cell Stem Cell 2014, Takagi S. et al. Blood 2012). Instead, they counted only some CD34+ cells at three and eleven weeks after transplantation. Therefore, the role of cADPR in the regulation of human HSC quiescence remained unknown.
In our original study, we showed that blocking the CD38 ecto-enzymatic activity stimulated both human HSC and mouse HSCs to exit from the G0 phase of the cell cycle. The role of CD38 enzymatic activity can be conservative for mice and humans and needs to be further investigated in future studies on human HSCs. For this reason, we decided to keep Fig. 4K and S6 in the paper.
-Ca2+ induction in cells can induce c-fos expression (as in an early response gene); in many cell types hence, it was not a surprising finding;
We agree with the reviewer that it has been shown previously that Ca2+ induction in cells could induce c-fos expression (as an early response gene to stress). However, we have shown for the first time that Ca2+ regulates c-Fos expression in LT-HSCs under steady-state conditions.
-c-fos was demonstrated to suppress cell cycle entry of dormant hematopoietic stem cells (Okada et al., 1999: PMID: 9920830).
In the cited publication (Okada et al., 1999: PMID: 9920830) the authors have only analyzed the in vitro proliferation and colony formation of Lin- Sca-1+ cells in the IFNα/β inducible c-Fos overexpression model. This population mainly contains progenitor cells and only 0.004% of dormant LT-HSCs (please find below an estimation of LT-HSC frequency). Therefore, the role of c-Fos in the regulation of dormant HSC cell cycle entry remained unexplored.
It would be useful to do ChIP-seq to determine to confirm that c-fos regulates p57 expression.
We have shown that inhibition of c-Fos transcriptional activity inhibits p57 expression (Fig. 6G). ChIP–seq with antibody against c-Fos will answer whether c-Fos directly activates the expression of p57. However, we can only isolate 200-300 CD38+ LT-HSCs from all bones of one mouse. Unfortunately, the ChIP-seq with such an amount of cells is technically very difficult, which explains the absence of publications using ChIP-seq for studying transcription factors in LT-HSCs. We added in the Discussion section that we couldn’t exclude indirect regulation of p57 expression by c-Fos, lines 307-308:” In contrast, although we couldn’t exclude indirect regulation of p57kip2 expression by c-Fos, our data clearly reveal that inhibiting the interaction between c-Fos and DNA in dHSCs reduced protein levels of the cell cycle inhibitor p57kip2 and stimulated cell cycle entry.”
So overall, many of the findings were already out there and the authors gathered many of the pieces of the puzzle and put them together (and demonstrated) in a nice and well-thought manner. This work does add useful information to the scientific community but unfortunately is not ground-breaking. It may contribute to other fields beyond hematopoiesis where CD38 function may play a role.
Thank you very much for the positive review of our work. As mentioned by the reviewer, CD38 is expressed by other normal (lymphocytes, Kupffer cells (Tarrago M.G. et al., Cell Metabolism 2018)) and cancer cells, e.g. hematological malignancies, lung cancer, prostate cancer (Hogan K.A. et al. Frontiers in Immunology, 2019),) but has not been studied in the context of quiescence regulation. Currently, anti-CD38 monoclonal antibodies are used to treat malignancies (Daratumumab) by mediating cytotoxicity (Lokhorst H.M et al., N. Engl. J. Med, 2015). However, the inhibition of CD38 enzymatic activity has not been used broadly. Therefore, our study can be groundbreaking and open new directions in anti-cancer therapy.
Reviewer #2 (Significance (Required)):
In this manuscript, the authors investigated the potential roles of CD38 (mainly) in mouse HSCs quiescent; the authors dissected the potential molecular mechanism by which this occurred, and it was via CD38/cADPR/Ca2+/cFos/p57Kip2. The authors used a combination of transplantation assays to test the importance of CD38 in vivo, followed by a series of simple in vitro experiments (mainly using pharmacological means) to dissect the molecular mechanisms. The manuscript is well-written/explained and the data presented is solid. There are no major issues in terms of reproducibility and clarity in this work.
We would like to thank the reviewer again for the detailed positive feedback.
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Referee #2
Evidence, reproducibility and clarity
Although the experiments were well done and supported their testing hypothesis, but the overall novelty of the whole work is not that strong and this is because:
- the use of CD38 to identify/select and to test mouse LT-HSCs' function in vivo (although not commonly used nowadays) was demonstrated a few times more than 20 years ago (Randall, et al., 1996: PMID: 8639761 and Tajima et al., 2001; PMID: 11313250); in fact, the authors didn't even reference/acknowledge these papers which they should have done so; hence, most of the results in Fig.2 were already known (despite this current work gave a more detailed/better analysis);
- it is known the generic roles of CD38 in producing cADPR, ADPR, etc and these can induce Ca2+ oscillation in cells; despite that, it was nicely demonstrated here that in mouse HSCs cADPR was the main signalling mediator;
- the roles of cADPR in human CD34+ were demonstrated (Podesta et al., 2023; PMID: 12475890: when CD34+ HSPCs were primed in vitro with cADPR it resulted in enhanced short-term while maintaining long-term (secondary transplant) engraftment in NOD/SCID mice, probably (mechanisms were not determined at that time) inducing cycling/expansion of human CD34+CD38+ progenitors while inhibiting cycling (hence, better long-term maintenance) of CD34+CD38- HSPCs); on this note; the data presented in Fig.4 K and S5 should be eliminated as it adds little to their story and it can be quite confusing when comparing to mouse data unless the authors wish to explore in a more detailed way the human part.
- Ca2+ induction in cells can induce c-fos expression (as in an early response gene); in many cell types hence, it was not a surprising finding;
- c-fos was demonstrated to suppress cell cycle entry of dormant hematopoietic stem cells (Okada et al., 1999: PMID: 9920830).
It would be useful to do ChIP-seq to determine to confirm that c-fos regulates p57 expression.
So overall, many of the findings were already out there and the authors gathered many of the pieces of the puzzle and put them together (and demonstrated) in a nice and well-thought manner. This work does add useful information to the scientific community but unfortunately is not ground-breaking. It may contribute to other fields beyond hematopoiesis where CD38 function may play a role.
Significance
In this manuscript, the authors investigated the potential roles of CD38 (mainly) in mouse HSCs quiescent; the authors dissected the potential molecular mechanism by which this occurred, and it was via CD38/cADPR/Ca2+/cFos/p57Kip2. The authors used a combination of transplantation assays to test the importance of CD38 in vivo, followed by a series of simple in vitro experiments (mainly using pharmacological means) to dissect the molecular mechanisms. The manuscript is well-written/explained and the data presented is solid. There are no major issues in terms of reproducibility and clarity in this work.
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Referee #1
Evidence, reproducibility and clarity
In their paper entitled "CD38 promotes hematopoietic stem cell dormancy via c-Fos", Ibneeva et al., present a set of data predominantly from mouse HSCs where they explore the cell cycle kinetics and self-renewal capacity of LT-HSCs expressing (or not) CD38. They perform a series of sophisticated in vitro and in vivo experiments, including transplantations and single cell cultures and arrive at the conclusion that CD38 can fractionate LT-HSCs that are more deeply quiescent. Overall, it is an interesting question and would be of interest to experimental hematologists. That said, I had a number of issues that concerned me throughout the manuscript with regard to the robustness of the conclusions around CD38 and I have tried to detail these below.
Major concerns:
- Novelty - It was unclear what the relationship of this CD38+ fraction had with other "segregators" of LT-HSCs - e.g., how does it compare with the Sca1 fractionation of Wilson et al, Cell Stem Cell 2015 or Gprc5c of Cabezas-Wallschied Cell 2017? Even if CD38 fractionated LT-HSCs, it was unclear what it would give beyond these two molecules (especially re: Sca-1 which is also a cell surface marker)
- Claims of CD38+ superiority in transplantation - I was surprised with the claim of CD38 negative cells being a less functional HSC when they are clearly still very strong in secondary transplantation assays. Both 38+ and 38- cells strongly repopulate secondary animals and only 5 mice were shown in the Figure. The legend suggests another experiment was undertaken, but these data are not presented. Did they substantially differ in their chimerism in primary and secondary animals? Was the magnitude of difference between the two fractions similar in both experiments? Is there a reason that the data could not be plotted on the same graph? Also, the typical experiment to establish a quantitative difference in HSC production would be a limiting dilution analysis with a much larger number of recipient animals - without such data it is difficult to ascertain how different the two fractions really are.
Furthermore the claim that CD38- HSCs do not ever produce CD38+ cells is a bit premature with so few mice and confusingly presented data (e.g., Fig 2I is 5 pooled mice in a single histogram plot - were these concatenated flow files? If so, how were they normalised? Did the other experiment look the same? And were all CD38+ HSCs capable of giving rise to both CD38+ and CD38- cells or was it a subfraction of mice/samples?). 3. Cell Cycle status differences and grades of quiescence - Ki67 and DAPI are really quite tricky for discerning G0 versus G1 and no flow cytometry plots are provided for the reader to assess how this has been done. Could another technique (e.g., Hoechst/Pyronin) be used to confirm the results? Perhaps more concerning is the variability of the assay in the authors own hands. If I am interpreting things correctly, the plots in 3G, 3H and 3I in the platelet depletion, pIpC and 5FU experiments are >10% higher in the CD38- control arm than the data in 3A which make me worried about the robustness of the cell cycle assay to distinguish G0 from G1.
Minor points:
Figure 3I was really confusing - it says it is the gating strategy for GFP retaining LT-HSCs, but only shows GFP versus cKit
Figure 4B suggests that only 40% of CD38+ cells divide in the first 3 days - are there survival differences or are the cells sat there as single cells? It would be important to carry these further to see if cells eventually divide.
Significance
I believe the study will be of interest to specialist readers in the HSC field, especially those working on quiescence and G0 exit. At present, I think the conclusion of a true subfractionation is a bit premature, but there are pieces of data that do look exciting and warrant further investigation. It was a little unclear how this would advance beyond Sca-1 or Gprc5c fractionation for finding more primitive HSCs, but having cleaner markers is always a useful advance for the field.
Regarding my own expertise - I have spent ~20 years in the field undertaking single cell assays of normal and malignant mouse and human HSCs, including many of the core functional assays described in this paper and consider myself very familiar with the topic area.
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Reply to the reviewers
Manuscript number: RC-2023-01862
Corresponding author(s): Lasse, Sinkkonen
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.
In our manuscript we have aimed to take an unbiased and data-driven high-throughput approach for identification of transcription factors important for dopaminergic neuron differentiation via repeated, combined transcriptomics and epigenomics measurements. We also provide the research community with an extensive dataset enabling further studies on dopaminergic neurons beyond the scope of a single manuscript. We validate identified transcription factors not previously recognized being involved in mDAN differentiation. While we believe our approach is powerful in unbiased identification of central regulators, it does not focus only on factors that are unique for dopaminergic neurons. Importantly, the ranking of transcription factors is based on the epigenomic data of the target genes, rather than expression of transcription factors themselves. We have aimed for the genome-wide identification of pathways controlled by the identified transcription factors, for example through transcriptome analysis.
For practical reasons, to gain the sufficient depth of data to accomplish our aim, only one iPSC line was used for the initial data generation. However, we fully agree on the need for validation of the key findings and overall gene expression profiles in additional independent cell lines. Please find below our detailed point-by-point plan on addressing the reviewers’ comments.
2. Description of the planned revisions
Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In this study, Ramos and colleagues defined gene regulatory networks and transcriptional landscape during differentiation of a human iPSC reporter line into dopaminergic neurons. Several omic techniques (RNA-seq, ATAC-seq, chromatin-IP) and modelling (EPIC-DREAM) allowed them to identify putative effectors of dopaminergic differentiation LBX1, NHLH1 and NR2F1/2. Using overexpression and shRNA-mediated knock down experiments, the authors attempted to validate the hits.
This manuscript is very difficult to read and is confusing. The data are interesting, but they need to be presented in a more concise and readable way, in addition to be validated using additional iPSC lines. Below are few comments.
We thank Reviewer1 for taking the time to evaluate our manuscript and for providing valuable feedback towards improving it further. We were happy to read that the Reviewer1 found the study interesting with only a few caveats. Here we will outline a detailed plan to address those limitations.
In the revised manuscript we will do our best to improve the readability of the manuscript. However, since Reviewer2 has found that the manuscript is “well written, the research laid out in a clear way, and the experiments well thought”, it is somewhat difficult for us to identify the exact changes to introduce. Perhaps these are related to field-specific vocabulary or methodology, which we will aim to make more readable for broader audience.
We agree on the concern of Reviewer1 that different human iPSC lines can show significant variability due to their individual genetic backgrounds. We have observed differences in the rate of neuronal differentiation, depending on the iPSC line, and transcriptomic analysis reveals hundreds of differentially expressed genes between independent iPSC lines. Still, in a case of a single healthy donor, we don’t expect an intra-individual variability to alter conclusions regarding key regulators of fundamental processes such as differentiation. To carry out our multi-omic analysis in the sufficient depth that we have applied and using only purified dopaminergic neurons with a TH-mCherry-reporter inserted using genome editing, it was (also budget-wise) not considered to include multiple independent iPSC lines for the entire panel of experiments (as our ambition was not to characterize a specific mutation). However, to address this point, we have generated a second iPSC line from a healthy donor with TH-mCherry-reporter inserted through genome editing. To address the concerns regarding variability between different human iPSC lines we plan to:
1) Perform transcriptomic profiling of the second TH-mCherry-reporter line at selected time points of dopaminergic neuron differentiation to confirm the similarity of changes in cell identity at transcriptome level.
2) Perform TH staining upon LBX1 or NHLH1 knock-down in additional iPSC lines following dopaminergic neuron differentiation, to confirm their effect on differentiation across iPSC lines. To do this we will apply the Yokogawa high content image analysis that has been recently established in our laboratories. This will also be related to the next point regarding microscopy images of the dopaminergic neuron differentiation and the effect of transcription factors on this.
Only relative numbers and mRNA level normalized to control are presented in main figures. This is very confusing because there is no real quantification. Images of cultures to show increased/decreased number of dopaminergic neurons in non-FACS purified cultures following overexpression/knock down should be presented in main figures. It is recommended to add absolute quantification (percent of DAPI) and statistical analysis based on N=3 independent experiments.
Thank you for raising this point. We are happy to clarify the quantification of dopaminergic neuron numbers and mRNA levels. All quantifications of dopaminergic neuron numbers were based on the mCherry reporter inserted in the TH locus through genome editing and expressed together with endogenous TH. While mCherry can be detected using microscopy (as shown in Figure 1), the signal is significantly weaker than what can be achieved through antibody staining and quantitative analysis is therefore much more accurate when systematically performed using FACS analysis and controlled by using a cell line without the mCherry reporter. Moreover, the approach is direct and not dependent on antibody specificity. Therefore, all quantifications of dopaminergic neuron numbers in the manuscript were performed using FACS.
Most in vitro cell differentiation protocols show variability in their efficiency between independent experiments, which is typically reflected as variable expression levels of the different marker genes (Grancharova et al. 2021). This is also true for dopaminergic neuron differentiation and in our experiments the number of obtained dopaminergic neurons can vary between 5-20% while differentiations performed in parallel as part of the same experiment are typically very similar. Summarizing absolute numbers between independent experiments can lead to large variation while the relative effect of perturbation is reproducible. Therefore, our results are presented as relative changes in dopaminergic neuron numbers and mRNA levels.
Nevertheless, to increase confidence in the impact of NHLH1 and LBX1 on dopaminergic neuron differentiation, we propose, as already described above, to perform TH staining upon LBX1 or NHLH1 knock-down in additional iPSC lines following dopaminergic neuron differentiation. To visualize the observed impact on differentiation.
Based on images shown in figure S4, the effect of rapamycin is very low (no quantification is presented).
We apologize for the unclear Figure Legend for Figure S4 that did not specify what is visualized in the image. The images represent the transduction efficiency of the neurons based on the GFP reporter co-expressed with the short hairpin constructs. The mCherry levels, that are quantified in Figure 6G, are not visualized in these images. We will correct the Figure Legend accordingly. As mentioned in the last sentence on page 20 of the manuscript (referring to Supplementary Figure S4), rapamycin did not induce similar level of reduction in cell numbers as LBX1 knock-down alone did.
Are the three hits altered in dopaminergic neurons in Parkinson's disease and other synucleinopathies that could explain dysfunction of dopamine neurons in disease? Nurr1, EN1 and many other genes required for differentiation of dopaminergic neurons from pluripotent stem cells have their expression decreased in Parkinson's. It is expected that the expression of LBX1, NHLH1 and NR2F1/2 would change under disease condition.
We have investigated the expression of LBX1, NHLH1 and NR2F1/2 using recent meta-analysis of post-mortem brain tissue transcriptomes of Parkinson’s disease patients (Tranchevent, Halder, & Glaab, 2023). None of these TFs was found to be dysregulated in Parkinson’s disease patients. This is consistent with the fact that the expression of these factors is not restricted only to A9 midbrain dopaminergic neurons that are primarily degenerating in Parkinson’s disease but can be detected also in several other types of neurons (please see also our response in section 4).
However, NHLH1 expression is reduced in dopaminergic neurons derived from iPSCs of Parkinson’s disease patients carrying a LRRK2-G2019S mutation based on our published single cell RNA-seq data (Walter et al., 2021).
Beyond this, our results implicate NHLH1 in the regulation of miR-124, which in turn has been found to be downregulated in Parkinson’s disease patients and neuroprotective in different animal models of Parkinson’s disease (Angelopoulou, Paudel, & Piperi, 2019; Saraiva, Paiva, Santos, Ferreira, & Bernardino, 2016; Yang, Li, Yang, Guo, & Li, 2021; Zhang et al., 2022). Similarly, a recent analysis of single nuclei RNA-seq of midbrains from Parkinson’s disease patients, showed that targets of NR2F2 were enriched in the vulnerable dopaminergic neuron population, promoting neurodegeneration (Kamath et al., 2022). Indicating the involvement of the pathway in disease progression without a change in transcription factor expression.
Finally, a polymorphism in NHLH1 locus (rs2147472) is associated with schizophrenia while a polymorphism in LBX1 locus (rs12242050) is associated with Parkinson's disease, suggesting further involvement of these genes in disease risk.
We propose to include these findings in the revised manuscript and discuss them in the context of the current literature.
__Reviewer #1 (Significance (Required)): __
Interesting study that needs to be replicated using additional cell lines.
We would like to thank the reviewer for this positive conclusion and plan to address the key concerns using additional iPSC lines for transcriptome profiling and knock-down experiments.
__ Reviewer #2 (Evidence, reproducibility and clarity (Required)):__
In this manuscript Ramos et al. present a novel and comprehensive transcriptomic and epigenomic profile that identifies a series of key regulators of mDANs differentiation, providing functional validation and characterization of two newly associated TFs: LBX1 or NHLH1. In order to discover key regulators of mDAN differentiation the authors use their previous EPIC-DREM pipeline together with ATAC-seq data for the first time. Then, they focus their attention on those TFs with a more probable regulatory role by performing low input ChIP-seq for H3K27ac leading to the identification of 6 TFs as novel candidate regulators of mDAN differentiation under the control of super-enhancers at day 30 and day 50 of differentiation. In vitro knock down and overexpression of candidate TFs revealed LBX1, NHLH1 as important regulators of DAn differentiation. The authors then interrogate the role of these two TFs through RNA-seq and an Ingenuity Pathway Analysis (IPA)/g:Profiler and proposed regulation of the mature form miR-124 and cholesterol biosynthesis-related genes as the main processes controlled by NHLH1 and LBX1, respectively.
Overall, the manuscript is well written, the research laid out in a clear way, and the experiments well thought. The novelty of this study lays in the combination of epigenomic and transcriptomic data at different time points in specific cells during DAn differentiation. I believe the conclusions are supported by the results presented and therefore recommend this paper for publication after addressing some minor points listed below:
We would like to thank the reviewer for the detailed and overall positive evaluation of our work. We are grateful for the suggestions for improvements and below we detail our plan for addressing them.
Minor comments:
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In page 15 the authors state "the list of 17 TFs was further explored to select the most promising candidates for functional analysis". However, they only named TCF4 and MEIS1 as examples of discarded TFs through literature search. It is not clear which of the remaining 15 TFs were discarded because of a literature search and which were by SE signal cutoff. Clarification is needed.
We will add clarification statements here, providing more evidence for the selection of our candidates. For that, we will add a supplementary figure showing the locus and expression of the 11 TFs that were not selected.
In page 15 the authors state "TFs, HOXB2, LBX1, NHLH1, NR2F1 (also known as COUP-TFI), NR2F2 (also known as COUP-TFII) and SOX4 were found to present the strongest SE signals and most dynamic gene expression profiles" however I could not find the data that corroborate this statement within tables or figures. Authors should provide hard data to support this statement.
With the clarification from point 1, point 2 will also be answered for a clear description and criteria of our selection.
In supplementary 3, in the IPA analysis some data appear with the warning "#¡NUM!" at the z-score. Some explanation should be given and if pertinent, added to the table legend.
Sorry for not clarifying that in the dataset. That term is produced when IPA cannot predict the Z-score and it is represented in our bar graphs in grey (see Figure 6B). We will add that information to the table header.
In methodology, some reagents and techniques appear with a code reference to catalog number and others don´t. Please keep it uniform throughout the text.
In this study, we performed most of the techniques using kits which contained all necessary reagents for it. We will better clarify which reagents were provided by the manufacturer and which ones were additional to the kits.
Supplementary table 1 has some TFs highlighted in yellow but there is no legend that explain what the yellow highlight symbolizes. Clarification is needed
This is an error and there should not be any TF highlighted in yellow. We apologize for the inconvenience. The highlights will be removed from the revised tables.
Format suggestions:
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For an easier to follow flow between figure 3A and the main text, it would be helpful if NR2F1 and NR2F2 graphs in Figure 3A appeared next to each other or one above the other.
We will follow the recommendation from the reviewer, and we will change the order of the TFs in the figure to have both NR2F TFs next to each other.
Supplementary table 2.
Data is presented in a confused way. For example, the Top20_TFs_EPIC-DREM is presented as a list of names without divisions of type node or scoring annotations. It would be more informative and easy to follow if proper labeling and scoring is given within this spreadsheet without the necessity of navigating sup.table1 in parallel.
it would be preferable to have an extra sheet showing the comparison between both data sets (SE and EPICDREAM) before providing a final list of relevant TFs.
To the existing table containing the TFs controlled by SE, we are going to add the information regarding EPIC-DREM, namely, the rank those TFs got in each node together with their median ranking, and their best rank across nodes. That will give a good overview on how they look in both analyses. With this approach, some of the TFs controlled by SE will have no information regarding EPIC-DREM because their motif is not known according to the Jaspar database.
Reviewer #2 (Significance (Required)):
-General assessment:
Overall, the manuscript is well written, the research laid out in a clear way, and the experiments well thought. The novelty of this study lays in the combination of epigenomic and transcriptomic data at different time points in specific cells during DAn differentiation and description of new roles in DAn differentiation for two TF: LBX1 or NHLH1.
We thank the Reviewer2 for this assessment.
-Limitations: One limitation, than the authors themselves mentioned, is the possibility that promising candidate TFs involved in mDAn differentiation are discarded or not taken in account by the EPIC-DREAM algorithm.
We agree with this limitation and will make all the data available for the larger research community to use for follow-up work. Importantly, the data can be easily used for re-analysis using the same pipeline when improved databases become available.
-Audience: This manuscript focuses on factors involved in mDAN differentiation which targets a highly specific audience however their multiomic and functional methodology might attract broader audiences looking to apply similar pipelines and/or experimentation in different areas of research.
-My field of expertise:
I am a geneticist and neuroscientist with expertise in molecular biology and epigenomics focused on age related neurodegenerative disorders.
-Recommendation:
I believe the conclusions are supported by the results presented and therefore recommend this paper for publication after addressing some minor points.
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.
No changes were introduced so far.
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.
Below we will provide a point-by-point response to concerns raised by the reviewers that we believe are outside of the scope of our study.
There is not data showing that the targets are specifically required for dopaminergic differentiation. One may argue that same targets may be identified and required for differentiation of other neuronal cell types. Hence, hits need to be validated for other neuronal cell types using knock in and shRNA mediated KO.
The novelty of this study resides in the use of epigenomic signatures to predict TF activity across differentiation and couple those predictions with the transcriptional changes occurring during this process to identify the TFs responsible for most of the transcriptional changes observed. Therefore, although our focus were TFs important for establishing cell identity, we did not select TFs with a selective/exclusive expression in these cells, namely, cell identity TFs. This gives another perspective regarding TF activity and their relevance for cellular processes like differentiation.
We believe the TFs identified in our study are likely to be involved in regulation in several other neuronal subtypes. There is a wide range of neuronal subtypes and selection and establishment of some of the those for testing of our factors seems biased but also outside of the scope of this study.
Are the neurons generated following overexpression/shRNA-mediated knock down of the three hits functional? Electrophysiological recordings could help.
What other functions are affected in dopaminergic neurons when targets are knocked-down? Is lysosomal activity changed? Is the level of synaptic proteins altered compared to control?
In order not to bias our approach towards particular phenotypes by selected analysis such as electrophysiological measurements or lysosomal activity assays, we performed a transcriptional profiling upon TF depletion for our selected candidates. Our transcriptional profiling highlighted the main pathways affected by the TFs and they are presented and discussed in our study. We exploit these data to find the processes controlled by our TFs that help to define dopaminergic neuron cell identity. We discussed them and tested the role of mTOR signaling and miR-124 as targets of our TFs. The results from the RNA-seq analysis did not indicate direct regulation of synaptic or lysosomal activity, and therefore we find such analysis to be outside of the scope of our study.
Moreover, since the knock-down of our candidate TFs is in general inhibiting dopaminergic differentiation, studying the dopaminergic neurons remaining after a knock-down risks focusing on cells that have either partially or completely escaped the knock-down. Thereby influencing the value of detailed analysis of their functionality.
References:
Grancharova, T., Gerbin, K.A., Rosenberg, A.B. et al. A comprehensive analysis of gene expression changes in a high replicate and open-source dataset of differentiating hiPSC-derived cardiomyocytes. Sci Rep 11, 15845 (2021). https://doi.org/10.1038/s41598-021-94732-1
Angelopoulou, E., Paudel, Y. N., & Piperi, C. (2019). miR-124 and Parkinson’s disease: A biomarker with therapeutic potential. Pharmacological Research, 150. https://doi.org/10.1016/J.PHRS.2019.104515
Kamath, T., Abdulraouf, A., Burris, S. J., Langlieb, J., Gazestani, V., Nadaf, N. M., … Macosko, E. Z. (2022). Single-cell genomic profiling of human dopamine neurons identifies a population that selectively degenerates in Parkinson’s disease. Nature Neuroscience, 25(5), 588–595. https://doi.org/10.1038/S41593-022-01061-1
Saraiva, C., Paiva, J., Santos, T., Ferreira, L., & Bernardino, L. (2016). MicroRNA-124 loaded nanoparticles enhance brain repair in Parkinson’s disease. Journal of Controlled Release : Official Journal of the Controlled Release Society, 235, 291–305. https://doi.org/10.1016/J.JCONREL.2016.06.005
Tranchevent, L. C., Halder, R., & Glaab, E. (2023). Systems level analysis of sex-dependent gene expression changes in Parkinson’s disease. Npj Parkinson’s Disease 2023 9:1, 9(1), 1–16. https://doi.org/10.1038/s41531-023-00446-8
Walter, J., Bolognin, S., Poovathingal, S. K., Magni, S., Gérard, D., Antony, P. M. A., … Schwamborn, J. C. (2021). The Parkinson’s-disease-associated mutation LRRK2-G2019S alters dopaminergic differentiation dynamics via NR2F1. Cell Reports, 37(3). https://doi.org/10.1016/J.CELREP.2021.109864
Yang, Y., Li, Y., Yang, H., Guo, J., & Li, N. (2021). Circulating MicroRNAs and Long Non-coding RNAs as Potential Diagnostic Biomarkers for Parkinson’s Disease. Frontiers in Molecular Neuroscience, 14, 28. https://doi.org/10.3389/FNMOL.2021.631553/BIBTEX
Zhang, F., Yao, Y., Miao, N., Wang, N., Xu, X., & Yang, C. (2022). Neuroprotective effects of microRNA 124 in Parkinson’s disease mice. Archives of Gerontology and Geriatrics, 99. https://doi.org/10.1016/J.ARCHGER.2021.104588
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Referee #2
Evidence, reproducibility and clarity
In this manuscript Ramos et al. present a novel and comprehensive transcriptomic and epigenomic profile that identifies a series of key regulators of mDANs differentiation, providing functional validation and characterization of two newly associated TFs: LBX1 or NHLH1. In order to discover key regulators of mDAN differentiation the authors use their previous EPIC-DREM pipeline together with ATAC-seq data for the first time. Then, they focus their attention on those TFs with a more probable regulatory role by performing low input ChIP-seq for H3K27ac leading to the identification of 6 TFs as novel candidate regulators of mDAN differentiation under the control of super-enhancers at day 30 and day 50 of differentiation. In vitro knock down and overexpression of candidate TFs revealed LBX1, NHLH1 as important regulators of DAn differentiation. The authors then interrogate the role of these two TFs through RNA-seq and an Ingenuity Pathway Analysis (IPA)/g:Profiler and proposed regulation of the mature form miR-124 and cholesterol biosynthesis-related genes as the main processes controlled by NHLH1 and LBX1, respectively. Overall, the manuscript is well written, the research laid out in a clear way, and the experiments well thought. The novelty of this study lays in the combination of epigenomic and transcriptomic data at different time points in specific cells during DAn differentiation. I believe the conclusions are supported by the results presented and therefore recommend this paper for publication after addressing some minor points listed below:
Minor comments:
- In page 15 the authors state "the list of 17 TFs was further explored to select the most promising candidates for functional analysis". However, they only named TCF4 and MEIS1 as examples of discarded TFs through literature search. It is not clear which of the remaining 15 TFs were discarded because of a literature search and which were by SE signal cutoff. Clarification is needed.
- In page 15 the authors state "TFs, HOXB2, LBX1, NHLH1, NR2F1 (also known as COUP-TFI), NR2F2 (also known as COUP-TFII) and SOX4 were found to present the strongest SE signals and most dynamic gene expression profiles" however I could not find the data that corroborate this statement within tables or figures. Authors should provide hard data to support this statement.
- In supplementary 3, in the IPA analysis some data appear with the warning "#¡NUM!" at the z-score. Some explanation should be given and if pertinent, added to the table legend.
- In methodology, some reagents and techniques appear with a code reference to catalog number and others don´t. Please keep it uniform throughout the text.
- Supplementary table 1 has some TFs highlighted in yellow but there is no legend that explain what the yellow highlight symbolizes. Clarification is needed
Format suggestions:
- For an easier to follow flow between figure 3A and the main text, it would be helpful if NR2F1 and NR2F2 graphs in Figure 3A appeared next to each other or one above the other.
- Supplementary table 2.
- a. Data is presented in a confused way. For example, the Top20_TFs_EPIC-DREM is presented as a list of names without divisions of type node or scoring annotations. It would be more informative and easy to follow if proper labeling and scoring is given within this spreadsheet without the necessity of navigating sup.table1 in parallel.
- b. it would be preferable to have an extra sheet showing the comparison between both data sets (SE and EPICDREAM) before providing a final list of relevant TFs.
Significance
General assessment:
Overall, the manuscript is well written, the research laid out in a clear way, and the experiments well thought. The novelty of this study lays in the combination of epigenomic and transcriptomic data at different time points in specific cells during DAn differentiation and description of new roles in DAn differentiation for two TF: LBX1 or NHLH1.
Limitations:
One limitation, than the authors themselves mentioned, is the possibility that promising candidate TFs involved in mDAn differentiation are discarded or not taken in account by the EPIC-DREAM algorithm.
Audience:
This manuscript focuses on factors involved in mDAN differentiation which targets a highly specific audience however their multiomic and functional methodology might attract broader audiences looking to apply similar pipelines and/or experimentation in different areas of research.
My field of expertise:
I am a geneticist and neuroscientist with expertise in molecular biology and epigenomics focused on age related neurodegenerative disorders.
Recommendation:
I believe the conclusions are supported by the results presented and therefore recommend this paper for publication after addressing some minor points.
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Referee #1
Evidence, reproducibility and clarity
In this study, Ramos and colleagues defined gene regulatory networks and transcriptional landscape during differentiation of a human iPSC reporter line into dopaminergic neurons. Several omic techniques (RNA-seq, ATAC-seq, chromatin-IP) and modelling (EPIC-DREAM) allowed them to identify putative effectors of dopaminergic differentiation LBX1, NHLH1 and NR2F1/2. Using overexpression and shRNA-mediated knock down experiments, the authors attempted to validate the hits.
This manuscript is very difficult to read and is confusing. The data are interesting, but they need to be presented in a more concise and readable way, in addition to be validated using additional iPSC lines. Below are few comments.
Only relative numbers and mRNA level normalized to control are presented in main figures. This is very confusing because there is no real quantification. Images of cultures to show increased/decreased number of dopaminergic neurons in non-FACS purified cultures following overexpression/knock down should be presented in main figures. It is recommended to add absolute quantification (percent of DAPI) and statistical analysis based on N=3 independent experiments.
There is not data showing that the targets are specifically required for dopaminergic differentiation. One may argue that same targets may be identified and required for differentiation of other neuronal cell types. Hence, hits need to be validated for other neuronal cell types using knock in and shRNA mediated KO.
Based on images shown in figure S4, the effect of rapamycin is very low (no quantification is presented).
Are the neurons generated following overexpression/shRNA-mediated knock down of the three hits functional? Electrophysiological recordings could help.
What other functions are affected in dopaminergic neurons when targets are knocked-down? Is lysosomal activity changed? Is the level of synaptic proteins altered compared to control?
Are the three hits altered in dopaminergic neurons in Parkinson's disease and other synucleinopathies that could explain dysfunction of dopamine neurons in disease? Nurr1, EN1 and many other genes required for differentiation of dopaminergic neurons from pluripotent stem cells have their expression decreased in Parkinson's. It is expected that the expression of LBX1, NHLH1 and NR2F1/2 would change under disease condition.
Significance
Interesting study that needs to be replicated using additional cell lines.
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Reply to the reviewers
Response to reviewer comments
Reviewer #1: Major Points
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I was hoping to see the gel run for various days of desiccation to support the conclusion that proteome remodeling occurs **during** the desiccation. Right now, the data in Fig. 2 come from a single day – 21 days post desiccation – so it still shows that proteomic remodeling happened during those 21 days but not exactly on which days. Response: Thank you for this suggestion. We have ourselves become quite interested in the exact nature and extent of proteome changes over time in this paradigm. Indeed, our findings in this study now open up so many future exciting directions including various possible molecular mechanisms that control this phenomenon. We are planning to carry out an extensive future study to compare the proteome of fresh and desiccated eggs quantitatively, and over time in order to explore these directions. At this stage though, a complete proteomic study is infeasible. However, our existing data still shows that Aedes eggs have acquired unique proteome – level changes which reiterates a distinct metabolic remodeling happening during the process of desiccation. We have added your point as an important consideration in the manuscript (L207-209).
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In Fig 2B: Unclear what you’re using as a reference to say that “45 proteins increased and 125 proteins decreased in amounts” (L147-148). Relative to fresh eggs that were laid 48 hours ago? Why is this a good reference instead of say, fresh eggs that are 21 days old (same age as the desiccated eggs)? Response: Thank you for this comment, and this helps us to now clarify this point. Throughout the study, “fresh eggs” refer to eggs that were 48 hours old, maintained in moist conditions and not subjected to desiccation. Placing the eggs under moist conditions for 48 hours after egg laying was critical to allow embryonic development (Clements, 1992, ISBN: 9780412401800; Mundim-Pombo et al., 2021, PMID: 34645492). By “desiccated eggs”, we mean fresh eggs (48 hours old) which are subsequently dried for a total period of 21 days by placing the eggs on Whatman filter paper. Therefore, the comparisons made in Figures 2 and 3 are between fresh eggs and desiccated eggs (21 days). Fresh eggs cannot be left for 21 days in moisture as they would hatch into larvae approximately between 48-72 hours after being laid (Clements, 1992; Mundim-Pombo et al., 2021, Rezende et al., 2008, PMID: 18789161). Therefore, the only possible comparison is of fresh eggs at a stage where it would have acquired desiccation tolerance, with the fully desiccated 21-day old egg. We have added new content in the methods section (L426-431) on how eggs were collected for various experiments including the ones described in Figure 2 and also included a figure (Figure S1D, L966-970) to demonstrate the same.
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L90-L91: "...dried for up to 21 days" But the methods section states that the eggs were dried for 10 days on Whatman filter paper. The 21 days refers to the fact that the authors looked at eggs that were stored for 21 days after the 10 days of desiccation, no? Isn't that why the x-axis goes up to 21 days in Fig. 1C? Please clarify. Response: As mentioned in the previous comment response, “21 days” refers to 48 hours of embryonic development (which was achieved by leaving the eggs in moist conditions for 48 hours), followed by 21 days of desiccation on Whatman paper. These dried eggs were then rehydrated to check the percentage hatching (Figure 1C). “21 days” does not mean 10 days of desiccation and 21 days of storage. We have accordingly modified the results section (L98-102), the figure (Figure 1A), its caption (L802-809) and the methods section (L401-415) to clarify and emphasize this point.
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- 1C: related to above. What does "0-day post desiccation" mean in the x-axis? Is these 10 days of desiccation on Whatman paper + 0 days of storage? Similarly, what is 12 days or 21 days post desiccation on the x-axis? These are 10 + 12 days and 10 +21 days respectively? Response: “0 days post desiccation” refers to fresh eggs that are 48 hours old post egg laying and not subject to desiccation. This has been the control throughout our study. As mentioned above, it does not mean 10 days of desiccation and 0 days of storage. We have rephrased the the results section (L98-102), the methods section (L401-415) and modified the illustration (Figure 1A) and its caption (L802-809)* appropriately to describe how the desiccation assay was performed.
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Methods section on desiccation is very unclear (related to above). I cannot determine what the days in Fig. 1C means based on this methods section and the main text (and caption for fig. 1C). Response: We acknowledge the original methods had very brief statements, and so we have substantially revised the text (L98-102), the methods section (L401-415) and improved the schematic (Figure 1A) and its caption (L802-809) to provide clarity on the experimental methods and on how the desiccation assays were designed. We have also included a separate section (L426-431) and an illustration (Figure S1D, L966-970) to demonstrate how samples were collected for various experiments.
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- 2A: What are "D1" and "D2"? These are two trials of desiccation? For each lane (e.g., D1), did you combine 150 eggs and lysed them together for the single lane in the gel? Specify these points in the caption. Response: Yes, D1 and D2 refer to two independently conducted trials from desiccated eggs. 150 eggs were used in each trial, where these eggs were combined and lysed together for protein extraction in order to ensure sufficient material for both the qualitative visualization on SDS-PAGE gel and proteomic analysis. We have incorporated your suggestions in the revised methods section (L443-447) figure legends (L841-845, 857-860)*.
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Related to above: Does the "21 day" correspond to 21 days **post** desiccation (i.e., "21" in the x-axis of Fig. 1C)? Or something else? Please specify in the figure caption. Response: Yes, 21 days in figure 1C corresponds to 21 days post-desiccation. We have clarified the definitions of fresh and desiccated eggs in response to comments 2, 3 and 4 above. To facilitate the understanding of how the desiccation assays were performed as well as the interpretations of Figure 1C, we have added text to the methods section (L401-415) and added explanations in the respective legends (Figure 1A, L802-809).
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L145-146: What is the emPAI score? Give a one-sentence explanation. * Response: The emPAI (exponentially modified protein abundance index) is an absolute quantitation method now widely used in proteomics, which allows comparisons of protein data acquired by LC-MS/MS (Ishihama et al., 2005, PMID: 15958392). The PAI is the protein abundance index, and this is proportional to the logarithm of absolute protein concentration, and since detection relies on mass spectrometry, PAI will indicate the ratio of observed to observable (due to inherent peptide/ionization and detection properties) peptides. The emPAI values of proteins from one sample can now be compared with those in another sample, especially those obtained in contiguous MS runs using the exact same method, to determine increasing or decreasing proteins (as we have done in this study). Thank you for pointing this out and we have added the necessary information to the text (L159-163)*.
Reviewer #2
- However, the method used to define the tolerance as anhydrobiosis, which forms the basis of this claim, is flawed. Physiological strategies for tolerating desiccation can be broadly divided into "desiccation avoidance," which involves maintaining the physiological state by preventing water loss, and "desiccation tolerance," which involves responding to water loss by changing the metabolic system. Desiccation tolerance can be further categorized into two types: hypometabolism, which reduces the metabolic rate, and ametabolism, which completely stops metabolism. The former is general desiccation tolerance, while the latter is defined as anhydrobiosis (Keilin, 1959. doi: 10.1098/rspb.1959.0013). To be classified as anhydrobiosis, the authors must demonstrate that metabolism, including respiration, has ceased completely, not merely that water content has been significantly reduced. The authors claim that the weight of Ae. aegypti eggs dropped by about 65% and that they were still able to hatch even after 21 days of desiccation, as evidence of anhydrobiosis. However, this only confirms the tolerance to desiccation exhibited by many insects living in arid regions. Response: We primarily see this study as a short discovery report that will open multiple directions of future inquiry in this space and we greatly appreciate these points. The responses below, therefore, are elaborate and considered, and we hope will clarify these points extensively.
We agree with the definition of anhydrobiosis as a phenomenon of the ability of some cells and animals to enter into a reversible state of suspended metabolism (ametabolism), and indeed we are admirers of the wonderful explanation of anhydrobiosis as explained by Keilin et al. in 1959. However, we would like to point out that even during such a state, the basal level of metabolism needed for cellular maintenance and repair has to exist (Bosch et al., 2021, PMID: 34347349; da Silva et al., 2019, PMID: 30266630; Garcia, 2011, PMID: 22116292; Pazos-Rojas et al., 2019, PMID: 31323038). The definitions of ‘hypometabolism’ and ‘ametabolism’ were made mostly in the 1950s, when it was primarily possible to only obtain bulk estimates of respiration or glycolysis. Indeed, in every known example of desiccation tolerance or dormancy, there is a decrease in the energetic arms of glycolysis and the TCA cycle (da Silva et al., 2019; Dinakar & Bartels, 2013, PMID: 24348488; Erkut et al., 2013, 2016, PMID: 24324795, PMID: 27090086; Hibshman et al., 2020, PMID: 33192606; Ryabova et al., 2020, PMID: 32723826; Thorat & Nath, 2018, PMID: 30622480; Zhang et al., 2019, PMID: 31019237). Entirely consistent with that, but with much more quantitative approaches that can make more complete inferences, our proteomics and metabolomics data (Figures 2 and 3), show a substantial decrease in glycolysis as well as the ATP and NADH producing arms of the TCA cycle (post α–ketoglutarate) clearly indicating a reduction in the key metabolic pathways involved in energy production (L245-255, Figure 3A).
However, what we are now able to observe, is that there is a rewiring of the central carbon metabolism to support the production of protective molecules such as polyamines (in this case). This would be from a rerouting of flux, away from energy metabolism, but when that happens, it is essential that this ‘carbon and nitrogen’ is put somewhere. Energy-producing pathways during desiccation now are only active at very low efficiencies. The desiccated Aedes aegypti eggs are therefore indeed hypometabolic, and this conclusion is not made merely based on the fact that the total water content and weight of desiccated eggs has been reduced. Note that it is practically almost impossible to measure active respiration in desiccated Aedes eggs, since these measurements require a water-environment (and the entire purpose is lost if we add back water to the desiccated eggs). We will also point out that more recent studies by Erkut et al., 2013 in nematodes, which primarily relied on some proteomic measurements, as well as limited metabolite measurements, already hint that such phenomena occur in bona fide anhydrobiotes such as the pre-conditioned dauer larvae of C. elegans. By using approaches similar to those in our studies, we anticipate that there is a tremendous amount of new learning to be obtained in this area, and we will be able to better revise the definitions of desiccation tolerance or anhydrobiosis.
A ~65% loss in mass, while also considering the mass of the egg shell (and therefore the actual loss of mass in the embryo will be an even higher percentage) is substantial. While we have revised the text thoroughly to avoid the description of these embryos as ‘true anhydrobiotes’, we have rephrased this as desiccation tolerant, and hope readers will appropriately consider these aspects.
Finally, regarding the point of “However, this only confirms the tolerance to desiccation exhibited by many insects living in arid regions.”, we agree, and point out that little or nothing is known about the pathways or means by which many of such insects (including insects that are major causes of diseases in human, livestock or agriculture) survive under extremely dry environments and till date remain phenomenological. Our entire molecular understanding of desiccation tolerance comes from a handful of model organisms such as yeasts, nematodes, and some tardigrades. This study demonstrates the systematic analysis of desiccation tolerance and survival under rapidly changing environmental conditions in a non-model insect - the mosquito, which is already known to have globally diversified due to its ability to adapt behaviorally and physiologically to environmental fluctuations (Diniz et al., 2017, PMID: 28651558; Halsch et al., 2021, PMID: 33431560 ; Miller & Loaiza, 2015, PMID: 25569303). Our study is a substantial advance in this regard, providing interesting insights into mechanisms of desiccation tolerance in mosquito eggs, a property which could in turn contribute to global expansion of this insect. We anticipate that this work will lay foundation to several studies to control the spread of Aedes mosquitoes.
Given the length of this report, we have chosen to avoid an extensive discussion section, and only briefly summarized this point (L65-78, L222-235, L245-255, L281-284).
- The lack of significant accumulation of trehalose and the absence of accumulation of IDPs suggest that the tolerance in the dried eggs is not anhydrobiosis, which means that the manuscript is actually a study of the desiccation tolerance of Aedes aegypti eggs (not anhydrobiosis, nor is it extreme desiccation tolerance). The manuscript should, therefore, be renamed as "Aedes aegypti eggs use rewired polyamine and lipid metabolism to survive desiccation". Response: We agree with your suggestion of changing the title of the manuscript and hence have renamed it to “Aedes aegypti eggs use rewired polyamine and lipid metabolism to survive desiccation”.
However, we believe that referring to organisms as anhydrobiotes just because of its ability to exclusively accumulate trehalose or IDPs during the desiccated state would be inappropriate, and hinders advances in this space. Please allow us a systematic explanation of the same, below, in three parts: on anhydrobiosis, on trehalose synthesis, and on IDPs.
Anhydrobiosis or desiccation tolerance involves drastic physiological changes during the induction of anhydrobiosis, survival during the desiccated state and exiting this state upon rehydration (Bosch et al., 2021; Crowe, 2014, PMID: 24548118; Dinakar & Bartels, 2013; Pazos-Rojas et al., 2019; Rajeev et al., 2013, PMID: 23739051; Ryabova et al., 2020). Multiple processes enable the cell to deal with physical challenges – to protect proteins and membranes, and to maintain cellular integrity (L49-59, L225-232) . Different molecular processes can be used to attain this. The role of trehalose has been best characterized, at a molecular level primarily in yeasts and in nematodes (Erkut et al., 2016). Trehalose functions to protect the integrity of the membrane by forming glass-like structures as well as functions as a protein chaperone (Crowe et al., 1998, PMID: 9558455; Erkut et al., 2011, PMID: 21782434; Tapia & Koshland, 2014, PMID: 25456447). In order for organisms to utilize trehalose, they must first accumulate it substantially, and this can only be done by shifting to very high rates of gluconeogenesis (Calahan et al., 2011, PMID: 21840858; Erkut et al., 2011, 2016; Tapia & Koshland, 2014). Two principles emerge from our own (Gupta et al., 2019, PMID: 31259691; Varahan et al., 2019, 2020, PMID: 31241462, PMID: 32876564; Varahan & Laxman, 2021, PMID: 34849891; Vengayil et al., 2019, PMID: 31604822), and other studies that have tried to a build systems-level understanding of various ways by which flux towards trehalose can be increased. First, cells need to have carbon reserves that can reroute towards trehalose biosynthesis, either if glycolytic flux is reduced and/or if gluconeogenic flux is increased. Second, the presumption of ‘ametabolic states’ is incorrect, since there is a primary reduction of glycolysis and respiration, with a concurrent rerouting of flux towards trehalose accumulation. While this flux re-routing is possible (through various means), as has been observed in several desiccation tolerant organisms like yeasts and nematodes, all of these organisms were present in media/growth conditions where various carbon sources are abundant. Note that a key point of this study is to highlight that mosquito eggs are different in their natural environment – eggs are essentially a ‘closed system’, with limited inputs of nutrients, and when in fresh water (where eggs are typically laid), these are very poor carbon sources (L79-85). Hence, rerouting of flux towards trehalose in such cases will be practically impossible.
Note that in this context, as a strategy to overcome desiccation stress, other organisms like tardigrades rarely accumulate trehalose but instead rely on intrinsically disordered proteins to survive desiccation (Boothby et al., 2017, PMID: 28306513; Hesgrove & Boothby, 2020, PMID: 33148259). Tardigrades, unlike nematodes or yeast are present typically in carbon-poor, water environments. Therefore, when viewed in the context we have explained above, unless they have suitable carbon stores, tardigrades will also be unable to ramp up trehalose production easily during the desiccation process. Therefore, it makes entirely more sense that tardigrades do not rely on trehalose, but instead utilize IDPs in desiccation tolerance. Before this study, there was no clear or established role for IDPs. Note that the function of the IDPs is also to protect proteins from denaturation, much like what was later found for trehalose (Crowe et al., 1998; Tapia & Koshland, 2014).
An alternate way to achieve similar physical ends would be to utilize polyamines. Studies suggest a critical role for polyamines in desiccation tolerance in nematodes, separate from trehalose (Erkut et al., 2013). The ability of polyamines at higher concentrations to protect DNA/RNA, or phase transition into glass-like forms (much like trehalose and IDPs) is extremely well established (Miller-Fleming et al., 2015, PMID: 26156863; Saminathan et al., 2002, PMID: 12202757). Therefore, our findings establishing a protective role for polyamines would be entirely consistent with interpretations made under these contexts (Figure 3A, 3B, L281-293).
Finally, we clarify the idea of desiccation tolerance in Aedes eggs. We establish the following – after desiccation, the eggs have substantially low glucose/glycolytic metabolism, and TCA cycle metabolites. This is seen both at the proteome and metabolite levels (Figure 2 and 3). In addition, we demonstrate substantially lower amounts of lipids, both in the desiccated state and after rehydration (Figure 2D and 2E). Our study points towards a novel aspect of how metabolic rewiring not only supports protection during the desiccated state, but also ensures reactivation of metabolism upon return of favourable conditions. In the Aedes eggs, desiccation tolerance which involves survival and sustenance of the pharate larvae inside the dried egg as well as the exit from this dried state upon exposure to water, can logically be achieved only by repurposing internal acetyl-CoA reserves, which come from increased fatty acid breakdown to synthesize polyamines (Figure 4E). The polyamines also confer protection from the consequences of desiccation together with other enzymatic antioxidants and molecular chaperones (Figure 2C). Fatty acids are utilized by the pharate larvae for its energetic needs during the dormant state as well as to fuel recovery upon rehydration.
Conclusively, we find that desiccation tolerance can be achieved not just by accumulating trehalose or IDPs, but also because of additional relevant mechanisms that are biochemically possible. Thereby, this study adds up to our current knowledge and understanding of possible ways by which cells can achieve the same end of desiccation tolerance, and survival upon rehydration.
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This manuscript provides interesting insights from the perspective of a metabolomic analysis for clarifying the mechanism of the "general" desiccation tolerance, not anhydrobiosis, in dried Ae. aegypti eggs. For instance, the accumulation of polyamines might contribute to desiccation tolerance. The authors suggest a relationship between the accumulation of polyamines and hatchability based on the fact that the inhibition of metabolic pathways resulted in a decrease in hatchability and polyamines. However, conclusive evidence of a causal relationship is not available. It is possible that the inhibitors disrupted metabolic pathways other than the polyamine synthesis, leading to a significant decrease in hatchability. Response: We understand the reviewer’s point made here; however, we would like to elaborate a clarification on this point. In order to test the role of polyamines in desiccation tolerance in Aedes eggs, we inhibited the polyamine biosynthetic pathway using difluoromethylornithine (DFMO). While there may be some non-target effects of a drug, as is true for every inhibitor, our choices of inhibitors were very deliberate and carefully considered. DFMO is extensively used as an anticancer drug to specifically target ornithine decarboxylase, the first (and rate-controlling) step of polyamine biosynthesis (LoGiudice et al., 2018, PMID: 29419804). Importantly, we made our inferences based on two sets of experiments with DFMO. First, we confirmed that DFMO reduces polyamine accumulation in desiccated eggs (Figure S4B). Next, we observed significant reductions in the hatching of desiccated eggs that were obtained from mosquitoes fed with the inhibitor (Figure 4A). This is consistent with a conclusion that the accumulation of polyamines is essential for desiccation tolerance. As critical controls, we included the hatching of fresh eggs obtained from mosquitoes fed with the inhibitor (in a concurrently conducted experiment, with the same sets of mosquitoes). These eggs showed a high percentage of hatching, which was very similar to the untreated controls (Figure 4A, L309-313). This minimizes the possibility that DFMO could inhibit other metabolic pathways that led to reduced hatching. While acknowledging the limitations of pharmacology, our data collectively (Figure 4A, S4B) are consistent with the likelihood that eggs where polyamine biosynthesis is inhibited, are sensitive to desiccation. Since it is not easily feasible to knock-out ODC in mosquitoes, which are still non-model organisms, it is practically implausible to do experiments that are more conclusive. In fact, such experiments as shown in this study have never been performed in mosquitoes (or other similar insects) before, and we therefore believe both the findings, and the approach (of feeding adult female mosquitoes with inhibitors before egg laying) to be substantial advances. We entirely anticipate that these approaches will stimulate future studies in the many new directions this study opens up.
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The quantitative values of polyamines were shown only as relative values based on the values in fresh eggs of the control group. Absolute quantification of polyamines, particularly ornithine, putrescine, and spermidine, should be essential for this manuscript. * Response: We thank the reviewer for raising an important point here. However, it is almost impossible to do such an experiment, since the concentrations of metabolites are usually calculated on the basis of total cellular volume of the extracted cells, normalized to the number of cells (Bennett et al., 2008, PMID: 18714298). Calculating the volume of a single egg, particularly that of a desiccated egg because of its distorted shape is almost impossible. Hence, the steady state levels of all measured metabolites including polyamines, are represented as relative values calculated using the peak areas which corresponds to the amount of the particular metabolite present in the sample, where we normalize to egg numbers (L878-879)*. We have provided the peak areas of all the measured metabolites in Table S4. Note that relative metabolite comparisons are a near-universally accepted approach to show fold-level increases or decreases and as a reference, we include this extensive methods paper where we and others discuss the different, appropriate ways of metabolite comparisons (Walvekar et al., 2018, PMID: 30345389).
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The statistical analysis throughout the study raises concerns, as the sole significant difference test employed is the student’s t-test. While this test is suitable for comparing two groups, it cannot be used for making comparisons between three or more groups. For instance, in the experiment depicted in Figure 4, a comparison of fresh and dried eggs in the control and inhibitor treatment combination would entail comparing four groups. To address this, a two-way analysis of variance ought to be conducted, followed by a post-test such as Bonferroni's or Tukey's multiple comparison test. Response: Thank you for allowing us to clarify this. In the case of our studies, it would be inappropriate to use a two-way ANOVA, and correct to use the unpaired t-tests, because we do not make any comparisons between three or more groups, although visually it might have appeared that way in Figure 4. The data in Figures 4A, 4B S4B and S4C consists of 4 samples – control fresh eggs, control desiccated eggs, treated fresh eggs and treated desiccated eggs. However, comparisons are only made between two groups at a time. These would be control fresh eggs versus control desiccated eggs; OR treated fresh eggs versus treated desiccated eggs OR control desiccated eggs versus treated desiccated eggs i.e., the comparisons are only made for the appropriate two sets. For illustrating these comparisons in an easily readable way, the graphs are presented together. A two-way ANOVA can only be used when comparisons are made between more than two groups or to determine the effect of 2 variables on an outcome which is not applicable in our case. Therefore, only an unpaired test (eg. a student t-test) is appropriate, and we make absolutely no point about multiple comparisons. We’ve included a table below, purely as a reference point, where the same comparisons were made using Wilcoxon’s ranked tests, which is a non-parametric test that only infers information in the magnitudes and signs of the differences between paired observations. Note that there is no change in the conclusions, nor is there any issue with significance for the specific samples compared (in the main manuscript figures). In addition to this, we have added additional text in the figure legends (L904-907, L918-921, L1015-1017, L1022-1025) and also modified the graphs in all the figures for a clearer illustration of the comparison sets.
Figure No.
Comparisons
__ Measurement__
__p value (Wilcoxon's rank-sum test) __
Significance
4A
Control fresh eggs vs Control desiccated eggs
% hatching
0.08143
ns
Treated fresh eggs vs Treated desiccated eggs
0.02857
*
Control desiccated eggs vs Treated desiccated eggs
0.02857
*
4B
Control fresh eggs vs Control desiccated eggs
% hatching
0.05714
ns
Treated fresh eggs vs Treated desiccated eggs
0.02857
*
Control desiccated eggs vs Treated desiccated eggs
0.02857
*
S4B (i)
Control fresh eggs vs Control desiccated eggs
Relative ornithine levels
0.02107
*
Treated fresh eggs vs Treated desiccated eggs
0.05907
ns
Control desiccated eggs vs Treated desiccated eggs
0.0294
*
S4B (ii)
Control fresh eggs vs Control desiccated eggs
Relative putriscene levels
0.02107
*
Treated fresh eggs vs Treated desiccated eggs
0.8857
ns
Control desiccated eggs vs Treated desiccated eggs
0.02857
*
S4B (iii)
Control fresh eggs vs Control desiccated eggs
Relative spermidine levels
0.02107
*
Treated fresh eggs vs Treated desiccated eggs
0.05907
ns
Control desiccated eggs vs Treated desiccated eggs
0.0294
*
S4C
Control fresh eggs vs Control desiccated eggs
Relative lipid levels
0.02107
*
Treated fresh eggs vs Treated desiccated eggs
1
ns
Control desiccated eggs vs Treated desiccated eggs
0.02857
*
*p<0.05, **p<0.01, ***p<0.001, ns - no significant difference.
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Referee #2
Evidence, reproducibility and clarity
This manuscript explores the mechanisms underlying extreme desiccation tolerance, known as anhydrobiosis, in Aedes aegypti eggs. The authors suggested that specific metabolites are involved in achieving this tolerance and provide a comparative metabolomic analysis between dried and fresh eggs to support their claim. In contrast to other anhydrobiotic animals, such as Polypedilum vanderplanki larvae and Artemia cysts, the dried eggs of Aedes aegypti do not accumulate large amounts of compatible solutes like trehalose or intrinsically disordered proteins (IDPs) such as LEA protein. Therefore, the authors want to contend that anhydrobiosis in Ae. aegypti eggs is achieved through a different mechanism.
Significance
However, the method used to define the tolerance as anhydrobiosis, which forms the basis of this claim, is flawed. Physiological strategies for tolerating desiccation can be broadly divided into "desiccation avoidance," which involves maintaining the physiological state by preventing water loss, and "desiccation tolerance," which involves responding to water loss by changing the metabolic system. Desiccation tolerance can be further categorized into two types: hypometabolism, which reduces the metabolic rate, and ametabolism, which completely stops metabolism. The former is general desiccation tolerance, while the latter is defined as anhydrobiosis (Keilin, 1959. doi: 10.1098/rspb.1959.0013). To be classified as anhydrobiosis, the authors must demonstrate that metabolism, including respiration, has ceased completely, not merely that water content has been significantly reduced. The authors claim that the weight of Ae. aegypti eggs dropped by about 65% and that they were still able to hatch even after 21 days of desiccation, as evidence of anhydrobiosis. However, this only confirms the tolerance to desiccation exhibited by many insects living in arid regions. The lack of significant accumulation of trehalose and the absence of accumulation of IDPs suggest that the tolerance in the dried eggs is not anhydrobiosis, which means that the manuscript is actually a study of the desiccation tolerance of Aedes aegypti eggs (not anhydrobiosis, nor is it extreme desiccation tolerance). The manuscript should, therefore, be renamed as "Aedes aegypti eggs use rewired polyamine and lipid metabolism to survive desiccation". This manuscript provides interesting insights from the perspective of a metabolomic analysis for clarifying the mechanism of the "general" desiccation tolerance, not anhydrobiosis, in dried Ae. aegypti eggs. For instance, the accumulation of polyamines might contribute to desiccation tolerance. The authors suggest a relationship between the accumulation of polyamines and hatchability based on the fact that the inhibition of metabolic pathways resulted in a decrease in hatchability and polyamines. However, conclusive evidence of a causal relationship is not available. It is possible that the inhibitors disrupted metabolic pathways other than the polyamine synthesis, leading to a significant decrease in hatchability. The quantitative values of polyamines were shown only as relative values based on the values in fresh eggs of the control group. Absolute quantification of polyamines, particularly ornithine, putrescine, and spermidine, should be essential for this manuscript. The statistical analysis throughout the study raises concerns, as the sole significant difference test employed is the Student's t-test. While this test is suitable for comparing two groups, it cannot be used for making comparisons between three or more groups. For instance, in the experiment depicted in Figure 4, a comparison of fresh and dried eggs in the control and inhibitor treatment combination would entail comparing four groups. To address this, a two-way analysis of variance ought to be conducted, followed by a post-test such as Bonferroni's or Tukey's multiple comparison test.
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Referee #1
Evidence, reproducibility and clarity
This manuscript valuably contributes to understanding how mosquito eggs survive desiccation: the authors establish that, during desiccation, the Ae. aegypti egg's TCA cycle and other metabolic pathways change in order to accumulate polyamines - these provide physical protection during desiccation - and breakdown of lipids which is required for both accumulating polyamines and fuel the recovery process once rehydration occurs (thereby helping the egg hatch after rehydration). The authors also establish that desiccation kills the eggs of another mosquito specie, An. stephensi, in which the above processes don't occur to provide protection during desiccation.
Much of the study uses mass spectrometry of desiccated eggs of Ae. aegypti to determine proteomic changes that occur during desiccation. Interestingly, these included increased superoxide dismutase, glutathione transferase, and theioredoxin peroxidase - all of these regulate the homeostasis of redox processes in cells. These are particularly interesting because, as the authors noted, other studies in different organisms had shown that Reactive Oxygen Species (ROS) are created during desiccation. These results thus suggest that the results of this study would be of interest to those studying desiccation of dauer C. elegans and yeast. Interestingly, recent studies have shown that ROS and glutathione (and other ROS-reducing enzymes) are the key determinants of whether yeast survives or not at extremely high and low temperatures. Some differences were observed though. For example, unlike in desiccated yeast and C. elegans, Intrinsically Disordered Proteins (IDPs) weren't upregulated during desiccation of the mosquito eggs.
For the most part, the experiments and analyses are rigorous and technically sound. The presentation and writing are clear, for the most part. But there are some aspects of the analyses and presentation that might benefit from clarifications. I specify these below.
I support the publication of this work with very minor revisions. The only additional experiment that I can recommend is in point #1 below (doing gel and mass spec on at least one intermediate day during desiccation instead of just at the final day (day 21) which is what has been done). But since mass spectrometry is expensive and time-consuming, this experiment is only suggested but not absolutely necessary. The authors' major conclusions are still valid without this additional experiment. It's just that we don't know how fast the proteomic changes are occurring during desiccation without some timcourse as the one that I suggest here. Perhaps this point can be mentioned as a deficiency of the current work in the discussion, in lieu of doing the additional experiment.
Major points:
- I was hoping to see the gel run for various days of desiccation to support the conclusion that the proteome remodeling occurs during the desiccation. Right now, the data in FIg. 2 come from a single day - 21 days post desiccation - so it still shows that proteomic remodeling happened during those 21 days but not exactly on which days.
- In Fig. 2B: unclear what you're using as a reference to say that "45 proteins increased and 125 porteins decreased in amounts" (L147-148). Relative to fresh eggs that were laid 48 hours ago? Why is this a good reference instead of, say, fresh eggs that are 21 days old (same age as the desiccated eggs)?
- L90-L91: "...dried for up to 21 days" But the methods section states that the eggs were dried for 10 days on Whatman filter paper. The 21 days refers to the fact that the authors looked at eggs that were stored for 21 days after the 10 days of desiccation, no? Isn't that why the x-axis goes up to 21 days in Fig. 1C? Please clarify.
- Fig. 1C: related to above. What does "0 day post desiccation" mean in the x-axis? Is this 10 days of desiccation on Whatman paper + 0 day of storage? Similarly, what is 12 days or 21 days post desiccation on the x-axis? These are 10 + 12 days and 10 +21 days respectively?
- Methods section on desiccation is very unclear (related to above). I cannot determine what the days in Fig. 1C mean based on this methods section and the main text (and caption for fig. 1c).
- Fig. 2A: what are "D1" and "D2"? These are two trials of desiccation? For each lane (e.g. D1), did you combine 150 eggs and lysed them together for the single lane in the gel? Specify these points in the caption.
- Related to above: Does the "21 day" correspond to 21 days post desiccation (i.e., "21" in the x-axis of Fig. 1C)? Or something else? Please specify in the figure caption.
- L145-146: What is emPAI score? Give a one-sentence explanation.
Significance
I support the publication of this work with very minor revisions. The only additional experiment that I can recommend is in point #1(doing gel and mass spec on at least one intermediate day during desiccation instead of just at the final day (day 21) which is what has been done). But since mass spectrometry is expensive and time-consuming, this experiment is only suggested but not absolutely necessary. The authors' major conclusions are still valid without this additional experiment. It's just that we don't know how fast the proteomic changes are occurring during desiccation without some timcourse as the one that I suggest here. Perhaps this point can be mentioned as a deficiency of the current work in the discussion, in lieu of doing the additional experiment.
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Reply to the reviewers
Manuscript number: RC-2022-01771
Corresponding author(s): Franck Pichaud and Rhian Walther
1. General Statements [optional]
We are grateful for the reviewers’ comments and suggestions. Both reviewers agree that our work addresses a poorly understood questions in biology and medicine, and that it will be of interest to the community of cell and developmental biologists.
We note that most of the comments/suggestions, especially from Rev#2, are concerned with the text. These include suggested references to be added, a need to expand on the Method description and suggested points of discussion. We have addressed all these issues in the revised manuscript.
Our work aims to understand which pathways control the basal geometry of epithelial cells, and how cells coordinate remodeling of their basal geometry to organize a tissue in 3D, from apical (top) to basal (bottom). This is a relatively understudied area, especially when compared to the breadth of work related to the pathways that control the apical geometry of epithelial cells.
The apical geometry of an epithelial cell is a direct function of the number of adherens junctions the cell shares with their neighbors. Suppression or extension of adherens junctions underpins apical geometry remodeling. Basally, this same cell will be attached to the basement membrane though integrin receptors. We use the fly retina, where cells adopt stereotyped basal geometry, to investigate whether and how integrin adhesion might induce cell basal geometry remodeling in morphogenesis.
The novel finding we report that a temporal sequence of event seems to underpin cell basal geometry remodeling in the retina, whereby i) laminin accumulates at specific location within the basement membrane, which is ii) accompanied by a concomitant accumulation of Dystroglycan (DG), and subsequently iii) integrin receptors are recruited to these sites of high Laminin-DG. This, along with our genetic experiments, suggests that a Laminin-DG-Integrin axis controls the basal geometry of retinal cells. In this axis, we envisage patterning of the basement membrane through Laminin-DG directs integrin recruitment, which in turn induces cell basal geometry remodeling. To our knowledge, this pathway in epithelial morphogenesis, spanning from ECM regulation to integrin polarization, has not been reported before. As the function of these components in basal adhesion is conserved across phyla, we anticipate our findings will be broadly relevant for our understanding of epithelial morphogenesis.
2. Description of the planned revisions
The main suggestion, common to both our reviewers, is that we should provide further re-assurance that the RNAi strains we use to target basement membrane components and the DG and integrin pathways are specific, and that these strains do not come with off-target effects.
We will follow this recommendation by i) including referencing when a line that we have used has been validated elsewhere, ii) by using at least two independent RNAi strains to target a gene of interest, iii) by making use of the deGrad-FP system (Caussinus et al., 2013) to target proteins instead of genes, iv) by making use of available mutant strains. This is all relatively straightforward, and I will detail the proposed experiments as part of the following point-by-point rebuttal and revision plan.
REVIEWER #1
Commenting on the need to provide further controls related to some of our RNAi experiments
1)* All the genetics experiments are based on RNAi induced knock-down approach. Although such an approach is easy to justify for genes associated with lethality when mutated, it becomes less relevant for non-lethal ones as Dystroglycan complex components (Dg, Dys, Sgc) for which null and viable mutants are published and available. The phenotype of such mutants should be provided. *
AND
*There is no data explaining how these RNAi lines were validated. The fact that it gives the phenotype expected by the authors is obviously not sufficient. This point is essential to exclude off-target effects and to be able to compare the different genotypes (see #2). For instance, the strong effect of sarcoglycan could be questioned. Is it really specific? If yes, is the difference with other Dystroglycan complex members only due to RNAi efficiency or does it have a specific function? *
AND
Line 255, "These perturbations led to a failure of bPS/Mys to accumulate at the grommet". Dg mutants are viable (PMID: 18093579); do they show consistent phenotypes?
__RE: __Our main methodology has been to use available RNAi strains to perturb composition of the basement membrane and to inhibit the expression of components of the DG and Integrin pathways. As pointed out by the reviewer, this approach allows us to assess the function of genes that might be embryonic lethal and allows us to specifically target the basal geometry remodeling step without perturbing earlier steps of retinal morphogenesis. This is important for the basement membrane and integrins, which are required although retinal tissue development. See for example: (Fernandes et al., 2014, Thuveson, 2019 #3787).
We are aware that mutant alleles are available for dg, dys and sgc allow for recovering adult homozygous (or trans-heterozygous) animals. However, based on our previous experience using mutants for which only very few flies make it to adulthood, we feel it is best not to examine those animals. Compensatory pathways might be at play that could mask a phenotype (Please see our recent work on the viable roughest null allele in cell intercalation (Blackie et al., 2021).
Therefore, we propose to induce mutant clones for dg, dys and sgc using the Flp/FRT system, using the strongest alleles that are available to us. Of note, in our experience stable proteins might not show a phenotype in small clones, but will develop a phenotype in larger ones, as the protein becomes further diluted upon multiple rounds of cell division. Bearing this in mind, we will generate animals where the whole retina is mutant for these genes. This will be done using the GMR-hid system (Stowers and Schwarz, 1999).
Specifically, we will target Dg, Dys and Sgc using:
Dystroglycan:
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The dg nonsense mutations, leading to expression of truncated proteins: DgO86 (stop codon at the R87 residue) and dgO43 (stop codon at the W462 residue) (Christoforou et al., 2008). While previous studies have suggested that these alleles are homozygous viable (Christoforou et al., 2008; Zhan et al., 2010), we have obtained this strain from the Bloomington Stock Centre, and note that no homozygous flies make it to adult. In preliminary work, we also note that clones mutant for the dgO86 allele generated with the flp-FRT system are very small, comprised of only one or two cells. This suggests that DG is required for cell proliferation or viability. These dg alleles are available on the G13 FRT which is not compatible with any FRT system designed to eliminate the wild type cells. To use the GMR-hid system, we will have to first recombine these dg alleles onto the appropriate FRT chromosome. Dystrophin:
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The dys3397 allele, which is semi-lethal P-element insertion in the dys Very few adult flies homozygous for this allele flies are recovered (Christoforou et al., 2008). We will have to recombine this allele onto an FRT chromosome to generate whole mutant retinas.
- The deficiency Df(3R)Exel6184, which removes the dys coding frame (Christoforou et al., 2008).
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We will also use dysE17, because it has been used before (Catalani et al., 2021; Cerqueira Campos et al., 2020; Mirouse et al., 2009). This lesion is a Q2807 Stop codon in the C-terminal region common to all 6 dys The Df(3R)Exel6184 and dysE17 alleles have been recombined onto FRT82B, which will allow us to make use of the GMR-hid system to generate whole mutant retinas. Sarcoglycan:
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Sgc (three subunits in Drosophila) using the deletion allele dscg169 (Allikian et al., 2007). We will have to recombine this mutation onto an FRT chromosome to generate whole mutant retinas. In addition, we will reproduce our RNAi phenotypes using additional available RNAi lines from stock centers and from previous studies, targeting different regions of dg, dys and scg. For dys we will use a validated RNAi line. For dg we will use a second RNAi line previously used in (Cerqueira Campos et al., 2020; Villedieu et al., 2023) For dys, we will use a second line previously used in (Cerqueira Campos et al., 2020). For Sarcoglycans, we will complement our work targeting scgd by also targeting scga.
Moreover, since a functional endogenously GFP-tagged Dg strain is now available (Villedieu et al., 2023) along with the Dys::GFP strain we have already used, we will target these proteins using the DeGrad-FP system (Caussinus et al., 2013). The main advantage with this system is that, as with RNAi, we can target a specific time window without affecting earlier steps in retinal morphogenesis. In addition, these experiments will address the possibility that DG and Dys might be stable in cells – inhibiting genes expression in flp-FRT induced clones does not always correlate with inhibiting protein function. We think that the well-established deGrad-GFP will be useful here to address the reviewer’s comment.
We trust these complementary approaches will more than address the reviewers’ comment by further ascertaining that the RNAi phenotypes we report here for Laminin, and the DG and integrin pathway, are specific.
Please note that we show in Fig.3 that the basal geometry phenotype we report for the talin RNAi, using an RNAi line reported in several previous studies (Lemke et al., 2019; Perkins et al., 2010; Xie and Auld, 2011; Xie et al., 2014), is comparable the phenotype we observed using the Flp-FRT system to induce mys1 mutant clones. So, we are confident this RNAi line is specific of talin. Nevertheless, we will also show results using second RNAi line targeting *talin. *
*- Authors claimed that laminin RNAi (or MMPs overexpression) affects cell geometry but why it is not analyzed by PCA? It is not consistent with the other figures. *
__RE: __To address this comment, we will provide the PCA analysis for the Laminin and MMP phenotypes.
__REVIEWER #2 __
- Line 208, "we found that LanB2 RNAi leads to defects in bPS/Mys Integrin localization". Here, because the authors use only single RNAi, there remains the possibility that the observed phenotype was caused by an off-target effect. The authors should exclude this possibility by using another RNAi or mutants. In case of LanB2, however, showing that one RNAi against LanB1 shows the same phenotype would be enough, because LanB1 is another single subunit of fly Laminin __RE: __We have now included loss-of-function mutant clones for LanB1, using the LanB1KG003456 allele, showing defects in integrin localization resembling the LanB2 RNAi (please refer to section 3: revision already done, Section). We trust that this is good validation of the LanB2 RNAi strain. These new results have been added to Figure 6 (6E-6F).
RE: “This is the same for all the RNAi experiments”. Please refer to our response to Reviewer 1, above.
2) *As the authors write "Laminin-rich domains", I suppose that they assume that LanA/B1 accumulates in a restricted region of the BM. However, it has been reported that the majority of Laminin in the fly embryo is soluble and floating in the haemolymph (fly's 'blood' or body fluid) (PMID: 29129537). Therefore, the LanA/B1 observed in the figures might be just floating in the intercellular space and doing nothing on the BM. The authors should exclude this possibility to support their idea that Laminin localised in a specific region of the BM recruits Integrin. For example, does secreted GFP (PMID: 12062063) not behave in the same way as LanA/B1? Can the authors show that the LanA/B1 is indeed incorporated in the BM by FRAP or any methods? *
RE: While formally possible, our data suggest that it is unlikely that “LanA/B1 is just floating in the intercellular space and doing nothing on the BM”. For instance, our results show that the DG pathway component Scgd is required for accumulation of LanA::GFP (Fig.7E-F). The most likely explanation for this requirement is DG binding to Laminin fibers.
Nevertheless, we will follow up on the reviewer’s comment and perform FRAP on LanA::GFP, as this is relatively straightforward. We will also try the GFP secretion experiment using the suggested GFPsecr transgene generated by the Vincent lab in 2000.
3) Line 240. "RNAi against dSarcoglycan led to a decrease in LanA::GFP expression at the presumptive grommet at 20h APF (Figure 7F)". As to this result, the authors seem to interpret that Laminin is not recruited to the "specific BM domain" in grommet in the absence of Dg signalling. However, other possibilities exist, e.g., that the global expression level of Laminin was reduced, or that the intercellular space into which soluble Laminin (see the issue 4 above) flows was narrowed down. The authors should show the data that exclude (or at least reduce) these possibilities.
__RE: __Addressing Rev2 point (1) will rule out that Laminin is in soluble form. To address the comment that the global expression level of Laminin might be decreased, we will quantify the amount of LanA::GFP that is not at the grommet and compare wild type animals with the scgd ones.
3. Description of the revisions that have already been incorporated in the transferred manuscript
__REVIEWER #1 __
- Line 208, "we found that LanB2 RNAi leads to defects in bPS/Mys Integrin localization". Here, because the authors use only single RNAi, there remains the possibility that the observed phenotype was caused by an off-target effect. The authors should exclude this possibility by using another RNAi or mutants. In case of LanB2, however, showing that one RNAi against LanB1 shows the same phenotype would be enough, because LanB1 is another single subunit of fly Laminin __RE: __We have included new results – LanB2 loss of function – showing the role of Laminin in being required for Integrin localization in the secondary and tertiary pigment cells (revised Figure 6 – panels E-F)
Line 237: For this, we used both RNAi against LanB2 and a loss-of-function allele of LanB1. Consistent with our model, we found that in both cases bPS/Mys Integrin localization was affected. bPS/Mys failed to accumulate at the grommet, and instead was distributed at the basal plasma membrane into punctate domains (Figure 6A-F). In addition, these perturbation experiments affected cell basal geometry remodeling (Figure 6A, 6C, 6E).
2)* Methods section describing genetic conditions is really sketchy. The genotype corresponding to each figure is not provided and I guess that GMR-Gal4 has been used in all experiments using the Gal4 system but it is never clearly stated. *
__RE: __We have revisited the Methods section and Figure Legends to ensure all appropriate information is readily accessible to the reader. The reviewer is correct that the retinal GMR-Gal4 driver was used to express the RNAi used in this study.
3) PCA analysis. - In the WT situation it would be really informative to know which variable(s) is/are really discriminant between the two cell populations and then maybe to focus a bit more on these parameters. For instance, a PCA correlation circle plotting both cells and variables would be very helpful.
__RE: __We have followed the reviewer’s advice and amended the Methods section accordingly. We now provide the PCA correlation circle plotting both cells and variables in Suppl. Fig. 3, for talin RNAi and MysDN, and Suppl. Fig. 10 for DG and Scgd RNAi
*Methods: *
Line 522 : Principle component analysis
Principal component analysis (PCA) was carried out using the Scikit-learn library in Python. The Standard scaler package was used to standardize the data across all metrics before calculating the principal components. The PCA package was then used to perform the PCA. Metrics included in the PCA were as follows: extent, major axis length, minor axis length, eccentricity, roundness, circularity, area, cell shape index, perimeter.
The cell types (secondary and tertiary pigment cells) were assigned by following the cells in 3D to the apical surface where the cell types could be identified. Cells that could not be clearly assigned as either secondary or tertiary pigment cells were excluded from the PCA.
Extent is the area of an object divided by the area or the smallest rectangle (bounding box) that can fit around the object.
Major axis length is the longest line that can be drawn through an object.
Minor axis length is the line that can be drawn through an object which is perpendicular to the major axis.
__Eccentricity __is the ratio of the length of the short (minor) axis to the length of the long
(major) axis.
Roundness is a comparison of an object to the best fit circle of an object. The closer the object is to a perfect circle, the more round it will be.
Circularity is a measure of the smoothness of an object.
Cell shape index is a dimensionless parameter to describe cell shape. When cells have smaller contacts with their neighbours the cell shape index is small.
Correlation circle plots were generated using the mlxtend plotting package in python using the plot PCA correlation graph function.
- Please also see the graphs we now provide in Suppl. Fig.4*. *
We are also commenting on these results.
Line 174: To understand which parameters explained most of the variance in the PCA analysis we generated correlation circle plots (Supplementary Figure 4). For wildtype cells, perimeter and circularity contribute most to the variance between secondary and tertiary pigment cells along the PC1 axis. Eccentricity and minor axis length contribute most to variance along the PC2 axis (Supplementary Figure 4A). For talin RNAi and MysDN cells, the correlation circle plots are remarkably similar (Supplementary Figure 4B-C), indicating that these genetic perturbations have similar effects on cell basal geometry. To confirm this result, we performed PCA comparing secondary and tertiary pigment cells for these two genotypes. In both genotypes, cells fail to form discrete clusters (Supplementary Figure 4D-E). For the secondary pigment cells, expressing talin RNAi or MysDN leads to an increase in cell roundness. For the tertiary pigment cell, these genotypes lead to an increase in circularity (Supplementary Figure 4D-E). Examining the original segmentation data confirmed that, relative to wildtype cells, either genetic perturbation has a similar effect on key cell shape parameters (Supplementary Figure 4F-G).
*- In loss of function conditions, when the tissue is strongly affected, how do the authors recognize the two cell populations if PCA cannot? *
__RE: __In these genotypes, each cell type is identified based on their apical position and geometry. When a cell cannot be identified it is not included in the analysis. This allowed us to track the cells from apical to basal. We now make this clear in the Methods section.
Line 529: The cell types (secondary and tertiary pigment cells) were assigned by following the cells in 3D to the apical surface where the cell types could be identified. Cells that could not be clearly assigned as either secondary or tertiary pigment cells were excluded from the PCA.
- On the opposite, based on the provided image, Dys RNAi seems to have a mild effect and it seems that my eyes can easily recognize those two cell populations based on their shape. So why PCA cannot?
__RE: __We respectfully disagree with this comment. In the Dys RNAi, one cannot tell which is a secondary and which is a tertiary by visual inspection of the basal surface only. This is consistent with the PCA analysis, now described more thoroughly in Supplemental Figure 4. The Dys RNAi cells tend to remain elongated and they do not round up as much as the Scgd RNAi cells, which gives the false impression that the phenotype is closer to that of the wild type.
- Based on the proposed images, some phenotypes look clearly different depending on the genotype, e.g. Talin and Mys (figure 3) or Dys and Sgc (Figure 8). In other words, the fact that PCA cannot separate the cell pollutions in these different genotypes does not necessarily mean that their effect is identical. Could authors perform PCA analysis between mutants? If they are different, again it might be very interesting to identify the discriminating parameters.
RE: We did not claim the defect was identical__. __
The basal geometries look somewhat different depending on the genotype, and we envisage this is due to differences in RNAi strength and perhaps differences in protein stability. This is the case for Dys and Scgd, as outlined in the preceding point. With respect to talin and mys, none of the authors can distinguish by eye the talin RNAi from mys1 phenotypes. We have informally asked our institutional colleagues, and they were also unable to distinguish these genotypes.
Nevertheless, we have expanded our PCA analysis between phenotypes, considering one cell type at a time. This analysis shows that these phenotypes show partial overlap, outside of the wildtype range. While there are similarities, it does not reveal, however, any specific relationship between genes of interest (see previous).
Line 178: For talin RNAi and MysDN cells, the correlation circle plots are remarkably similar (Supplementary Figure 4B-C), indicating that these genetic perturbations have similar effects on cell basal geometry. To confirm this result, we performed PCA comparing secondary and tertiary pigment cells for these two genotypes. In both genotypes, cells fail to form discrete clusters (Supplementary Figure 4D-E). For the secondary pigment cells, expressing talin RNAi or MysDN leads to an increase in cell roundness. For the tertiary pigment cell, these genotypes lead to an increase in circularity (Supplementary Figure 4D-E). Examining the original segmentation data confirmed that, relative to wildtype cells, either genetic perturbation has a similar effect on key cell shape parameters (Supplementary Figure 4F-G).
*- From what I can understand, each PCA analysis has been done on a single retina. If true, more replicates should be included. If not true, the number of independent retinas should be mentioned. *
__RE: __All PCA analyses have been done using multiple retinas from different animals. We have clarified this in the figure legends.
4) Minor comments: - Globally, the article suffers from a lack of details, especially in the methods section and/or in figure legends.
RE: please see what we have done to address this comment, in section (2) above.
*- Also, several points could be advantageously discussed. For instance, why MMPs have different effects according to their specificity? Also, what could be the meaning of the nice differential pattern between integrin alpha subunits? *
__RE: __We were concerned this would be seen as too speculative by our reviewers. Following the reviewer’s advice, we are happy to share our current working model and speculations on this.
Results:
Line 242: Moreover, and consistent with basement membrane regulation being important for cell basal geometry remodeling, we found that degrading the basement membrane by expressing Matrix Metalloproteases MMP1 or MMP2 in retinal cells leads to a failure in bPS/Mys localization at the grommet and prevented cell basal geometry remodeling (Figure 6G-J). While recombinant Drosophila MMP1 and 2 can degrade Col-IV, only MMP2 can degrade Laminin (Wen et al., 2020). The MMP2 phenotype we observed in basal surface organization is stronger than that of the MMP1 overexpression. Our results, therefore, suggest that both Col-IV and Laminin play a role in controlling the basal geometry of retinal cells. This suggestion is consistent with our finding that both these basement membrane proteins are enriched at the grommet once cells have acquired their basal geometry.
Discussion:
Line 386: Integrins can bind to Col-IV and to Laminin (Hynes, 2002). Our experiments show that MMP2 overexpression leads to a stronger phenotype than MMP1. In addition to catalyzing Collagen-IV proteolysis, MMP2 can degrade Laminin, which is something MMP1 does not seem to be able to do (Wen et al., 2020). Therefore, our results suggest that both Col-IV and Laminin are required for cell basal geometry remodeling.
Line 408*: *
The cone cells express two Integrin receptors, ____a____PS1/Mew-____b____PS/Mys and ____a____PS2/if-____b____PS/Mys
We found that while the interommatidial cells express aPS1/Mew-bPS/Mys, the cone cells express both aPS1/Mew-bPS/Mys and aPS2/if-bPS/Mys. Thus, different cell types express different aPS subunits. It is not clear why the cone cells express two a-subunits. In the developing follicular epithelium of the fly oocyte, cells switch from expressing aPS1/Mew-bPS/Mys, to expressing aPS2/if-bPS/Mys (Delon and Brown, 2009). In this tissue, the developmental switch between aPS1 and aPS2 expression was shown to correlate with a change in stress fiber orientation. In addition, aPS1-bPS/Mys was also shown to be required to control F-actin levels basally. aPS1 mutant cells presented elevated levels of F-actin, a phenotype not seen in aPS2 mutant cells. Remarkably, in this tissue, aPS2-bPS/Mys, but not aPS1/Mew-bPS/Mys was able to recruit the integrin adapter Tensin. The authors envisaged that the aPS2 Tensin interaction might confer robustness in basal surface remodeling. With analogy to the follicular epithelium, we speculate that in the cone cells, aPS1-bPS/Mys and aPS2/Mew-bPS/Mys synergize in mediating robust attachment to the basement membrane, to ensure these cells do not detach as the retina lengthens along the apical-basal axis (Longley and Ready, 1995). We also note that in retinal development, the cone cells form new adherens and septate junctions at their basal feet (Banerjee et al., 2008). These cells, therefore, present two sets of adherens and Septate junctions. It is also possible that the atypical situation seen with the cone cells expressing two a subunits, is linked to the formation of these new junctions at the basal pole of these cells. It will be interesting to examine these possibilities, and to establish the role these two a-subunits play in cone cell morphogenesis. Further, the presence of two distinct integrin subunits within the cone cells may have implications when considering Integrin signaling during cone cell morphogenesis.
*- In Methods, a list of metrics is given for the PCA analysis but some look very similar and it would be helpful to define them briefly. *
RE: Please refer to what we have done to address this comment in section (2) above.
*- Figures are not always color-blind adjusted (e.g. dots on PCA graphs). *
__RE: __We have rectified this oversight.
__REVIEWER #2 __
1)* Line 169, "From these experiments, we conclude that Integrin adhesion is required for cell basal geometry remodeling during retinal morphogenesis". It has been long known that integrin is necessary for the gross morphogenesis of the eye (e.g., Zusman et al. 1993, PMID: 8076515). The authors need to cite these preceding researches and should clarify what new findings this new work adds to the previous knowledge. *
__RE: __Following the reviewer’s suggestion, we have added this reference which precedes (Longley and Ready, 1995)mentioned in the paper. Both references show that integrins are required for eye integrity and attribute this function to the contraction phase of retinal development. Notably, contraction occurs after cells have remodelled their basal geometry, which we have focused on in this study.
Line 128: The Integrin bPS subunit (Myspheroid, Mys) is required to maintain surface integrity late in retinal development, as the tissue surface undergoes basal contraction (Longley and Ready, 1995; Zusman et al., 1993).
4) Line 180, "Using available functional GFP protein traps [49, 50]", the authors investigate the behaviour of Laminin subunits LanA and LanB1. First, ref [50] is not relevant here and should be removed. Moreover, the Laminin-GFPs the authors used are not protein traps, but transgenic strains harbouring genes and most of their regulatory information, with the ORFs tagged with GFP [49]. Furthermore, while the ref [49] reported the functionality of LanB1-GFP, this reference did not fully address the functionality of LanA-GFP. The authors need another reference on it (PMID: 29129537), which demonstrated that LanA-GFP rescues LanA mutants.
5) Related to the issue above, in addition to LanA and LanB1, the authors examine the localisation of the following BM proteins using GFP-fusion: Perlecan/Trol, Collagen IV/Viking, Nidogen, and SPARC. The authors do not explicitly describe the nature of these GFP fusions, but I am afraid that the authors think all of them are "functional protein traps". However, in fact while Perlecan and Collagen IV are protein traps, Nidogen and SPARC are transgenics including regulatory sequences made in the ref [49]. This must be clarified. Moreover, to rely on the data obtained using these GFP fusions, their functionality must be confirmed by appropriate references or/and the authors' own data. For information, ref [62] showed the functionality of Perlecan-GFP and Collagen IV-GFP protein traps (they are both homozygous viable), and the Nidogen-GFP transgene rescues the BM deficiency of Ndg mutants (PMID: 30260959). These reports must be explained in the text, and I would like the authors collect and show more information.
__RE: __We have deleted ref 50. We thank the reviewer for flagging the issue with our referencing. We have now amended this section.
Line 204: To this end, we examined the localization and requirement of the Laminin A and B1 subunits (Laminina, LanA and Lamininb, LanB1), Perlecan/Trol, Collagen-IV/Viking (Col-IV), the glycoprotein Nidogen (Entactin/Ndg), and the secreted glycoprotein protein-acidic-cysteine-rich (Sparc), which are all components of the basement membrane (Walma and Yamada, 2020). For Laminin, Ndg and SPARC, we used strains generated from a fosmid library, and expressing a functional GFP-tagged transgene under the control of their own respective promoter (Dai et al., 2018; Matsubayashi et al., 2017; Sarov et al., 2016). For Col-IV and Perlecan, we used functional GFP exon-trap strains (Morin et al., 2001).
6) Line 200, "These specific patterns of expression for LamininA/B1, Collagen IV, Perlecan, Nidogen and Sparc". I have several comments here: - 5A. These patterns are discussed only using single optical sections. To highlight the difference in their localisation patterns more objectively, multiple sections and/or 3D images should be shown.
RE: (a) These are all projections of 3 to 5 confocal sections, and we have amended the manuscript to make this point clearer. (b) Following the reviewer’s advice, we now provide sagittal sections so the reader can better appreciate what is detected above and below the grommet. Please see new Fig. 5.
5B. Can the authors discuss, hypothesise, or speculate the biological meaning of the difference? * AND*
*5C. It has been reported that in the mammalian skin BM, different components show distinct localisation patterns (PMID: 33972551). It would be interesting to cite this paper and discuss the generality of the non-uniform distribution of BM components. *
__RE: __The revised manuscript offers a short discussion in this topic.
Line: 367 The idea that different cell types in a tissue can express different ECM components, and thus induce localized specialization of a basement membrane is well-supported by recent work in the mouse hair follicle. In this sensory organ, the architecture and composition of the basement membrane is highly specialized depending on the cell-cell and cell-tissue interface considered (Cheng et al., 2018; Fujiwara et al., 2011; Joost et al., 2016). Moreover, different cell populations – epithelial stem cells and fibroblasts, express different ECM components in the hair follicle (Tsutsui et al., 2021), supporting the notion that specific basement membrane organization contributes to cell-cell communication and overall 3D tissue architecture.
7) Line 215, "However, inhibiting the expression of Collagen IV, Ndg, Perlecan and Sparc individually, by expressing RNAi against these genes in all retinal cells, did not lead to defects in bPS/Mys localization". To conclude so, the authors must demonstrate that the used RNAis efficiently removed its target proteins.
__RE: __We have removed this section referring to Collagen IV, Ndg, Perlecan and Sparc.
Instead, we now focus solely on Laminin. Because Laminin accumulation at the presumptive grommet precedes that of the other ECM factors examined in our study, we favor a model in which Laminin plays a key role in promoting integrin localization.
8)* Line 222, "DG is required to organize the ECM in several experimental settings [42, 43, 45, 51]". Here, the authors must mention to a preceding paper that reported the eye deficiency of Dg mutant flies (PMID: 20463973), and discuss what new findings authors can add to the previous report. *
__RE: __We have followed this recommendation.
Line 441: We also note that a previous study showed that early in retinal development, DG localizes at the apical membrane of the photoreceptors. This study proposed that DG promotes elongation of these sensory neurons, independently to any potential role this surface receptor might play in basement membrane organization (Zhan et al., 2010). This conclusion was based on Df(2R)Dg248 mutant clones and trans-heterozygous retinas, where DG function was impaired not only in photoreceptors, but in all interommatidial cell types. Moreover, the basement membrane was not examined in this study. Our work, and the fact the bulk of retinal cell elongation occurs late in retinal development(Longley and Ready, 1995), is consistent with DG playing a role in retinal cell elongation and overall tissue thickening.
Under “Advance”:
*The 3D imaging of ommatidia development is beautiful and of good descriptive value. ** However, as mentioned in the major comments 1, 2, 3, and 8 above, I am afraid that the search of preceding literature seems insufficient, and it is often unclear what this manuscript add to existing knowledge. *
__RE: __The logic of how the reviewer links points 2, and 3 they raise as part of their review, to their assessment of how our work advances the field, is unclear to me. Their Points 2 and 3 have to do with making sure we better explain how the functional ECM transgenes were generated and by whom. The importance the reviewer places on points 2, 3 when considering the Advance our work provides to the field does not appear justified to me.
Point 1 refers to a previous study by Zusman et al., published in 1993. Using partial loss of function alleles and heat-shock inducible rescue constructs they show that bPS/Mys plays a role in eye development. They note that in adult eyes, retinal cells are not attached to their basement membrane. They show this is accompanied by a failure for the retina to elongate along the apical-basal axis. These phenotypes are consistent with a role for integrins in mediating attachment of epithelial cells to the basement membrane, and we are now referring to this work in the revised manuscript. A much more relevant reference to our work however, is (Longley and Ready, 1995), which we have used repeatedly in our manuscript to stress what was novel about our work.
Point 8 refers to a previous report implicating DG in photoreceptor elongation, which is a developmental phase that mostly occurs after the process we are studying here (please see Fig.3 of (Longley and Ready, 1995) for quantification using sections). The photoreceptors do no contribute basal profiles at the basal surface of the retina. The DysGFP signal we detect at this tissue surface, in the presumptive and established grommet, is clearly coming from the pigment cells, not from the photoreceptor axons which are found at this basal location. We now discuss this previous report, to make what is clearer what is novel about our own work.
.
Minor comments: - Line 85, "This is the case in the follicular epithelium for example". Here, the text would be more reader-friendly if the authors could clarify this is the follicular epithelium of the fly ovary.
__RE: __We have modified the text to address this comment.
- Line 203-, regarding all the experiments involving the Gal4-UAS system. Not all the readers are familiar with the system. A brief explanation on it should be added in the main text. Moreover, in the Results section, not in the Methods, the authors should show what Gal4 they used, and where is the Gal4 expressed.
__RE: __We have amended the manuscript accordingly.
*- Line 239, "We found that inhibiting the expression of the DG cofactor, dSarcoglycan [53] was most effective in inhibiting this pathway in retinal cells". Here, the authors should show the data. *
__RE: __This statement is based on the results shown in Fig.8 and Suppl. Fig.9, which make use of a PCA representation to quantify the Dg, Dys and dScg RNAi phenotypes in cell basal geometry. We have re-phrased this statement to make it clear that we are referring to the RNAi-based perturbation of these genes’ expression.
4. Description of analyses that authors prefer not to carry out
We will address all the reviewer comments as they will consolidate our findings.
Our further validation of the few RNAi lines used in our study that have not been used before in publications will also be valuable to the community.
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Xie, X., Gilbert, M., Petley-Ragan, L., and Auld, V.J. (2014). Loss of focal adhesions in glia disrupts both glial and photoreceptor axon migration in the Drosophila visual system. Development 141, 3072-3083.
Zhan, Y., Melian, N.Y., Pantoja, M., Haines, N., Ruohola-Baker, H., Bourque, C.W., Rao, Y., and Carbonetto, S. (2010). Dystroglycan and mitochondrial ribosomal protein L34 regulate differentiation in the Drosophila eye. PLoS One 5, e10488.
Zusman, S., Grinblat, Y., Yee, G., Kafatos, F.C., and Hynes, R.O. (1993). Analyses of PS integrin functions during Drosophila development. Development 118, 737-750.
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Referee #2
Evidence, reproducibility and clarity
Summary:
Cell shape remodelling is essential for tissue morphogenesis. To model this event, the fruit fly Drosophila melanogaster has been widely used. In the pupal retina, ommatidial cells change their structure to form the photo-sensing machinery in the compound eye. Previous studies investigating this event mainly focused on the cell shape change at the apical plane. However, the cell shape at the basal side and the three-dimensional (3D) structure of the cells have been little studied.
In this manuscript, the authors address this issue by combining state-of-art 3D imaging and fly genetics. They report that at the initial stage of eye development, a basement membrane (BM) component Laminin accumulates at the basal side of the ommatidial cells in a manner dependent on the BM-receptor molecule dystroglycan (Dg). The authors propose that this Dg-dependent Laminin accumulation induces the polarisation of integrin at the basal surface, which is essential for proper ommatidia morphogenesis.
Major comments:
The beautiful images presented here provide interesting descriptions of the events occurring during eye development. Also, the authors propose an attractive and simple hypothesis that the Dg-dependent recruitment of Laminin leads to integrin polarisation and tissue morphogenesis. However, I'm afraid that this hypothesis is not supported enough by the presented data. In addition, the novelty of some conclusions and the reliability of a number of reagents used are unclear. Specific concerns are described below:
- Line 169, "From these experiments, we conclude that Integrin adhesion is required for cell basal geometry remodeling during retinal morphogenesis". It has been long known that integrin is necessary for the gross morphogenesis of the eye (e.g., Zusman et al. 1993, PMID: 8076515). The authors need to cite these preceding researches and should clarify what new findings this new work adds to the previous knowledge.
- Line 180, "Using available functional GFP protein traps [49, 50]", the authors investigate the behaviour of Laminin subunits LanA and LanB1. First, ref [50] is not relevant here and should be removed. Moreover, the Laminin-GFPs the authors used are not protein traps, but transgenic strains harbouring genes and most of their regulatory information, with the ORFs tagged with GFP [49]. Furthermore, while the ref [49] reported the functionality of LanB1-GFP, this reference did not fully address the functionality of LanA-GFP. The authors need another reference on it (PMID: 29129537), which demonstrated that LanA-GFP rescues LanA mutants.
- Related to the issue above, in addition to LanA and LanB1, the authors examine the localisation of the following BM proteins using GFP-fusion: Perlecan/Trol, Collagen IV/Viking, Nidogen, and SPARC. The authors do not explicitly describe the nature of these GFP fusions, but I am afraid that the authors think all of them are "functional protein traps". However, in fact while Perlecan and Collagen IV are protein traps, Nidogen and SPARC are transgenics including regulatory sequences made in the ref [49]. This must be clarified. Moreover, to rely on the data obtained using these GFP fusions, their functionality must be confirmed by appropriate references or/and the authors' own data. For information, ref [62] showed the functionality of Perlecan-GFP and Collagen IV-GFP protein traps (they are both homozygous viable), and the Nidogen-GFP transgene rescues the BM deficiency of Ndg mutants (PMID: 30260959). These reports must be explained in the text, and I would like the authors collect and show more information.
- Line 182-, LanA and LanB1 "accumulate at the center of the ommatidium, in a pattern resembling the grommet structure (Figure 4A and Supplementary Figure 4)"... "LamininA/B1 accumulation at the presumptive grommet precedes Integrin accumulation at this location. It suggests that localized Laminin might control Integrin localization in the interommatidial cells". Based on these results, the authors discuss that "generating specific polygonal geometries at the basal surface of cells starts with organizing the ECM to establish a pattern of Laminin-rich domains, distributed across the tissue basal surface" (Line 267).
As the authors write "Laminin-rich domains", I suppose that they assume that LanA/B1 accumulates in a restricted region of the BM. However, it has been reported that the majority of Laminin in the fly embryo is soluble and floating in the haemolymph (fly's 'blood' or body fluid) (PMID: 29129537). Therefore, the LanA/B1 observed in the figures might be just floating in the intercellular space and doing nothing on the BM. The authors should exclude this possibility to support their idea that Laminin localised in a specific region of the BM recruits Integrin. For example, does secreted GFP (PMID: 12062063) not behave in the same way as LanA/B1? Can the authors show that the LanA/B1 is indeed incorporated in the BM by FRAP or any methods? 5. Line 200, "These specific patterns of expression for LamininA/B1, Collagen IV, Perlecan, Nidogen and Sparc". I have several comments here: 5A. These patterns are discussed only using single optical sections. To highlight the difference in their localisation patterns more objectively, multiple sections and/or 3D images should be shown. 5B. Can the authors discuss, hypothesise, or speculate the biological meaning of the difference? 5C. It has been reported that in the mammalian skin BM, different components show distinct localisation patterns (PMID: 33972551). It would be interesting to cite this paper and discuss the generality of the non-uniform distribution of BM components. 6. Line 208, "we found that LanB2 RNAi leads to defects in bPS/Mys Integrin localization". Here, because the authors use only single RNAi, there remains the possibility that the observed phenotype was caused by an off-target effect. The authors should exclude this possibility by using another RNAi or mutants. This is the same for all the RNAi experiments. In case of LanB2, however, showing that one RNAi against LanB1 shows the same phenotype would be enough, because LanB1 is another single subunit of fly Laminin. 7. Line 215, "However, inhibiting the expression of Collagen IV, Ndg, Perlecan and Sparc individually, by expressing RNAi against these genes in all retinal cells, did not lead to defects in bPS/Mys localization". To conclude so, the authors must demonstrate that the used RNAis efficiently removed its target proteins. 8. Line 222, "DG is required to organize the ECM in several experimental settings [42, 43, 45, 51]". Here, the authors must mention to a preceding paper that reported the eye deficiency of Dg mutant flies (PMID: 20463973), and discuss what new findings authors can add to the previous report. 9. Line 240. "RNAi against dSarcoglycan led to a decrease in LanA::GFP expression at the presumptive grommet at 20h APF (Figure 7F)". As to this result, the authors seem to interpret that Laminin is not recruited to the "specific BM domain" in grommet in the absence of Dg signalling. However, other possibilities exist, e.g., that the global expression level of Laminin was reduced, or that the intercellular space into which soluble Laminin (see the issue 4 above) flows was narrowed down. The authors should show the data that exclude (or at least reduce) these possibilities. 10. Line 255, "These perturbations led to a failure of bPS/Mys to accumulate at the grommet". Dg mutants are viable (PMID: 18093579); do they show consistent phenotypes?
Minor comments:
- Line 85, "This is the case in the follicular epithelium for example". Here, the text would be more reader-friendly if the authors could clarify this is the follicular epithelium of the fly ovary.
- Line 203-, regarding all the experiments involving the Gal4-UAS system. Not all the readers are familiar with the system. A brief explanation on it should be added in the main text. Moreover, in the Results section, not in the Methods, the authors should show what Gal4 they used, and where is the Gal4 expressed.
- Line 239, "We found that inhibiting the expression of the DG cofactor, dSarcoglycan [53] was most effective in inhibiting this pathway in retinal cells". Here, the authors should show the data.
Referee cross-commenting
This session includes comments from both reviewers
Reviewer 2: I almost totally agree with Reviewer 1, who is also mainly concerned about the functional analyses part of the paper while being impressed by the authors' beautiful imaging. One issue that Reviewer 1 and I apparently disagree with is the Estimated time to Complete Revisions: while they say 1-3 months, I say 3-6. However, actually I don't think this is a serious discrepancy. Thinking of the time to obtain flies and carry out their crosses necessary for the requested experiments, I'm afraid that the revision cannot be done in 1 month. However, if the authors are fortunate, they may finish the revision in 2-3 months. As I still think that the authors may struggle, I would say the time 2-6 months. I'd be glad if the comments of Reviewer 1 and me could complement with each other to help the revision of the manuscript.
Reviewer 1:As Reviewer #2 mentioned, there is a strong convergence of our opinions on this article, which should make the work of the authors easier. In fact, I hesitated between 1-3 or 3-6 months for the estimated revision time.
Reviewer2: Thank you Reviewer #1 for your response. I guess we (Reviewers #1 and #2) have reached an agreement now, haven't we?
Significance
General assessment:
The beautiful images presented here provide interesting descriptions of the events occurring during eye development. Also, the authors' hypothesis on the Dg-dependent recruitment of Laminin leading to integrin polarisation and tissue morphogenesis is simple and attractive. However, I'm afraid that this hypothesis is not supported enough by the presented data. In addition, the novelty of some conclusions and the reliability of a number of reagents used are unclear. Therefore, I cannot say that the conclusions of this manuscript are solid.
Advance:
The 3D imaging of ommatidia development is beautiful and of good descriptive value. However, as mentioned in the major comments 1, 2, 3, and 8 above, I am afraid that the search of preceding literature seems insufficient, and it is often unclear what this manuscript add to existing knowledge.
Audience:
If the issues mentioned above have been solved, this manuscript would be of general interest to researchers in various fields in cell and developmental biology. Would not be restricted to those using Drosophila.
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Referee #1
Evidence, reproducibility and clarity
Walther and colleagues address the role of the cell/ECM interface for cell shape, focusing on the basal domain of epithelial cells. More specifically, they present a thorough descriptive approach on the intricate morphology of the neuroepithelial cells composing Drosophila ommatidia in the retina and relate it to the organization of the basal lamina and the complexes interacting with it, Dystroglycan and integrins. Based on genetics and quantitative imaging approaches, they propose a linear mechanism where 1) Dystroglycan organizes the basal membrane 2) this organization guides the localization of integrins 3) integrin localization defines the shape of the basal domain.
Major comments:
First, the 3D description of the ommatidia organization is really nice and interesting, refreshing quite old data using better imaging tools. In particular, it illustrates the extreme difference in morphology between the apical pole and the basal pole of the cells composing the ommatidia, making it a paradigm for understanding how the basal shape is defined independently of the apical one. It also provides a nice and detailed spatiotemporal cartography of basement membrane components, integrin and dystroglycan. However, functional data are less convincing, mainly for technical issues, but could be really improved in a reasonable timeline. My criticisms mainly converge on two aspects of the experimental work :
1) Genetics :
- All the genetics experiments are based on RNAi induced knock-down approach. Although such an approach is easy to justify for genes associated with lethality when mutated, it becomes less relevant for non-lethal ones as Dystroglycan complex components (Dg, Dys, Sgc) for which null and viable mutants are published and available. The phenotype of such mutants should be provided.
- There is no data explaining how these RNAi lines were validated. The fact that it gives the phenotype expected by the authors is obviously not sufficient. This point is essential to exclude off-target effects and to be able to compare the different genotypes (see #2). For instance, the strong effect of sarcoglycan could be questioned. Is it really specific? If yes, is the difference with other Dystroglycan complex members only due to RNAi efficiency or does it have a specific function?
- Methods section describing genetic conditions is really sketchy. The genotype corresponding to each figure is not provided and I guess that GMR-Gal4 has been used in all experiments using the Gal4 system but it is never clearly stated.
2) Image analysis by PCA
After segmentation, authors analyzed their images by PCA using various parameters, which allows them to discriminate between two cell populations that correspond to SC and TC. Then, whatever the genotype they studied, PCA failed to separate those two cell populations leading the authors to propose that they all lead to similar morphological defects, arguing for a linear pathway Dystroglycan / BM / integrins. However, this approach raises many questions: - In the WT situation it would be really informative to know which variable(s) is/are really discriminant between the two cell populations and then maybe to focus a bit more on these parameters. For instance, a PCA correlation circle plotting both cells and variables would be very helpful. - In loss of function conditions, when the tissue is strongly affected, how do the authors recognize the two cell populations if PCA cannot? On the opposite, based on the provided image, Dys RNAi seems to have a mild effect and it seems that my eyes can easily recognize those two cell populations based on their shape. So why PCA cannot? - Based on the proposed images, some phenotypes look clearly different depending on the genotype, e.g. Talin and Mys (figure 3) or Dys and Sgc (Figure 8). In other words, the fact that PCA cannot separate the cell pollutions in these different genotypes does not necessarily mean that their effect is identical. Could authors perform PCA analysis between mutants? If they are different, again it might be very interesting to identify the discriminating parameters. - Authors claimed that laminin RNAi (or MMPs overexpression) affects cell geometry but why it is not analyzed by PCA? It is not consistent with the other figures. - From what I can understand, each PCA analysis has been done on a single retina. If true, more replicates should be included. If not true, the number of independent retinas should be mentioned.
Minor comments: - Globally, the article suffers from a lack of details, especially in the methods section and/or in figure legends.
Also, several points could be advantageously discussed. For instance, why MMPs have different effects according to their specificity? Also, what could be the meaning of the nice differential pattern between integrin alpha subunits?
In Methods, a list of metrics is given for the PCA analysis but some look very similar and it would be helpful to define them briefly.
Figures are not always color-blind adjusted (e.g. dots on PCA graphs).
Significance
This article addresses a relevant and still poorly answered question, which is how the shape of epithelial cells is defined on the side of their basal domain. Indeed, the vast majority of studies tackle this issue for the apical domain with the role of adherens junction and their regulators. Instead, here, the authors explore the role of BM/cell interface. They especially propose a specific sequence of events leading in fine to the proper subcellular targeting of integrins. Whereas many studies on other systems have reached similar conclusions on each of the different steps of this sequence, the main interest of the paper is to bring them together, allowing the proposal of a general framework. Of notice, they made it possible by first doing a nice description of their system. However, functional analysis is somehow superficial and does not really provide mechanistic clues for each step (i.e. how Dystroglycan allows BM assembly and/or secretion, how Integrins controls cell shape.... ).
Nonetheless, such an article might interest anyone working on tissue morphogenesis in vivo or ex vivo and wondering what the role of cell/BM interplay could be in its own system. Moreover, these protein complexes are highly conserved and involved in many diseases in humans. Thus, getting a more global understanding of their relationships is also relevant for readers working on the aetiology and pathophysiology of those diseases.
I am a developmental biologist interested in morphogenesis.
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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 authors presented a comprehensive analysis of the effects of RBM12 on cAMP signaling and cAMP-induced transcription. All data point to hyperactivity in the absence of RBM12, suggesting that RBM12 negatively regulates cAMP signaling, particularly transcriptional response to CAMP in the nucleus. The authors found that increased expression of two adenylyl cyclase isoforms and reduced expression of PKA regulatory subunit and some isoforms of cAMP-destroying PDE is the molecular basis of excessive cAMP signaling in the absence of RBM12. The authors showed that two disease-associated RBM12 mutants are loss-of-function, as, in contrast to WT RBM12, they fail to normalize cAMP signaling and transcriptional response. The authors should be commended for confirming their findings in iPSC-derived neurons. The study is well performed and clearly described.
Significance
Identification of earlier unappreciated mechanism regulating cAMP signaling has broad implications.
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Referee #2
Evidence, reproducibility and clarity
Summary
The authors have previously carried out a CRISPR screen of b2-AR regulators of transcriptional responses. In this manuscript, the authors proceed to characterize one of the top candidates from this screen, RNA-binding motif 12 (RBM12). They perform numerous studies in HEK293 cells and iPSC-derived neurons to show that loss of RBM12 leads to a hyperactive response of ligand-induced b2AR transcription, cAMP responses and PKA activity. This increase in transcriptional responses is independent in changes of b2AR receptor expression or internalization and can be observed upon activation of other Gs-coupled GPCRs, namely ligands for adenosine A1/2R and dopamine D1R. The hyperactive transcriptional responses can also be mimicked in wild-type cells with forskolin, isoproterenol plus phosphodiesterase inhibitor, or use of cAMP analog 8-CPT-cAMP. The authors also show that variants of RPM12, that lead to familial psychosis, show hyperactive responses to isoproterenol and cannot rescue loss of wild-type RPM12. Finally, transcriptomics of loss of RPM12 in iPSC-derived neurons show altered transcriptional profiles upon stimulation with b2AR agonists.
Major comments
Overall this is a comprehensive study of the effects of RBM12 on cAMP-dependent transcriptional responses. The study is highly rigorous and the authors generate several novel findings, supplying a mechanism for disease-altering variants for RBM12. There are a few issues that distract somewhat as detailed below.
- The authors are highly focused on the GPCR responses; thus, they fail to discuss the fact that supplemental figures 1D-F show that the effects of RBM12 lie downstream of the receptor and are independent of b2AR. Stimulation with forskolin shows prominent enhancement of cAMP accumulation, pointing to enhancement of adenylyl cyclase and/or decreases in PDE activity. This effect should be quantitated. The is consistent with the fact that stimulation with multiple Gs-coupled receptors show similar enhancements. Given that, much of Fig 2, particularly 2E should be moved to supplemental. The order of figures may need to be re-examined.
- 1b. The cAMP responses in Supplemental Fig 3 should also be quantitated with statistics.
- The use of 8-CPT-cAMP is not appropriate as a pure cAMP analog. It not only activates PKG, but it can also increase cGMP due to inhibition of phosphodiesterases that breakdown cGMP (PDE5).
- It is not clear why the authors are overexpressing the b2AR in the iPSC-derived neurons. The application of isoproterenol under conditions of overexpressed receptor is likely similar to stimulating the cell with forskolin or any agonist of an overexpressed Gs-coupled receptor. Thus it appears to be a stretch to call these "b2AR Targets". Moreover, although it is true that loss of PDE activity and/or RII subunits may contribute to loss of compartmentalization of signaling, overexpression of the GPCR could also lead to loss of compartmentalization. This must be discussed.
- 3b. The actual list of genes in Table 3 should be shown (not just GO terms).
- 3c. The fact that PDE1C was decreased could point to more than just cAMP-induced transcriptional changes. This is a dual PDE and its decrease may also increase cGMP.
Minor comments:
Missing "ISO" labels for Fig S2 C, D Need better labeling of bars for Fig 7B
Significance
This is a very rigorous and detailed study to characterize a novel regulator of cAMP signaling systems. Although the data do not support, RBM12 as a specific regulator of beta2AR signaling, it is nevertheless an important regulator of general cAMP signaling and could potentially have effects on cGMP signaling. The study has clinical value, as RPM12 variants drive familial psychosis but this study will also appeal to basic scientists.
- The authors are highly focused on the GPCR responses; thus, they fail to discuss the fact that supplemental figures 1D-F show that the effects of RBM12 lie downstream of the receptor and are independent of b2AR. Stimulation with forskolin shows prominent enhancement of cAMP accumulation, pointing to enhancement of adenylyl cyclase and/or decreases in PDE activity. This effect should be quantitated. The is consistent with the fact that stimulation with multiple Gs-coupled receptors show similar enhancements. Given that, much of Fig 2, particularly 2E should be moved to supplemental. The order of figures may need to be re-examined.
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Referee #1
Evidence, reproducibility and clarity
RBM12 is an RNA-binding protein predominantly localized to the nucleus. Mutations in RBM12 have been linked to heritable psychosis and neurodevelopmental defects. The gene appeared in a previously published CRISPRi screen for potential regulators of cAMP signaling. The authors confirm that loss of RPM12 leads to increased basal and induced cAMP, activation of cAMP-dependent protein kinase, and induction of cAMP-CREB induced gene transcription. Similar effects were seen following direct activation of adenylyl cyclase and overexpression of the kinase catalytic subunit. The figures are clearly presented, well controlled, and show significant differences that largely support the central conclusion that RBM12 regulates cAMP. The authors have taken on an extremely challenging problem. The paper is very well written.
Significance
The significance of the findings are limited for a number of reasons, which the authors acknowledge as summarized under major comments. We know from prior CRISPRi work that RBM12 regulates cAMP signaling (ref. 8). The findings are publishable, but the advance is modest and the potential target audience is specialized.
Major comments.
First, the authors are not able to mechanistically link RBM12 to any particular component of the cAMP pathway. Without a mechanistic link, direct or otherwise, to proteins to make or degrade cAMP, the findings are descriptive.
OPTIONAL: Does RBM12 bind to and regulate a subset of mRNAs or proteins that are part of the pathway?
Second, while the link to psychosis and neurodevelopmental defects figures very prominently in the title and text, the link to psychosis is not supported by the approach and most of the text should be removed. The experiments performed here don't come close to recapitulating the physiological setting. Is there ever a situation where individuals don't express any RBM12 (patients with the variants will be heterozygous)?
OPTIONAL: What happens in a mouse model?
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Reply to the reviewers
We would truly like to thank all 3 reviewers for insightful, helpful and thus constructive comments.
Reviewer #1
Summary
In this manuscript, Lockyer et al. provide novel insights into the mechanism by which Toxoplasma gondii avoids parasite restriction in IFNγ-activated human cells. To identify potentially secreted proteins supporting parasite survival in IFNγ-activated human foreskin fibroblasts (HFF), the authors designed a CRISPR screen of Toxoplasma secretome candidates based on hyperLOPIT protein localization data. By this approach, they identified novel secreted proteins supporting parasite growth in IFNγ-activated cells. Among the gene identified, they found MYR3 a known component of the putative translocon in charge of protein export through the parasitophorous vacuole membrane. Therefore, the authors focused their investigations on GRA57, a dense granule protein of unknown function, which affects parasite survival to a lesser extent than the MYR component. The resistance phenotype conferred by GRA57 was confirmed by fluorescence microscopy. Importantly, the authors provide evidence that the protective function of GRA57 is not as well conserved in murine cells of the same type (MEF) as in HFF. To further explore the mechanism by which GRA57 protect the parasites in IFNγ-activated cells, the authors searched for protein partners by biochemistry. By immunoprecipitation and tandem mass spectrometry, they identified two other putative dense granule proteins, GRA70 and GRA71, which co-purified with GRA57-HA tagged protein. Noteworthy, both proteins were also found in the CRISPR screens with significant score conferring resistance. High-content imaging analysis confirmed the protective effect conferred by GRA57, GRA70, and GRA71 individually at similar levels. After ruling out an effect of tryptophan deprivation in parasite clearance, or a role of GRA57 in protein export normally mediated by the MYR translocon, and a role on host cell gene expression by RNA-Seq, the authors investigated the ubiquitination of the parasitophorous vacuole membrane, a marker previously thought to initiate parasite clearance. A reduction in ubiquitin labeling around the vacuole of mutant parasites is observed, which is quite surprising given the correlated increase in parasite clearance. The authors concluded that ubiquitin recruitment may not be directly linked to the parasite clearance mechanism.
Major comments
- Figure 2C. In this figure, the restriction effect of IFNγ is about 60% (or 40% survival) for RHdeltaUPRT parasites grown in HFFs, which is quite different from the 85% mentioned earlier in the results section. How was actually done the first assay? Settings with 60% restriction sounds reasonable and indicates that a substantial fraction of the parasite population evades the restrictive effect of IFNγ, which provides a clear rationale for the main objective of this study, namely the identification of effectors supporting parasite development in human cells in the presence of IFNγ.
This discrepancy in restriction likely arises from the differences in the parasites used in these assays and the measurements of restriction. The 85%/90% restriction initially mentioned is from the pooled CRISPR screens using the effector knockout pool. This restriction level was assessed by counting of parasites retrieved following infection of IFNg-stimulated HFFs. The 60% restriction of wildtype parasites seen in Figure 2 is a separate assay. This percentage was calculated by measuring total mCherry fluorescence area within infected HFFs. We expect the restriction of the pooled CRISPR population to be higher than in restriction assays performed with either wild type parasites or single genetic knockouts. We included the 85%/90% numbers to highlight that the HFFs were highly restrictive in the screen, but we have now removed references to these numbers in the results section to avoid confusion with later results that use more accurate measures of survival. We refer to this restriction level instead in the discussion section.
Optional comment: GRA70 and GRA71 were both copurified with GRA57, but what about GRA71 expression and localization? Is there a reason why this protein partner has not been studied further just like GRA70?
Tagging of GRA71 was attempted but was not successful in a first attempt. We have not re-attempted this tagging as Krishnamurthy et al 2023 (PMID: 36916910) recently tagged and localised GRA71, demonstrating it is also an intravacuolar dense granule protein with similar localisation to GRA57 and GRA70- we feel there is minimal value in us repeating this.
*Is there any change in GRA57, GRA70, and GRA71 localization and/or amount when cells were pretreated with IFNγ? *
Thank you for this suggestion, we have now conducted further investigation to address this. We checked the localisation of GRA57-HA and GRA70-V5 in IFNg-stimulated HFFs and found no change to their localisation. This data has been added in Supplementary Figure S4 in our revised manuscript. Alignment of our RNA-Seq data to the Toxoplasma genome, now included as Supplementary Data 4, also shows there is no significant up or downregulation in expression of any of the three proteins when HFFs are pretreated with IFNg.
Do they still form a complex in the absence of IFNγ?
We did not investigate this in this manuscript, however in Krishnamurthy et al 2023 (PMID: 36916910) CoIPs using GRA57 and GRA70 in the absence of IFNγ also identified these three proteins as interaction partners, so formation of the complex is likely IFNg-independent.
- In the absence of GRA70 or GRA71 is GRA57 expression and/or localization affected?*
We did not investigate this possibility in this manuscript, however doing so would require the generation of epitope tagged lines in knockout backgrounds. We believe this represents a significant body of work and would therefore be suitable for a future study focused on the further characterisation of this complex. The RNA-Seq data shows that GRA70 and GRA71 expression levels are not significantly different in the RH∆GRA57 strain (Supplementary Data 4) which we have now included as a statement in the results section.
- *Page 13, result section. To determine whether GRA57 has any direct or indirect effect on host cell gene expression, the authors performed RNA-Seq analysis of HFF cells pretreated or not with IFNγ. First, as for proteomic data, were the data deposited on GEO or another repository database? *
Second, were any effect detected on parasite gene expression? Reads alignment could be done using the T. gondii reference genome to determine whether IFNg or gra57 KO has any effect on parasite genes. Possibly, other secreted proteins not necessarily expressed at the tachyzoite stage and therefore not captured in the hyperLOPIT protein analysis are specifically expressed in these conditions.
We will deposit the RNA-Seq data on GEO prior to final publication. We did perform read alignment using the Toxoplasma gondii reference genome, and we agree it would be useful to include this analysis. We have now provided this data in Supplementary Data 4. Comparison of parasite gene expression between RH∆Ku80 and RH∆GRA57 revealed very few major changes (L2FC 2) that were also rescued in the RH∆GRA57::GRA57 line, irrespective of IFNg stimulation. Of the few genes that were up or downregulated in the RH∆GRA57 parasites, these were all uncharacterised. Collectively this data did not provide any mechanistic insight into the function of GRA57, and we think it unlikely the GRA57 phenotype is related to major changes in host or parasite gene expression. We have amended the manuscript to highlight this.
Optional comment: RNA-Seq analysis points to a clear induction of GBPs upon IFNγ treatment in HFF. Given the clear function of GBP in parasite clearance, have the authors ever hypothesized that GRA57 could be involved in preventing GBP binding to the PVM?
We have not tested if GBP recruitment is influenced by GRA57, however GBPs have previously been shown to be dispensable for restriction of Toxoplasma growth in HFFs (Niedelman et al 2013, PMID: 24042117) despite being robustly induced by IFNg stimulation (Kim et al 2007, PMID: 17404298). We have modified the manuscript to highlight this.
Minor comments
- Page 4, introduction, 8th paragraph. Regarding the role of IST, it might be less prone to controversy to state: 'a condition that may only be met in the early stages of infection.'
We agree and have changed this.
- Page 4, end of introduction. Changing '... indicating that the three proteins function in a complex'. Changing to '... indicating that the three proteins function in the same pathway.' might be more appropriate for the conclusion.
We agree and have changed this.
- Page 4, result section, first paragraph. 'strain specific and independent effectors'. Are the authors talking about strain-specific and non-strain-specific factors?
Yes- we have changed the text to reflect this.
- Page 6, result section. 'GRA25, an essential virulence factor in mice'. It is not clear to the reviewer how a virulence factor is essential since both parasite and mouse survival is achieved in the GRA25 mutant. I suggest to replace 'essential' by 'major'.
We agree and have changed this.
- Page 7. 'showing that GRA57 resides in the intravacuolar network (IVN) (Figure 2A)'. From the image shown, GRA57 clearly localizes into the PV, but it is hard to tell whether GRA57 is associated with the intravacuolar network. Colocalization assay or electron microscopy would be necessary to draw such conclusions.
We agree and have changed all references to this localisation as ‘intravacuolar’ instead of specifically the IVN.
- 'uprt locus'. Lower case letters and italic are generally preferred to designate mutants, whereas upper case letters are generally used for wild type alleles. (Sibley et al., Parasitology Today, 1991. Proposal for a uniform genetic nomenclature in Toxoplasma gondii).
We agree and have changed this.
- The authors mentioned in the introduction that ROP1 contributes to T. gondii resistance to IFNγ in murine and human macrophages. However, they did not comment on whether ROP1 was found important in the screen performed here in human HFF cells. It may be useful to reference ROP1 in Figure 1 as GRA15, GRA25, etc.
ROP1 was not found to be important in the HFF screens (+IFNg L2FCs in RH: -0.1, PRU: -0.46). As ROP1 was characterised as an IFNg resistance effector in macrophages, this discrepancy may therefore represent a cell type-specific difference, so we feel it is not relevant to highlight for the purposes of the screens presented here.
- Figure 2D. The authors compared the restriction effect of IFNγ on parasites grown in HFF and MEF host cells. However, as represented - % + IFNγ/- IFNγ - it cannot be estimated whether the parasites grew similarly in the two host cell types in the absence of IFN. Please indicate whether or not the growth was similar in both cell types.
As these restriction assays were not carried out concurrently and were designed to measure IFNg survival, we feel it would be inaccurate to compare parasite growth between the two cell types using this data. The focus of these experiments was to investigate the restrictive effect of IFNg across parasite strains, using the -IFNg condition to control for differences in growth rate or MOI. Therefore we feel it is appropriate for the focus of our manuscript to represent the data in this way.
- pUPRT plasmid. Any reference or vector map would be appreciated.
We have added the reference for this plasmid.
- Page 9, figure 3A, mass spectrometry analysis. I did not find the MS data in supplementals. Were the data deposited in on PRIDE database or another data repository?
The table was included as Supplementary Data 2, however this was not referred to in the main text. We have now amended the text to include this. The data will be deposited on PRIDE prior to final publication.
- Figures 3E and 3F. It might be worth mentioning, at least in the figure legend, that GRA3 localizes at PV membrane and is exposed to the host cell cytoplasm (to mediate interactions with host Golgi). The signal for GRA3 following saponin treatment is here an excellent control that should be highlighted, indicating that saponin effectively permeabilized the host cell membrane.
We agree and have updated the figure legend and the main text. We have also added a reference to Cygan et al 2021__ (__PMID: 34749525) in support of this data, which found GRA57, but not GRA70 or GRA71, enriched at the PVM.
- Page 11, section title. I think that the authors meant 'GRA57, GRA70 and GRA71 confer resistance to vacuole clearance in IFNγ-activated HFFs.'
We agree and have changed this.
- Page 11, in the result section comparing the effect of GRA57 mutant with MYR component KO, the authors are referring to host pathways that are counteracted by MYR-dependent effectors released into the host cell. It is not clear which pathways the authors are referring to.
It is not known exactly which host pathways mediate vacuole clearance or parasite growth restriction, or which MYR-dependent parasite effectors specifically resist these defences, therefore we have removed this statement from the text for clarity.
- Page 16, discussion, end of 4th paragraph. '... to promote parasite survival in IFNγ activated cells' sounds better.
We agree and have changed this.
- Page 22-23, Methods section, c-Myc nuclear translocation assays and elsewhere. Please indicate how many events were actually analyzed. For example, in this assay, to determine the median nuclear c-Myc signal, how many infected cells were analyzed for each biological replicate?
We have updated the methods section for the c-Myc nuclear translocation and ubiquitin-recruitment assays to include details on how many events were analysed.
**Referees cross-commenting**
Overall, I agree with most of the co-reviewers' remarks. I agree with reviewer #2 that this manuscript reports interesting data for the field of parasitology, but that the broad interest for immunologists is somewhat limited by the lack of a description of the mechanism by which these effectors oppose IFNgamma-inducible cell-autonomous defenses. I also agree with the other reviewers' comments regarding the GRA57, 70, and 71 heterotrimeric complex, which would require further description. In its present form, the manuscript undoubtedly represents an interesting starting point for further investigations and any additional data regarding the mode of interaction of the identified effectors and their function related or not to ubiquitylation would bring a significant added value.
Reviewer #1 (Significance (Required)):
Despite the fact that humans are accidental intermediate hosts for Toxoplasma gondii, the parasite may develop a persistent infection, demonstrating that it has effectively avoided host defenses. While Toxoplasma gondii has been extensively studied in mice, much less is known about the mechanisms by which the parasite establishes a chronic infection in humans. In this context, this article described very interesting data about the way this parasite counteracts human cell-autonomous innate immune system. This is a fascinating and important topic lying at the interface between parasitology and immunology. Indeed, the highly specialized secretory organelles characteristics of apicomplexan parasites are key to govern host-cell and parasite interactions ranging from host cell transcriptome modification to counteracting immune defense mechanisms. Overall, this article presents a significant contribution to the field of parasitology by identifying novel players involved in Toxoplasma gondii's evasion of human cell-autonomous immunity. Most conclusions are generally well supported by cutting-edge approaches and state of the art methods. Despite being a highly competitive field, this article stands out as the first screen designed specifically to identify virulence factors for human cells and extends our understanding of the secreted dense granule proteins resident of the parasitophorous vacuole. Importantly, the authors provide evidence that these players are active in different strain backgrounds and act in a way that is independent of the export machinery in charge of delivering effector proteins directly into the host cell. However, substantial further research is needed to fully understand the mechanism by which these novel players confer resistance to the parasite in IFNγ activated human cells and how their mode of action differs from that mediated by the translocation machinery (MYR complex). As a microbiologist and biochemist, I find this work of a particular interest to a broad audience, especially to parasitologists and immunologists, as it may unveil unexpected aspects of human innate immunity involved in parasite clearance with proteins unique to Apicomplexa phylum.
Reviewer #2
This paper reports high-quality genetic screening data identifying three novel Toxoplasma virulence factors (Gra57,70, and 71) that promote survival of two distinct Toxoplasma strains (type I RH and type II Pru) inside IFN-gamma primed human fibroblasts. Follow-up studies, exclusively focused on type I RH Toxoplasma, confirm the screening data. Gra57 IP Mass-Spec data suggest that Gra57, 70, and 71 may form a protein complex, a model supported by comparable IF staining patterns
Major:
- It is unclear what statistical metric was used to define screen hits as strain-dependent vs strain-independent. A standard approach would be to use a specific z-score value (often a z-score of 2) above or below best fit linear relationship between L2FCU for RH vs Pru as depicted in Fig.1D. Gra25 and Gra35 appear to be specific for Pru but it would be helpful to approach this type of categorization statistically. Also, such an analysis may reveal that only Pru-specific but not RH-specific hits were identified. Could the authors speculate why that would be?
We did not use a specific statistical metric to define screen hits as strain-dependent vs strain-independent, but GRA57 was selected as a strain-independent hit based on having a L2FC of RH specific: TGME49_309600 (GRA71) & CST9
PRU specific: GRA35, GRA25, ROP17, GRA23 & GRA45
Strain-independent: MYR3, GRA57, TGME49_249990 (GRA70) & MYR1
This agrees with our selection of strain-independent hits. However, we feel that using either L2FC or Z-score cut-offs is equally arbitrary, and we would therefore prefer to leave the data displayed without these cut-offs. It is indeed interesting that there appear to be more strain-specific hits in the PRU screen, but we cannot speculate as to why this may be as we did not explore this further here.
*- The paper proposes that Gra57, 70, and 71 form a heterotrimeric complex. This is based on the Mass-spec data from the original Gra57 pulldown, similar IF staining patterns, and comparable phenotypic presentation of the individual KO strains. However, only the MS data provide somewhat direct evidence for the formation a trimeric complex, and these data are by no means definitive. As this is a key finding of the MS, it should be further supported by additional biochemical data. Ideally, the authors should reconstitute the trimeric complex in vitro using recombinant proteins. Admittedly, this could be quite an undertaking with various potential caveats. Alternatively, reciprocal pulldowns of the 3 components could be performed. Super-resolution microscopy of the 3 Gra proteins might present another avenue to obtain more compelling evidence in support of the central claim of this work, *
We attempted a reciprocal pulldown using our GRA70-V5 line which unfortunately failed to verify the MS data, but we believe this is primarily due to differences in the affinity matrix that we used for this pulldown (anti-V5 vs anti-HA) and would require further optimisation or generation of a GRA70-HA line. However, while these revisions were being performed, another group published data demonstrating through pulldown of GRA57 and GRA70 that these proteins interact with each other, GRA71, and GRA32__ (__Krishnamurthy et al 2023, PMID: 36916910). We also identified GRA32 as enriched in our MS data, but to a less significant degree than GRA70 and GRA71. Together we believe that this independent data set is a robust validation of our findings, and strongly justifies the conclusion that these proteins form a complex.
We agree with the reviewer that further biochemical characterisation of the complex will be an interesting avenue for future research, but we feel it would require a substantial amount of further work. As suggested, super-resolution microscopy of the 3 proteins would require the generation of either double or triple tagged Toxoplasma lines, or antibodies against one or more of the complex members. Again, we feel this would represent a substantial body of further work. Reconstitution of the complex in vitro would require recombinant expression and purification of multiple large proteins that are all multidomain and possibly membrane associated/integrated. Assuming a 1:1:1 stoichiometric assembly this complex would be 446kDa. Purification of such proteins and reconstitution of the complex in vitro is therefore likely to represent many challenges and we do not feel this would be trivial to accomplish.
- The ubiquitin observations made in this paper are a bit preliminary and the authors' interpretation of their data is vague. The authors may want to re-consider that ubiquitylated delta Gra57 PVs are being destroyed with much faster kinetics than ubiquitylated WT PVs. The reduced number of ubiquitylated delta Gra57 PVs compared to ubiquitylated WT PVs across three timepoints (as shown by the authors in Fi. S8) does not disprove the 'fast kinetics model.' To test the fast kinetics ubiquitin-dependent null hypothesis, video microscopy could be used to measure the time from PV ubiquitylation onset to PV destruction
We agree with the reviewer that the possibility remains that GRA57 knockouts are cleared within the first hour of infection, and we have amended our text to reflect this. However, we think this is unlikely given that GRA57 knockouts are also less ubiquitinated in unstimulated cells, yet do not show any growth differences in unstimulated HFFs. Also considering the new data we have provided showing reduced recognition of GRA57 knockouts by the E3 ligase RNF213 (Figure 5D), we expect that the observed reduction in ubiquitination is highly likely to be unlinked to the increased susceptibility of GRA57 knockouts to IFNg. We have amended the discussion to state this conclusion more strongly.
The recently published manuscript that also identified GRA57/GRA70/GRA71 as effectors in HFFs showed that deletion of these effectors leads to premature egress from IFNg-activated HFFs__ (__Krishnamurthy et al 2023, PMID: 36916910). In light of this new data, we hypothesised that early egress could be causing the apparent reduction in ubiquitination. We have now provided data that disproves this hypothesis (Figure S10), as inhibition of egress did not rescue the ubiquitination phenotype. We also did not observe enhanced restriction of GRA57 knockout parasites at 3 hours post-infection (Figure S10B), suggesting clearance, or egress, happens after this time point.
We agree with the reviewer that determining the kinetics of IFNg restriction of these knockouts in HFFs would be interesting, however we feel this is more suited to future work. Imaging ubiquitin recruitment in live cells would also require the generation of new reporter host cell lines which would require a substantial amount of further work.
- Related to the point above. We know that different ubiquitin species are found at the PVM in IFNgamma-primed cells but to what degree each Ub species exerts an anti-parasitic effect is not well established. The paper only monitors total Ub at the PVM. Could it be that delta Gra57 PVs are enriched for a specific Ub species but depleted for another? The authors touch on this in the Discussion but these are easy experiments to perform and well within the scope of the study. At least the previously implicated ubiquitin species M1, K48, and K63 should be monitored and their colocalization with Toxo PVMs quantified
We agree that these experiments are within the scope of this study. We have now investigated the ubiquitin phenotype further by assessing the recruitment of M1, K48 and K63 ubiquitin linkages to the vacuoles of GRA57 knockouts. We observed depletion of both M1 and K63 linked ubiquitin. This data is now included in Figure 5 and Figure S8.
The E3 ligase RNF213 has recently been shown to facilitate recruitment of M1 and K63-linked ubiquitin to Toxoplasma vacuoles in HFFs (Hernandez et al 2022, PMID: 36154443 & Matta et al 2022, DOI: https://doi.org/10.1101/2022.10.21.513197 ). We therefore additionally assessed the recruitment of RNF213 to GRA57 knockouts, and found RNF213 recruitment was also reduced. Given that a reduction in RNF213 recruitment should correlate with a decrease in restriction, this data further supports our conclusion that the ubiquitin and restriction phenotypes are not causally linked. The observation that GRA57 knockouts are less susceptible to recognition by RNF213 also opens an exciting avenue for further research into the host recognition of Toxoplasma vacuoles by RNF213, for which currently the target is unknown.
Minor:
- For readers not familiar with Toxo genetics, the authors should include a sentence or two in the results section explaining the selection of HXGPRT deletion strains for the generation of Toxo libraries
We agree and have added this in.
- the highest scoring hits from the Pru screen (Gra35 &25) weren't investigated further. These hits appear to be specific for Pru. Some discussion as to why there are Pru-specific factors (but maybe not RH-specific factors) seems warranted
As mentioned above, we agree that it is indeed interesting that there appear to be more strain-specific hits in the PRU screen, but we cannot speculate as to why this may be as we did not explore the reasons for this further in this manuscript. Without substantial further investigation it cannot be determined whether these represent true strain-specific differences or reflect technical variability between the independent screens. We therefore feel it is sufficient to highlight effectors with the strongest phenotypes in each screen, without drawing strong conclusions regarding strain-specificity.
**Referees cross-commenting**
My reading of the comments is that there's consensus that this is a high quality study revealing novel Toxo effectors that undermine human cell-autonomous immunity and an important study in the field of parasitology. I might be the outlier that doesn't see much of an advance for the field of immunology since we don't really know what these effectors are doing, and the preliminary studies addressing this point are not well developed, with some confusing results.
My major comment #2 and rev#1's major comment #2 are, I think, essentially asking for the same thing, namely some more robust data on substantiating the formation of a trimeric complex.
My co-reviewers made great comments all across and I don't see any real discrepancies between the reviewers' comments - just some variation in what we, the reviewers, focused on
Reviewer #2 (Significance (Required)):
The discovery of a novel set of secreted Gra proteins critical for enhanced Toxoplasma survival specifically in IFNgamma primed human fibroblasts (but not mouse fibroblasts) is an important discovery for the Toxoplasma field. However, the study is somewhat limited in its scope as it fails to determine which, if any, specific IFNgamma-inducible cell-autonomous immune pathway is antagonized by Gra57 &Co. Instead, the paper reports that parasitophorous vacuoles (PVs) formed by Gra57 deletion mutants acquire less host ubiquitin than PVs formed by the parental WT strain. Because host-driven PV ubiquitylation is generally considered anti-parasitic, this observation is counterintuitive, and no compelling model is presented to explain these unexpected findings. Overall, this is a well conducted Toxoplasma research study with a few technical shortcomings that need to be addressed. However, in its current form, the study provides only limited insights into possible mechanisms by which Toxoplasma undermines human immunity. This study certainly provides an exciting starting point for further explorations.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary:
Toxoplasma gondii virulence and immune responsed upon infection in mice are well described. In contrast, little is known about human responses, particularly upon IFNγ-activation. However, host ubiquitination of the parasitophorous vacuole has been shown to be associated with parasite clearence in human cells.
Targeted CRISPR screens were used in the type I RH and type II Pru strain of Toxoplasma gondii to identify dense granule and rhoptry proteins. Human foreskin fibroblasts (HFFs) stimulated with IFNγ were used for infection of the knock-out parasites to identify guide RNAs and thus their corresponding genes to identify genes conferring growth benefits. Beside components of the MYR translocon, gra57 was identified. This gene was then knock-out or epitope-tagged in RH. The tagged line confirmed GRA57 localisation in the intravacuolar network confirming previously published work from another lab. Knock-out of gra57 lead to a moderate decrease in survival in HFFs, but not in mouse cells. Co-immunoprecipitation experiments with GRA57 identified 2 dense granule proteins that also display IFNγ-specific phenotypes with similar localisation as GRA57, and all are resistance factors in IFNγ-activated HFFs. Knock-out of GRA57 does not impact tryptophan metabolism, effector export of gene expression of the host cells. However, deletion of GRA57 or its interaction partners reduces ubiquitination of the parasitophorous vacuole.
Major comments:
This is a well executed study with informative, novel data. Here a few comments and questions:
- LFC cut-off of the CRISPR screen should be clearly stated.
We have amended this in the text.
- What is the rationale for using Prugniaud as the type II strain of choice and not ME49?
Both ME49 and PRU strains are widely used in the field, but as the PRU strain was used previously by our group for in vivo screens of Toxoplasma effectors (Young et al 2019 PMID: 31481656, Butterworth et al 2022 PMID: 36476844) ,using PRU here allows for direct comparison of our screening datasets.
- Figure 4A does not list all the significant genes that are then mentioned in the text below. This should be amended.
It is unclear what the reviewer is referring to here (Figure 4A displays restriction assay data).
*- RNA-Seq data is inadequately presented. Although, the actual genes regulated may be of secondary importance in this study, it would still be good to have a few key genes mentioned as a quality control statement. *
This was also raised by reviewer 1. We have now modified the manuscript to highlight that we observed robust induction of interferon-stimulated genes in our IFNg-treated conditions, but minimal differential gene expression between HFFs infected with the different parasite strains.
*- It is stated that "...GRA57 is not as important for survival in MEFs as in HFFS". With no significant change observed, it should be re-phrased to something like ""...indicatin that GRA57 is s important for survival in MEFs as in HFFS." *
We have re-phrased this statement.
*- Optional: GRA57 was described by the Bradley lab to be in the PV in tachyzoites and in the cyst wall in bradyzoites. Although it tissue cysts are not the focus of this paper and the knock-out is created also in a cyst-forming strain, it would have been useful to look for a phenotype of the knockout in cysts, in vitro at least, better both in in vitro and in vivo. In future, this could also be useful for the authors bringing in more citations. *
We agree with the reviewer that the impact of GRA57 on cyst formation would be an interesting topic for further exploration, however the focus of our study is on the role of secreted Toxoplasma effectors during the acute stages of infection.
Minor comments:
- Line numbers would be useful for an efficient review process.
We have added these to the revised manuscript.
- Strictly speaking, we have to talk about the sexual development taking place in felid and not feline hosts (Introduction; Felidae versus Felinae).
We have amended this in the text.
- Please insert spaces between numbers and units.
We have corrected this.
- Domain structures are presented, but maybe the AlphaFold 3D predictions could be added in a supplemental figure?
For GRA70 and GRA71 the AlphaFold 3D predictions are readily available on ToxoDB, whereas for GRA57 the prediction is not available due its size. We therefore independently analysed GRA57 using the full implementation of AlphaFold 2 (not ColabFold). We attempted submissions of putative discrete domains as well as the full-length protein, however both approaches yielded predictions with low confidence and low structural content, except for a ~100aa region of helical residues. We chose not to include the AlphaFold 3D predictions for all three proteins as the confidence for these predictions is low with pLDDT scores of commonly *- To improve the confidence of the co-immunoprecipitation, it would be necessary to use another tagged protein GRA70 or 71) and see if the same complex can be pulled down. Like this, one could also address what happens in a GRA57KO line? Do GRA70 and 71 stay together in the absence of GR57 forming a dimer? *
Reviewer 2 raised a similar point regarding the reciprocal pulldown, please see above for our detailed response to this. As suggested, we attempted a reciprocal pulldown using our GRA70-V5 line which unfortunately did not reconstitute the complex, but we believe this was due to technical differences in the epitope tag (V5 vs HA) and affinity matrix used. Overall, we believe that more detailed study of the assembly and biochemistry of this complex will require substantially more work and the generation of further cell lines, which would be beyond the scope of this study.
Reviewer #3 (Significance (Required)):
Significance:
This study endeavours to start closing an important knowledge gab of host defence in non-rodent hosts, especially humans. The data is solid using two different strains and yields novel insights into players of host cell resistance in humans against T. gondii. Using a targeted screening approach of rhoptry and dense granule proteins, they focused their interest on a subcategory of secreted proteins. The authors have not limited themselves to the screening and localisation study, but also investigated effect on host cells and host cell response. The identification of GRA57 being an important resistance factor and forming a heterodimer with GRA70 and GRA71 is novel. This study is of interest to cell biologists in the field of cyst-forming Coccidia, especially T. gondii and researchers interested in host resistance, parasite clearance by the host and parasite virulence.
I am a cell biologist working in Toxoplasma gondii and other Coccidians.
-
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Referee #3
Evidence, reproducibility and clarity
Summary:
Toxoplasma gondii virulence and immune responsed upon infection in mice are well described. In contrast, little is known about human responses, particularly upon IFNγ-activation. However, host ubiquitination of the parasitophorous vacuole has been shown to be associated with parasite clearence in human cells.
Targeted CRISPR screens were used in the type I RH and type II Pru strain of Toxoplasma gondii to identify dense granule and rhoptry proteins. Human foreskin fibroblasts (HFFs) stimulated with IFNγ were used for infection of the knock-out parasites to identify guide RNAs and thus their corresponding genes to identify genes conferring growth benefits. Beside components of the MYR translocon, gra57 was identified. This gene was then knock-out or epitope-tagged in RH. The tagged line confirmed GRA57 localisation in the intravacuolar network confirming previously published work from another lab. Knock-out of gra57 lead to a moderate decrease in survival in HFFs, but not in mouse cells. Co-immunoprecipitation experiments with GRA57 identified 2 dense granule proteins that also display IFNγ-specific phenotypes with similar localisation as GRA57, and all are resistance factors in IFNγ-activated HFFs. Knock-out of GRA57 does not impact tryptophan metabolism, effector export of gene expression of the host cells. However, deletion of GRA57 or its interaction partners reduces ubiquitination of the parasitophorous vacuole.
Major comments:
This is a well executed study with informative, novel data. Here a few comments and questions:
- LFC cut-off of the CRISPR screen should be clearly stated.
- What is the rationale for using Prugniaud as the type II strain of choice and not ME49?
- Figure 4A does not list all the significant genes that are then mentioned in the text below. This should be amended.
- RNA-Seq data is inadequately presented. Although, the actual genes regulated may be of secondary importance in this study, it would still be good to have a few key genes mentioned as a quality control statement.
- It is stated that "...GRA57 is not as important for survival in MEFs as in HFFS". With no significant change observed, it should be re-phrased to something like ""...indicatin that GRA57 is s important for survival in MEFs as in HFFS."
- Optional: GRA57 was described by the Bradley lab to be in the PV in tachyzoites and in the cyst wall in bradyzoites. Although it tissue cysts are not the focus of this paper and the knock-out is created also in a cyst-forming strain, it would have been useful to look for a phenotype of the knockout in cysts, in vitro at least, better both in in vitro and in vivo. In future, this could also be useful for the authors bringing in more citations.
Minor comments:
- Line numbers would be useful for an efficient review process.
- Strictly speaking, we have to talk about the sexual development taking place in felid and not feline hosts (Introduction; Felidae versus Felinae).
- Please insert spaces between numbers and units.
- Domain structures are presented, but maybe the AlphaFold 3D predictions could be added in a supplemental figure?
- To improve the confidence of the co-immunoprecipitation, it would be necessary to use another tagged protein GRA70 or 71) and see if the same complex can be pulled down. Like this, one could also address what happens in a GRA57KO line? Do GRA70 and 71 stay together in the absence of GR57 forming a dimer?
Significance
This study endeavours to start closing an important knowledge gab of host defence in non-rodent hosts, especially humans. The data is solid using two different strains and yields novel insights into players of host cell resistance in humans against T. gondii. Using a targeted screening approach of rhoptry and dense granule proteins, they focused their interest on a subcategory of secreted proteins. The authors have not limited themselves to the screening and localisation study, but also investigated effect on host cells and host cell response. The identification of GRA57 being an important resistance factor and forming a heterodimer with GRA70 and GRA71 is novel. This study is of interest to cell biologists in the field of cyst-forming Coccidia, especially T. gondii and researchers interested in host resistance, parasite clearance by the host and parasite virulence.
I am a cell biologist working in Toxoplasma gondii and other Coccidians.
-
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Referee #2
Evidence, reproducibility and clarity
This paper reports high-quality genetic screening data identifying three novel Toxoplasma virulence factors (Gra57,70, and 71) that promote survival of two distinct Toxoplasma strains (type I RH and type II Pru) inside IFN-gamma primed human fibroblasts. Follow-up studies, exclusively focused on type I RH Toxoplasma, confirm the screening data. Gra57 IP Mass-Spec data suggest that Gra57, 70, and 71 may form a protein complex, a model supported by comparable IF staining patterns
Specific criticisms
Major:
- It is unclear what statistical metric was used to define screen hits as strain-dependent vs strain-independent. A standard approach would be to use a specific z-score value (often a z-score of 2) above or below best fit linear relationship between L2FCU for RH vs Pru as depicted in Fig.1D. Gra25 and Gra35 appear to be specific for Pru but it would be helpful to approach this type of categorization statistically. Also, such an analysis may reveal that only Pru-specific but not RH-specific hits were identified. Could the authors speculate why that would be?
- The paper proposes that Gra57, 70, and 71 form a heterotrimeric complex. This is based on the Mass-spec data from the original Gra57 pulldown, similar IF staining patterns, and comparable phenotypic presentation of the individual KO strains. However, only the MS data provide somewhat direct evidence for the formation a trimeric complex, and these data are by no means definitive. As this is a key finding of the MS, it should be further supported by additional biochemical data. Ideally, the authors should reconstitute the trimeric complex in vitro using recombinant proteins. Admittedly, this could be quite an undertaking with various potential caveats. Alternatively, reciprocal pulldowns of the 3 components could be performed. Super-resolution microscopy of the 3 Gra proteins might present another avenue to obtain more compelling evidence in support of the central claim of this work
- The ubiquitin observations made in this paper are a bit preliminary and the authors' interpretation of their data is vague. The authors may want to re-consider that ubiquitylated delta Gra57 PVs are being destroyed with much faster kinetics than ubiquitylated WT PVs. The reduced number of ubiquitylated delta Gra57 PVs compared to ubiquitylated WT PVs across three timepoints (as shown by the authors in Fi. S8) does not disprove the 'fast kinetics model.' To test the fast kinetics ubiquitin-dependent null hypothesis, video microscopy could be used to measure the time from PV ubiquitylation onset to PV destruction
- Related to the point above. We know that different ubiquitin species are found at the PVM in IFNgamma-primed cells but to what degree each Ub species exerts an anti-parasitic effect is not well established. The paper only monitors total Ub at the PVM. Could it be that delta Gra57 PVs are enriched for a specific Ub species but depleted for another? The authors touch on this in the Discussion but these are easy experiments to perform and well within the scope of the study. At least the previously implicated ubiquitin species M1, K48, and K63 should be monitored and their colocalization with Toxo PVMs quantified
Minor:
- For readers not familiar with Toxo genetics, the authors should include a sentence or two in the results section explaining the selection of HXGPRT deletion strains for the generation of Toxo libraries
- the highest scoring hits from the Pru screen (Gra35 &25) weren't investigated further. These hits appear to be specific for Pru. Some discussion as to why there are Pru-specific factors (but maybe not RH-specific factors) seems warranted
Referees cross-commenting
My reading of the comments is that there's consensus that this is a high quality study revealing novel Toxo effectors that undermine human cell-autonomous immunity and an important study in the field of parasitology. I might be the outlier that doesn't see much of an advance for the field of immunology since we don't really know what these effectors are doing, and the preliminary studies addressing this point are not well developed, with some confusing results.
My major comment #2 and rev#1's major comment #2 are, I think, essentially asking for the same thing, namely some more robust data on substantiating the formation of a trimeric complex.
My co-reviewers made great comments all across and I don't see any real discrepancies between the reviewers' comments - just some variation in what we, the reviewers, focused on
Significance
The discovery of a novel set of secreted Gra proteins critical for enhanced Toxoplasma survival specifically in IFNgamma primed human fibroblasts (but not mouse fibroblasts) is an important discovery for the Toxoplasma field. However, the study is somewhat limited in its scope as it fails to determine which, if any, specific IFNgamma-inducible cell-autonomous immune pathway is antagonized by Gra57 &Co. Instead, the paper reports that parasitophorous vacuoles (PVs) formed by Gra57 deletion mutants acquire less host ubiquitin than PVs formed by the parental WT strain. Because host-driven PV ubiquitylation is generally considered anti-parasitic, this observation is counterintuitive, and no compelling model is presented to explain these unexpected findings. Overall, this is a well conducted Toxoplasma research study with a few technical shortcomings that need to be addressed. However, in its current form, the study provides only limited insights into possible mechanisms by which Toxoplasma undermines human immunity. This study certainly provides an exciting starting point for further explorations.
-
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Referee #1
Evidence, reproducibility and clarity
Summary
In this manuscript, Lockyer et al. provide novel insights into the mechanism by which Toxoplasma gondii avoids parasite restriction in IFNγ-activated human cells. To identify potentially secreted proteins supporting parasite survival in IFNγ-activated human foreskin fibroblasts (HFF), the authors designed a CRISPR screen of Toxoplasma secretome candidates based on hyperLOPIT protein localization data. By this approach, they identified novel secreted proteins supporting parasite growth in IFNγ-activated cells. Among the gene identified, they found MYR3 a known component of the putative translocon in charge of protein export through the parasitophorous vacuole membrane. Therefore, the authors focused their investigations on GRA57, a dense granule protein of unknown function, which affects parasite survival to a lesser extent than the MYR component. The resistance phenotype conferred by GRA57 was confirmed by fluorescence microscopy. Importantly, the authors provide evidence that the protective function of GRA57 is not as well conserved in murine cells of the same type (MEF) as in HFF. To further explore the mechanism by which GRA57 protect the parasites in IFNγ-activated cells, the authors searched for protein partners by biochemistry. By immunoprecipitation and tandem mass spectrometry, they identified two other putative dense granule proteins, GRA70 and GRA71, which co-purified with GRA57-HA tagged protein. Noteworthy, both proteins were also found in the CRISPR screens with significant score conferring resistance. High-content imaging analysis confirmed the protective effect conferred by GRA57, GRA70, and GRA71 individually at similar levels. After ruling out an effect of tryptophan deprivation in parasite clearance, or a role of GRA57 in protein export normally mediated by the MYR translocon, and a role on host cell gene expression by RNA-Seq, the authors investigated the ubiquitination of the parasitophorous vacuole membrane, a marker previously thought to initiate parasite clearance. A reduction in ubiquitin labeling around the vacuole of mutant parasites is observed, which is quite surprising given the correlated increase in parasite clearance. The authors concluded that ubiquitin recruitment may not be directly linked to the parasite clearance mechanism.
Major comments
- Figure 2C. In this figure, the restriction effect of IFNγ is about 60% (or 40% survival) for RHdeltaUPRT parasites grown in HFFs, which is quite different from the 85% mentioned earlier in the results section. How was actually done the first assay? Settings with 60% restriction sounds reasonable and indicates that a substantial fraction of the parasite population evades the restrictive effect of IFNγ, which provides a clear rationale for the main objective of this study, namely the identification of effectors supporting parasite development in human cells in the presence of IFNγ.
- Optional comment: GRA70 and GRA71 were both copurified with GRA57, but what about GRA71 expression and localization? Is there a reason why this protein partner has not been studied further just like GRA70? Is there any change in GRA57, GRA70, and GRA71 localization and/or amount when cells were pretreated with IFNγ? Do they still form a complex in the absence of IFNγ? In the absence of GRA70 or GRA71 is GRA57 expression and/or localization affected?
- Page 13, result section. To determine whether GRA57 has any direct or indirect effect on host cell gene expression, the authors performed RNA-Seq analysis of HFF cells pretreated or not with IFNγ. First, as for proteomic data, were the data deposited on GEO or another repository database? Second, were any effect detected on parasite gene expression? Reads alignment could be done using the T. gondii reference genome to determine whether IFNg or gra57 KO has any effect on parasite genes. Possibly, other secreted proteins not necessarily expressed at the tachyzoite stage and therefore not captured in the hyperLOPIT protein analysis are specifically expressed in these conditions.
- Optional comment: RNA-Seq analysis points to a clear induction of GBPs upon IFNγ treatment in HFF. Given the clear function of GBP in parasite clearance, have the authors ever hypothesized that GRA57 could be involved in preventing GBP binding to the PVM?
Minor comments
- Page 4, introduction, 8th paragraph. Regarding the role of IST, it might be less prone to controversy to state: 'a condition that may only be met in the early stages of infection.'
- Page 4, end of introduction. Changing '... indicating that the three proteins function in a complex'. Changing to '... indicating that the three proteins function in the same pathway.' might be more appropriate for the conclusion.
- Page 4, result section, first paragraph. 'strain specific and independent effectors'. Are the authors talking about strain-specific and non-strain-specific factors?
- Page 6, result section. 'GRA25, an essential virulence factor in mice'. It is not clear to the reviewer how a virulence factor is essential since both parasite and mouse survival is achieved in the GRA25 mutant. I suggest to replace 'essential' by 'major'.
- Page 7. 'showing that GRA57 resides in the intravacuolar network (IVN) (Figure 2A)'. From the image shown, GRA57 clearly localizes into the PV, but it is hard to tell whether GRA57 is associated with the intravacuolar network. Colocalization assay or electron microscopy would be necessary to draw such conclusions.
- 'uprt locus'. Lower case letters and italic are generally preferred to designate mutants, whereas upper case letters are generally used for wild type alleles. (Sibley et al., Parasitology Today, 1991. Proposal for a uniform genetic nomenclature in Toxoplasma gondii).
- The authors mentioned in the introduction that ROP1 contributes to T. gondii resistance to IFNγ in murine and human macrophages. However, they did not comment on whether ROP1 was found important in the screen performed here in human HFF cells. It may be useful to reference ROP1 in Figure 1 as GRA15, GRA25, etc.
- Figure 2D. The authors compared the restriction effect of IFNγ on parasites grown in HFF and MEF host cells. However, as represented - % + IFNγ/- IFNγ - it cannot be estimated whether the parasites grew similarly in the two host cell types in the absence of IFN. Please indicate whether or not the growth was similar in both cell types.
- pUPRT plasmid. Any reference or vector map would be appreciated.
- Page 9, figure 3A, mass spectrometry analysis. I did not find the MS data in supplementals. Were the data deposited in on PRIDE database or another data repository?
- Figures 3E and 3F. It might be worth mentioning, at least in the figure legend, that GRA3 localizes at PV membrane and is exposed to the host cell cytoplasm (to mediate interactions with host Golgi). The signal for GRA3 following saponin treatment is here an excellent control that should be highlighted, indicating that saponin effectively permeabilized the host cell membrane.
- Page 11, section title. I think that the authors meant 'GRA57, GRA70 and GRA71 confer resistance to vacuole clearance in IFNγ-activated HFFs.'
- Page 11, in the result section comparing the effect of GRA57 mutant with MYR component KO, the authors are referring to host pathways that are counteracted by MYR-dependent effectors released into the host cell. It is not clear which pathways the authors are referring to.
- Page 16, discussion, end of 4th paragraph. '... to promote parasite survival in IFNγ activated cells' sounds better.
- Page 22-23, Methods section, c-Myc nuclear translocation assays and elsewhere. Please indicate how many events were actually analyzed. For example, in this assay, to determine the median nuclear c-Myc signal, how many infected cells were analyzed for each biological replicate?
Referees cross-commenting
Overall, I agree with most of the co-reviewers' remarks. I agree with reviewer #2 that this manuscript reports interesting data for the field of parasitology, but that the broad interest for immunologists is somewhat limited by the lack of a description of the mechanism by which these effectors oppose IFNgamma-inducible cell-autonomous defenses. I also agree with the other reviewers' comments regarding the GRA57, 70, and 71 heterotrimeric complex, which would require further description. In its present form, the manuscript undoubtedly represents an interesting starting point for further investigations and any additional data regarding the mode of interaction of the identified effectors and their function related or not to ubiquitylation would bring a significant added value.
Significance
Despite the fact that humans are accidental intermediate hosts for Toxoplasma gondii, the parasite may develop a persistent infection, demonstrating that it has effectively avoided host defenses. While Toxoplasma gondii has been extensively studied in mice, much less is known about the mechanisms by which the parasite establishes a chronic infection in humans. In this context, this article described very interesting data about the way this parasite counteracts human cell-autonomous innate immune system. This is a fascinating and important topic lying at the interface between parasitology and immunology. Indeed, the highly specialized secretory organelles characteristics of apicomplexan parasites are key to govern host-cell and parasite interactions ranging from host cell transcriptome modification to counteracting immune defense mechanisms. Overall, this article presents a significant contribution to the field of parasitology by identifying novel players involved in Toxoplasma gondii's evasion of human cell-autonomous immunity. Most conclusions are generally well supported by cutting-edge approaches and state of the art methods. Despite being a highly competitive field, this article stands out as the first screen designed specifically to identify virulence factors for human cells and extends our understanding of the secreted dense granule proteins resident of the parasitophorous vacuole. Importantly, the authors provide evidence that these players are active in different strain backgrounds and act in a way that is independent of the export machinery in charge of delivering effector proteins directly into the host cell. However, substantial further research is needed to fully understand the mechanism by which these novel players confer resistance to the parasite in IFNγ activated human cells and how their mode of action differs from that mediated by the translocation machinery (MYR complex). As a microbiologist and biochemist, I find this work of a particular interest to a broad audience, especially to parasitologists and immunologists, as it may unveil unexpected aspects of human innate immunity involved in parasite clearance with proteins unique to Apicomplexa phylum.
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- Mar 2023
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Reply to the reviewers
Response to reviewers
We thank all reviewers for their comments and suggestions. In line, below, are our responses, marked in Bold. Textural changes in the manuscript are also marked in Bold.
Reviewer #1__ (__Evidence, reproducibility and clarity (Required)):
**Summary:**
Anuculeate red blood cell (RBC) is one of the interesting biological models that indicate the presence of eukaryotic circadian system independent of transcription-translation feedback. In this manuscript, the authors set up a new method for quantifying the circadian rhythmicity in RBC. The method called "Bloody Blotting" was developed through the careful and insightful investigation of "non-specific band" observed in the western blotting of peroxiredoxin, which has been used for the circadian monitoring of RBC. The authors characterized that the "non-specific' circadian-fluctuating signals, which can be observed by ECL imaging without any antibodies(-HRP), were attributed to ferrous-haem, but not ferric-haem, cross-linked to Hb upon cell lysis. Through the Bloody Blotting, this study suggests that the circadian fluctuation of ferrous-/ferric-haem exist in human and mouse RBC, and the period of rhythmicity is not affected by the canonical clock genes.
**Major comments:**
1)Although the authors conducted a careful biochemical evaluation of the "Bloody Blotting" signal, it is still unclear whether the changes in the Hb* (or Hb2*) signal corresponds to the changes in the ferrous-haem level in vivo. A direct perturbation on the level of in vivo ferrous-/ferric-haem is required. For example, is the Hb* (or Hb2*) signal decreased by the administration of amyl nitrite (in mice)?
__Thank you for the suggestion. We have addressed this and the second reviewer’s comment in a new Figures 4 & S4 and section titled “Effect of rhythms in metHb on vascular flow and body temperature”. __
For clarity, we have relabelled the schematic in A to “rest phase” and “activity phase” to consolidate data from humans and mice which both feature in the manuscript. We performed two experiments to test the model in Fig 4A and perturb metHb in vivo. The first is a direct perturbation of metHb levels in vivo with sodium nitrite, an oxidising agent that causes methaemoglobinemia. Reflecting our results ex vivo, RBC from differentially entrained mice sampled at the same external time, but 12h apart in terms of the light:dark cycle, contained significantly different metHb levels, with more metHb in the rest phase (revised Figure 4B, C). Whereas, RBCs from mice also given nitrite in their active phase contained more metHb (and thus lower Hb2* activity) than control (revised Figure 4B and S4). The second experiment tests the effect of sodium nitrite on core body temperature. Our hypothesis predicts that nitrite should accentuate the daytime drop in core body temperature, via the increased metHb-mediated production of NO to stimulate increased vasodilation (Ignacio et al 1981 and Cosby et al 2003). Revised figures 4D and E show that the effect of nitrite on body temperature (which has a large active vs inactive difference) is indeed daytime-specific.
Methods for these experiments have been added to Experimental Procedures.
2)The authors speculated that the higher PRX-SO2/3 signal during the first 24 hrs in mice is due to the sapling time at the resting phase (line ~235). The effect of sampling time should be easily tested by maintaining the mice group in 12-hr shifted L/D cycles and sampling the blood in the same o'clock (i.e., now the active phase). This type of experiment is also critical for the evaluation of Bloody Blotting because the level of Hb*/Hb2* signals may be affected by not only the circadian timing of mice but also the daily environmental fluctuation of a biochemistry laboratory (this is particularly important for the Bloody Blotting because some of the critical steps including the cross-linking between haem and Hb are supposed to occur in a test tube). If the signal of Bloody Blotting reflects the in vivo circadian rhythmicity, the 12-hr shifted L/D mice RBCs should have 12-hr shifted Bloody Blotting fluctuation pattern.
__We acknowledge this possibility. To test this, we sampled RBCs from mice kept under DL and LD conditions, as detailed in the new sections in the Experimental Procedures, harvesting blood at the same clock time. This gave us blood from mice in the “active” phase and “rest” phase – labels as per Figure 4B. Figure 4B shows that Hb2* signal significantly differs between mice in active and rest phases, even though these samples were collected and processed at the same external time. __
Separately from Hb2* activity, upon further reading of the literature we suspect that the higher PRX-SO2/3 signal detected in mouse RBCs (Fig 2) compared with human may be due to blood acidification during animal sacrifice by CO2. Additional text has been added to Supplementary Figure S3 to remark upon this, as follows:
"Interestingly, compared with human RBC time courses (Henslee et al., 2017; O’Neill and Reddy, 2011), we observed that murine PRX-SO2/3 immunoreactivity was extremely high during the first 24 hours of each 72-hour time course (Figure S3A). We attribute this to the different conditions under which blood was collected: blood was collected from mice culled by CO2 asphyxiation during their habitual rest phase by cardiac puncture and exposed immediately to atmospheric oxygen levels, whereas human blood was collected from subjects during their habitual active phase through venous collection into a vacuum-sealed collection vial. Thus, the initial high PRX-SO2/3 signal in mice may be related to CO2-acidification of the blood during culling, which affects PRX-SO2/3 but does not affect Hb oxidation status____."
3)Do the casein kinase inhibitors (ref: Beale, JBR 2019) affect the period of Bloody Blotting signals?
We have not experimentally addressed this as we consider it beyond the scope of the current study, which has instead focused on the in vivo relevance of the rhythms in metHb. Nevertheless, given the identical periodicity of PRX rhythms and Hb* rhythms (this paper), and the periodicity of PRX rhythms and rhythms in membrane conductance (Henslee et al, Nat Commun, 2018), we see no reason why the period lengthening of rhythms in membrane conductance reported in Beale et al, JBR, 2019 would not also been seen in PRX or Hb* rhythms.
**Minor comments:**
4)The authors quantify the dimer of Hb (Hb2*). This is important information but only explained in the supplementary figure legend. It should be explained in the main text. In addition, it is difficult to evaluate the fluctuation of Hb* (not Hb2*) because, as the authors stated, most of the Hb* signals are saturated. The saturation problem should be easily solved by reducing the sample loading volume. Quantification of Hb* is important at least experiments shown in figure 1A-G because the dimerization of Hb can be also affected by factors other than the in vivo ferrous-/ferric-haem conversion.
Thank you for pointing this out. Indeed the data throughout the original manuscript is Hb2*. We have brought this explanation into Figure 1 legend and labelled all figures consistently with Hb2*. We include quantification of Hb* and Hb2* of the in vivo metHb perturbation experiment (Figure 4) in the uncropped membranes shown in Supplementary Figure 4. The quantification of Hb* (Supplementary Figure 4D) gives the same result as the quantification of Hb2* (Figure 4B).
5)In the quantification of Hb2* (Figure 1A, 2E, 3C), were the signals normalized to Total Hb?
In the quantification of Hb2* throughout, signals were normalised to total protein through coomassie stain, apart from Figure 4B which used SYPRO Ruby. Each figure presents the Hb band of coomassie or SYPRO Ruby for simplicity, but the full gels are included in Supplementary Figures 1, 3 and 4.
6)The explanation and interpretation of the experiment shown in figure 3D should be more careful. The pulse-oximetry was conducted in normal working day conditions (real world setting) and thus should be affected by environmental and social daily signals.
__We have changed the section to the following (edits in bold): __
"Remarkably, in contrast to total Hb (SpHb) that displayed no significant 24h variation, the proportion of metHb (SpMet) in the blood exhibited a striking daily variation that rose during the evening and peaked during the night (Figure 3D). These subjects were in a real-world setting, and thus affected by environmental and social cues from a normal working day. However, the evening rise and night-time peak is consistent with ____the reduction in Hb2* activity at the end of the waking period in laboratory conditions (Figure 3B)____."
7)Typos at figure indicators in supplementary figure legends. Sup figure 1A legend refers to main figure "2" (should be 1), and figure S3 legend refers to main figure 1 (should be 3).
Thank you for pointing this out. We have corrected these legends.
Reviewer #1 (Significance (Required)):
The detection of circadian oscillation in RBC has been not easy because the experiment requires careful sample preparation and specific antibodies (Milev Methods Enzymol 2016) or a specific instrument for dielectrophesis (Henslee). The Bloody Blotting technic developed in this study will overcome this technical problem because Bloody Blotting does not rely on specific antibody and only requires conventional tools for western blotting. Because circadian biology of RBC is particularly important in the field of circadian research to evaluate the presence of eukaryotic circadian oscillator without transcription-translation feedback loops, this study will be interested a wide community of circadian clock researchers. This reviewer has expertise in the field of circadian genomics, biochemistry, animal experiments in mice as well as human.
Thank you for taking the time to read and constructively comment on our work
Reviewer #2 (Evidence, reproducibility and clarity (Required)): **Summary**
The study aims to provide a new tool for detecting the hemoglobin oxidative status named "Bloody blotting". It is based on redox- sensitive covalent linkage between the haem and the haemoglobin. This linkage is a consequence of an artifactual reaction provoked by the protein extraction, due to the lysis buffer's properties. In addition, using an in vitro (red blood cells) or in vivo (patients' blood) model the authors provide insight in the oscillating nature in the oxygen-carrying and nitrite reductase capacity of the blood, which is unaffected by the mutation of CK1εtau/tau and Fbxl3aafh/fh
**Major comments:**
In my honest opinion, the work does not provide interesting addition to what it is known in literature. The conclusions are summarized into a model (Fig.4) t, which is too speculative related to the amount and quality of results showed in the paper.
__We are disappointed by the reviewer's response. The physiological basis for daily rhythms in body temperature cooling is not currently understood, this work provides a testable basis for understanding it. Whilst we understand that the reviewer might not find immediate value in the biochemical mechanisms that initially informed our investigation, the recent publication of our investigation of human brain temperature rhythms (Rzechorzek et al., Brain, 2022) demonstrates that daily biological temperature rhythms are of broad interest (Altmetric score >2000). Daily temperature rhythms have almost exclusively been assumed to result from daily rhythms in heat production, yet the evidence for a contribution via daily rhythms of cooling is equally strong yet has received scant attention. __
__The speculative model that the reviewer refers to was a hypothesis that drew together multiple lines of published evidence for future experimental testing, not a conclusion, and was labelled as such in the original manuscript. To accommodate the reviewer's critique, however, we tested the model with new experiments, that are included in the revised Figure 4 and section titled “Effect of rhythms in metHb on vascular flow and body temperature”. __
For clarity, we have relabelled the schematic in A to “rest phase” and “active phase” to consolidate data from humans and mice which both feature in the manuscript, and described it as a hypothesis to avoid confusion. We performed two experiments to test this model. The first is a direct perturbation of metHb levels in vivo with sodium nitrite, an oxidising agent that causes methaemoglobinemia. RBCs from mice given nitrite in their active phase contain more metHb (and thus lower Hb2* activity) than control (Figure 4B). Reflecting our results ex vivo, RBC from mice sampled 12h apart contain significantly different metHb levels, with more metHB in the rest phase (Figure 4B, C). The second experiment tests the effect of sodium nitrite on core body temperature. Our model predicts that nitrite should further reduce core body temperature in the daytime, via the increased production of metHb (Figure 4C) and vasodilation (Ignacio et al 1981 and Cosby et al 2003). Figure 4D and E show that body temperature (which has a large active vs inactive difference) is further lowered upon nitrite treatment, and that this effect is restricted to the daytime, consistent with our hypothesis.
__Methods for these experiments have been added to Experimental Procedures. __
The title is misleading. The authors did not use any mutant for clock factors, but they used a kinase (CK1εtau/tau) and a ubiquitin ligase (Fbxl3aafh/afh) mutant, which are important in the regulation of proteins belonging to the clock machinery.
We respectfully disagree that the title was misleading. Mice and cultured cells/tissues that are mutant for CK1 and FBXL3 demonstrably show altered clock gene activity (See Godhino et al, Science, 2007, also Meng et al, Neuron, 2008, also Fig 2). Moreover, CK1 and FBXL3 are generally regarded as key components of the circadian clock due to their critical function in the regulation of clock proteins (e.g., Hirano et al, Nat. Struct. Mol. Biol., 2016). Being anucleate, RBCs lack the capacity for changes in clock gene activity and the period of oscillation is not affected by mutations that affect the activity and period of clock gene-oscillations in nucleated cells and whole mice. Since the rhythms of Hb oxidation persist in isolated RBCs, they cannot be dependent on clock gene activity and so must be considered to function independent of clock genes.
In light of the new data on mouse body temperature presented in revised Fig 4D/E, however, we have changed the title to better communicate the revised scope of the manuscript, as follows:
"Mechanisms and physiological function of daily haemoglobin oxidation rhythms in red blood cells"
Speaking of the specific points described in the paper, there are aspects that are not convincing. First, the bloody blotting is a consequence of a specific reagent contained in the lysis buffer used for the protein extraction, which reacts with the haemoglobin beta and alpha (as shown by Mass Spec). The peroxidase reaction is an artifact coming from this reaction, which simply follows the rhythmicity of peroxiding accumulation in the red blood cells, whose rhythmicity is known to be circadian. I do not really understand the utility of this technique, which anyway is limited to the specific lysis buffer, but for scientific reasons, researchers need often a different kind of lysis buffer. This means that the approach shows strong limitation to the chemical environment of the lysis buffer. I do not see in it a useful tool that can replace antibodies.
Apologies, we have not been clear enough. The bloody blotting is indeed a consequence of lysis, since that lysis condition fixes the cellular state at the time of lysis. In this case, the variation in Hb oxidation status is fixed at the time of lysis. The peroxidase activity we report is indeed revealed on membranes by the covalent interaction of the haem and Hb, which occurs at the point of lysis, and reports the oxidation state of the haem at the point of lysis. As we detail, haem exhibits peroxidase activity, so the signal we observe at molecular weights corresponding to Hb and Hb2 is peroroxidase activity due to covalently bound haem, where the peroxidase activity varies with the oxidation state of the haem. We have reorganised text associated with Figure 1, including changes to the final paragraph of the section to make explicitly clear that that the rhythm is due to a fixing of the redox state of Hb at the time of lysis – that a true underlying rhythm is revealed.
This technique is indeed limited to the observation of haem-peroxidase activity in RBCs on membranes. But as we explain in the manuscript, this is a far quicker and simpler method of observing RBC circadian rhythms than other methods, including immunoblotting for peroxiredoxins. Furthermore, it is common to change lysis buffer according to the downstream purpose.
Second, the oscillation in the peroxidase activity of PRX-SO2/3 is well known to be circadian (Edgar et al., 2012. doi:10.1038/nature11088.).
Many apologies, we do not understand the point. It is indeed correct that PRX-SO2/3 abundance oscillations have been reported in RBCs and other cells and organisms. Here we report another rhythm, separate to PRX: the rhythm in Hb:metHb. The PRX-SO2/3 blots serve as a positive control for rhythmicity.
Finally the circadian rhythms of red blood cells is already described and the corresponding author already published different papers about. The info provided in this paper do not add any new piece to the puzzle.
Respectfully, we report a novel rhythm in RBCs and demonstrate its functional relevance in vivo in humans (Figure 3) and mice (Figure 4), i.e., it is the identity of the rhythmic species that is novel, not that there are rhythms. What we further add with this study is that rhythms are not influenced by the cellular/organismal environment during RBC development (Figure 2), occur in vivo, in freely moving people (Figure 3) and metHb has a functionally significant role in body temperature rhythms (Figure 4). Furthermore, we report a novel technique for uncovering this rhythm in RBCs.
At this stage I do not consider the paper suitable for a publication. Other observations. Authors should describe how cells were synchronized.
RBCs in vitro were not synchronised by external cues. As reported in the Methods section, they were maintained at constant temperature after isolation. Fibroblasts were synchronised by temperature cycles as detailed and employed previously.
In experiments performed in vitro should be used the SD instead of the SEM.
We respectfully disagree. The SEM quantifies how precisely you know the true mean of the population - in each case we use it, we also present replicates’ data from which the mean is calculated (e.g. Fig 1A, Fig 2E, Fig 3B and Fig 4B). This gives the real scatter of the data, as a SD would.
**Minor comments:**
There are many English mistakes in the article, also errors in naming figures in the figure legends.
We have carefully re-examined the manuscript to find and fix these errors.
Figure 1B needs an appropriate loading control.
We have added the coomassie loading control to revised Figure 1B, with uncropped membranes shown in revised Supplementary Figure 1B
In experiments performed in vitro should be used the SD instead of the SEM.
SD vs SEM, see reply above.
Reviewer #2 (Significance (Required)):
Nature and significance of the advance At this stage I do not see any significance or advance in the field.
Compared to existing published knowledge. The The bloody blotting seems to be an original approach although full of limitation and based on artifactual reactions. PRX-SO2/3 is well known to be circadian (Edgar et al., 2012. doi:10.1038/nature11088.), therefore the paper does not add any new insight. The clock mutation do not affect the circadian rhythm in RBC is also known (O' Neill and Reddy, 2011). Therefore the results showed in the figure 3 support already published observations but do not add any particular insight.
It is unclear to us how the reviewer has misunderstood the scope and focus of the manuscript to such an extent. All previous work in this area by our own and other labs has been appropriately acknowledged. To reiterate the novel elements of this work:
- A daily rhythm of Hb redox state in mouse and human red blood cells, in vitro and in vivo. This was speculated about in O'Neill & Reddy (Nature, 2011) but never directly tested until now.
- That clock gene mutations that post-translationally regulate circadian period in nucleated mammalian cells do not affect circadian period in anucleate mammalian cells. O'Neill & Reddy (Nature, 2011) did not show this, rather we looked at (nucleated) fibroblasts that were deficient for Cry1/2 (a transcriptional repressor).
- A novel assay for measuring mammalian RBC rhythms - nowhere is it proposed that the assay would be useful in any other context, as the reviewer seems to imply.
- A mechanistic basis for understanding how daily rhythms in cooling of body temperature might arise, a poorly studied aspect of mammalian physiology.
__The elements in this work that are not completely novel are included as controls, they are not the focus of the manuscript e.g. PRX-SO2/3 rhythms have not previously been shown under these conditions in mouse RBCs, only human, so these blots are included as a control for rhythmicity in Fig2. Similarly, the period of oscillation of a genetically-encoded Cry1:Luc reporter in mouse fibroblasts would be predicted to be longer and shorter in Fbxl3 and Ck1 mutants, respectively, but nowhere this been published so we have included it as a control. __
Audience Chronobiologists, and medical science.
Fild of expertises (reviewer) Chronobiology, molecular biology, medical science.
**Referees cross-commenting**
I read your comment and they were very detailed. From my point of view I am very skeptical, as I discussed about the utility of the Bloody Blotting. Also the results showed in the paper are not very innovative fro my point of view. I would like to know what do you think about.
The rhythmicity is given by the elements present in the protein extraction. The reaction is given by the specific lysis buffer used in that experiment. Using another lysis buffer would not allow anybody to see some signal without a proper antobody. The authors claim that bloody blotting is useful because a researcher does not need to buy an antibody, but what if you don't work with a total total extract of proteins? In that case, you need to change the lysis buffer, and, therefore, the bloody blotting is not useful anymore. However, If you believe in that way, and you are two people agreeing in that, I will not oppose myself although I do not agree.
Reviewer #3 (Evidence, reproducibility and clarity (Required)): **Summary:** Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).
The manuscript "Clock gene-independent daily regulation of haemoglobin oxidation in red blood cells" describes a new assay for quantification of haemoglobin oxidation status (bloody blotting) in anucleate red blood cells". This study furthers our understanding of the role of a post-translational oscillator (PTO) in generating circadian rhythms in biology. The authors first describe how earlier work demonstrated 24h rhythms in the intensity of chemiluminescent bands on membranes blotted with protein from red blood cells (RBCs) in the absence of antibodies after exposure to ECL. They go on to address what these bands represent (through various approaches including the use of chemical inhibitors and mass spectrometry) and conclude that they are observing haemoglobin oxidation status. It is proposed that this assay represents a novel manner (complementary to earlier work) in which to report circadian rhythms in RBCs. The manuscript goes on to demonstrate the persistence of 24h rhythms in haemoglobin oxidation status in murine RBCs, including cells isolated from two clock mutant mice. Finally, the study utilises RBCs collected from human volunteers maintained under controlled conditions and demonstrate robust rhythms via "blood blotting", this data is presented alongside pulse co-oximetry data to examine physiological relevance of these rhythms.
**Major comments:** -Are the key conclusions convincing?
The key conclusions are well supported by the data. The discussion does become quite speculative, and this needs to be addressed.
-Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
The discussion around the physiological relevance of daily regulation of haemoglobin redox status is extensive (lines 366-403) as is the discussion on RBCs and the TTFL-less clock mechanisms (lines 405-429). Whilst interesting and well thought out, and well supported by the literature, these sections are very speculative and in my opinion should be toned down.
Thank you to the reviewer for both the compliment and suggestion. Indeed, these discussion sections were too long. We have reorganised the physiological relevance section to reduce its length and better accommodate the new data presented in the new experiments in Figure 4.
We have cut the TTFL-less section text by more than half.
-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.
Further experiments would be required to support the discussion about the role of daily rhythms in haemoglobin oxidation status in regulating oxygen carrying capacity of the blood, vascular tone, body temperature and sleep-wake cycle. As the authors state, these experiments are beyond the scope of this study, but are of course of major interest. It would be more appropriate to limit the discussion to what has been demonstrated directly by the data presented, with just a few sentences speculating on physiological relevance.
__As above, we acknowledge that we were speculative in that section and we have curtailed the discussion as suggested. __
-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.
If the focus of the discussion is shifted as suggested, there is no need to pursue any further experiments. -Are the data and the methods presented in such a way that they can be reproduced? Yes. The methods are complete, and data presented very well. -Are the experiments adequately replicated and statistical analysis adequate?
Yes
**Minor comments:**
-Specific experimental issues that are easily addressable.
1.In the murine fibroblasts/RBC experiments in Figure 2 - what genotype were the wildtype controls? The main text suggests PER2::luc (line 226) but methods suggest Cry1:luc - could the authors clarify this?
__Thank you for pointing out this mistake, corrected text to Cry1:luciferase __
2.In figure 2B and 2D the blots show two samples for each time point (except for 72h where there is just one) are these technical repeats? This should be clarified.
Apologies, the labelling of this figure was not clear – for space reasons we only labelled every 2nd timepoint – the time course was 3-hourly. We have corrected the figure to label each timepoint.
3.The controls for the bloody blots are referred to as coomassie in Figure 1. In Figure 2, the controls for PRX-SO2/3 are referred to as "loading" but are coomassie stained gels - could this be standardised? Also Figure 2D - no controls? In Figure 3B controls are referred to as 'Total Hb from coomassie staining - I wasn't clear what this was.
Thank you. Throughout we have now labelled loading controls by their method (coomassie or SYPRO Ruby). Figure 2D is taken from the same gel as Figure 2B and so the same coomassie gel stain is used as a loading control. We have altered the figure legend to reflect this. Each figure presents the Hb band of coomassie or SYPRO Ruby for simplicity, but the full gels are included in Supplemetary Figures 1, 3 and 4. We have changed each figure legend to reflect: “coomassie stained gels were used as loading controls; the Hb band from the coomassie stained gel is shown”.
4.Figure 3A "S1" and "S2" stated in legend but only "S" used in the schematic
Many thanks for pointing this out. We have corrected the schematic to S1 and S2.
-Are prior studies referenced appropriately? Yes absolutely. -Are the text and figures clear and accurate? Mostly, few comments above.
-Do you have suggestions that would help the authors improve the presentation of their data and conclusions? No
Reviewer #3 (Significance (Required)): -Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
The study describes a rapid and relatively simple assay for observing 24h rhythms in RBC function. On a technical basis - this will likely be of significant use to others in the field. Further work examining rhythms in haemoglobin oxidation in RBCs in clock mutant mice confirms independence from the transcriptional-translational feedback loop, which further supports earlier work in this field. Finally, studies in humans (bloody blotting in combination with pulse co-oximetry) provide a glimpse into the functional relevance of these daily oscillations
-Place the work in the context of the existing literature (provide references, where appropriate).
The authors have done an excellent job of reviewing the literature in the field and contextualising their data. This current data is a significant advance in the field.
-State what audience might be interested in and influenced by the reported findings.
This work will be of interest to circadian biologists and adds weight to the relatively new concept of a post-translational oscillator (PTO). Further work showing the relevance of this PTO on physiological function will be of great interest.
-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.
Circadian, Clock genes, mouse models,
I do not have a background in biochemistry and do not feel overly qualified to comment constructively on approaches taken to address what is driving the observed rhythmic peroxidase activity in RBCs (e.g NiNTA affinity chromatography, use of reductants to reduce thioester bonds and use of NEM to alkylate Hb cysteine residues).
**Referees cross-commenting**
In terms of the utility, as my review indicated, I do feel that this manuscript advances the field, providing a rapid and relatively simple way to measure rhythms in RBCs. Reviewer 1 explained this nicely in their significance summary.
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Referee #3
Evidence, reproducibility and clarity
Summary:
Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).
The manuscript "Clock gene-independent daily regulation of haemoglobin oxidation in red blood cells" describes a new assay for quantification of haemoglobin oxidation status (bloody blotting) in anucleate red blood cells". This study furthers our understanding of the role of a post-translational oscillator (PTO) in generating circadian rhythms in biology. The authors first describe how earlier work demonstrated 24h rhythms in the intensity of chemiluminescent bands on membranes blotted with protein from red blood cells (RBCs) in the absence of antibodies after exposure to ECL. They go on to address what these bands represent (through various approaches including the use of chemical inhibitors and mass spectrometry) and conclude that they are observing haemoglobin oxidation status. It is proposed that this assay represents a novel manner (complementary to earlier work) in which to report circadian rhythms in RBCs. The manuscript goes on to demonstrate the persistence of 24h rhythms in haemoglobin oxidation status in murine RBCs, including cells isolated from two clock mutant mice. Finally, the study utilises RBCs collected from human volunteers maintained under controlled conditions and demonstrate robust rhythms via "blood blotting", this data is presented alongside pulse co-oximetry data to examine physiological relevance of these rhythms.
Major comments:
- Are the key conclusions convincing?
The key conclusions are well supported by the data. The discussion does become quite speculative, and this needs to be addressed.
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
The discussion around the physiological relevance of daily regulation of haemoglobin redox status is extensive (lines 366-403) as is the discussion on RBCs and the TTFL-less clock mechanisms (lines 405-429). Whilst interesting and well thought out, and well supported by the literature, these sections are very speculative and in my opinion should be toned down.
- 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.
Further experiments would be required to support the discussion about the role of daily rhythms in haemoglobin oxidation status in regulating oxygen carrying capacity of the blood, vascular tone, body temperature and sleep-wake cycle. As the authors state, these experiments are beyond the scope of this study, but are of course of major interest. It would be more appropriate to limit the discussion to what has been demonstrated directly by the data presented, with just a few sentences speculating on physiological relevance.
- 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.
If the focus of the discussion is shifted as suggested, there is no need to pursue any further experiments.
- Are the data and the methods presented in such a way that they can be reproduced?
Yes. The methods are complete, and data presented very well.
- Are the experiments adequately replicated and statistical analysis adequate?
Yes
Minor comments:
- Specific experimental issues that are easily addressable.
1.In the murine fibroblasts/RBC experiments in Figure 2 - what genotype were the wildtype controls? The main text suggests PER2::luc (line 226) but methods suggest Cry1:luc - could the authors clarify this?
2.In figure 2B and 2D the blots show two samples for each time point (except for 72h where there is just one) are these technical repeats? This should be clarified.
3.The controls for the bloody blots are referred to as Coomassie in Figure 1. In Figure 2, the controls for PRX-SO2/3 are referred to as "loading" but are Coomassie stained gels - could this be standardised? Also Figure 2D - no controls? In Figure 3B controls are referred to as 'Total Hb from Coomassie staining - I wasn't clear what this was.
4.Figure 3A "S1" and "S2" stated in legend but only "S" used in the schematic
- Are prior studies referenced appropriately?
Yes absolutely.
- Are the text and figures clear and accurate?
Mostly, few comments above.
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
No
Significance
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
The study describes a rapid and relatively simple assay for observing 24h rhythms in RBC function. On a technical basis - this will likely be of significant use to others in the field. Further work examining rhythms in haemoglobin oxidation in RBCs in clock mutant mice confirms independence from the transcriptional-translational feedback loop, which further supports earlier work in this field. Finally, studies in humans (bloody blotting in combination with pulse co-oximetry) provide a glimpse into the functional relevance of these daily oscillations
- Place the work in the context of the existing literature (provide references, where appropriate).
The authors have done an excellent job of reviewing the literature in the field and contextualising their data. This current data is a significant advance in the field.
- State what audience might be interested in and influenced by the reported findings.
This work will be of interest to circadian biologists and adds weight to the relatively new concept of a post-translational oscillator (PTO). Further work showing the relevance of this PTO on physiological function will be of great interest.
- 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.
Circadian, Clock genes, mouse models,
I do not have a background in biochemistry and do not feel overly qualified to comment constructively on approaches taken to address what is driving the observed rhythmic peroxidase activity in RBCs (e.g NiNTA affinity chromatography, use of reductants to reduce thioester bonds and use of NEM to alkylate Hb cysteine residues).
Referees cross-commenting
In terms of the utility, as my review indicated, I do feel that this manuscript advances the field, providing a rapid and relatively simple way to measure rhythms in RBCs. Reviewer 1 explained this nicely in their significance summary.
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Referee #2
Evidence, reproducibility and clarity
Summary
The study aims to provide a new tool for detecting the hemoglobin oxidative status named "Bloody blotting". It is based on redox-sensitive covalent linkage between the haem and the haemoglobin. This linkage is a consequence of an artifactual reaction provoked by the protein extraction, due to the lysis buffer's properties. In addition, using an in vitro (red blood cells) or in vivo (patients' blood) model the authors provide insight in the oscillating nature in the oxygen-carrying and nitrite reductase capacity of the blood, which is unaffected by the mutation of CK1εtau/tau and Fbxl3aafh/fh
Major comments:
In my honest opinion, the work does not provide interesting addition to what it is known in literature. The conclusions are summarized into a model (Fig.4) t, which is too speculative related to the amount and quality of results showed in the paper. The title is misleading. The authors did not use any mutant for clock factors, but they used a kinase (CK1εtau/tau) and a ubiquitin ligase (Fbxl3aafh/afh) mutant, which are important in the regulation of proteins belonging to the clock machinery.
Speaking of the specific points described in the paper, there are aspects that are not convincing. First, the bloody blotting is a consequence of a specific reagent contained in the lysis buffer used for the protein extraction, which reacts with the haemoglobin beta and alpha (as shown by Mass Spec). The peroxidase reaction is an artifact coming from this reaction, which simply follows the rhythmicity of peroxiding accumulation in the red blood cells, whose rhythmicity is known to be circadian. I do not really understand the utility of this technique, which anyway is limited to the specific lysis buffer, but for scientific reasons, researchers need often a different kind of lysis buffer. This means that the approach shows strong limitation to the chemical environment of the lysis buffer. I do not see in it a useful tool that can replace antibodies.
Second, the oscillation in the peroxidase activity of PRX-SO2/3 is well known to be circadian (Edgar et al., 2012. doi:10.1038/nature11088.). Finally the circadian rhythms of red blood cells is already described and the corresponding author already published different papers about. The info provided in this paper do not add any new piece to the puzzle.
At this stage I do not consider the paper suitable for a publication. Other observations. Authors should describe how cells were synchronized. In experiments performed in vitro should be used the SD instead of the SEM.
Minor comments:
There are many English mistakes in the article, also errors in naming figures in the figure legends. Figure 1B needs an appropriate loading control. In experiments performed in vitro should be used the SD instead of the SEM.
Significance
Nature and significance of the advance At this stage I do not see any significance or advance in the field.
Compared to existing published knowledge. The The bloody blotting seems to be an original approach although full of limitation and based on artifactual reactions. PRX-SO2/3 is well known to be circadian (Edgar et al., 2012. doi:10.1038/nature11088.), therefore the paper does not add any new insight. The clock mutation do not affect the circadian rhythm in RBC is also known (O' Neill and Reddy, 2011). Therefore the results showed in the figure 3 support already published observations but do not add any particular insight.
Audience Chronobiologists, and medical science.
Fild of expertises (reviewer) Chronobiology, molecular biology, medical science.
Referees cross-commenting
I read your comment and they were very detailed. From my point of view I am very skeptical, as I discussed about the utility of the Bloody Blotting. Also the results showed in the paper are not very innovative fro my point of view. I would like to know what do you think about.
The rhythmicity is given by the elements present in the protein extraction. The reaction is given by the specific lysis buffer used in that experiment. Using another lysis buffer would not allow anybody to see some signal without a proper antobody. The authors claim that bloody blotting is useful because a researcher does not need to buy an antibody, but what if you don't work with a total extract of proteins? In that case, you need to change the lysis buffer, and, therefore, the bloody blotting is not useful anymore. However, If you believe in that way, and you are two people agreeing in that, I will not oppose myself although I do not agree.
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Referee #1
Evidence, reproducibility and clarity
Summary:
Anuculeate red blood cell (RBC) is one of the interesting biological models that indicate the presence of eukaryotic circadian system independent of transcription-translation feedback. In this manuscript, the authors set up a new method for quantifying the circadian rhythmicity in RBC. The method called "Bloody Blotting" was developed through the careful and insightful investigation of "non-specific band" observed in the western blotting of peroxiredoxin, which has been used for the circadian monitoring of RBC. The authors characterized that the "non-specific' circadian-fluctuating signals, which can be observed by ECL imaging without any antibodies(-HRP), were attributed to ferrous-haem, but not ferric-haem, cross-linked to Hb upon cell lysis. Through the Bloody Blotting, this study suggests that the circadian fluctuation of ferrous-/ferric-haem exist in human and mouse RBC, and the period of rhythmicity is not affected by the canonical clock genes.
Major comments:
- Although the authors conducted a careful biochemical evaluation of the "Bloody Blotting" signal, it is still unclear whether the changes in the Hb (or Hb2) signal corresponds to the changes in the ferrous-haem level in vivo. A direct perturbation on the level of in vivo ferrous-/ferric-haem is required. For example, is the Hb (or Hb2) signal decreased by the administration of amyl nitrite (in mice)?
- The authors speculated that the higher PRX-SO2/3 signal during the first 24 hrs in mice is due to the sapling time at the resting phase (line ~235). The effect of sampling time should be easily tested by maintaining the mice group in 12-hr shifted L/D cycles and sampling the blood in the same o'clock (i.e., now the active phase). This type of experiment is also critical for the evaluation of Bloody Blotting because the level of Hb/Hb2 signals may be affected by not only the circadian timing of mice but also the daily environmental fluctuation of a biochemistry laboratory (this is particularly important for the Bloody Blotting because some of the critical steps including the cross-linking between haem and Hb are supposed to occur in a test tube). If the signal of Bloody Blotting reflects the in vivo circadian rhythmicity, the 12-hr shifted L/D mice RBCs should have 12-hr shifted Bloody Blotting fluctuation pattern.
- Do the casein kinase inhibitors (ref: Beale, JBR 2019) affect the period of Bloody Blotting signals?
Minor comments:
- The authors quantify the dimer of Hb (Hb2). This is important information but only explained in the supplementary figure legend. It should be explained in the main text. In addition, it is difficult to evaluate the fluctuation of Hb (not Hb2) because, as the authors stated, most of the Hb signals are saturated. The saturation problem should be easily solved by reducing the sample loading volume. Quantification of Hb* is important at least experiments shown in figure 1A-G because the dimerization of Hb can be also affected by factors other than the in vivo ferrous-/ferric-haem conversion.
- In the quantification of Hb2* (Figure 1A, 2E, 3C), were the signals normalized to Total Hb?
- The explanation and interpretation of the experiment shown in figure 3D should be more careful. The pulse-oximetry was conducted in normal working day conditions (real world setting) and thus should be affected by environmental and social daily signals.
- Typos at figure indicators in supplementary figure legends. Sup figure 1A legend refers to main figure "2" (should be 1), and figure S3 legend refers to main figure 1 (should be 3).
Significance
The detection of circadian oscillation in RBC has been not easy because the experiment requires careful sample preparation and specific antibodies (Milev Methods Enzymol 2016) or a specific instrument for dielectrophesis (Henslee). The Bloody Blotting technic developed in this study will overcome this technical problem because Bloody Blotting does not rely on specific antibody and only requires conventional tools for western blotting. Because circadian biology of RBC is particularly important in the field of circadian research to evaluate the presence of eukaryotic circadian oscillator without transcription-translation feedback loops, this study will be interested a wide community of circadian clock researchers.
This reviewer has expertise in the field of circadian genomics, biochemistry, animal experiments in mice as well as human.
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www.biorxiv.org www.biorxiv.org
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Reply to the reviewers
Manuscript number: RC- 2023-01819
Corresponding author(s): Gernot Längst and Harald Wodrich
Full revision of the manuscript
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.
2. Point-by-point description of the revisions
Dear Reviewers, thank you very much for your appreciation of our study and your input. In this point-to-point response, we amended our text marked in blue colour.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The authors have addressed the nucleoprotein structure of human adenovirus during the very early stages of infection, and its relationship to onset of expression of viral genes, using a combination of RNA-seq, MNase-seq, ChIP-seq and single genome imaging. They show that in the virion and the newly-infecting DNA, protein VII is precisely position at specific sites on the viral DNA, with greater accessibility at early gene promoters compared to other regions. Nucleosomes containing H3.3 replace specific protein VII at distinct positions at the transcription start sites of genes, which are then acetylated. Association with histones and nucleosomes occurs prior to transcription. These studies confirm and greatly expand on results already in the literature, and also elucidate a novel role for protein VII in orchestrating positioning of nucleosomes prior to initiation of transcription.
The authors provide excellent data in support of their conclusions and, in many instances, use alternative experiments (i.e. two different approaches) to support their claims. The details of methods are adequate (with small exceptions outlined below) and statistical methods appropriate.
Minor comments:
Line 561 "Protein VII molecules were exchanged for positioned nucleosomes at the +1 site of actively transcribed genes". This statement seems to suggest that the +1 position almost acts as a nucleating site, where replacement of a single, specific protein VII molecule at +1 is an initiating event, which then spreads from that site and into the rest of the gene. Data shown in Figure 6G and 6H shows that H3.3 appears to be found equally along the full length of E1A as early as 1 hr post infection (with no real "enhancement" at the +1 position), and that the overall levels simply increase over the next 4 hrs.
As the reviewer pointed out, the histone ChIP-seq peaks are broader than the +1 nucleosome region, extending into the transcribed regions of the gene. This is expected, as the mean length of the immunoprecipitated DNA is about 400bp long. Still, ChIP-seq peaks are in proximity to the transcription start site and overlap with the position of the +1 nucleosome. As we do not have the required resolution, we toned done our statement. The text now reads as follows: “Protein VII molecules were exchanged for nucleosomes downstream of the transcription start site, overlapping the +1 nucleosome site, of actively transcribed genes“ (line 568 ff).
Curiously, the authors chose not to use a wildtype virus for their studies - the virus contains a deletion in the E3 region. For clarity, I suggest that the authors should preferentially use an alternative designation for their virus rather than HAd-C5. Perhaps HAd-C5delE3 to differentiate this work from studies that truly use wildtype virus.
As requested by the reviewer we have updated the nomenclature to HAd-C5dE3 throughout the text and the figures.
The obvious limitation of the studies using the fluorescent TAF1-beta to label Ad genomes is that as protein VII is replaced by nucleosomes, the genomes would have declining detection by this method. Genomes devoid of protein VII would be "invisible".
Our MNase data show that within the first 4h only a fraction of pVII is removed from the viral genome e.g. at early genes, while most of the genome remains bound by protein VII. This should provide enough binding sites for TAF1-beta to label Ad genomes without a significant drop in the signal. Furthermore, our recent work (PMID:29997215, Fig. 1D) compared the TAF1-beta labelling system with a second in vivo detection system (AnchOR3) that directly labels the viral DNA independently of protein VII in the same cells. This direct comparison of two technically non-related methods to detect individual incoming adenoviral genomes in living cells showed the equivalence of both methods, at least for the first hours of infection showing that partial removal of protein VII does not affect the fluorescent TAF1-beta staining.
Line 275 "Interestingly, a central region of the viral genome (Late3) and a region between the E3 and E4 genes exhibited almost no peaks" for protein VII. The virus utilized in this study lacked at least part of the E3 region. Did this deletion "cause" this region to be devoid of protein VII? Is the same absence of protein VII peaks observed in a fully wildtype virus? Also, can the authors provide any speculation as to why the Late3 region also lacks protein VII?
We confirm the reviewer's observation. The region marked as Late3 and the region between E3 and E4 is present in the genome and is, as the reviewer observed, not chromatinized in our analysis. At this point, we can only speculate. We have two not mutually exclusive hypotheses. First, both regions could be involved in the proper packaging of the viral genome into the capsid. Physical constraints during packaging may preclude this region from being packaged into pVII. Second, as we observed that pVII positioning correlates with distinct DNA sequence patterns (revised Fig.4 D and E, see response to reviewer 3 for details), it might be that the sequence composition at the pVII depleted regions disfavour pVII assembly to keep those regions available for cellular factors that drive processes post genome delivery, such as transcription. Our time-resolved MNase analysis shows that indeed post genome delivery, this site in the Late3 region becomes protected (Fig. 5C), suggesting the binding of one or more cellular factors. As shown in Figure S6 we find conserved binding sites for several transcription factors at this MNase protected site.
Whether the chromatinization devoid regions would shift in position, remain in place or be chromatinized in a wildtype virus has to be addressed in the future and cannot be answered at this point. To address the comment, we have expanded the discussion (line 620 ff)
Line 569 "Reasons could be that the few genomes undergoing nucleosome assembly and active transcription produce the replication enzymes, whereas the bulk of genomes enters replication without activation as an elegant way to avoid repeated chromatinization." This argument may make sense in the context of a high MOI infection, but would certainly limit virus function during normal, pathogenic infection where the MOI is likely extremely low. Essentially, the authors data predicts that 80% of normal, low MOI infections don't progress to gene expression (at least during the first 4 hrs analyzed in this study).
We follow the argument of the reviewer. The high MOI in our study was necessary to perform the combined ‘omics’ approach to arrive at meaningful data within reasonable sequencing depth. To have equivalence we also used high MOI for the imaging approach. A detailed analysis for the effect of low MOI as well as positioning effects (see reviewer comment below) on transcriptional activation is an important question and will be addressed in future studies that require different techniques in addition. To address this comment, we have updated the discussion to emphasize the importance of MOI and positioning effects (line 587 ff).
Line 576 "This observation is in agreement with recent pVII-ChIP experiments showing transcription and replication independent pVII removal in early infection (Giberson et al., 2018; Komatsu and Nagata, 2012; Komatsu et al., 2011)." The authors can also state that histone and nucleosome deposition is also independent of transcription and replication, as has been alluded to in the same cited studies but proven more directly in this study.
We have changed the text accordingly (line 576 and 598).
Line 672 - the authors should be more definitive in the MOI that are used in all of their experiments. Line 672 states that an MOI of 3000 physical particles are applied per cell. There can be great variation between cell lines in how much virus binds to (and enters) a cell based on the surface levels of Ad receptors on different cell types. However, in general, 3000 is very high. Work by Wang et al. (PMID:24139403) showed that at an MOI of 200 or below most Ad will traffic correctly to the nucleus, whereas at an MOI above 200 there is a significant defect in Ad trafficking within the cell. How is this expected to affect all of the results in this study?
We agree with this and the other reviewer that this is an important issue. The actual dose of virus that enters a given cell is dependent on the concentration of virus particles in the inoculum and the time and temperature this inoculum is in contact with the cells and the cells respective susceptibility to the virus. We applied an infection dose of 3000 physical particles per cell in a defined volume (1ml) at 37˚C for 30min followed by inoculum removal. We prefer this description because with these infection conditions, we find on average well below 100 virus particles that enter the cell (=> This is e.g., reflected in the number of accumulating genomes shown in figure 2A). In contrast, this permits to have enough viruses inside the cell to perform the different “omics” techniques applied in our study to obtain meaningful results at reasonable sequencing depths. This experimental setting was carefully chosen in full awareness of the work by Wang et al., cited by the reviewer, to avoid e.g., overloading the nuclear import rate. Thus, our experimental conditions do not exceed the “MOI of >200” that would affect nuclear import rates. The number (>200) in the Wang et al. study refers to the number of virus particles inside the cell, the infection condition used in the Wang study was an MOI of 30 bound to Hela cells in the cold for 30min and warmed for 150min which is significantly more virus than we have used in our study. We have expanded the information on the MOI used in the material and methods section to clarify this point (line 685 ff).
Figure 5 is of low resolution and was difficult to read.
We thank the reviewer for spotting it. It seems that the Figure quality was compromised during the PDF conversion. We updated the Figures and checked the resolution after PDF conversion.
Figure S3 is missing a box from the top set of images indicating the region that is expanded in the detail picture.
We updated Figure S3
While I realize it is supplemental data, the difference in quality between the agarose gels shown in Figure S4A and S5A is shocking.
The nature of the experiments is very different and therefore the expected MNase digestion profiles on agarose gels look different. In Figure S5 viral particles were digested with MNase, resulting in a smeary decrease in DNA size. This looks very different from the regular MNase pattern of whole cells that is dominated by the regularly spaced nucleosomes in the heterochromatic regions of the genome. As pVII protects only about 70bp of DNA and its spacing is not as homogenous as the nucleosomal spacing, the pictures shown in Figure S5A were expected as they are.
Figure S7 is of low resolution.
We updated the Figures and checked the resolution after PDF conversion.
Reviewer #1 (Significance (Required)):
At least in the field of adenovirus research, this is a very important study. There has been considerable debate in the field regarding the timing and degree of protein VII removal and histone deposition, and the necessity of active transcription for these two events. The data provided in this manuscript clearly shows that some protein VII is removed from early active genes and replaced by nucleosomes, and that these events occur prior to initiation of transcription. The authors speculate that the specific placement of protein VII, a protamine-like protein, on the Ad genome prescribes where nucleosomes are placed. This finding should be of interest to a broad general audience, as it provides novel information on chromatin assembly within mammalian cell. Key words for this reviewer: adenovirus research, HAdV nucleoprotein structure
Reviewer #2 (Evidence, reproducibility and clarity (Required))
The submitted manuscript presents a detailed and comprehensive analysis of the adenoviral nucleoprotein complexes as infection progresses, starting with the "adenosome" assembled with pVII which are then progressively replaced with H3.3.-containing nucleosomes as the infection progresses. The submission presents a combination of in situ and populational analyses of the viral DNA accessibility and complexes through infection. I brief, the infecting viral genomes are assembled in some 250 adenosomes with pVII, which become progressively replaced as infection progresses with nucleosomes containing H3.3 and acetylated H3K17, starting at the active promoters of the E genes. Chromatin remodeling precedes transcription, and the accessibility differs for genes of different kinetic classes at differ times after infection, although there is no correlation between accessibility and H3.3. or acetylation content. Only about 20% of the genomes become transcriptionally active, though, which somewhat complicates the analyses of the populational studies of accessibility and occupancy. Overall, the study is well conceived, performed and presented. A few issues that deserve further analyses and discussion, as described below.
Major issues.
As figure 2 nicely shows, only about 20% of the intranuclear genomes become transcriptionally active. However, MNase and ChIP analyses cannot differentiate these genomes from the 80% that are transcriptionally inactive. The interpretation of the positioning of pVII (figure 4) or the changes in compaction of the adenoviral chromatin at different loci (figure 5) does not appear to consider this heterogeneity other than for a brief comment about the stringent MNase digestion in page 11. The authors favor a model in which the changes in compaction shown in figure 5, at mild MNase digestions, directly correlate with transcription of the respective genes. This could well be correct, and in fact the correlation may be underestimated as 80% of the genomes may not undergo any changes, but it may also be incorrect. The analyses presented cannot differentiate whether the changes in chromatin compaction occur in only a subset of genomes or in all the genomes, regardless of whether they are transcribed or not, or even only in the non-transcribed genomes (which appears extremely unlikely). This intrinsic limitation to the methods used (and I know of no better alternative) should be acknowledged and discussed for the benefit of the reader. This limitation also impacts the analyses of the lack of correlation between H3.3 and acetylated H3K27 occupancy and compaction.
A discussion is amended and located starting from line 571 in the text. “The heterogeneity of 80% inactive genomes and 20% activated genomes complicates the analysis of the MNase-seq data. High MNase concentrations do not differentiate between both states, and we suggest that low MNase conditions capture the dynamic viral proportion, changing and preparing its genome for gene activation. The data nicely suggest such a scenario, but there is the caveat that we catch an effect of the mixed population that we cannot differentiate.”
The analysis of the histone ChIP is discussed below.
Perhaps out of necessity to reach the required sensitivity, a high multiplicity of infection was used (although the actual moi is not stated, there are about 25-30 pVII foci/ per nuclei). The presentation, analyses and discussion of the results should emphasize this context. For example, one would presume that at low moi, when only one genome enters each cell, the percentage of transcriptionally active genomes in a given cell will be either 0 or 100%, but the "system" becomes saturated as more and more genomes enter the nucleus at higher moi resulting in only a subset of them being transcriptionally active. Along this line of reasoning, it is intriguing that the percentage of genomes estimated to be in nucleosomes at 4 hpi (14%) approaches the percentage of transcribed genomes.
This issue was also raised by reviewer 1 (see detailed comment above). The reviewer is correct that we chose to use a higher MOI to reach the required sensitivity in our different “Omics” assays. The imaging approach was adapted to reach the morphological equivalence to fit this analysis. We agree that it would be interesting to also study the MOI effect on transcriptional activation (as well as positioning effects, see comment below) but this requires different approaches and will be addressed in a future study. To address this comment (and others in this review) we revised the text in the discussion to emphasize the importance of MOI and possible other effects such as positioning (line 587 ff).
The changes in chromatin compaction presented in figure 5 are in some respect puzzling. The compaction of most of the late genes increases as infection progresses, at least for the first four hours, as the authors discuss. However, the L genes appear to be at least as accessible as the E ones at the early times, when only the E are transcribed to high levels. This appears counterintuitive, and may not be consistent with the main conclusion that increase accessibility to a given gen directly correlates to its transcriptional activity level. The data presented in Figure 5C deserves a more nuanced analysis and discussion, parsing out the changes in accessibility to each given gene at different times from the different accessibility to the different genes at any given time. The later does not appear to support the main conclusion reached by the authors that accessibility to each individual gen correlates with its transcriptional level.
We thank the reviewer for raising this point. While the viral genomes enter the nucleus, the viral chromatin structure is tightly condensed. Therefore, it is unlikely that after nuclear entry the viral chromatin undergoes further compaction. With our analysis, we expect to detect only decompaction of genomic sites relative to 0 hpi, when the virus has not entered the nucleus yet. At some sites and particularly at the Late genes the signal is decreasing, most likely due to normalization to sequencing depth and the variation in the number of viral genomes but not due to changes in compaction. We realized that the negative accessibility scores we used in the study are misleading and give a false impression. Therefore, we changed the analysis in that way, that negative values were not permitted and converted to zeros.
Additionally, we raised the temporal resolution of the analysis and compared the accessibility at all available timepoints against 0 hpi as suggested by the reviewer. Now, we clearly observe, that most accessibility changes are accomplished rapidly after nuclear import, already at 1 hpi and do not change much after, until 4 hpi. Regions of decompaction coincide with early expressed genes and occur before transcription, underscoring the conclusions made in the study. Nevertheless, while most genomic regions covering late genes do not show decompaction, we observed some local sites showing a high accessibility score. As transcription at those sites appears later in the life cycle of the virus, we can only speculate about the function e.g. as enhancer elements.
The Text and Figures were changed accordingly (line 347 ff).
New legend:
__C) __Profile illustrates HAd-C5dE3 genome coverage by low MNase-seq fragments. The average of two replicates is shown, except at timepoint 0 hpi where only one replicate was available. The accessibility score was calculated as the log(fold-change) between the indicated timepoint and 0 hpi. The score was assessed for each pVII peak (orange bars) and negative scores were set to 0. A new accessibility peak arising during infection in the Late3 region is marked by an asterisk. __D) __Boxplot showing the accessibility score distribution in each domain at each tested timepoint after infection.
Minor comments
The authors may wish to highlight in the discussion that the analyses are so far limited to a single adenovirus.
We have taken up the suggestion of the reviewer and included it in the discussion part, starting at line 607:
“The structural analysis is still limited to a single adenovirus genotype and it will be interesting to test whether these dynamic changes are conserved among other adenoviruses. Furthermore, reproducing such organization in adenoviral vectors could result in efficient and sustained transgene expression.”
The y-axes in the transcriptome figures (figure 1 B, S2) could be presented in Log(2) scale, such that transcript levels at all times can be appreciated in the same graph (the earlier times are just not visible in a linear scale)
As requested by the reviewer we changed the data to log2 scale. As there is no qualitative difference to the log10 scale, presented in the original version, we would like to keep the figure as it is. To highlight changes at early time points we generated the average expression of early genes in Fig1C.
As an information for the reviewer, we provide here the data plotted as log2 scale.
The (lack of) phenotype of the 24xMS2 binding site recombinant adenovirus used should be shown.
We observed no difference in phenotype between the parental and the MS2 modified virus. We updated Figure S3 and included a gel analysis and specific infectivity data to show this absence of difference.
The kymograph analyses presented in figure 3B appear to show that there are some sites of transcript accumulation sites which do not harbor viral genomes (i.e., green only tracks). Moreover, the interpretation of the TAF1beta-mCherry signal is complicated by the (fully expected) significant "background" signal. Although these results are consistent with those obtained by RNAscope/pVII staining, there appears to be intrinsic limitations to the system, which preclude reaching strong conclusions from it. These confirmatory analyses should probably be moved to the supplementary information section and removed from the main text and figures. The longer evaluation data mentioned as not shown in page 8 is critical to the conclusions and should be shown.
Here we disagree with the reviewer and prefer to keep the data as main figure. All (immobile) transcript accumulation sites are identified by the kymograph analysis and coincide with a genome while free transcripts show a high mobility that is not picked up in the kymograph analysis. This is independently verified in the provided supplemental movies. Depending on the positioning of the genome inside the living cell, accumulating transcripts can appear adjacent to or on top of a genome. This explains the slight shift between RNA and DNA signal for some genomes in the merged image of the kymograph. This is expected as only fully transcribed transcripts and not nascent transcripts are marked by MS2 (the MS2 loops are positioned in the 3’UTR). Also, all genomes (transcribing and non-transcribing) can be identified in the kymograph above background level. To clarify the representation, we have added labels to the kymograph to show which signal is DNA and RNA and a merge respectively. We are convinced that this data set is in strong support of our study, as it is the only technique that permits the discrimination of transcribing and non-transcribing genomes in living cells at real time.
As requested, we have also added two additional examples for a longer observation period (10min) into the supplemental data Fig. S3C.
Although the plot of cleavage frequency presented in figure S5 is clear, it would be beneficial to the reader if the actual peaks were also presented to compare their distribution (if any) in gDNA and virus particle.
In Figure S5 we wanted to test whether the regions lacking pVII peaks are resulting from the absence of pVII, protecting the DNA, and therefore being fully hydrolyzed by MNase, or whether this region is tightly packed by pVII thereby protecting DNA from MNase digestion. To test both possibilities we used a very limited MNase digestion approach, where even free DNA is not fully hydrolyzed, allowing the capture of DNA fragments. Therefore, the sequenced fragments comprise a mixture of protected and un-protected fragments. In this assay, the pVII protected fragments are not fully digested to the monomeric state, but a mix of mono-, di- and other multimers are present. As reflected by the fragment size distribution with the peak between 100-200 bp (Fig S5B), pVII dimers are predominantly enriched when compared to the high MNase digestion used to map pVII positions (compare to Fig4 B). Therefore, the peaks in the S5 data set have a low resolution and do not provide exact pVII positions (see below). Therefore, we would like to keep S5 as it is. We clarified this point in the text (line 279 ff)
Legend:
Fragment coverage plot of MNase digestions of gDNA (black) or Ad chromatin in virus particles (purple).
The mRNA analyses of selected transcription factors provides little information, as there is no context, there is variability between experiments, and in most cases the changes appear modest. As these results are not critical to the conclusions or analyses, perhaps the authors may wish to remove them from the manuscript. Alternatively, more in-depth analyses would be required.
We agree with the reviewer, that more information for the reader is needed. Therefore, we performed a statistical analysis of expression changes between 0 hpi and 4 hpi of the shown transcription factors using DESeq2. We added the corresponding log2(fold-change) and p-values to the figure. And adapted the text (line 471) and figure accordingly.
Legend:
Gene expression changes of transcription factors over the infection time course. P-values and log2(fold-changes) from differential gene expression analysis between 4 hpi and 0 hpi using DESeq2 are indicated. ns = not significant
It is unclear why the even distribution of H3.1-flag signal across the genome is considered indicative of no specific recruitment. The results presented are equally consistent with equal incorporation across the genome. Perhaps the authors have some additional information, such as an irrelevant antibody, input DNA, or the like, to support the conclusion. If so, that evidence should be presented and discussed. If not, the interpretation should be revisited. As an added complexity, endogenous H3.1 is normally expressed during S-phase. It is possible that Adenovirus infection may induce higher levels of expression of (untagged)endogenous H3.1, which would outcompete the tagged ectopically expressed histone. These analyses deserve a more nuanced and in-depth analysis.
We have taken several measures in the study to address the concern of the reviewer. We consider timepoint 0 hpi as background control as the viral genome has not entered the nucleus yet. Consistently, we observe very few reads mapped to the Ad genome regardless of antibody and construct used (Fig 6B). Additionally, all samples at 0 hpi cluster together in PCA (Fig 6C) and correlation analysis (Fig S7D)
H3.1 Flag tagged samples show at later timepoints (1 - 4hpi) slightly higher percentages of mapped reads to Ad, but plateau already at 1 hpi (Fig 6B) and cluster together in PCA (Fig 6C) and correlation analysis (Fig S7D) with 0 hpi samples. The low background signal starting at 1 hpi for H3.1 might arise due to the change of Ad genome location to the nucleus.
Even though, the number of Ad mapped reads at later timepoints was low in H3.1 Flag tagged samples, it could still be that they accumulate at few sites on the Ad genome indicating a specific deposition. We tested this by plotting the signal across the whole Ad genome (Fig S7E) and zooming into the data (compare scale of H3.3 and H3.1 plot), but we could not detect any reproducible local enrichments. To enable the reader a better comparison between the levels of H3.1 incorporation with H3.3 we put now both on the same scale (Fig 6D and Fig S7D) clearly showing that we cannot detect H3.1 incorporation at Ad genomes in the first 4 hours of infection. The H3.1 signal corresponds to the background noise. We think for two reasons, that it is very unlikely that endogenous H3.1 outcompetes the tagged H3.1:
- The time scale for the cells to transition into S-Phase and upregulate endogenous H3.1 would be only 1-2 hours in our timeseries experiments and therefore too short. To also show these experimentally we amended an experiment for the reviewer that is not included in the manuscript. The Western blots below show that the protein amount of H3 does not increase in the first 4hours of infection. Cells were infected and whole cell extracts were prepared 4hpi.
- As most cells are not in S-phase in our experiments, the expression levels of H3.3 variant is higher than H3.1. With the Flag ChIPs we can clearly show that the tagged H3.3 are not outcompeted by endogenous H3.3. As there is a high sequence similarity between H3.3 and H3.1 it is very unlikely that they behave in that regard differently.
It is highly unlikely that the somewhat higher H3K27ac signal observed in the H3.3 than in the H3.1 expressing cells may result from higher H3.3. occupancy in the viral genome as speculated in page 13. The total levels of H3.3. are unlikely to increase by the ectopically expressed one, and even if they did it is not likely that the occupancy of the viral genome would be limited by the levels of H3.3. This speculation should be removed.
We removed the speculation.
Materials and methods are too concise. A longer more detailed version, as supplementary information, would be highly desirable.
We extended the materials and methods part.
Reviewer #2 (Significance (Required)):
The major strengths of this manuscript lie on its comprehensiveness, using several in situ and populational approaches to address biologically critical questions regarding the regulation of viral replication by chromatin and epigenetics. Experiments appears very well designed and performed and are mostly clearly presented. The interpretation analyses and discussion of the results may benefit from a more nuanced analysis of the issues posed by the existence of different populations of viral genomes in the cells infected at high moi and the accessibility across different genes at any given time versus the levels of transcription of the different genes, which appears not to be fully consistent with one of the main conclusions reached.
This study makes a very significant contribution, describing the dynamic changes in the adenoviral nucleoprotein complexes at the early times of infection and providing a full description of both the adenosomes and the nucleosomes in more and less transcribed loci. The results are properly analyzed in context of what is known about the regulation of viral gene transcription by chromatin dynamics in other systems, including similarities and differences. This study is likely to be of high interest to a wide audience, ranging from virologist to epigeneticists, to those working in gene therapy and vectored vaccines.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
The manuscript "Adenoviral chromatin organization primes for early gene activation" combines RNA-seq, MNase-seq, ChIP-seq, and single genome and transcript imaging (immunofluorescence, RNA-scope, and live cell techniques) during early Adenovirus infection in vitro to characterise the spatiotemporal dynamics of viral chromatin organisation and association with gene transcription. The manuscript is an interesting read and the authors have combined multiple complimentary techniques to make a substantial contribution to understanding the early events occurring after nuclear import of viral genomes. Adenoviruses are important causes of human and animal pathology, are a useful model of non-integrating extra-chromosomal DNA virus infection in mammalian cells, and are useful vectors for vaccination and the discoveries may influence gene therapy DNA vector design. The chromatin organisation in adenovirus infection is distinct from other DNA viruses, and is relatively poorly understood compared to, for example, SV40 or herpesviruses. The manuscript describes an early transition from purely viral chromatin with Adenovirus protein pVII packaging the virus in virions, to a viral-human hybrid chromatin pattern with apparently strategically positioned H3.3 nucleosomes and viral pVII "Adenosomes" in the early hours after nuclear import of the viral genome. The data shows that packaged Adenoviruses are in a transcriptionally accessible form and gene expression occurs rapidly after infection, the combination of the MNase-seq data with ChIP-seq data is particularly interesting demonstrating and average ~238 adenosomes positioned by specific DNA code protecting 60-70bp of DNA, and that the genome is accessible at loci that also decondense on infection, with adenosomes being replaced by cellular H3.3 containing nucleosomes at distinct sites. Particularly they show that +1 H3K27 acetylated nucleosomes are acquired at the TSS of key early genes. The authors argue that their spatiotemporal data imply that this chromatin transition "primes" for early gene transcription. The manuscript is well written, uncovers important viral chromatin biology by combining multiple experimental techniques, and the data is generally very clearly presented. A few comments follow. Major concerns: • Abstract and Title: o the abstract and title suggest that because the chromatin changes are observed coincidentally or before transcriptional changes, and that this means that these chromatin changes "prime" (title) or are "required" and play a "central role" (abstract) in early gene expression. The temporal relationship would be consistent with chromatin changes being required for transcriptional changes, but do not imply necessity. Experiments to demonstrate the necessity of these changes for early gene transcription are lacking, and I recommend amending the text or additional experiments to provide this evidence directly.
We observe a clear timing of events, with chromatin opening, nucleosome assembly at the 5’ end of the gene followed by transcriptional activation, suggesting that these structural changes are essential for gene activation. Still, we cannot prove the direct dependency. Therefore we toned down the title of our manuscript and formulate the findings more conservatively.
The title now reads: “Changes in adenoviral chromatin organization precede early gene activation”
Results:o The IF data in Fig S1 is convincing, showing viral particles are accessible quickly in the nucleus. Although no statistics are provided for S1B and C, pVII foci appear at 0.5hpi and appear to mostly accumulate between 0.5hpi and 1hpi with further import between 1hpi and 4hpi. Can the authors be sure that a single pVII IF focus represents a single genome? If genomes tend to aggregate as they accumulate the number of foci per nucleus may not increase linearly with the number of genomes imported. Have the authors considered analysing the intensity of the individual pVII foci over the time points? A related question is whether the authors assume that all packaged virions contain intact complete viral genomes? Many viruses comprise some mixture of complete and incomplete packaged genomes, and the subsequent analyses determine the proportion of transcriptionally active copies with RNA-Scope to a single transcript E1A which lies at one end of the viral genome. Please comment explicitly on whether this is assumed and whether this assumption is realistic in light of known Adenovirus biology.
We appreciate the reviewer's concern. Several studies in the adenovirus field have shown equivalence between protein VII nuclear foci and individual genomes, including our own (PMID: 26332038). Probably the most accurate study was performed by Daniel Engels lab PMID: 19406166, who used nuclear protein VII foci to titrate viral as well as vector genomes. In contrast, a different study from Patrick Hearings lab PMID: 21345950 showed that past 4hpi, the number of nuclear protein VII foci gradually declines. Based on our experience and because our study is limited to 4 hpi we are confident that protein VII foci accurately reflect individual viral genomes.
Concerning genome packaging, adenovirus particles contain a single viral genome that is protected at each end by a covalently attached protein preventing its degradation. The packaging of adenoviruses is extremely efficient and only complete genomes are packaged into fully assembled particles. All viruses used in this study have been purified by double CsCl gradient purification. This density gradient based purification protocol removes all particles that are either empty or damaged or would contain partial genomes.
o The RNA-Seq data in Fig 1 and Fig S2 and Table S1 demonstrates transcription of early genes is barely observable at 1hpi but is observable by 2hpi and is clearly much increased by 4hpi. Fig 2C, visualising pVII foci directly within single cells, suggests that approximately 80% of foci are observed by 1hpi and a further 20% between 1hpi and 2hpi and little thereafter. These data convincingly demonstrate that nuclear import is rapid, typically occurring in the first hour. The E1A RNA-Scope data in figure 2, visualising individual mRNA transcripts of E1A, is more sensitive than the bulk RNA-Seq, and shows transcripts at 1hpi with clearly discernible transcription by 2hpi (2A&D) which suggests that transcription occurs early, by 2hpi. Thus transcription lags nuclear genome import by approximately one hour by these methods. However, the conclusions of the subsequent analyses depend on the chromatin changes clearly preceding, rather than being approximately coincident with transcription, therefore transcription being evident by 2hpi is relevant as figure 6A and D suggest that the chromatin remodelling is subtle before 2hpi on the bulk sequencing analyses. The authors should comment on this given the importance to their argument.
As stated by the reviewer we observe a clear lag between nuclear import and transcriptional activation. And we do also observe the largest changes in nucleosome occupancy (ChIP-seq data) between 1 and 2 hpi (Fig6A and D). Compared to 0hpi, we observe the strongest increase of nucleosome occupancy between 1hpi and 2hpi (4-8fold effect), whereas depending on the area a 2-3fold increase in occupancy can be observed from 2hpi to 4hpi (Fig6D). An effect that one would expect with chromatin structure preceding gene activation. Furthermore, the timing of nucleosome assembly perfectly matches the increase of MNase accessibility at 1 hpi, supporting our conclusions.
o The validation of the E1A probe specificity in Fig 2B looks convincing, but there are no data presented for multiple cells to reassure that this image is representative. The equivalent figure for 2D for the Ad5-GFP control would address this.
We include a large field overview with multiple cells for virus and vector control as new supplemental figure S2B showing that the RNAscope detection of the E1A transcript is highly specific.
o Figure 2E is presented as a colocalization analysis but appears to be a ratio of mRNA foci to pVII foci per cell. If this is an incorrect interpretation then some clarification in the figure legend would be helpful. If this interpretation of these data is correct, then it is not truly a colocalization analysis, as a single genome may give rise to multiple transcripts and so a ratio We apologize that this figure was not clear. The data are based on real colocalizations and represent the number of pVII dots positive for E1A normalized with the total number of nuclear pVII. We have clarified the figure legend accordingly.
o The live cell imaging experiments are elegant and convincing, but the agreement in Fig 3D of the % colocalization in MS2-BP data with the RNA-scope data is potentially misleading for the reasons outlined in the prior comment. Is the data in Fig 2E the same as the data in the right hand panel of Fig 3D. If so please comment on the n discrepancy (n=30 in 2E vs n=22 in 3D). The observation that 20% of genomes are transcriptionally active, via bursting or otherwise, is interesting, and would be consistent with the Suomalainen et al reference. The authors discuss two hypotheses to explain these findings: transcriptional bursting or a subset ~20% of genomes being transcriptionally active. This is an interesting and begs the question as to why this may occur. Assuming all imported genomes are intact (previous comment), it appears from the presented images that the foci at the radial periphery of the nucleus may be more frequently transcriptionally active, despite the nuclear periphery being enriched for heterochromatin. The authors might consider analysing the radial position of their TAF1B-mCherry genomes (active and inactive) as this might support position effect variegation rather than bursting as an explanation and they appear to already have the data to perform such analyses.
o In the presented images (Fig 3A and Fig S3) it appears a higher proportion of genomes than 20% appear to be transcriptionally active, particularly in the low MOI experiment. The authors may wish to comment on this and quantify whether the proportion of transcribing genomes was affected by the input MOI.
This and the previous comment concerning the influence of MOI, transcriptional bursting and the positioning effect of the genome on the transcriptional activity have also been in part raised above. As stated in our response to reviewer 1 we have used a high MOI in our experiments to have equivalence between all experimental approaches. We agree with the reviewers that all aspects (dose, bursting and positioning) merit a detailed investigation, which we plan in future studies. To be consistent and comparable in our comprehensive approach we decided to not include such studies here as they would address a different question. Nevertheless, to address this (and the above) comments we now mention positioning effects in the results (line 214) and enlarged the discussion (line 587 ff) where we especially raised awareness that such pertinent questions can be addressed with the tools presented in our study.
We also decided to visually separate the comparison of MS2 and RNAscope data to avoid misleading the reader. Furthermore, the RNAscope data have been replaced. The RNAscope data are indeed from Fig. 2. The difference in n was due to our mistake showing two different normalized data sets. Data were either normalized using total amount of nuclear protein VII (Fig. 2E) or the total amount of nuclear E1A signals (Fig 3D), which due to the more heterogenous signal did not include all cells. In the updated version both figures display data normalized by total amount of nuclear protein VII
o Fig 4C suggests that there is a large GC preference (or bias) in the pVII occupied regions. The authors may wish to comment on this and present a track with Adenovirus GC composition in Fig 4D.
We thank the reviewer for raising this point. As suggested by the reviewer we analysed the GC content under pVII peaks and in the linker DNA. Indeed, pVII occupied regions have a significant higher GC content indicating that pVII preferentially positions at GC rich regions. We included this analysis as an additional Figure 4E (line 302 f).
Legend:
Boxplot showing GC content of pVII occupied (pVII) or free (linker) regions. Two biological replicates are shown side by side and the p-value of a students t-test of the corresponding pairs is indicated above.
o Figure 6 presents convincing data showing H3.3. nucleosome positioning and acetylation at E1A and the data is nicely presented showing these changes occur early being observable by 2 and 4 hpi. Again, these changes are not convincingly prior to early gene activation but are certainly occurring early, and may occur prior to early gene activation at the level of individual foci, however, this is not demonstrated definitively.
This question belongs to the same context addressed by the reviewer above. Please refer to the answer given above.
Minor comments:
Introduction: o Paragraph 1 - Introduction for DNA viruses in general, but the authors appear to be talking about Adenoviruses specifically, "little is known about the structural organization of the genome" and "nuclear viral genomes could undergo different parallel fates", arguably these statements are not accurate for other DNA viruses (e.g. Epstein Barr Virus) suggest amending the wording for clarity.
The manuscript text was updated as suggested.
o paragraph 2 - Why do the authors say that Adenoviruses are prototypic DNA viruses?
We removed the term prototypic.
o Paragraph 3 - A recent study is referenced but multiple references are given.
The references were updated
o "Protein VII stays associated with the viral genome imported to the nucleus, while pV dissociates from the viral DNA following ubiquitylation (Puntener et al., 2011). The fate of the μ-peptide is not known". - The reference suggests that pV dissociates on entry to the cytoplasm and during capsid disassembly at the nuclear pore. I find this sentence confusing as it doesn't make it clear that pV is lost before nuclear entry which is important for interpreting the data.
We clarified this in the manuscript text
Results:
o Figure 5 is almost unreadable due to low resolution.
We updated the Figures and checked the resolution after PDF conversion.
o Reference to Fig 4C in text comes after Fig4D.
The order of Figure panels was changed accordingly.
Reviewer #3 (Significance (Required)):
The manuscript is well written, uncovers important viral chromatin biology by combining multiple experimental techniques, and the data is generally very clearly presented
-
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Referee #3
Evidence, reproducibility and clarity
The manuscript "Adenoviral chromatin organization primes for early gene activation" combines RNA-seq, MNase-seq, ChIP-seq, and single genome and transcript imaging (immunofluorescence, RNA-scope, and live cell techniques) during early Adenovirus infection in vitro to characterise the spatiotemporal dynamics of viral chromatin organisation and association with gene transcription. The manuscript is an interesting read and the authors have combined multiple complimentary techniques to make a substantial contribution to understanding the early events occurring after nuclear import of viral genomes.
Adenoviruses are important causes of human and animal pathology, are a useful model of non-integrating extra-chromosomal DNA virus infection in mammalian cells, and are useful vectors for vaccination and the discoveries may influence gene therapy DNA vector design. The chromatin organisation in adenovirus infection is distinct from other DNA viruses, and is relatively poorly understood compared to, for example, SV40 or herpesviruses. The manuscript describes an early transition from purely viral chromatin with Adenovirus protein pVII packaging the virus in virions, to a viral-human hybrid chromatin pattern with apparently strategically positioned H3.3 nucleosomes and viral pVII "Adenosomes" in the early hours after nuclear import of the viral genome. The data shows that packaged Adenoviruses are in a transcriptionally accessible form and gene expression occurs rapidly after infection, the combination of the MNase-seq data with ChIP-seq data is particularly interesting demonstrating and average ~238 adenosomes positioned by specific DNA code protecting 60-70bp of DNA, and that the genome is accessible at loci that also decondense on infection, with adenosomes being replaced by cellular H3.3 containing nucleosomes at distinct sites. Particularly they show that +1 H3K27 acetylated nucleosomes are acquired at the TSS of key early genes.
The authors argue that their spatiotemporal data imply that this chromatin transition "primes" for early gene transcription. The manuscript is well written, uncovers important viral chromatin biology by combining multiple experimental techniques, and the data is generally very clearly presented. A few comments follow.
Major concerns:
- Abstract and Title:
- the abstract and title suggest that because the chromatin changes are observed coincidentally or before transcriptional changes, and that this means that these chromatin changes "prime" (title) or are "required" and play a "central role" (abstract) in early gene expression. The temporal relationship would be consistent with chromatin changes being required for transcriptional changes, but do not imply necessity. Experiments to demonstrate the necessity of these changes for early gene transcription are lacking, and I recommend amending the text or additional experiments to provide this evidence directly.
- Results:
- The IF data in Fig S1 is convincing, showing viral particles are accessible quickly in the nucleus. Although no statistics are provided for S1B and C, pVII foci appear at 0.5hpi and appear to mostly accumulate between 0.5hpi and 1hpi with further import between 1hpi and 4hpi. Can the authors be sure that a single pVII IF focus represents a single genome? If genomes tend to aggregate as they accumulate the number of foci per nucleus may not increase linearly with the number of genomes imported. Have the authors considered analysing the intensity of the individual pVII foci over the time points? A related question is whether the authors assume that all packaged virions contain intact complete viral genomes? Many viruses comprise some mixture of complete and incomplete packaged genomes, and the subsequent analyses determine the proportion of transcriptionally active copies with RNA-Scope to a single transcript E1A which lies at one end of the viral genome. Please comment explicitly on whether this is assumed and whether this assumption is realistic in light of known Adenovirus biology.
- The RNA-Seq data in Fig 1 and Fig S2 and Table S1 demonstrates transcription of early genes is barely observable at 1hpi but is observable by 2hpi and is clearly much increased by 4hpi. Fig 2C, visualising pVII foci directly within single cells, suggests that approximately 80% of foci are observed by 1hpi and a further 20% between 1hpi and 2hpi and little thereafter. These data convincingly demonstrate that nuclear import is rapid, typically occurring in the first hour. The E1A RNA-Scope data in figure 2, visualising individual mRNA transcripts of E1A, is more sensitive than the bulk RNA-Seq, and shows transcripts at 1hpi with clearly discernible transcription by 2hpi (2A&D) which suggests that transcription occurs early, by 2hpi. Thus transcription lags nuclear genome import by approximately one hour by these methods. However, the conclusions of the subsequent analyses depend on the chromatin changes clearly preceding, rather than being approximately coincident with transcription, therefore transcription being evident by 2hpi is relevant as figure 6A and D suggest that the chromatin remodelling is subtle before 2hpi on the bulk sequencing analyses. The authors should comment on this given the importance to their argument.
- The validation of the E1A probe specificity in Fig 2B looks convincing, but there are no data presented for multiple cells to reassure that this image is representative. The equivalent figure for 2D for the Ad5-GFP control would address this.
- Figure 2E is presented as a colocalization analysis but appears to be a ratio of mRNA foci to pVII foci per cell. If this is an incorrect interpretation then some clarification in the figure legend would be helpful. If this interpretation of these data is correct, then it is not truly a colocalization analysis, as a single genome may give rise to multiple transcripts and so a ratio <1 could be expected even if all pVII foci were transcribing genomes. In addition, the text suggests that because there is no statistically significant difference between 2hpi and 4hpi a plateau has been reached. However, the difference between 1h and 2h is barely significant (p=0.04) and the mean is increased between 2h and 4h, albeit non-significantly, so the plateau is not convincingly demonstrated. If the authors wish to perform a colocalization analysis rather than a ratio, they might assign each transcript to the nearest pVII IF focus within the nucleus and count the proportion of pVII foci with any transcripts assigned over time. Alternatively, they can amend the description of this analysis in the figure and text.
- The live cell imaging experiments are elegant and convincing, but the agreement in Fig 3D of the % colocalization in MS2-BP data with the RNA-scope data is potentially misleading for the reasons outlined in the prior comment. Is the data in Fig 2E the same as the data in the right hand panel of Fig 3D. If so please comment on the n discrepancy (n=30 in 2E vs n=22 in 3D). The observation that 20% of genomes are transcriptionally active, via bursting or otherwise, is interesting, and would be consistent with the Suomalainen et al reference. The authors discuss two hypotheses to explain these findings: transcriptional bursting or a subset ~20% of genomes being transcriptionally active. This is an interesting and begs the question as to why this may occur. Assuming all imported genomes are intact (previous comment), it appears from the presented images that the foci at the radial periphery of the nucleus may be more frequently transcriptionally active, despite the nuclear periphery being enriched for heterochromatin. The authors might consider analysing the radial position of their TAF1B-mCherry genomes (active and inactive) as this might support position effect variegation rather than bursting as an explanation and they appear to already have the data to perform such analyses.
- In the presented images (Fig 3A and Fig S3) it appears a higher proportion of genomes than 20% appear to be transcriptionally active, particularly in the low MOI experiment. The authors may wish to comment on this and quantify whether the proportion of transcribing genomes was affected by the input MOI.
- Fig 4C suggests that there is a large GC preference (or bias) in the pVII occupied regions. The authors may wish to comment on this and present a track with Adenovirus GC composition in Fig 4D.
- Figure 6 presents convincing data showing H3.3. nucleosome positioning and acetylation at E1A and the data is nicely presented showing these changes occur early being observable by 2 and 4 hpi. Again, these changes are not convincingly prior to early gene activation but are certainly occurring early, and may occur prior to early gene activation at the level of individual foci, however, this is not demonstrated definitively.
Minor comments:
- Introduction:
- Paragraph 1 - Introduction for DNA viruses in general, but the authors appear to be talking about Adenoviruses specifically, "little is known about the structural organization of the genome" and "nuclear viral genomes could undergo different parallel fates", arguably these statements are not accurate for other DNA viruses (e.g. Epstein Barr Virus) suggest amending the wording for clarity.
- paragraph 2 - Why do the authors say that Adenoviruses are prototypic DNA viruses?
- Paragraph 3 - A recent study is referenced but multiple references are given.
- "Protein VII stays associated with the viral genome imported to the nucleus, while pV dissociates from the viral DNA following ubiquitylation (Puntener et al., 2011). The fate of the μ-peptide is not known". - The reference suggests that pV dissociates on entry to the cytoplasm and during capsid disassembly at the nuclear pore. I find this sentence confusing as it doesn't make it clear that pV is lost before nuclear entry which is important for interpreting the data.
- Results:
- Figure 5 is almost unreadable due to low resolution.
- Reference to Fig 4C in text comes after Fig4D.
Significance
The manuscript is well written, uncovers important viral chromatin biology by combining multiple experimental techniques, and the data is generally very clearly presented
- Abstract and Title:
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Referee #2
Evidence, reproducibility and clarity
The submitted manuscript presents a detailed and comprehensive analysis of the adenoviral nucleoprotein complexes as infection progresses, starting with the "adenosome" assembled with pVII which are then progressively replaced with H3.3.-containing nucleosomes as the infection progresses. The submission presents a combination of in situ and populational analyses of the viral DNA accessibility and complexes through infection. I brief, the infecting viral genomes are assembled in some 250 adenosomes with pVII, which become progressively replaced as infection progresses with nucleosomes containing H3.3 and acetylated H3K17, starting at the active promoters of the E genes. Chromatin remodeling precedes transcription, and the accessibility differs for genes of different kinetic classes at differ times after infection, although there is no correlation between accessibility and H3.3. or acetylation content. Only about 20% of the genomes become transcriptionally active, though, which somewhat complicates the analyses of the populational studies of accessibility and occupancy. Overall, the study is well conceived, performed and presented. A few issues that deserve further analyses and discussion, as described below.
Major issues.
As figure 2 nicely shows, only about 20% of the intranuclear genomes become transcriptionally active. However, MNase and ChIP analyses cannot differentiate these genomes from the 80% that are transcriptionally inactive. The interpretation of the positioning of pVII (figure 4) or the changes in compaction of the adenoviral chromatin at different loci (figure 5) does not appear to consider this heterogeneity other than for a brief comment about the stringent MNase digestion in page 11. The authors favor a model in which the changes in compaction shown in figure 5, at mild MNase digestions, directly correlate with transcription of the respective genes. This could well be correct, and in fact the correlation may be underestimated as 80% of the genomes may not undergo any changes, but it may also be incorrect. The analyses presented cannot differentiate whether the changes in chromatin compaction occur in only a subset of genomes or in all the genomes, regardless of whether they are transcribed or not, or even only in the non-transcribed genomes (which appears extremely unlikely). This intrinsic limitation to the methods used (and I know of no better alternative) should be acknowledged and discussed for the benefit of the reader. This limitation also impacts the analyses of the lack of correlation between H3.3 and acetylated H3K27 occupancy and compaction.
Perhaps out of necessity to reach the required sensitivity, a high multiplicity of infection was used (although the actual moi is not stated, there are about 25-30 pVII foci/ per nuclei). The presentation, analyses and discussion of the results should emphasize this context. For example, one would presume that at low moi, when only one genome enters each cell, the percentage of transcriptionally active genomes in a given cell will be either 0 or 100%, but the "system" becomes saturated as more and more genomes enter the nucleus at higher moi resulting in only a subset of them being transcriptionally active. Along this line of reasoning, it is intriguing that the percentage of genomes estimated to be in nucleosomes at 4 hpi (14%) approaches the percentage of transcribed genomes.
The changes in chromatin compaction presented in figure 5 are in some respect puzzling. The compaction of most of the late genes increases as infection progresses, at least for the first four hours, as the authors discuss. However, the L genes appear to be at least as accessible as the E ones at the early times, when only the E are transcribed to high levels. This appears counterintuitive, and may not be consistent with the main conclusion that increase accessibility to a given gen directly correlates to its transcriptional activity level. The data presented in Figure 5C deserves a more nuanced analysis and discussion, parsing out the changes in accessibility to each given gene at different times from the different accessibility to the different genes at any given time. The later does not appear to support the main conclusion reached by the authors that accessibility to each individual gen correlates with its transcriptional level.
Minor comments
The authors may wish to highlight in the discussion that the analyses are so far limited to a single adenovirus.
The y-axes in the transcriptome figures (figure 1 B, S2) could be presented in Log(2) scale, such that transcript levels at all times can be appreciated in the same graph (the earlier times are just not visible in a linear scale)
The (lack of) phenotype of the 24xMS2 binding site recombinant adenovirus used should be shown.
The kymograph analyses presented in figure 3B appear to show that there are some sites of transcript accumulation sites which do not harbor viral genomes (i.e., green only tracks). Moreover, the interpretation of the TAF1beta-mCherry signal is complicated by the (fully expected) significant "background" signal. Although these results are consistent with those obtained by RNAscope/pVII staining, there appears to be intrinsic limitations to the system, which preclude reaching strong conclusions from it. These confirmatory analyses should probably be moved to the supplementary information section and removed from the main text and figures. The longer evaluation data mentioned as not shown in page 8 is critical to the conclusions and should be shown.
Although the plot of cleavage frequency presented in figure S5 is clear, it would be beneficial to the reader if the actual peaks were also presented to compare their distribution (if any) in gDNA and virus particle.
The mRNA analyses of selected transcription factors provides little information, as there is no context, there is variability between experiments, and in most cases the changes appear modest. As these results are not critical to the conclusions or analyses, perhaps the authors may wish to remove them from the manuscript. Alternatively, more in-depth analyses would be required.
It is unclear why the even distribution of H3.1-flag signal across the genome is considered indicative of no specific recruitment. The results presented are equally consistent with equal incorporation across the genome. Perhaps the authors have some additional information, such as an irrelevant antibody, input DNA, or the like, to support the conclusion. If so, that evidence should be presented and discussed. If not, the interpretation should be revisited. As an added complexity, endogenous H3.1 is normally expressed during S-phase. It is possible that Adenovirus infection may induce higher levels of expression of (untagged)endogenous H3.1, which would outcompete the tagged ectopically expressed histone. These analyses deserve a more nuanced and in-depth analysis.
It is highly unlikely that the somewhat higher H3K27ac signal observed in the H3.3 than in the H3.1 expressing cells may result from higher H3.3. occupancy in the viral genome as speculated in page 13. The total levels of H3.3. are unlikely to increase by the ectopically expressed one, and even if they did it is not likely that the occupancy of the viral genome would be limited by the levels of H3.3. This speculation should be removed.
Materials and methods are too concise. A longer more detailed version, as supplementary information, would be highly desirable.
Significance
The major strengths of this manuscript lie on its comprehensiveness, using several in situ and populational approaches to address biologically critical questions regarding the regulation of viral replication by chromatin and epigenetics. Experiments appears very well designed and performed and are mostly clearly presented. The interpretation analyses and discussion of the results may benefit from a more nuanced analysis of the issues posed by the existence of different populations of viral genomes in the cells infected at high moi and the accessibility across different genes at any given time versus the levels of transcription of the different genes, which appears not to be fully consistent with one of the main conclusions reached.
This study makes a very significant contribution, describing the dynamic changes in the adenoviral nucleoprotein complexes at the early times of infection and providing a full description of both the adenosomes and the nucleosomes in more and less transcribed loci. The results are properly analyzed in context of what is known about the regulation of viral gene transcription by chromatin dynamics in other systems, including similarities and differences. This study is likely to be of high interest to a wide audience, ranging from virologist to epigeneticists, to those working in gene therapy and vectored vaccines.
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Referee #1
Evidence, reproducibility and clarity
The authors have addressed the nucleoprotein structure of human adenovirus during the very early stages of infection, and its relationship to onset of expression of viral genes, using a combination of RNA-seq, MNase-seq, ChIP-seq and single genome imaging. They show that in the virion and the newly-infecting DNA, protein VII is precisely position at specific sites on the viral DNA, with greater accessibility at early gene promoters compared to other regions. Nucleosomes containing H3.3 replace specific protein VII at distinct positions at the transcription start sites of genes, which are then acetylated. Association with histones and nucleosomes occurs prior to transcription. These studies confirm and greatly expand on results already in the literature, and also elucidate a novel role for protein VII in orchestrating positioning of nucleosomes prior to initiation of transcription.
The authors provide excellent data in support of their conclusions and, in many instances, use alternative experiments (i.e. two different approaches) to support their claims. The details of methods are adequate (with small exceptions outlined below) and statistical methods appropriate.
Minor comments:
- Line 561 "Protein VII molecules were exchanged for positioned nucleosomes at the +1 site of actively transcribed genes". This statement seems to suggest that the +1 position almost acts as a nucleating site, where replacement of a single, specific protein VII molecule at +1 is an initiating event, which then spreads from that site and into the rest of the gene. Data shown in Figure 6G and 6H shows that H3.3 appears to be found equally along the full length of E1A as early as 1 hr post infection (with no real "enhancement" at the +1 position), and that the overall levels simply increase over the next 4 hrs.
- Curiously, the authors chose not to use a wildtype virus for their studies - the virus contains a deletion in the E3 region. For clarity, I suggest that the authors should preferentially use an alternative designation for their virus rather than HAd-C5. Perhaps HAd-C5delE3 to differentiate this work from studies that truly use wildtype virus.
- The obvious limitation of the studies using the fluorescent TAF1-beta to label Ad genomes is that as protein VII is replaced by nucleosomes, the genomes would have declining detection by this method. Genomes devoid of protein VII would be "invisible".
- Line 275 "Interestingly, a central region of the viral genome (Late3) and a region between the E3 and E4 genes exhibited almost no peaks" for protein VII. The virus utilized in this study lacked at least part of the E3 region. Did this deletion "cause" this region to be devoid of protein VII? Is the same absence of protein VII peaks observed in a fully wildtype virus? Also, can the authors provide any speculation as to why the Late3 region also lacks protein VII?
- Line 569 "Reasons could be that the few genomes undergoing nucleosome assembly and active transcription produce the replication enzymes, whereas the bulk of genomes enters replication without activation as an elegant way to avoid repeated chromatinization." This argument may make sense in the context of a high MOI infection, but would certainly limit virus function during normal, pathogenic infection where the MOI is likely extremely low. Essentially, the authors data predicts that 80% of normal, low MOI infections don't progress to gene expression (at least during the first 4 hrs analyzed in this study).
- Line 576 "This observation is in agreement with recent pVII-ChIP experiments showing transcription and replication independent pVII removal in early infection (Giberson et al., 2018; Komatsu and Nagata, 2012; Komatsu et al., 2011)." The authors can also state that histone and nucleosome deposition is also independent of transcription and replication, as has been alluded to in the same cited studies but proven more directly in this study.
- Line 672 - the authors should be more definitive in the MOI that are used in all of their experiments. Line 672 states that an MOI of 3000 physical particles are applied per cell. There can be great variation between cell lines in how much virus binds to (and enters) a cell based on the surface levels of Ad receptors on different cell types. However, in general, 3000 is very high. Work by Wang et al. (PMID:24139403) showed that at an MOI of 200 or below most Ad will traffic correctly to the nucleus, whereas at an MOI above 200 there is a significant defect in Ad trafficking within the cell. How is this expected to affect all of the results in this study?
- Figure 5 is of low resolution and was difficult to read.
- Figure S3 is missing a box from the top set of images indicating the region that is expanded in the detail picture.
- While I realize it is supplemental data, the difference in quality between the agarose gels shown in Figure S4A and S5A is shocking.
- Figure S7 is of low resolution.
Significance
At least in the field of adenovirus research, this is a very important study. There has been considerable debate in the field regarding the timing and degree of protein VII removal and histone deposition, and the necessity of active transcription for these two events. The data provided in this manuscript clearly shows that some protein VII is removed from early active genes and replaced by nucleosomes, and that these events occur prior to initiation of transcription.
The authors speculate that the specific placement of protein VII, a protamine-like protein, on the Ad genome prescribes where nucleosomes are placed. This finding should be of interest to a broad general audience, as it provides novel information on chromatin assembly within mammalian cell.
Key words for this reviewer: adenovirus research, HAdV nucleoprotein structure
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Reply to the reviewers
*Summary: This paper illustrates the role of GDF15 in ganglionic eminence featuring the influence on neurogenesis and progenitor proliferation. Using the conventional knockout GDF-15 mouse lines, the authors provide a series of counting data indicating that GDF15 controls neurogenesis in the late embryonic or adult neural stem cells in the ventral forebrain. *
We would like to thank the reviewer to reading our manuscript and providing comments. As the reviewer highlights, we have used a conventional GDF15 knock-in knock-out model since the growth factor is expressed not only at tissue levels but also at a systemic level. Therefore, targeted ablation of GDF15 would be complicated and the results difficult to interpret. Moreover, GDF15 and its receptor GFRAL in normal conditions are expressed at very low levels in adult mice and mutant mice do not display any obvious developmental phenotype. However, GDF15 is characteristically expressed during development and our previous data have shown that its expression is particularly increased at later developmental ages and particularly in neural precursors, which are both the focus of our analysis. Although these previous analyses have long highlighted that GDF15 is particularly expressed in the V-SVZ and in the choroid plexus, its physiological role in this system remains to the best of our knowledge unknown. It is important to investigate this issue because, as we mention below, GDF15 expression is increased, including in NSCs, upon brain injury and aging. As the reviewer rightly mentions, using this conventional approach and straightforward quantitative analyses, instruments available and normally used for the investigation of biological phenomena, we have discovered that GDF15 directly affects the number of ependymal cells and neural stem cells thereby providing a first function for the expression of the growth factor in this region.
Major comments:
The entire story in this manuscript seems similar to the previous findings where the authors demonstrated the role of GDF15 in the hippocampal neural stem cells in relation to EGF and CXCR4.
As the reviewer rightly mentions we have in a previous paper investigated the effect of GDF15 on the stem cells of the hippocampus. However, we would like respectfully to disagree with the reviewer that our current manuscript describes similar findings. Whereas we have previously shown that the effect of GDF15 in hippocampal stem cells and neurogenesis is a transient inhibition of proliferation due to reduced EGFR expression, we here found that absence of GDF15 leads instead to increased proliferation and a permanent increase of stem cell number, besides of ependymal cells. As the reviewer rightly mentions, on the basis of our previous observations, also in this study we have analyzed EGFR expression and signalling. However, although our data clearly show that EGFR expression and more importantly signalling are altered also in this niche, we could show that the effect of GDF15 is more complex than altering EGFR signalling. Since we show for the first time in this study, that besides GDF15, neural progenitors also express GFRAL, our data point at a selective effect of GDF15 in the development of neural stem cell in the GE and in the deriving adult niche, which include change in EGFR signalling.
*The data and the conclusion presented here sound reasonable to me. The current manuscript, however, gave me the impression that the story is less impactful and rather descriptive. To improve the quality of the current draft, the authors may wish to clearly highlight the novelty of the findings, not simply apply the previous strategy to the other anatomical brain regions. Alternatively, the draft could emphasize the similarity of utilising the same biological strategies to control the number of adult stem cells in the distinct stem cell niche. *
We would like to thank again the reviewer for the positive consideration of our quantitative analyses, although we cannot agree with the referee’s conclusion about the impact of our current study. In particular, we would like to focus here not only on the specific findings of the two studies that, as we mentioned above, reach different conclusions, but also on the general meaning of our new study in the context of understanding the role of GDF15. Besides during development and aging, GDF15 expression is promptly upregulated in several pathologies including, cancer, injury and neurodegeneration. Indeed, a growing body of evidence has highlighted the possible role of GDF15 as stress hormone and mitokine, which could be part of a conserved mechanism of the body to signal and respond to stress. Within this context, it would be very important to understand the effect of GDF15 on stem cells, as it may prompt not only understanding of the physiological role of GDF15 but also of the mechanism underlying the response and contribution of stem cell to stress and injury. Supporting this view, it was recently shown that GDF15 is upregulated in quiescent neural stem cells following brain injury (Llorens-Bobadilla et al., 2015). However, the main problem in investigating the physiological role of GDF15 is that the expression of its recently discovered receptor is very limited in the brain. Therefore, our data here are important not only because of the novel effect that they describe for GDF15 in NSC development, but also because they show that GDF15 directly affects stem cell behavior. We have now followed the suggestion of the reviewer and re-edited several parts of the manuscript including editorial changes to highlight the relevance of our findings and the figures to better illustrate them. In particular, we have added also additional analyses to support our conclusions. These include data illustrated in Fig.1B, C; Fig. 4B, G and Fig. 5G.
*I also have two concerns which may help to improve the current draft. Firstly, I would suggest considering the data presentation as many of the counting data are not accompanied by representative images or a detailed description of the methods, which could impede the credibility of the data. For instance, it is not clear to me how the authors judged the apical vs subapical progenitor counting as neither the pictures nor the methods clearly specified how these are distinguished. Same to the Figures 3 and 8. *
We thank the reviewer for these suggestions, which we have now implemented in our revised manuscript. These changes include addition of representative images to Figs. 1, 2, 3, 4, 5, 6, as well as an illustration of how apical vs subapical cells were counted in Fig. 2A, an illustration showing how ependymal and single-ciliated cells were determined in Fig. 8A, and more detailed descriptions in the materials and methods section.
*I would also suggest the authors may wish to carefully review the text as many abbreviations are not properly stated (for example, what are P+ progenitors?), or not properly explained why the particular gene expression is analysed (EGF, Sox2, CXCR4). This is also applied to the anatomical jargon (like apical, subapical etc), which can be specified in the figure by introducing the cartoons or point-on images. *
We thank the reviewer for pointing these shortcomings out. We have now done a careful proofreading of the text and implemented changes in the relative figures.
The changes include: Explanation of Prominin-1-expressing (P+) progenitors (p. 10, line 35) and apical and subapical progenitors (p.3, line 11-23), as well as more detailed reasoning for the analysis of gene expression for EGFR, Sox2 and CXCR4 (p. 9, line 5-7; p.12, line 44 and following)
*Last not least, I should point out that the author uses less commonly used terminology. To my knowledge, the SVZ progenitors in the GE are now called basal progenitors (Bandler et al 2017 for example) and the word intermediate progenitors is used for the Tbr2+ IP cells in the developing cortex. MASH-1 is an old gene name as it is revised as Ascl1 (please refer to any recent papers and web databases such as Mouse Genome Informatics, and NCBI, for instance). The use of prevailed wording will help the readers to understand the presented story. *
We have now revised the terminology according to the reviewer’s suggestion.
Minor comments:
Abstract Line 12-15 is confusing: What does "genotype" means?
We used the term to refer to the genetic differences between WT and GDF15 mutant mice with respect to GDF15 expression. We apologize for the lack of clarity. We have now modified the paragraph in an effort to improve its clarity.
Introduction Despite the focus of this paper being on the proliferation in GE, the introduction mixed up the references describing the dorsal telencephalon. It's better to cite the ventral GE as some progenitor behaviours are different from the ones in the dorsal. Maybe it's better to dedicate more to describing the lineage trajectory in the ventral GE and the molecular players (such as EGF), which makes it harder to understand the rationales of the several experiments.
We would like to thank the reviewer for making this helpful comment. In the introduction we have tried to make two points: firstly, to clarify how the different progenitor types in the VZ can be distinguished based on the localization of their site of mitosis and secondly the importance of studying GDF15 in the context of NSCs in the subependymal zone of the lateral ventricle. For the first point we have several studies referring to dividing dynamics of radial glia in the developing cortex. This reflect the fact that many papers have studied both apical and subapical radial glia within the context of the developing cortex, unlike subapical progenitors, which were first discovered in the developing ganglionic eminence. A similar problem applies to the analysis of EGFR expression in the context of VZ progenitors, although we agree with the reviewer that it should introduced for a better understanding of our analyses. Therefore, we have now introduced several changes in our introduction to eliminate the shortcomings and to offset the imbalance in terms of citations.
Results
Fig1: V/SVZ -> VZ? I think V means ventricles while VZ is for the ventricular zone. Single-channel images should be presented to demonstrate the positive or negative cells for each antigen. Only a subset of progenitors in the adult SVZ is GDF15 positive although this is not described in the text.
We have now replaced V/SVZ with V-SVZ, meaning ventricular-subventricular zone, throughout the manuscript and added single channel images to all figures where it is relevant.
*Why the GDP15 staining was performed only in the adult sections, but not in E18 while the GFRAL is shown in both stages? The text claims "GDF15 is particularly expressed in the germinal region of the GE" but I did not find the data shown in this draft. *
The fact that GDF15 is expressed in the choroid plexus and in the subependymal region of the lateral ventricle was first observed in the neonatal rat brain and prompted us to investigate the hypothesis that GDF15 may affect NSCs. Moreover, in our previous manuscript we have confirmed that GDF15 is expressed in neural progenitors of the embryonic murine GE (Carrillo-Garcia et al., 2014). In this new manuscript, we have complemented these data by adding the missing information concerning the expression of the protein in the adult V-SVZ. Notably, we also investigate for the first time the expression of the receptor in this area. This is key issue in the field, since the expression of GFRAL has been reported only in few regions of the brain, which is in apparent contrast with the growing list of effects in which GDF15 has been involved. For completeness of information and to further strengthen our conclusions we have now added new set of images in figure 1B, C showing co-expression of GFRAL and EGFR.
*Line 24-25: I did not understand this statement. *
The sentence refers to the results published in our previous paper, as mentioned in our reply above, which illustrate expression of GDF15 in the GE at different ages of development and in the adult V-SVZ. In an effort to improve its clarity, we have now modified the sentence into: “Consistent with these observations, we have previously reported that in the GE, Gdf15 transcripts increase at late developmental age and remain high in the adult V-SVZ.”
Fig. 2 Line 33: what are apical P+ progenitors?
We apologize for this shortcoming. P+ is the abbreviation for Prominin-1 immunopositive progenitors. This information has been now added to the text.
*Fig. 2A: The total analysed cells are not described in M&M. *
We have now added this information in the relevant section of the manuscript (p. 7, lines 36-43).
*Fig 2 C and D. While the counting of apical or subapical progenitors has been done respectively, the representative images of which regions are judged as apical or subapical are not shown. This comment also applies to Line 41: I did not get the logic of how this analysis will be able to distinguish apical or subapical cell division. *
Mitotic apical and subapical progenitors have been detected on the basis of the position of their nuclei. Namely, mitosis was considered apical if the nucleus of the dividing cell was within two nuclei distance (~ 10 µm) of the apical surface, and considered subapical if the nuclei of the dividing cells was at a greater distance from the apical surface. Besides adding this information to the manuscript, see “Image analysis” in the “Materials and Methods” section, we have now illustrated our approach in the new Fig. 2B.
*Fig. 2 E and F: I am not sure why the proliferation was assessed in vitro whole mount cultures. IP injection in vivo animals would be more convincing. *
We have used the same whole mount preparation to determine changes in proliferation upon acute fixation of the tissue. We have then determined the effect of growth factors and pharmacological modulators in whole-mount explants preparation as this would allow us to test their effect in standardized conditions. For the sake of consistency, we have then used the same whole mount explant setting to investigate proliferation by means of IdU incorporation. We selected this mean of analysis because changes in proliferation were already detected upon tissue fixation, and direct exposure of the tissue to the pharmacological modulators allowed us to investigate the direct effect of the drugs on proliferation behavior. Using this setting, we have obtained data that are compatible and consistent with our analysis on acutely fixed preparations. We agree with the reviewer that these experiments could be also repeated by injecting the IdU in vivo, however this would be against the current animal 3R guidelines that prompt to minimize the use of animal in vivo experiments and only when they cannot be replaced by alternative approaches in vitro or ex vivo.
*Fig. 3 I am not sure the mitotic spindle orientation analysis is very informative to stand out as one independent figure. In some contexts (Noctor et al 2008), it does not correlate to the asymmetric or symmetric division modes. *
We would like to like to respectfully disagree on this issue. The reason why we think this data set is important is twofold. Firstly, previous papers pointing at changes in the number of NSCs in the GE, have established that this was caused by a change in the spindle orientation leading to the generation of extra SNP (Falk et al., 2017), indicating a role for the orientation of the mitotic spindle in this context. Since we observed that GDF15 promotes not only progenitor proliferation but also apical divisions, it is important to show that this effect does not reflect a change in spindle orientation. Secondly, these data set highlights an age-dependent effect on the orientation of the mitotic spindle that is fully consistent with previously published data supporting the solidity of our findings. However, since we did not see any significant differences between the WT and Gdf15-/- animals, we have decided to move this data to a supplementary figure (new supplementary figure S3).
*Fig. 4 I am not convinced by this data since how the fluorescent intensity is measured is not described. If the internal controls to adjust the staining variation among samples are not used, the data is not convincing to me. The representative pictures are not convincing either to claim the substantial differences. Perhaps immunoblotting is better to be employed to quantify the protein expression difference. *
We have now added additional pictures with higher magnification to show the difference in EGFR intensity, including a calibration bar (Fig. 4). Quantitative analysis showed a trend decrease at E18 which is strongly significant in the adult V-SVZ. We now also show analysis of phEGFR and modified extensively the relative result section (see also our reply to the comment on Evidence, reproducibility and clarity of reviewer 2). Furthermore, we have added the following paragraph to the methods section:
“For fluorescence intensity measurements of EGFR, slices stained at the same time with the same antibody solutions, and imaged on the same day with constant confocal microscope settings (laser intensity, gain, pixel dwell time), were measured using Fiji/ImageJ. Raw immunofluorescence intensity was normalized by subtracting background fluorescence levels, i.e. fluorescence in cells considered negative for EGFR. To rule out any unspecific secondary antibody binding, fluorescence was compared to slices incubated with secondary, but not primary antibodies (2nd only control); no difference was found between 2nd only control and cells considered negative in EGFR-labelled samples, or between 2nd only controls of different genotypes.”
*Fig. 5 This is very busy figure composed of mainly counting graphs of different experiments. I think at least it is better to separate the data in vivo or culture. *
We have now rearranged the figure according to the reviewer’s suggestion. We have moved, also according to Reviewer 2’s suggestions, some less relevant data to supplementary figure S4 (that is, previous panels G-J) and added confocal images to illustrate the results of previous panels C-E. We hope that this improved the focus and clarity of this figure.
*Fig. 6. Pictures of Day 2 and Day 7 should be presented to highlight the difference between them. *
We have now added pictures showing the cell culture at DIV2 and DIV7, as well as the different treatments, in Fig. 6A.
*Fig. 7 Mash-1 should be rephrased as Ascl1. *
We have now changed the name of the gene throughout the manuscript.
Fig. 8 A: I am not sure why these pictures are B&W even though the two antigens are stained. The main text needs more description since no explanation of FOP, b-catenin etc. The picture of GFD15 KO looks having massive numbers of FOP+ cells, which is not correlated to the counting, I guess?
We apologize for the lack of clarity. We have now added additional panels (Fig. 8A) to illustrate the rationale behind the analysis and to demonstrate how ependymal and single-ciliated cells were counted. We have added the following sections to the manuscript text:
Materials and methods:
“Both the β-catenin and fibroblast growth factor receptor 1 oncogene partner (FOP) primary antibodies are mouse monoclonal antibodies of the same immunoglobulin class. Therefore, for this double immunostaining both antigens were revealed using the same secondary antibody and each was distinguished based on the localization and morphology of the labelling, which is lining the cell boundaries or at the basal body of the cilia for β-catenin and FOP, respectively.”
Results:
“We here used β-catenin to label cell-cell contacts, thereby visualizing cell boundaries, and fibroblast growth factor receptor 1 oncogene partner (FOP), a centrosomal protein, to visualize the basal body of the cilia. As both β-catenin and FOP-antibodies where derived from the same host species, the antigens were labelled in a single fluorescent channel and differentiated based on label localisation and intensity (Fig. 8A). Cells with a single centrosome or centrosome pair (one to two FOP+ dots) were counted as single-ciliated (SC), whereas cells with more than two centrosomes, i.e. multiciliated cells, were counted as ependymal (Epen; Fig. 8A).”
We have also added the following paragraph to the figure legend:
“(A) Schematic showing counting of ependymal (Epen) and single-ciliated (SC) cells using FOP and β-catenin as markers. (a’) Closeup of WT image in (B), showing β-catenin, indicating cell-cell-contacts, and FOP, indicating ciliary basal bodies/centrosomes, in a single channel. Scale bar = 10 µm. (a’’) β-catenin and FOP labels are distinguished by location, morphology and label intensity, with FOP being single dots that are more intense than β-catenin and located within the cell boundaries. (a’’’) Cells containing one or two centrosomes were considered SC cells (red), while cells with more than two centrosomes were considered multiciliated and therefore Epen (blue).”
We would also like to point out to the reviewer that since FOP was used as a label for the ciliary base, the “massive numbers of FOP+ cells” (i.e., multiciliated cells) were indeed quantified in Fig. 8B (now 8C) as ependymal cells (Epen).
** Referees cross-commenting**
I agree with Reviewer #2's comment that despite the amount of data presented, they are not presented in a coherent manner. I would suggest revising carefully before submitting to any journals. As detailed above the manuscript has been revised to improve clarity and coherence according the reviewer’s suggestions.
Reviewer #1 (Significance (Required)):
*The presented finding of the role of GDF15 in the ventral progenitors are evident and a new finding has not been reported. Since the same effects and signalling pathways involved in adult hippocampus neurogenesis are previously published by the same authors, the impact of the current manuscript is limited. I think heightening the role of GDF15 in the biological context of ventral progenitors, or alternatively, making a comparison to the previous finding would greatly improve the quality of the draft. In my opinion, this work would be appealing to the community of neural stem cells but maybe not to the broad audience. My expertise is neurodevelopmental biology focusing on neuronal lineages and neurogenesis. *
We have already clarified that the effect that we report here of GDF15 on NSCs is not only novel, but is also very different from what we have previously observed in the hippocampus (see also our reply above to the comment on evidence, reproducibility and clarity of reviewer 1). Although many environmental signals and growth factors have been implicated in the regulation of NSC proliferation and self-renewal, GDF15 is, to our knowledge, one of the few factors directly regulating the number of apical NSCs. Following the suggestion of the reviewer, we have now revised our manuscript in order to highlight the difference between the two studies. Besides being important within the field of NSCs, we believe that our data are also important for understanding the physiological role of GDF15, whose expression is increased during development and in the response to a growing list of stressors. For such an understanding, it is essential to identify target cell populations which can directly respond to the growth factor. Our finding that the GDF15 receptor is expressed in NSCs provide first evidence that GDF15 can directly modulate stem cell development, providing a first function for the increase in its expression. Moreover, our observation that GFRAL continues to be expressed in adult NSCs opens up to the possibility that the increase in the expression of the growth factor in the stress response is to recruit/modulate stem cell behavior. Consistent with this scenario, it was recently observed that brain injury promoted and increase of GDF15 expression in NSCs (Llorens-Bobadilla et al., 2015).
- Reviewer #2 (Evidence, reproducibility and clarity (Required)): *
* Here the authors explore the role of GDF15 during development of the adult neural stem cell niche at the lateral wall of the lateral ventricle using GDF15 knock-out mice. They find increased progenitor proliferation at neonatal stages and at 8weeks, compensated by neuronal death. Further they report that EGFR+ cells are arranged differently in the GDF15 mutants (in clusters rather than columns) with also lower levels of EGFR. This is surprising to me, as the authors observe an increase in proliferation. They then report that addition of EGF leads to an increase in prominin+ progenitors in the GDF15KO, but not the WT, but there is lower levels of EGFR in the KOs. They then block CXCR4, which is allegedly required for GDF15 to modulate EGFR expression, and they find that this blocking reduces proliferation mostly in WT cells. As can be seen from this summary, to me, the model of how GDF15 loss is supposed to increase proliferation is not clear. Even less so, when in adult SVZ, EGFR+ progenitors were increased, while EGFR was reduced at postnatal stages. Beyond this, the authors show convincingly that ependymal cells are increased at adult stages, while I see no data supporting their claim of NSCs to be increased (at least not reaching levels of significance).*
- Taken together, this manuscript contains a lot of data, but to me no coherent picture emerges. If the picture is that the higher proliferation rate of apical progenitors at E18 generates more ependymal cells, then this should be shown (by including analysis e.g. at P5 when ependymal cells emerge). How GDF15 would affect proliferation in general is also not clear to me - maybe an unbiased analysis by RNA-seq could help to separate the main effects from diving into known candidates that seem not to explain the main aspects.*
The reviewer mentions multiple aspects of our study that we would like to clarify. Therefore, we apologize for our lengthy reply.
Firstly, the apparent contradiction between the increase in progenitor proliferation despite the concomitant decrease in EGFR levels. It is long known activation of EGFR regulates multiple aspects of progenitor behavior including proliferation, migration and differentiation. It is also known that responsiveness of NSCs to EGF increases during development, a process that is paralleled by an increase in expression of EGFR expression increase with developmental age, peaking around the perinatal age. However, since NSCs start to slow their cell cycle and enter quiescence exactly at the same time in which the increase in responsiveness to EGF and in EGFR expression in NSCs during this same period, it is clear that there is not a linear correlation between NSC proliferation and EGFR expression. A possible explanation for this apparently counterintuitive observation is that the increase in EGFR expression is paralleled by an increase in the expression of Lrig1, a developmental negative regulator of EGFR (Jeong et al., 2020). Moreover, in our study we report that lack of GDF15 leads to a decrease in the expression of EGFR protein and not in the levels of EGFR mRNA. In light of the well-known feedback mechanism by which in the presence of high EGFR activation the receptor transits to late endosome for degradation, a decrease in the protein levels could actually represent a higher level of activation EGFR signalling in the mutant progenitors than in the wild type counterpart. This is consistent with the characteristics of punctuate EGFR immunostaining we see in the mutant tissue and our analysis of EGFR activation. Our data show that despite difference in activation kinetics, wild type and mutant progenitors similarly respond to exogenous stimulation with EGF. Moreover, there is no difference between the two genotypes in the expression of EGFR in mitotic cells, and blockade of EGFR more dramatically affects the proliferation of mutant than WT progenitors. Finally, exposure to exogenous EGF promotes the proliferation of WT but not mutant progenitors. Taken together, these observations suggest that endogenous activation of EGFR driving proliferation is higher in mutant than WT progenitors. Consistent with this hypothesis, our new data illustrated in Fig. 5A-G of the revised manuscript, show that EGFR is similarly phosphorylated in mutant and in WT progenitors and that levels of Phospho-EGFR are observed in regions with low levels of EGFR expression, especially in the postnatal V-SVZ.
With respect to the effect of CXCR4, we have investigated its effect with respect to the ability of GDF15 to promote EGFR expression at the cell surface and secondly with respect to affect proliferation in vivo and in vitro. Both experiments reveal a permissive role of the receptor, whose activity is necessary for GDF15 to promote EGFR expression at the cell surface and for cell to undergo proliferation. While these observations confirm in part our previously published data, the molecular mechanisms underlying these effects remain unclear. However, since AMD on its own does not affect EGFR expression in either WT or mutant progenitors, the two effects are not related. Despite the absence of a clear mechanism by which CXCR4 affects proliferation, our data indicate that the permissive effect of CXCR4 is more important for the proliferation of TAPs rather than for NSCs. Therefore, the different effect of CXCR4 inhibition between WT and mutant progenitors likely reflect the fact that the latter are enriched in NSCs.
Finally, the evidence that NSCs are significantly increased in the mutant V-SVZ is reported in Fig. 8. In this figure, it is clearly reported that compared to the WT counterpart at early postnatal stages, only the multiciliated ependymal cells are significantly increased in the mutant niche, whereas uniciliated progenitors display only a trend increase (Panel C). However, the total number of apical cells is increased in the mutant V-SVZ, indicating that the number of both cell types are likely increased. Consistent with this hypothesis, in panel G of the same figure we show that in the adult V-SVZ, when the ependymal cells are fully differentiated, also apical GFAP+ NSCs are significantly increased. Notably, in this figure we show that GFAP+ NSCs also display a primary cilium, an elongated morphology and lack multiple cilia, and therefore are not atypical ependymal cells. Finally, in supplementary table S6, we show no difference in terms of % of clone forming cells between dissociated cell preparations of the WT and mutant V-SVZ. These observations and our finding of increased Ki67 apical expression in the adult V-SVZ, illustrated in supplementary figure S2B, clearly show that apical NSCs are increased.
We have now introduced multiple modification in text and figures to clarify the mechanisms underlying the effect of GDF15 ablation on EGFR expression and activation and the differential effect of CXCR4 on WT and mutant progenitors. The new data set illustrating phosphoEGFR are illustrated in figure 4B, G. We have also modified figure 8 in an effort to illustrate more clearly the effect of lack of GDF15 on NSC number.
*Major comments: *
*1) Inconsistencies start already in Figure 1: The authors show expression of the receptor at neonatal stages (much higher) and adult stages, but GDF15 is shown only in adult stages and the citations of their previous work suggests that indeed it may not be present at this early stage in the GE VZ (p.8, line 10). If it is, please show. If it isn't, could it be that it is in the CSF and signals only to apical cells? *
As the reviewer rightly mentions, GDF15 is present in the CSF and signals mainly to apical cells, as it is known to be secreted by the choroid plexus (Böttner et al., 1999; Schober et al., 2001). However, we would like to respectfully disagree with the reviewer. In our previous work, we clearly showed that GDF15 expression increases at E16 and is highest at E18 in the GE, which is the reason we specifically chose this timepoint for analysis (compare Carrillo-Garcia et al. (2014), Fig. 1A). In this manuscript we have also shown that EGFR expressing progenitors in the GE express GDF15. As the expression of GDF15 at embryonic and neonatal ages has already been investigated by us and others for two decades (see also Schober et al. (2001)), we refrained from showing expression of GDF15 at these ages again. However, we have now modified the relevant result section to clearly highlight the existence of this previous findings.
*2) An overview of the KO phenotype by lower power pictures would be helpful. For example an overview over the GE and PH3 immunostaining WT and KO at comparable section levels. *
Our analysis is based on whole-mount preparation of the whole GE. To standardize our analysis the same number of pictures were taken at similar locations to obtain a quantification representative of the apical surface of the whole GE. Therefore, the areas of interest were not selected on the basis of the number of mitotic cells and the differences observed do not reflect a positional effect. Lower power pictures illustrating the whole GE, are unlikely to be helpful, because they would not show the nuclear immunostaining. However, we have now modified the relevant Material and Methods section as follows to describe the standardization of our quantitative analysis: “Whole mounts were imaged using a Leica TCS SP8 confocal microscope with a 40x or 63x oil immersion objective and LASX software (Leica). For the quantification, an average of three different regions of interest were chosen at fixed rostral, dorsal and ventral position of the GE or V-SVZ and averaged for the collection of a single data set.”
* 3) Figure 2B- where is the apical surface, where are we in the GE? Where was quantification done? *
We have now added images detailing the localization of apical and subapical cells in new Fig. 2A, as well as further clarifications of the imaging and quantification in the materials and methods section.
* 4) Clarify the part with EGF signaling and/or take a more comprehensive view by a proteomic or transcriptomic approach, as EGFR and CXCR4 which were already investigated previously, may not explain the phenotype. *
We agree with the reviewer that our data should prompt a more comprehensive approach. However, this is surely a work worthy of a separate manuscript, since we agree with the reviewer that changes in EGFR and CXCR4 do not fully explain the effect of GDF15 on proliferation. We have now clarified our conclusions about EGF signalling, modifying the relevant part in the result section. We have also modified the abstract as follows:
“From a mechanistic point of view, we show that active EGFR is essential to maintain proliferation in the developing GE and that GDF15 affects EGFR trafficking and signal transduction. Consistent with a direct involvement of GDF15, exposure of the GE to the growth factor normalized proliferation and EGFR expression and it decreased the number of apical progenitors. A similar decrease in the number of apical progenitors was also observed upon exposure to exogenous EGF. However, this effect was not associated with reduced proliferation, illustrating the complexity of the effect of GDF15.”
*5) Do the authors actually think that the effects on EGFR are in the cells expressing the GDF15 receptor? Then please show co-localization. *
As both EGFR and GFRAL are widely expressed in the embryonic GE (see Figs 1B and 4B), making overlap inevitable, we did previously not assume the need to show co-localization. We have now added images showing co-localization of EGFR and GFRAL in E18 and adult brain sections in Fig. 1B.
*6) Figure 5D shows virtually no apical mitosis in WT, but indeed there are apical mitosis in WT E18 GE as one can also see in panel 5A. *
We apologize for the confusion. In the manuscript, we use Ki67 and analysis of nuclear morphology to determine the number of cells undergoing cell division, i.e. in meta-, ana- or telophase and immunostaining with antibody with phH3+, which stains additionally cells also at late G2 and early mitotic stages. Consistent with this, the number of mitotic cells scored with Ki67 and quantified in Fig. 5D is smaller than the number of phH3+ cells that is illustrated in Fig. 5A. Throughout the manuscript, cells labeled by phH3 immunoreactivity are named “phH3+ cells”, as quantified in Fig. 5B, whereas with “dividing cells” we refer to cells with Ki67 labeling that show nuclear morphology of meta-, ana- or telophase. We have, also according to the suggestions of reviewer 1, added images of the whole mounts analyzed for Fig. 5D, as well as the following text in the materials and methods section: “Cells were considered dividing if the nuclei were labelled with Ki67 and the nuclear morphology showed signs of division, i.e. meta-, ana- or telophase, in DAPI and Ki67-channels. For the sake of clarity, “dividing cells” only refers to this way of detection, while cells positive for phH3 are termed “phH3+ cells”, as phH3 also labels cells in interphase and prophase, as well as late G2 phase.”
*7) For the effect on ependymal cell generation it could be good to include an intermediate age, such as P5-7, when ependymal cells differentiate, staining e.g. for Lynkeas or Mcidas, known fate determinants regulating ependymal cell differentiation at that time. *
Most of our research was performed in either E18 or adult animals, where ependymal cells are either not yet present or already fully differentiated. Since ependymal cell differentiation starts at birth, we used P2 animals to look at ependymal cell differentiation. As shown in Fig. 8B, C this age is appropriate to study early ependymal differentiation, as a lot of multiciliated ependymal cells are already present at this age, and the difference between WT and Gdf15-/- animals is clearly visible and significant. While another age or additional markers might be interesting, we argue that it would not add to the conclusion or significance of this paper, as we can see this phenotype already at age P2 and it can still be detected it in adult animals.
*Minor comments: *
*-) p. 8, subapical progenitors are mentioned in line 42 without explaining how they are defined. *
We have now added more detailed definitions of apical and subapical progenitors to the introduction.
*-) p.8, line 44: the word increased in mentioned 2x *
We have removed the additional word.
*-) In the description of Figure 8 C and D seem to have been mixed up. *
We have changed the description of Fig. 8.
* ** Referees cross-commenting***
*I also fully agree with the point that this manuscript is very difficult to read. I think that anyhow the results have to be reorganized to focus on the most important data, so rewriting will have to be done for clarity either way. *
We apologize for the lack of clarity we have now extensively modified and re-edited the manuscript in an effort to improve its clarity.
* Reviewer #2 (Significance (Required)): *
* Exploring signmalling factors important for the stem cell niche is important, and the GDF15 indeed seems to have an effect there. The problem is, that much has been done with this factor already, but of course a mechanistic understanding of whats going on is important and could be the strength of this manuscript. However, it is really not clear, which mechanisms causes what. What is clear, is that the increased proliferation of neuronal progenitors is counterbalanced by death. Its also clear that ependymal cells are increased, which is an interesting effect. But how and why is not clear and may be the best to focus in this paper. *
As the reviewer mentions, several publications focus on GDF15. However, there is only one publication investigating the effect of GDF15 on neural stem cells and this focuses on the hippocampus. Therefore, we would like to respectively disagree with the conclusion of the reviewer “that much has been done with this factor”. Moreover, a serious problem with previous studies investigating GDF15 is the fact that its receptor is scarcely expressed and therefore it is not clear if these studies investigate direct or indirect effects of the growth factor. Since we here for the first time show that neural stem cells in the GE and V-SVZ express GDF15-receptor GFRAL, our study for the first time show a direct involvement of GDF15 on proliferation, number of ependymal cells and, as detailed in our reply above, apical NSCs. This knowledge is not only relevant to the field of normal and cancer stem cells, but also within the context of the role of GDF15 as mitokine and as stress hormone (see also our reply to major comments 2 of reviewer 1). Therefore, although we agree with the reviewer that the molecular mechanisms underlying the effect of GDG15 need further investigation, our data are novel and of relevance to the general scientific community.
References:
Böttner, M., Suter-Crazzolara, C., Schober, A., Unsicker, K., 1999. Expression of a novel member of the TGF-beta superfamily, growth/differentiation factor-15/macrophage-inhibiting cytokine-1 (GDF-15/MIC-1) in adult rat tissues. Cell Tissue Res 297, 103-110.
Carrillo-Garcia, C., Prochnow, S., Simeonova, I.K., Strelau, J., Hölzl-Wenig, G., Mandl, C., Unsicker, K., von Bohlen Und Halbach, O., Ciccolini, F., 2014. Growth/differentiation factor 15 promotes EGFR signalling, and regulates proliferation and migration in the hippocampus of neonatal and young adult mice. Development 141, 773-783.
Falk, S., Bugeon, S., Ninkovic, J., Pilz, G.A., Postiglione, M.P., Cremer, H., Knoblich, J.A., Gotz, M., 2017. Time-Specific Effects of Spindle Positioning on Embryonic Progenitor Pool Composition and Adult Neural Stem Cell Seeding. Neuron 93, 777-791 e773.
Jeong, D., Lozano Casasbuenas, D., Gengatharan, A., Edwards, K., Saghatelyan, A., Kaplan, D.R., Miller, F.D., Yuzwa, S.A., 2020. LRIG1-Mediated Inhibition of EGF Receptor Signaling Regulates Neural Precursor Cell Proliferation in the Neocortex. Cell Rep 33, 108257.
Llorens-Bobadilla, E., Zhao, S., Baser, A., Saiz-Castro, G., Zwadlo, K., Martin-Villalba, A., 2015. Single-Cell Transcriptomics Reveals a Population of Dormant Neural Stem Cells that Become Activated upon Brain Injury. Cell Stem Cell 17, 329-340.
Schober, A., Böttner, M., Strelau, J., Kinscherf, R., Bonaterra, G.A., Barth, M., Schilling, L., Fairlie, W.D., Breit, S.N., Unsicker, K., 2001. Expression of growth differentiation factor-15/ macrophage inhibitory cytokine-1 (GDF-15/MIC-1) in the perinatal, adult, and injured rat brain. J Comp Neurol 439, 32-45.
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Referee #2
Evidence, reproducibility and clarity
Here the authors explore the role of GDF15 during development of the adult neural stem cell niche at the lateral wall of the lateral ventricle using GDF15 knock-out mice. They find increased progenitor proliferation at neonatal stages and at 8weeks, compensated by neuronal death. Further they report that EGFR+ cells are arranged differently in the GDF15 mutants (in clusters rather than columns) with also lower levels of EGFR. This is surprising to me, as the authors observe an increase in proliferation. They then report that addition of EGF leads to an increase in prominin+ progenitors in the GDF15KO, but not the WT, but there is lower levels of EGFR in the KOs. They then block CXCR4, which is allegedly required for GDF15 to modulate EGFR expression, and they find that this blocking reduces proliferation mostly in WT cells. As can be seen from this summary, to me, the model of how GDF15 loss is supposed to increase proliferation is not clear. Even less so, when in adult SVZ, EGFR+ progenitors were increased, while EGFR was reduced at postnatal stages. Beyond this, the authors show convincingly that ependymal cells are increased at adult stages, while I see no data supporting their claim of NSCs to be increased (at least not reaching levels of significance). Taken together, this manuscript contains a lot of data, but to me no coherent picture emerges. If the picture is that the higher proliferation rate of apical progenitors at E18 generates more ependymal cells, then this should be shown (by including analysis e.g. at P5 when ependymal cells emerge). How GDF15 would affect proliferation in general is also not clear to me - maybe an unbiased analysis by RNA-seq could help to separate the main effects from diving into known candidates that seem not to explain the main aspects.
Major comments:
- Inconsistencies start already in Figure 1: The authors show expression of the receptor at neonatal stages (much higher) and adult stages, but GDF15 is shown only in adult stages and the citations of their previous work suggests that indeed it may not be present at this early stage in the GE VZ (p.8, line 10). If it is, please show. If it isn't, could it be that it is in the CSF and signals only to apical cells?
- An overview of the KO phenotype by lower power pictures would be helpful. For example an overview over the GE and PH3 immunostaining WT and KO at comparable section levels.
- Figure 2B- where is the apical surface, where are we in the GE? Where was quantification done?
- Clarify the part with EGF signaling and/or take a more comprehensive view by a proteomic or transcriptomic approach, as EGFR and CXCR4 which were already investigated previously, may not explain the phenotype.
- Do the authors actually think that the effects on EGFR are in the cells expressing the GDF15 receptor? Then please show co-localization.
- Figure 5D shows virtually no apical mitosis in WT, but indeed there are apical mitosis in WT E18 GE as one can also see in panel 5A.
- For the effect on ependymal cell generation it could be good to include an intermediate age, such as P5-7, when ependymal cells differentiate, staining e.g. for Lynkeas or Mcidas, known fate determinants regulating ependymal cell differentiation at that time.
Minor comments:
- p. 8, subapical progenitors are mentioned in line 42 without explaining how they are defined.
- p.8, line 44: the word increased in mentioned 2x
- In the description of Figure 8 C and D seem to have been mixed up.
** Referees cross-commenting**
I also fully agree with the point that this manuscript is very difficult to read. I think that anyhow the results have to be reorganized to focus on the most important data, so rewriting will have to be done for clarity either way.
Significance
Exploring signmalling factors important for the stem cell niche is important, and the GDF15 indeed seems to have an effect there. The problem is, that much has been done with this factor already, but of course a mechanistic understanding of whats going on is important and could be the strength of this manuscript. However, it is really not clear, which mechanisms causes what. What is clear, is that the increased proliferation of neuronal progenitors is counterbalanced by death. Its also clear that ependymal cells are increased, which is an interesting effect. But how and why is not clear and may be the best to focus in this paper.
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Referee #1
Evidence, reproducibility and clarity
Summary:
This paper illustrates the role of GDF15 in ganglionic eminence featuring the influence on neurogenesis and progenitor proliferation. Using the conventional knockout GDF-15 mouse lines, the authors provide a series of counting data indicating that GDF15 controls neurogenesis in the late embryonic or adult neural stem cells in the ventral forebrain.
Major comments:
The entire story in this manuscript seems similar to the previous findings where the authors demonstrated the role of GDF15 in the hippocampal neural stem cells in relation to EGF and CXCR4.
The data and the conclusion presented here sound reasonable to me. The current manuscript, however, gave me the impression that the story is less impactful and rather descriptive. To improve the quality of the current draft, the authors may wish to clearly highlight the novelty of the findings, not simply apply the previous strategy to the other anatomical brain regions. Alternatively, the draft could emphasize the similarity of utilising the same biological strategies to control the number of adult stem cells in the distinct stem cell niche.
I also have two concerns which may help to improve the current draft.
Firstly, I would suggest considering the data presentation as many of the counting data are not accompanied by representative images or a detailed description of the methods, which could impede the credibility of the data. For instance, it is not clear to me how the authors judged the apical vs subapical progenitor counting as neither the pictures nor the methods clearly specified how these are distinguished. Same to the Figures 3 and 8.
I would also suggest the authors may wish to carefully review the text as many abbreviations are not properly stated (for example, what are P+ progenitors?), or not properly explained why the particular gene expression is analysed (EGF, Sox2, CXCR4). This is also applied to the anatomical jargon (like apical, subapical etc), which can be specified in the figure by introducing the cartoons or point-on images.
Last not least, I should point out that the author uses less commonly used terminology. To my knowledge, the SVZ progenitors in the GE are now called basal progenitors (Bandler et al 2017 for example) and the word intermediate progenitors is used for the Tbr2+ IP cells in the developing cortex. MASH-1 is an old gene name as it is revised as Ascl1 (please refer to any recent papers and web databases such as Mouse Genome Informatics, and NCBI, for instance). The use of prevailed wording will help the readers to understand the presented story.
Minor comments:
Abstract Line 12-15 is confusing: What does "genotype" means?
Introduction Despite the focus of this paper being on the proliferation in GE, the introduction mixed up the references describing the dorsal telencephalon. It's better to cite the ventral GE as some progenitor behaviours are different from the ones in the dorsal.
Maybe it's better to dedicate more to describing the lineage trajectory in the ventral GE and the molecular players (such as EGF), which makes it harder to understand the rationales of the several experiments.
Results
Fig1: V/SVZ -> VZ? I think V means ventricles while VZ is for the ventricular zone
Single-channel images should be presented to demonstrate the positive or negative cells for each antigen. Only a subset of progenitors in the adult SVZ is GDF15 positive although this is not described in the text. Why the GDP15 staining was performed only in the adult sections, but not in E18 while the GFRAL is shown in both stages? The text claims "GDF15 is particularly expressed in the germinal region of the GE" but I did not find the data shown in this draft.
Line 24-25: I did not understand this statement.
Fig. 2 Line 33: what are apical P+ progenitors ?
Fig. 2A: The total analysed cells are not described in M&M.
Fig 2 C and D. While the counting of apical or subapical progenitors has been done respectively, the representative images of which regions are judged as apical or subapical are not shown. This comment also applies to Line 41: I did not get the logic of how this analysis will be able to distinguish apical or subapical cell division.
Fig. 2 E and F: I am not sure why the proliferation was assessed in vitro whole mount cultures. IP injection in vivo animals would be more convincing.
Fig. 3 I am not sure the mitotic spindle orientation analysis is very informative to stand out as one independent figure. In some contexts (Noctor et al 2008), it does not correlate to the asymmetric or symmetric division modes.
Fig. 4 I am not convinced by this data since how the fluorescent intensity is measured is not described. If the internal controls to adjust the staining variation among samples are not used, the data is not convincing to me. The representative pictures are not convincing either to claim the substantial differences. Perhaps immunoblotting is better to be employed to quantify the protein expression difference.
Fig. 5 This is very busy figure composed of mainly counting graphs of different experiments. I think at least it is better to separate the data in vivo or culture.
Fig. 6. Pictures of Day 2 and Day 7 should be presented to highlight the difference between them.
Fig. 7 Mash-1 should be rephrased as Ascl1.
Fig. 8 A: I am not sure why these pictures are B&W even though the two antigens are stained. The main text needs more description since no explanation of FOP, b-catenin etc. The picture of GFD15 KO looks having massive numbers of FOP+ cells, which is not correlated to the counting, I guess? written
** Referees cross-commenting**
I agree with Reviewer #2's comment that despite the amount of data presented, they are not presented in a coherent manner. I would suggest revising carefully before submitting to any journals.
Significance
The presented finding of the role of GDF15 in the ventral progenitors are evident and a new finding has not been reported. Since the same effects and signalling pathways involved in adult hippocampus neurogenesis are previously published by the same authors, the impact of the current manuscript is limited. I think heightening the role of GDF15 in the biological context of ventral progenitors, or alternatively, making a comparison to the previous finding would greatly improve the quality of the draft. In my opinion, this work would be appealing to the community of neural stem cells but maybe not to the broad audience. My expertise is neurodevelopmental biology focusing on neuronal lineages and neurogenesis.
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Reply to the reviewers
General comments:
We thank the reviewers for recognizing the importance of our work and for their supportive and insightful comments.
Our planned revisions focus on addressing all the comments and especially in further elucidating the molecular mechanism underpinning our observations, their consequences for cell phenotypes and reproducing our observations in an additional cell line. Our revision plan is backed up in many cases by preliminary data.
Our submitted manuscript demonstrated that DNMT3B’s recruitment to H3K9me3-marked heterochromatin was mediated by the N-terminal region of DNMT3B. Data generated since submission suggest that DNMT3B binds indirectly to H3K9me3 nucleosomes through an interaction mediated by a putative HP1 motif in its N-terminal region.
Specifically, we have found that DNMT3B can pull down HP1a and H3K9me3 from cell extracts and that this interaction is abrogated when we remove the N-terminal region of DNMT3B (revision plan, figure 1a). Using purified proteins in vitro, we have shown binding of DNMT3B to HP1a that is dependent on the presence of DNMT3B’s N-terminus suggesting that the interaction with HP1a is direct and that this mediates DNMT3B’s recruitment to H3K9me3 (revision plan, figure 1b). Alphafold multimer modelling identified that DNMT3B's N-terminus binds the interface of a HP1 dimeric chromoshadow domain through a putative HP1 motif. Two point mutations in this motif ablate DNMT3B’s interaction with HP1a in vitro (revision plan, figure 1b - DNMT3B L166S I168N).
We propose to further characterize DNMT3B’s interaction with HP1a in vitro and determine the significance of these observations in cells by microscopy in a revised manuscript. Together with the other proposed experiments and analyses, we believe the extra detail regarding the molecular mechanisms through which DNMT3B is recruited to H3K9me3 heterochromatin will help address the reviewer’s comments.
Point by point response:
We have reproduced the reviewer’s comments in their entirety and highlighted them in blue italics.
Reviewer #1 (Evidence, reproducibility and clarity (Required)): Summary:
This paper by Francesca Taglini, Duncan Sproul, and their coworkers, examines the mechanisms of DNA methylation in a human cancer cell line. They use the human colorectal cancer line HCT116, which has been very widely used to look at epigenetics in cancer, and to dissect the contribution of different proteins and chromatin marks to DNA methylation.
The authors focus on the role of the de novo methyltransferase DNMT3B. It has been shown in ES cells in 2015 that its PWWP domain directs it to H3K36me3, typically found in gene bodies. More recently, the authors showed similar conclusions in colorectal cancer (Masalmeh Nat Comm 2021). Here they examine, more specifically, the role of the PWWP. The conclusions are described below.
Major comments:
- *1-I feel that this paper has several messages that are somewhat muddled. The main message, as expressed in the title and in the model, is that the PWWP domain of DNMT3B actively drags the protein to H3K36me3-marked regions. Inactivation of this domain by a point mutation, or removal of the Nter altogether, causes DNMT3B to relocate to other genomic regions that are H3K9me3-rich, and that see their DNA methylation increase in the mutant conditions. This first message is clear.
We thank the reviewer for their positive comments on our observations. However, we note that our results suggest that removal of the N-terminal region has a different effect to point mutations in the PWWP domain. The data we present suggest that the N-terminus facilitates recruitment to H3K9me3 regions.
The second message has to do with ICF. A mutant form of DNMT3B bearing a mutation found in ICF, S270P, is actually unstable and, therefore, does not go to H3K9me3 regions. I feel that here the authors go on a tangent that distracts from message #1. This could be moved to the supp data. At any rate, HCT116 are not a good model for ICF. In addition, a previous paper has looked at the S270P mutant, and it did not seem unstable in their hands (Park J Mol Med 2008, PMID: 18762900). So I really feel the authors do not do themselves a favor with this ICF angle.
While we agree with the reviewer that HCT116 cells as a cancer cell line are not a good model for ICF1 syndrome, our observation that S270P destabilizes DNMT3B is important to consider in the context of this disease. In addition, the S270P mutant was reported to abrogate the interaction between DNMT3B and H3K36me3 (Baubec et al 2015 Nature PMID: 25607372) making it important to compare it to the other mutations we examine. In our revised version of the manuscript, we propose to move these data to the supplementary materials and add a statement to the discussion noting the caveat that HCT116 cells are likely not to model many aspects of ICF1.
With regard to the differences between our results and that of Park et al, we note that stability of the S270P mutant was not assessed in that study whereas we directly assess stability in vitro and in cells. We propose to add discussion of this previous study to the revised manuscript.
2-I feel that some major confounders exist that endanger the conclusions of the work. The most worrisome one, in my opinion, is the amount of WT or mutant DNMT3B in the cells. It is clear in figure 4C that the WT rescue construct is expressed much more than the W263A mutant (around 3 or 4 times more). Unless I am mistaken, we are never shown how the level of exogenous rescue protein compares to the level of DNMT3B in WT cells. This bothers me a lot. If the level is too low, we may have partial rescue. If it is too high, we might have artifactual effects of all that DNMT3B. I would also like to see the absolute DNA methylation values (determined by WGBS) compared to the value found in WT. From figure S1A, it looks like WT is aroun 80% methylation, and 3BKO is around 77% or so. I wonder if the rescue lines may actually have more methylation than WT?
The rescue cell lines do express DNMT3B to a greater level than observed endogenously. In our manuscript we controlled for this effect by generating the knock-in W263A cells and, as reported in the manuscript, we observe similar effects to the rescue cells (manuscript, figure 2d) suggesting that our observations are not driven by the overexpression.
We also expressed ectopic DNMT3B from a weaker promoter (EF1a) in DNMT3B KO cells but did not include these data in the submitted manuscript. We have previously shown that this promoter expresses DNMT3B at lower levels than the CAG promoter used in the submitted manuscript (Masalmeh et al 2021 Nature Communications PMID: 33514701). Bisulfite PCR of representative non-repetitive loci within heterochromatic H3K9me3 domains show that we observe similar gains of methylation with DNMT3BW263A (revision plan, figure 2).
Revision plan figure 2. Expression of DNMT3BW236A from a weaker promoter leads to increased DNA methylation at selected H3K9me3 loci. Barplot of mean methylation by BS-PCR at H3K9me3 loci alongside the H3K4me3-marked BRCA2 promoter in DNMT3B mutant cells were DNMT3B is expressed from the EF1 promoter. P-values are from two-sided Wilcoxon rank sum tests.
To reinforce that our conclusions are not solely a result of the level of DNMT3B expression, we propose to include these data in the revised manuscript.
The reviewer is also correct that by WGBS, the rescue cell lines have higher levels of overall DNA methylation than HCT116 cells. We will note this in revised manuscript and include HCT116 cells in a revised version of Figure S1e.
3-I guess the unarticulated assumption is that the gain of DNA methylation seen at H3K9me3 region upon expression of a mutant DNMT3B is due to DNMT3B itself. But we do not know this for sure, unless the authors test a double mutant (PWWP inactive, no catalytic activity). I am not necessarily asking that they do it, but minimally they should mention this caveat.
The hypothesis that the gains in DNA methylation at H3K9me3 loci result from the direct catalytic activity of DNMT3B is supported by our observation that a catalytic dead DNMT3B does not remethylate heterochromatin (manuscript, figures 1d and e). However, we acknowledge that we have not formally shown that the additional DNA methylation seen with DNMT3BW263A are a direct result of its catalytic activity. We will conduct an analysis of the effect of catalytically dead DNMT3BW263A on DNA methylation at Satellite II and selected H3K9me3 loci and include this in the revised manuscript.
4-I am confused as to why the authors look at different genomic regions in different figures. In figure 1 we are looking at a portion of the "left" arm of chr 16. But in figure 2B, we now look at a portion of the "right" arm of the same chromosome, which has a large 8-Mb block of H3K9me3, and is surprisingly lowly methylated in the 3BKO. This seems quite odd, and I wonder if there is a possible artifact, for instance mapping bias, deletion, or amplification in HCT116. Showing the coverage along with the methylation values would eliminate some of these concerns.
By choosing different regions of the genome for different figures, we intended to reassure the reader that our results were not specific to any one region of the genome. In the revised manuscript, we propose to display a consistent genomic region between these figures.
With regard to the low levels of DNA methylation in H3K9me3 domains in DNMT3B KO cells, H3K9me3 domains are partially methylated domains which have reduced methylation in HCT116 cells (see page 5 of the manuscript):
… we found that hidden Markov model defined H3K9me3 domains significantly overlapped with extended domains of overall reduced methylation termed partially methylated domains (PMDs) defined in our HCT116 WGBS (Jaccard=0.575,p=1.07x10-6, Fisher’s test).
These domains lose further DNA methylation in DNMT3B KO cells leading to the low methylation level noted by the reviewer. The methylation percentages calculated from WGBS are based on the ratio of methylated to total reads. Thus, a lack of coverage generates errors from division by zero rather than the low values observed in this domain in DNMT3B KO cells.
We include a modified version of figure 2b from the manuscript below. This includes coverage for the 3 cell lines (revision plan, figure 3). Although WGBS coverage is slightly reduced in H3K9me3 domains, reads are still present and overall coverage equal between different cell lines.
While we could potentially include the coverage tracks in revised versions of figures, we note that doing so for multiple cell lines would make these figures extensively cluttered and it would likely be difficult to observe the differences in DNA methylation in these figure panels due to shrinkage of the other tracks.
Minor comments:
1-The WGBS coverage is not very high, around 2.5X on average, occasionally 2X. I don't believe this affects the findings, as the authors look at large H3K9me3 regions. But the info in table S2 was hard to find and it is important. I would make it more accessible.
In the revised manuscript we will specify the mean coverage in the text to ensure this is clearer.
2-It would be nice to have a drawing showing exactly what part of the Nter was removed.
We will add this in the figure in the revised manuscript.
3-some figures could be clearer. I was not always sure when we were looking at a CRISPR mutant clone (W263A) versus a piggyBac rescue.
In the revised manuscript we will clarify in the figure labels to ensure it is clear which data were generated using CRISPR clones.
4-unless I am mistaken, all the ChIP-seq data (H3K9me3, H3K36me3 etc) come from WT cells. It is not 100% certain that they remain the same in the 3BKO, is it? This should be discussed.
We performed ChIP-seq on both HCT116 and 3BKO cell lines and used ChIP-seq data from the 3BKO cell line for the rescue experiments where DNMT3Bs were expressed in 3BKO cells. We will ensure this is clearer in the revised version.
Reviewer #1 (Significance (Required)):
Strengths:
The experiments are for the most part well done and well interpreted (save for the limitations mentioned above). The techniques are appropriate and well mastered by the team. The paper is well written, the figures are nice. The authors know the field well, which translates into a good intro and a good discussion. The bioinformatics are convincing.
Limitations:
All the work is done in a single cancer cell line. One might assume the conclusions will hold in other systems, but there is no certainty at this point.
We acknowledge this limitation. To demonstrate that our results are applicable beyond HCT116 cells, we will include analysis of experiments on an independent cell line in the revised manuscript.
HCT116 are not the best model system to study ICF, which mostly affects lymphocytes
At present, I feel that the biological relevance of the findings is fairly unclear. The authors report what happens when DNMT3B has no functional PWWP domain. I am convinced by their conclusions, but what do they tell us, biologically? Are there, for instance, mutant forms of DNMT3B expressed in disease that have a mutant PWWP? Are there isoforms expressed during development or in certain cell types that do not have a PWWP? In these cell types, does the distribution of DNA methylation agree with what the authors predict?
As stated in response to point 1, although we acknowledge the limitations of HCT116 cells as a model of ICF, we believe are finding that the S270P mutation results in unstable DNMT3B are still important to consider for ICF syndrome.
We are not aware of reports of mutations affecting the residues of DNMT3B’s PWWP domain we have studied. Our preliminary analysis suggests that although mutations in DNMT3B’s PWWP domain are frequent, residues in the aromatic cage such as W263 and D266 are absent from the gnomAD catalogue (Karczewski et al 2020 Nature, PMID: 32461654). This suggests that they are incompatible with healthy human development.
A number of different DNMT3B splice isoforms have been reported. These include DDNMT3B4 which lacks the PWWP domain and a portion of the N-terminal region (Wang et al 2006 International Journal of Oncology, PMID: 16773201). DDNMT3B4 is proposed to be expressed in non-small cell lung cancer (Wang et al 2006 Cancer Research, PMID: 16951144).
We will include analysis of gnomAD and discussion of these points in the revised manuscript.
In its present state, I feel the appeal of the findings is towards a semi-specialized audience, that is interested in aberrant DNA methylation in cancer and other diseases. This is not a small audience, by the way.
We thank the reviewer for their comments and the suggestion that our findings are of interest to a cross-section of researchers.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Note, we have added numbers to the comments made by reviewer 2 to aid cross-referencing.
In this manuscript, Taglini et al., describe an increased activity of DNMT3B at H3K9me3-marked regions in HCT cells. They first identify that DNA methylation at K9me3-marked regions is strongly reduced in absence of DNMT3B. Next, the authors re-express DNMT3B and DNMT3B mutant variants in the DNMT3B-KO HCT cells and assess DNA methylation by WGBS where they identify a strong preference for re-methylation of K9me3 sites. Based on genome-wide binding maps for DNMT3B, including the mutant variants, they address how the localization of DNMT3B relates to the observed changes in methylation.
Major points:
- The authors show increased reduction of mCG at H3K9me3 (and K27me3) sites in absence of DNMT3B. This is based on correlating delta %mCG with histone modifications in 2kb bins. I find this approach to not fully support the major claim. First, the correlation coefficients are very small -0.124 for K9me3 and -0.175 for K27me3, and just marginally better compared to, for example, K36me3 that does not seem to have any influence on mCG according to Sup Fig S1b. While I agree that mCG seems more reduced at K9me3 in absence of DNMT3B (e.g. in Fig 1a), is there a better way to visualize the global effect? The delta mCG Boxplots based on bins are not ideal (this applies to many figures using the same approach in the current manuscript).*
Our choice to examine the global effects using correlations in windows across the genome was motivated by similar previous analyses in other studies (for example: Baubec et al. 2015 Nature PMID 25607372, Weinberg at al 2021 Nature PMID:33986537, Neri et al 2017 Nature PMID: 28225755). These global analyses result in modest correlation coefficients because the vast majority of genomic windows are negative for a given mark. For this reason, we included specific analyses of H3K36me3, H3K9me3 and H3K27me3 domains in the manuscript (eg manuscript figure 1b, c and d) which reinforce the conclusions drawn from our global analyses.
However, we acknowledge that while our data support a specific activity at H3K9me3 marked heterochromatin, these are not the only changes in DNMT3B KO cells as DNMTs are promiscuous enzymes that are localized to multiple genomic regions. We will add discussion of this point to the revised manuscript.
2. Second, the calculation based on delta mCpG does not allow to see how much methylation was initially there. For example, S1b shows a median decrease of ~ 10% in K9me3 and ~7-8% in H3K4me3. What does this mean given that the starting methylation for both marks is completely different?
Following this point, the authors mention that mCG is already low at K9me3 domains in HCT cells (compared to other sites in the genome). I am curious if this may influence the accelerated loss of methylation in absence of DNMT3B? Any comments on this?
The observation that there is a greater loss at H3K9me3 domains than H3K27me3-only domains which also have low DNA methylation levels in HCT116 argue that the losses are not solely driven by the lower initial level of methylation in H3K9me3 domains. Our analyses later in the manuscript also support a specific activity at H3K9me3. In addition, we propose to reinforce this point through further data on exploring how DNMT3B interacts with HP1a (see general comments, revision plan figure 1).
However, we acknowledge the possibility that part of the loss seen at H3K9me3 domains in DNMT3B KO cells could be in part a result of their low initial level of methylation. In the revised manuscript we propose to include discussion of this possibility.
3. One issue is the lack of correlation in DNMT3B binding to H3K9me3 sites in WT cells (Fig 3). How does this explain the requirement for DNMT3B for maintenance of methylation at H3K9me3? While some of the tested mutants show some weak increase at K9me3 sites, these are not comparable to the strong binding preferences observed at K36me3 for the wt or delta N- term version.
Using ChIP-seq we cannot say that DNMT3BWT does not bind at H3K9me3, only that it binds here to a lower level than at K36me3-marked loci. The normalized DNMT3BWT signal at H3K9me3 domains is higher than the background signal from DNMT3B KO cells (manuscript figure 3d) supporting the hypothesis that DNMT3BWT localizes to H3K9me3. This hypothesis is also supported by the observation that the correlation between DNMT3BDN and H3K9me3 is reduced compared to that of DNMT3BWT (manuscript figure 6c compared to figure 3c).
There are several reasons why the apparent enrichment of DNMT3B at H3K9me3 may appear weaker than at H3K36me3 by ChIP-seq. Previous work has also suggested that formaldehyde crosslinking fails to capture transient interactions in cells (Schmiedeberg et al. 2009 PLoS One PMID: 19247482). H3K9me3-marked heterochromatin is also resistant to sonication (Becker et al. 2017 Molecular Cell PMID: 29272703) and this could further affect our ability to detect DNMT3B in these regions using ChIP-seq. Our new data also suggest that DNMT3B binds to H3K9me3 indirectly through HP1a (see general comments, revision plan figure 1) and this may also lead to weaker ChIP-seq enrichment at H3K9me3 compared to the direct interaction with H3K36me3 through DNMT3B’s PWWP domain.
We propose to add discussion of these issues to the revised manuscript.
4. Following the above comment, what about other methyltransferases in HCT cells? Could DNMT1 or DNMT3A function be altered in absence of DNMT3B, and the observed methylation changes could be indirectly influenced by DNMT3B? The authors could create a DNMT-TKO HCT cell line and re-introduce DNMT3B in this background and measure methylation to exclude that DNMT1 or DNT3A could have an influence. In this case, only H3K9me3 should gain DNA methylation.
As discussed in response to reviewer 1 (point 3), we propose to examine the changes in DNA methylation upon expression of catalytically dead DNMT3BW263A to further strengthen the evidence that DNMT3BW263A is directly responsible for the increased DNA methylation at H3K9me3-marked loci.
5. DNMT3B lacking N-terminal shows reduced K9me3 methylation & some localization by imaging. While the presented experiments show some support for this conclusion, I suggest to re-introduce a W263A mutant lacking the N-terminal part and measure changes in DNA methylation at H3K9. This should help to test the requirement for the N-terminal regions and further indicate which protein part (PWWP or N-term) is more important in regulating the balance between K9me3 and K36me3.
We have performed this experiment and the data are shown in manuscript figure S6c and d. The results of these experiments show that DNMT3BΔN+W263A cells showed less methylation at H3K9me3 loci than DNMT3BW263A cells, supporting a role for the N-terminus in recruiting DNMT3B to H3K9me3-marked heterochromatin. In the revised version, we will ensure that these data are more clearly indicated.
In the first paragraph of the discussion, the authors state: "Our results demonstrate that DNMT3B is recruited to and methylates heterochromatin in a PWWP- independent manner that is facilitated by its N-terminal region." Same statement is found in the abstract. This contradicts the ChIP-seq results that do not indicate a recruitment of DNMT3B to heterochromatin, and the N- terminal deletions are not fully supporting a role in this targeting since there is no localization to K9me3 to begin with. While changes in methylation are observed, it remains to be determined if this is indeed through direct DNMT3B delocalization or indirectly through influencing the remaining DNMTs.
As discussed above, there are several potential reasons why DNMT3B ChIP-seq signal at H3K9me3 is weak (reviewer 2, point 3). The additional experiments we propose to include in the revised manuscript could reinforce this statement by clarifying whether DNMT3B is directly responsible for methylating H3K9me3-marked regions (reviewer 1, point 3) and by delineating the role of the putative HP1a motif in DNMT3B’s N-terminal region (general comments, revision plan figure 1).
Reviewer #2 (Significance (Required)):
Advance: detailed analysis of DNMT3B mutants in relation to K9me3. Builds up on previous studies. Audience: specialised audience
We thank the reviewer for their insights.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
- *In this work, Taglini et al. examine how the de novo DNA methyltransferase DNMT3B localizes to constitutive heterochromatin marked by the repressive histone modification H3K9me3. The authors utilize a previously generated DNMT3B KO colorectal carcinoma cell line, HCT116 to study recruitment and activity of DNMT3B at constitutive H3K9me3 heterochromatin. The authors noted preferential decrease of DNA methylation (DNAme) at regions of the genome marked with H3K9me3 in DNMT3B KOs. The authors then rescued the deficiency through overexpression of WT and catalytic dead DNMT3A/B and confirmed that DNA methylation increase at H3K9me3+ region in the WT DNMT3B, but not catalytically inactive mutant nor DNMT3A. To examine which protein domains may be mediating DNMT3B's recruitment to H3K9me3 regions, the authors designed a series of mutants, primarily focusing on the PWWP domain which normally recognizes H3K36me3. In the PWWP mutants, DNMT3B binding to the genome is altered, showing depletion at some H3K36me3-marked regions and gain at H3K9me3 heterochromatin, which coincides with DNAme increase at satellites. In contrast, the clinically relevant ICF1 mutation S270P, shows DNMT3B protein destabilization and no such loss of DNAme at heterochromatin. Finally, the authors truncate the N-terminal portion of DNMT3B, and saw that this region of the protein is necessary for heterochromatin localization and subsequent DNAme of H3K9me3+ regions.
The experiments are well done with extensive controls, and the results are interesting and convincing. The structure of the manuscript could be improved for clarity and flow - for example, the PWWP mutations and truncations should be mentioned and compared together. I also found the section on ICF1 mutant to be out-of-place.
As described above (reviewer 1, point 1), we propose to move these data to the supplementary materials in the revised manuscript.
- *
More emphasis should be placed on the N- terminal mutant as this region seems to be critical to heterochromatin recruitment, and this may address whether the interaction to H3K9me3 is direct or indirect.
As described above (general comments), the revised manuscript will include experiments clarifying the nature of DNMT3B’s interaction with H3K9me3. Our preliminary data support that it is an indirect interaction mediated through HP1a (revision plan figure 1).
Finally, while the epigenetic crosstalk is well-examined in this work, I would strongly urge the authors to add RNA-seq data to determine the transcriptional consequence of such chromatin disruptions (e.g. are repetitive sequences up-regulated in DNMT3B KOs?).
As suggested by the reviewer, we propose to generate and analyse RNA-seq data in the revised manuscript to understand the impact of DNMT3B on transcriptional programs.
Comments
1. A potential caveat to the study is the use of a single cell line - colorectal cancer cell HCT116 - to draw major conclusions on the function of DNMT3B. It is worth noting the Baubec et al. study examining DNMT3B recruitment to H3K36me3 was mainly performed in murine embryonic stem cells (mESCs). It would greatly strengthen the study if the authors could perform similar type of data analysis on an independent DNMT3B KO cell line. For example, does DNMT3B localize to H3K9me3 regions in WT mESCs?
As described above in response to reviewer 1, we will include analysis in an additional cell line in the revised manuscript to demonstrate that our results are generalizable beyond HCT116 cells.
2. Did the PWWP mutant W263A show the expected loss of DNAme at H3K36me3-marked regions? In other words, was there evidence of DNAme redistribution in loss at H3K36me3+ regions and inappropriate gain at H3K9me3+ regions? Please perform intersection analysis of DMRs with other epigenomic marks (e.g. H3K27me3, H3K36me3, CpG shores) in the PWWP mutants.
Our analysis of DNMT3B KO cells (manuscript figure s1d) show that losses of DNA methylation in these cells are not correlated with H3K36me3 in gene bodies suggesting that DNMT3A and DNMT1 are sufficient to compensate in maintaining their methylation in DNMT3B KO cells. To clarify this point for the DNMT3BW263A knock in clones, in the revised manuscript we will directly examine whether these cells show loss of methylation at H3K36me3 marked gene bodies in a similar analysis and add discussion of these results.
The study would also be strengthen greatly with the in addition of biochemical studies to confirm direct loss of binding, and possibly gain of H3K9me3 binding, in the DNMT3B PWWP mutants.
As detailed above (general comments, revision plan figure 1), our data suggest that DNMT3B interacts indirectly with H3K9me3 through an HP1 motif in its N-terminal region. We will undertake further biochemical studies on this interaction which will be included in the revised manuscript. Specifically we will focus on using EMSAs with synthetic nucleosomes to clarify the degree to which the HP1a interaction is responsible for binding of DNMT3B to H3K9me3 modified nucleosomes.
We also propose to undertake in vitro biochemical characterization of the effect of DNMT3B PWWP mutations on interaction with H3K36me3 using synthetic nucleosomes. However, we note that in the manuscript we have shown similar effects using two independent point mutations that are predicted to affect H3K36me3 binding (W263A and D266A) and deletion of the entire PWWP domain.
3. Examining the tracks in Figure 3A,B, the PWWP mutants showed almost indiscriminate increase across the genome, and not specifically to H3K9me3-marked regions. Would ask the authors to speculate as to why the ChIP-seq of DNMT3B mutants do not recapitulate the heterochromatin co-localization shown by immunofluorescence.
As discussed in response to reviewer 2 (point 3) we believe that the weak DNMT3B ChIP-seq signal at H3K9me3 loci is likely due to the nature of the interaction that DNMT3B has with chromatin in these regions. We will add discussion of these points to the revised manuscript.
4. It's a shame that the ICF1 mutation S270P was not characterized to the same extent as the PWWP mutants. Would consider adding WGBS for this clinically relevant mutation.
We have shown that this mutant does not produce stable protein in vitro or in our cells and we observe little difference in DNA methylation at selected loci. As WGBS is expensive, we believe that carrying out this experiment is not an efficient use of limited research resources.
5. Figure 7 - please draw in the ICF1 and the N-terminal mutations in the model figure. Also provide legends.
We will modify the manuscript to include these details in the revised manuscript.
Reviewer #3 (Significance (Required)):
This is an intersting study on a timely subject. It will be of interest to multiple fields from epigenetics to development and cancer. My expertise is in cancer, epigenetics, development.
We thank the reviewer for highlighting the broad interest of our study.
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Referee #3
Evidence, reproducibility and clarity
In this work, Taglini et al. examine how the de novo DNA methyltransferase DNMT3B localizes to constitutive heterochromatin marked by the repressive histone modification H3K9me3. The authors utilize a previously generated DNMT3B KO colorectal carcinoma cell line, HCT116 to study recruitment and activity of DNMT3B at constitutive H3K9me3 heterochromatin. The authors noted preferential decrease of DNA methylation (DNAme) at regions of the genome marked with H3K9me3 in DNMT3B KOs. The authors then rescued the deficiency through overexpression of WT and catalytic dead DNMT3A/B and confirmed that DNA methylation increase at H3K9me3+ region in the WT DNMT3B, but not catalytically inactive mutant nor DNMT3A. To examine which protein domains may be mediating DNMT3B's recruitment to H3K9me3 regions, the authors designed a series of mutants, primarily focusing on the PWWP domain which normally recognizes H3K36me3. In the PWWP mutants, DNMT3B binding to the genome is altered, showing depletion at some H3K36me3-marked regions and gain at H3K9me3 heterochromatin, which coincides with DNAme increase at satellites. In contrast, the clinically relevant ICF1 mutation S270P, shows DNMT3B protein destabilization and no such loss of DNAme at heterochromatin. Finally, the authors truncate the N-terminal portion of DNMT3B, and saw that this region of the protein is necessary for heterochromatin localization and subsequent DNAme of H3K9me3+ regions.
The experiments are well done with extensive controls, and the results are interesting and convincing. The structure of the manuscript could be improved for clarity and flow - for example, the PWWP mutations and truncations should be mentioned and compared together. I also found the section on ICF1 mutant to be out-of-place. More emphasis should be placed on the N-terminal mutant as this region seems to be critical to heterochromatin recruitment, and this may address whether the interaction to H3K9me3 is direct or indirect. Finally, while the epigenetic crosstalk is well-examined in this work, I would strongly urge the authors to add RNA-seq data to determine the transcriptional consequence of such chromatin disruptions (e.g. are repetitive sequences up-regulated in DNMT3B KOs?).
Comments
- A potential caveat to the study is the use of a single cell line - colorectal cancer cell HCT116 - to draw major conclusions on the function of DNMT3B. It is worth noting the Baubec et al. study examining DNMT3B recruitment to H3K36me3 was mainly performed in murine embryonic stem cells (mESCs). It would greatly strengthen the study if the authors could perform similar type of data analysis on an independent DNMT3B KO cell line. For example, does DNMT3B localize to H3K9me3 regions in WT mESCs?
- Did the PWWP mutant W263A show the expected loss of DNAme at H3K36me3-marked regions? In other words, was there evidence of DNAme redistribution in loss at H3K36me3+ regions and inappropriate gain at H3K9me3+ regions? Please perform intersection analysis of DMRs with other epigenomic marks (e.g. H3K27me3, H3K36me3, CpG shores) in the PWWP mutants. The study would also be strengthen greatly with the in addition of biochemical studies to confirm direct loss of binding, and possibly gain of H3K9me3 binding, in the DNMT3B PWWP mutants.
- Examining the tracks in Figure 3A,B, the PWWP mutants showed almost indiscriminate increase across the genome, and not specifically to H3K9me3-marked regions. Would ask the authors to speculate as to why the ChIP-seq of DNMT3B mutants do not recapitulate the heterochromatin co-localization shown by immunofluorescence.
- It's a shame that the ICF1 mutation S270P was not characterized to the same extent as the PWWP mutants. Would consider adding WGBS for this clinically relevant mutation.
- Figure 7 - please draw in the ICF1 and the N-terminal mutations in the model figure. Also provide legends.
Significance
This is an intersting study on a timely subject. It will be of interest to multiple fields from epigenetics to development and cancer.
My expertise is in cancer, epigenetics, development.
-
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Learn more at Review Commons
Referee #2
Evidence, reproducibility and clarity
In this manuscript, Taglini et al., describe an increased activity of DNMT3B at H3K9me3-marked regions in HCT cells. They first identify that DNA methylation at K9me3-marked regions is strongly reduced in absence of DNMT3B. Next, the authors re-express DNMT3B and DNMT3B mutant variants in the DNMT3B-KO HCT cells and assess DNA methylation by WGBS where they identify a strong preference for re-methylation of K9me3 sites. Based on genome-wide binding maps for DNMT3B, including the mutant variants, they address how the localization of DNMT3B relates to the observed changes in methylation.
Major points:
The authors show increased reduction of mCG at H3K9me3 (and K27me3) sites in absence of DNMT3B. This is based on correlating delta %mCG with histone modifications in 2kb bins. I find this approach to not fully support the major claim.
First, the correlation coefficients are very small -0.124 for K9me3 and -0.175 for K27me3, and just marginally better compared to, for example, K36me3 that does not seem to have any influence on mCG according to Sup Fig S1b. While I agree that mCG seems more reduced at K9me3 in absence of DNMT3B (e.g. in Fig 1a), is there a better way to visualize the global effect? The delta mCG Boxplots based on bins are not ideal (this applies to many figures using the same approach in the current manuscript).
Second, the calculation based on delta mCpG does not allow to see how much methylation was initially there. For example, S1b shows a median decrease of ~ 10% in K9me3 and ~7-8% in H3K4me3. What does this mean given that the starting methylation for both marks is completely different?
Following this point, the authors mention that mCG is already low at K9me3 domains in HCT cells (compared to other sites in the genome). I am curious if this may influence the accelerated loss of methylation in absence of DNMT3B? Any comments on this?
One issue is the lack of correlation in DNMT3B binding to H3K9me3 sites in WT cells (Fig 3). How does this explain the requirement for DNMT3B for maintenance of methylation at H3K9me3? While some of the tested mutants show some weak increase at K9me3 sites, these are not comparable to the strong binding preferences observed at K36me3 for the wt or delta N-term version.
Following the above comment, what about other methyltransferases in HCT cells? Could DNMT1 or DNMT3A function be altered in absence of DNMT3B, and the observed methylation changes could be indirectly influenced by DNMT3B? The authors could create a DNMT-TKO HCT cell line and re-introduce DNMT3B in this background and measure methylation to exclude that DNMT1 or DNT3A could have an influence. In this case, only H3K9me3 should gain DNA methylation.
DNMT3B lacking N-terminal shows reduced K9me3 methylation & some localization by imaging. While the presented experiments show some support for this conclusion, I suggest to re-introduce a W263A mutant lacking the N-terminal part and measure changes in DNA methylation at H3K9. This should help to test the requirement for the N-terminal regions and further indicate which protein part (PWWP or N-term) is more important in regulating the balance between K9me3 and K36me3.
In the first paragraph of the discussion, the authors state: "Our results demonstrate that DNMT3B is recruited to and methylates heterochromatin in a PWWP- independent manner that is facilitated by its N-terminal region." Same statement is found in the abstract. This contradicts the ChIP-seq results that do not indicate a recruitment of DNMT3B to heterochromatin, and the N-terminal deletions are not fully supporting a role in this targeting since there is no localization to K9me3 to begin with. While changes in methylation are observed, it remains to be determined if this is indeed through direct DNMT3B delocalization or indirectly through influencing the remaining DNMTs.
Significance
Advance: detailed analysis of DNMT3B mutants in relation to K9me3. Builds up on previous studies.
Audience: specialised audience
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Referee #1
Evidence, reproducibility and clarity
Summary:
This paper by Francesca Taglini, Duncan Sproul, and their coworkers, examines the mechanisms of DNA methylation in a human cancer cell line. They use the human colorectal cancer line HCT116, which has been very widely used to look at epigenetics in cancer, and to dissect the contribution of different proteins and chromatin marks to DNA methylation.
The authors focus on the role of the de novo methyltransferase DNMT3B. It has been shown in ES cells in 2015 that its PWWP domain directs it to H3K36me3, typically found in gene bodies. More recently, the authors showed similar conclusions in colorectal cancer (Masalmeh Nat Comm 2021). Here they examine, more specifically, the role of the PWWP. The conclusions are described below.
Major comments:
- I feel that this paper has several messages that are somewhat muddled. The main message, as expressed in the title and in the model, is that the PWWP domain of DNMT3B actively drags the protein to H3K36me3-marked regions. Inactivation of this domain by a point mutation, or removal of the Nter altogether, causes DNMT3B to relocate to other genomic regions that are H3K9me3-rich, and that see their DNA methylation increase in the mutant conditions. This first message is clear.
The second message has to do with ICF. A mutant form of DNMT3B bearing a mutation found in ICF, S270P, is actually unstable and, therefore, does not go to H3K9me3 regions. I feel that here the authors go on a tangent that distracts from message #1. This could be moved to the supp data. At any rate, HCT116 are not a good model for ICF. In addition, a previous paper has looked at the S270P mutant, and it did not seem unstable in their hands (Park J Mol Med 2008, PMID: 18762900). So I really feel the authors do not do themselves a favor with this ICF angle. 2. I feel that some major confounders exist that endanger the conclusions of the work. The most worrisome one, in my opinion, is the amount of WT or mutant DNMT3B in the cells. It is clear in figure 4C that the WT rescue construct is expressed much more than the W263A mutant (around 3 or 4 times more). Unless I am mistaken, we are never shown how the level of exogenous rescue protein compares to the level of DNMT3B in WT cells. This bothers me a lot. If the level is too low, we may have partial rescue. If it is too high, we might have artifactual effects of all that DNMT3B. I would also like to see the absolute DNA methylation values (determined by WGBS) compared to the value found in WT. From figure S1A, it looks like WT is aroun 80% methylation, and 3BKO is around 77% or so. I wonder if the rescue lines may actually have more methylation than WT? 3. I guess the unarticulated assumption is that the gain of DNA methylation seen at H3K9me3 region upon expression of a mutant DNMT3B is due to DNMT3B itself. But we do not know this for sure, unless the authors test a double mutant (PWWP inactive, no catalytic activity). I am not necessarily asking that they do it, but minimally they should mention this caveat.<br /> 4. I am confused as to why the authors look at different genomic regions in different figures. In figure 1 we are looking at a portion of the "left" arm of chr 16. But in figure 2B, we now look at a portion of the "right" arm of the same chromosome, which has a large 8-Mb block of H3K9me3, and is surprisingly lowly methylated in the 3BKO. This seems quite odd, and I wonder if there is a possible artifact, for instance mapping bias, deletion, or amplification in HCT116. Showing the coverage along with the methylation values would eliminate some of these concerns.
Minor comments:
- The WGBS coverage is not very high, around 2.5X on average, occasionally 2X. I don't believe this affects the findings, as the authors look at large H3K9me3 regions. But the info in table S2 was hard to find and it is important. I would make it more accessible.
- It would be nice to have a drawing showing exactly what part of the Nter was removed.
- some figures could be clearer. I was not always sure when we were looking at a CRISPR mutant clone (W263A) versus a piggyBac rescue.
- unless I am mistaken, all the ChIP-seq data (H3K9me3, H3K36me3 etc) come from WT cells. It is not 100% certain that they remain the same in the 3BKO, is it? This should be discussed.
Significance
Strengths:
The experiments are for the most part well done and well interpreted (save for the limitations mentioned above). The techniques are appropriate and well mastered by the team. The paper is well written, the figures are nice. The authors know the field well, which translates into a good intro and a good discussion. The bioinformatics are convincing.
Limitations:
All the work is done in a single cancer cell line. One might assume the conclusions will hold in other systems, but there is no certainty at this point.
HCT116 are not the best model system to study ICF, which mostly affects lymphocytes
At present, I feel that the biological relevance of the findings is fairly unclear. The authors report what happens when DNMT3B has no functional PWWP domain. I am convinced by their conclusions, but what do they tell us, biologically? Are there, for instance, mutant forms of DNMT3B expressed in disease that have a mutant PWWP? Are there isoforms expressed during development or in certain cell types that do not have a PWWP? In these cell types, does the distribution of DNA methylation agree with what the authors predict?
In its present state, I feel the appeal of the findings is towards a semi-specialized audience, that is interested in aberrant DNA methylation in cancer and other diseases. This is not a small audience, by the way.
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Reply to the reviewers
- General Statements
We thank all the reviewers for their time and effort in the peer-review process. We appreciate the positive reflections on the study and the feedback comments which were well thought-out and articulated. Considering these comments has led us to deeper reflections on the conceptualization of the mechanisms at play, and we hope that our responses here and revisions of the manuscript have improved the presentation of the data and our interpretation of these complex matters. As a result, we have now incorporated a new supplementary figure 5 and present a new model figure with the corresponding comments in the text.
- Point-by-point description of the revisions
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
In this manuscript Sanchez-Martinez et al investigated the function of ntc, a Drosophila homologue of FBXO7. The mechanisms by which mutations in this protein cause autosomal recessive PD are poorly understood. The protein has previously been implicated in PINK1/Parkin mitophagy however the mechanistic detail is lacking. The data presented here provide an important insight into the molecular functions of ntc as well as mitophagy in vivo in general. Ntc was found to promote ubiquitination of mitochondrial proteins which is counteracted by USP30. The basal ubiquitination regulated by these two enzymes is proposed to act as a permissive factor for the initiation of Pink1/Parkin mitophagy. The conclusions are based on strong data in vivo and there is a lot to like about this paper. The analyses are done rigorously, conclusions are balanced and well supported and there is a lot of conceptual novelty in the dataset. At the same time the paper raises some questions with regard to the role of mitophagy, at least in Drosophila. Not all of these could be answered during revisions but it would be useful to address the points outlined below.
- The functional measurements such as climbing, flight and lifespan are used to complement the data on mitophagy and mitochondrial health. However, it is clear that these do not correlate. Ntc KOs and Pink1/Parkin flies have reduced climbing and flight ability, however ntc KO does not affect mitochondrial function. In case of Pink1/Parkin the assumption is that impaired fly functionality is due to damaged mitochondria. This is clearly not the case with Ntc. How relevant is climbing/flight/lifespan to the role of Ntc in mitophagy?
- The reviewer raises a very good point, and we agree that there isn’t a strict, linear connection between the cellular process of mitophagy and the presentation of organismal neuromuscular phenotypes such as motor behaviours and lifespan. Considering this point further, starts to highlight the complexity of the situation at hand: it is becoming clear that there are many different forms of mitophagy, and these perform different functions in cellular remodelling and homeostasis. And, of course, there are many ways to interfere with neuromuscular function (as well as lifespan). So, it follows that some forms of mitophagy may dramatically impact neuromuscular homeostasis when disrupted, while others may not. We and others have described that basal mitophagy is minimally by loss of Pink1/parkin in vivo, so the organismal phenotypes clearly do not relate to this biology. But it is currently unclear how the phenotypes may relate to physiologically relevant stress-induced mitophagy as the precise nature of this, as well as the methods to experimentally manipulate it, are lacking.
Here, we are initially documenting new phenotypes for ntc, with no bias for the mechanistic cause, all of which are worthy of description to gain a holistic view of the overall contribution of this gene function to organismal integrity. It is clear from the literature that ntc/FBXO7 has multiple functions, for instance, regulating proteasome function and caspase activation, so it follows that genetic loss is likely to impinge on multiple cellular functions causing pleiotropic effects.
We have always been careful not to consider (or claim) that the organismal phenotypes, such as motor function or lifespan, are specifically due to defective mitophagy but are an overall readout of the health and functioning of the neuromuscular system. Nevertheless, these phenotypes are useful in investigating manipulations that improve or worsen the effect of Pink1/parkin (or ntc) mutants, which, a priori, may or may not also modulate mitophagy. While we have documented these new organismal phenotypes of ntc mutants and analysed the impact on basal and stress- induced mitophagy, we have not drawn a cause-effect link between the two but a correlation at least. Nevertheless, this issue raises some important considerations for the field in terms of the different kinds of mitophagy, and when they may be needed, and the impact on cells, systems or whole-organisms when they are defective. This issue is explored more in answer to Q3 below.
- Fig 3 is somewhat patchy, mitophagy is shown for USP30 and ntc KO epistasis but climbing index used in OE setting. These data do not match, and it feels like experiments that are shown are the ones that worked. The relevance of climbing index to mitophagy is unclear as mentioned above. Does KO/OE of ntc and USP30 affect levels of mitochondria, e.g. Marf used as a maker for mitochondria in Fig. 1? And if not why not, considering that ntc/USP30 but not PINK/Parkin control basal mitophagy?
- The main purpose of the data in Figure 3 was to document the impact of ntc manipulation on basal mitophagy, and by extension to link this to the known mitophagy regulator, USP30, whose loss of function has been documented to promote stress-induced mitophagy. Here, we successfully demonstrated USP30 RNAi and ntc OE cause an increase in mitophagy, and established their genetic relationship. However, it is very important to our modus operandi that we have orthogonal evidence for this relationship and understand the impact at an organismal level. As the reviewer indicates, the obvious choice that would align with the mitophagy data would be to assess whether loss of ntc prevents a USP30 RNAi phenotype. However, in our hands USP30 knockdown using the same RNAi line had no discernible impact on viability or behaviour in adult flies, precluding this experiment. Of note, we did observe a detrimental impact of USP30 knockdown on adult viability using a different RNAi line (KK) but this has 2 known off-targets so this result is unreliable. An alternative approach to genetically test the antagonistic relationship between USP30 and ntc, and equally valid in our view, is to assess whether ntc OE can counteract a USP30 OE phenotype. Here, we were fortunate that USP30 OE does indeed provoke an organismal phenotype, and this was suppressed by ntc OE consistent with the mitophagy data. It is unfortunate that the more obvious option was not workable on this occasion, but we hold that the genetic relationship was nevertheless substantiated as expected, albeit with alternative manipulations. Importantly, we established the validity of this approach by demonstrating the known genetic interaction between USP30 and parkin, whereby USP30 OE locomotor phenotype is suppressed by parkin OE (now, Fig. S3D). To substantiate this approach more clearly, we have now added to the text (lines 200-201) and figure (Fig. S3C) the lack of observable effect by USP30 knockdown as noted above.
As to the second point, assessing whether levels of mitochondria are changed by ntc/USP30 manipulations; according to the immunoblot presented in new Supplementary Figure 5A (and replicates), the levels of ATP5a are not notably changed by ntc O/E or USP30 RNAi. Marf levels are also unchanged though this is not shown. This is in line with our expectations since, as discussed above, ntc/USP30 are only one set of regulators of one type of mitophagy and several others exist. The reviewer will likely be aware that the levels of mitochondria are tightly regulated and fine-tuned for the specific need in different tissue types, and that substantial changes to mitochondrial content can be catastrophic for cell and tissue viability. While this is relatively straightforward to achieve in cultured cells, substantial reductions in mitochondrial content are non-viable in an in vivo context. Of course, in physiological conditions, rates of degradation are kept in fine-balance with biogenesis and proliferation so non-catastrophic alterations in mitochondrial content are usually counteracted by compensatory changes in proliferation or degradation.
- What is the role of mitophagy in the maintenance of mitochondrial function in Drosophila in general? Pink1/Parkin KO assumed to result in dysfunctional mitochondria due to impairment of damage-induced mitophagy which is a minor contributor to mitophagy as has previously been published by the authors and confirmed in this dataset using mitophagy reporter. At the same time ntc is clearly required for mitophagy, but mitochondria remains structurally and functionally intact in ntc KO. The most straightforward interpretation of these data is that Pink1/Parkin contribute little to mitophagy in flies and their effect on mitochondria and fly function is independent of mitophagy. Instead ntc (and USP30) strongly regulate mitophagy but mitophagy is not important for the maintenance of mitochondrial function. The effect of ntc on fly function is also independent of its role in mitophagy/mitochondria. Unless there is an alternative explanation the entire dataset would need to be reinterpreted and discussed differently.
- We agree that this is an important point raised by the study findings and needs to be clearly articulated in the text, but we don’t think it is as simple as whether ‘mitophagy’ contributes to mitochondrial and organismal integrity. First, as mentioned above, it is becoming apparent that it is crucial for the field to clearly and consciously distinguish between basal and induced forms of mitophagy. Basal mitophagy is likely, though not yet proven, to be an important component of mitochondrial quality control in metazoans and largely act in a house-keeping manner providing continual surveillance of mitochondrial quality and quantity. As such, like many other critical biological processes, it is likely to be supported in a ‘belt-and-braces’ manner by several mechanisms working in parallel with a degree of functional redundancy. In contrast, induced mitophagy is presumed to be quiescent until stimulated into action at specific times for specific purposes. For instance, it is assumed, though not yet proven, that PINK1/Parkin stress-induced mitophagy is stimulated in response to some kind of physiological stress or damage to mitochondria that may be catastrophic if left unchecked.
We and others have shown before that PINK1/Parkin are minimally involved in basal mitophagy in vivo but they are well-established to promote stress-induced mitophagy. In contrast, we have found that ntc regulates basal mitophagy and, we posit, facilitates PINK1/Parkin mitophagy by providing the initiating ubiquitination. How does this map onto the mitochondrial/organismal phenotypes? There are clear disruptions to energy-intensive, mitochondria-rich tissues inPink1/parkin mutants which are not grossly affected in ntc mutants. On the other hand, ntc mutants show a dramatically short lifespan, much shorter than Pink1/parkin mutants, while other measures of mitochondrial integrity are fine.
The Pink1/parkin phenotypes are consistent with a catastrophic loss of tissue integrity caused by the lack of a crucial protective measure (induced mitophagy) for a specific circumstance (we think, mitochondrial ‘damage’ arising from a huge metabolic burst). In contrast, while loss of ntc causes a partial (but not complete) loss of basal mitophagy, these same tissues appear to be able to cope with this impact on house-keeping QC but importantly are also able to mount a stress-induced response via Pink1/parkin still being present. On the other hand, it should be remembered that ntc is known to perform other important cellular functions, such as regulating proteasome function and caspase activation, and it is perhaps loss of these functions that causes the dramatic loss of vitality.
Importantly, although Pink1/parkin do not contribute to basal (steady-state) mitophagy, we think it is not appropriate to think of Pink1/parkin mitophagy as a ‘minor’ contribution. Since, under the particular triggering conditions of damage or stress that stimulate Pink/parkin mitophagy, apparently only Pink1/parkin can perform this role in certain Drosophila tissues, and this stress- induced mitophagy is crucial to tissue integrity, as exemplify by the fact that increasing basal mitophagy via ntc O/E still is not sufficient to rescue Pink1 mutants. In this specific context, this is a major mitophagy pathway.
In summary, the connection between mitochondrial autophagic degradation and mitochondrial/organismal health is not a simple one and we would avoid conflating different aspects of mitochondrial QC with the expectation that the consequences of their dysfunction would be the same. Nevertheless, these well-considered feedback comments have crystallised the need to elaborate these ideas in the Discussion where we have added a new section (lines 359-387).
Reviewer #1 (Significance (Required)):
Very strong genetic data presented; novel functions for human Park15 homologue in Drosophila; mechanistic insight into the ubiquitination of mitochondria by two opposing enzymes. Overall very interesting paper but interpretation is less clear which needs to be addressed.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this ms. Sanchez-Martinez and colleagues study the role of the ub ligase FBXO7, in regulating mitophagy - highlighting that mutations in FBXO7 associate with Parkinson's disease and defects in mitochondrial homeostasis. Using the fly as model, they carry out a series of expts. investigating ntc (Drosophila ortholog of FBX07) demonstrating that it can functionally rescue Parkin but not PINK1 deficiency. Expanding on this, they propose a model whereby ntc/FBX07 regulates basal mitophagy and also acts as a priming Ub-ligase for Parkin mediated mitophagy, finding that the dub USP30 counteracts these ntc function. Overall the data are robust and support the authors' conclusions and model, the manuscript is well written and I think can be accepted as is.
- We thank the reviewer for their appreciation of the work and the time taken to provide supportive feedback.
While outside the scope of this study to understand why, I find it very interesting that ntc cannot rescue the PINK1 deficient phenotype, argues that PINK1 may be having additional effects beyond regulating mitochondrial ubiquitylation.
- We entirely agree with the reviewer, this is a very intriguing finding. Indeed, there are several examples in the literature showing that PINK1 performs additional functions than just triggering mitophagy. But in the current context we interpret these data as further support for a clear mechanistic distinction between basal mitophagy and stress-induced mitophagy as discussed at length to the other reviewers’ comments.
Reviewer #2 (Significance (Required)):
Importance for understanding the role of FBX07 function - relevant for Parkinson's disease, also demonstrates a role for it in priming for PINK1/Parkin dependent mitophagy.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
In this manuscript, Sanchez-Martinez et al characterise the role of nutracker (ntc), the presumed Drosophila orthologue of human FBXO7 (whose gene is mutated in autosomal recessive PD), in mitophagy and phenotypes associated with neurodegeneration in flies (climbing index, dopaminergic neuron loss, rough eye phenotype, and others). FBXO7 (human) has been previously shown to restore parkin (not Pink1) phenotypes and mitochondrial morphology in Drosophila and implicated in Pink1-parkin mitophagy, however the role of ntc in basal mitophagy and its genetic interaction with USP30 has not been previously reported. Key findings include: evidence for functional homology between ntc and FBXO7, and that Ntc/FBXO7 is required for basal mitophagy (and reverses USP30 function) in a Pink1-parkin independent manner.
FBXO7/ntc is clearly an important regulator of mitophagy and its overexpression can suppress Parkin phenotypes, however FBX07/ntc has not been studied as intensively as Parkin and Pink1, therefore this work represents important insight into mitophagy regulators (broad interest to many overlapping fields).
However, in addition to minor points and controls requested below, some further characterisation of the signals on the mitochondria induced by ntc/FBXO7 would improve the novelty of the study and the mechanistic insight provided. For example, the authors look at total ubiquitin and pS65- Ub, whereas if they looked at specific substrates that they mention in the discussion (e.g. OMM and translocon proteins) it would allow a less speculative discussion.
Figure 1: The authors show that overexpression of ntc can rescue Parkin null phenotypes but not Pink1 phenotypes. In very similar experiments, overexpression of FBXO7 (human) has been shown to rescue Parkin phenotypes but not pink1 phenotypes (Burchell), appropriately mentioned by the authors.
The western blots are not terribly clear and would benefit from quantification (particularly H).
- We had previously performed the quantification on replicate experiments but had considered that the result was clear enough without quantification, and that including a quantification may make the figure too crowded. However, we have now added the quantification to the figure to support these results.
Specific ubiquitylated substrates like translocon proteins would be very interesting (alternatively, this could be provided in figure 7).
- We agree that this would be a very interesting aspect to investigate, but we feel that since the emphasis of the current study is clearly on the regulation of mitophagy, and not on specific substrates as has been published elsewhere (Phu et al., Mol Cell, 2020 (Ref. 42); Ordureau et al., Mol Cell, 2020 (Ref. 39)), investigating the impact of ntc and USP30 on the ubiquitination of the translocon would be a distraction to the focus of the study.
If the rough eye phenotype is highly homogenous, state in text otherwise, a relative roughness quantification would be more informative.
- The rough eye phenotype described here is indeed highly stereotyped and homogeneous. We have added this comment to the text for clarity (lines 124-126).
Figure 2: Although mainly in agreement with Burchell et al findings (that there is no disruption of mito morphology or dopaminergic neuron loss caused by ntc loss), the loss flight ability in the ntc mutant is partially discrepant with Burchell et al (results not shown in Burchell et al). Can the authors explain the discrepancy? It is important finding that the ntc functionally orthogue of FBXO7 and differs from the Burchell et al conclusions.
- The reviewer raises a good point regarding discrepant interpretations with earlier preliminary work that we didn’t specifically elaborate in the current manuscript. For the Burchell et al study we performed a series of non-exhaustive analyses with reagents that were most readily available at the time. The flight data described in Burchell et al (as ‘data not shown’) were done with what we now know to be a hypomorphic allele, which did not give a strong flight defect that we were expecting to see as a phenocopy of parkin mutants. Moreover, experiments aimed at testing the functional homology sought to rescue the only reported ntc phenotype at that time – male sterility – which did not work. It is worth noting that GAL4/UAS-mediated expression is known to be very inefficient in the male germline, so we originally interpreted the lack of rescue with this caveat in mind. It is also worth adding that, subsequent to the Burchell et al study, we have seen that expression of FBXO7 can rescue the caspase-3 activation in ntc mutant spermatocytes, supporting their functional homology. Importantly, during the Burchell et al study we did not have reagents to test the effects of ntc overexpression, obtained subsequently, which have provided compelling data that support a functional homology between ntc and FBXO7. At the time of writing the current manuscript we did not specifically revisit the Burchell et al text to note this strongly stated conclusion. We realise that this requires unequivocal clarification and thank the reviewer for pointing this out. We have amended the text to clarify this important point (lines 285-293).
Figure 7: A,B. It is not clear that mitochondria have been enriched - can the authors show on mitochondria or show the fractionation quality?
- Mitochondrial enrichment is a standard procedure in our lab, with consistently acceptable results, so we apologize for omitting a demonstration of this. We have now added these data to a new supplementary figure S5A. The corresponding information has also been added to the text (line 253). We have also extended this analysis to now show that total ubiquitination is not changed in ntc OE or USP30 RNAi, highlighting the specificity for accumulated ubiquitination on the mitochondria. This has been added to supplementary figure S5Band text lines 253-254.
C/D. The text that accompanies these figures needs further explanation and clarification and I found this result hard to understand without referring to the discussion. I think the authors are concluding that pS65 is ubiquitylated by FBXO7? I think this should be re-written in the results section. If it is a major point that the authors want to make, a complementary approach would be advised - possibly human cells/mass spectrometry.
- We apologise that this was confusing and have simplified the text accordingly to improve the clarity (lines 260-262). While this specific analysis is not a major point of the study, it provides a useful additional measure of how ntc/USP30 contributes to mitochondrial ubiquitination which *is* a key focus of the study so we have revised the Discussion to better highlight this point (lines359- 387).
As for Figure 1, specific ubiquitylated substrates at the OMM such as the translocon subunits would be informative.
- As discussed above, the role of USP30, at least, on ubiquitination of protein import in the translocon has been documented elsewhere and further specific analysis on this here would be a distraction from the main focus of the study.
Minor points
Figure 8 model and discussion: Nice discussion. However, unless protein import/ubiquitylation of translocon factors/localisation of FBXO7 to the translocon is shown in the manuscript, I would recommend more clarity in the figure legend to emphasise what is speculation based on other papers and what are new findings from the paper.
- This is a fair point and we agree that it is good to be clear about which aspects of the working model are reflections of the data presented here and which are extrapolation/speculation from the literature. We have modified the figure and the figure legend accordingly.
Reviewer #3 (Significance (Required)):
FBXO7/ntc is clearly an important regulator of mitophagy however its mechanism of action has not been studied as intensively as Parkin and Pink1, therefore this work contains important insight into mitophagy regulators.
It will be of broad interest to many overlapping fields, and has translational impact in that mitophagy is disrupted in many diseases and FBXO7 itself is mutated in Parkinson's disease.
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Referee #3
Evidence, reproducibility and clarity
In this manuscript, Sanchez-Martinez et al characterise the role of nutracker (ntc), the presumed Drosophila orthologue of human FBXO7 (whose gene is mutated in autosomal recessive PD), in mitophagy and phenotypes associated with neurodegeneration in flies (climbing index, dopaminergic neuron loss, rough eye phenotype, and others). FBXO7 (human) has been previously shown to restore parkin (not Pink1) phenotypes and mitochondrial morphology in Drosophila and implicated in Pink1-parkin mitophagy, however the role of ntc in basal mitophagy and its genetic interaction with USP30 has not been previously reported. Key findings include: evidence for functional homology between ntc and FBXO7, and that Ntc/FBXO7 is required for basal mitophagy (and reverses USP30 function) in a Pink1-parkin independent manner.
FBXO7/ntc is clearly an important regulator of mitophagy and its overexpression can suppress Parkin phenotypes, however FBX07/ntc has not been studied as intensively as Parkin and Pink1, therefore this work represents important insight into mitophagy regulators (broad interest to many overlapping fields).
However, in addition to minor points and controls requested below, some further characterisation of the signals on the mitochondria induced by ntc/FBXO7 would improve the novelty of the study and the mechanistic insight provided.
For example, the authors look at total ubiquitin and pS65-Ub, whereas if they looked at specific substrates that they mention in the discussion (e.g. OMM and translocon proteins) it would allow a less speculative discussion.
Figure 1: The authors show that overexpression of ntc can rescue Parkin null phenotypes but not Pink1 phenotypes. In very similar experiments, overexpression of FBXO7 (human) has been shown to rescue Parkin phenotypes but not pink1 phenotypes (Burchell), appropriately mentioned by the authors.
The western blots are not terribly clear and would benefit from quantification (particularly H). Specific ubiquitylated substrates like translocon proteins would be very interesting (alternatively, this could be provided in figure 7).
If the rough eye phenotype is highly homogenous, state in text otherwise, a relative roughness quantification would be more informative.
Figure 2: Although mainly in agreement with Burchell et al findings (that there is no disruption of mito morphology or dopaminergic neuron loss caused by ntc loss), the loss flight ability in the ntc mutant is partially discrepant with Burchell et al (results not shown in Burchell et al). Can the authors explain the discrepancy? It is important finding that the ntc functionally orthogue of FBXO7 and differs from the Burchell et al conclusions.
Figure 7: A,B. It is not clear that mitochondria have been enriched - can the authors show on mitochondria or show the fractionation quality? C/D. The text that accompanies these figures needs further explanation and clarification and I found this result hard to understand without referring to the discussion. I think the authors are concluding that pS65 is ubiquitylated by FBXO7? I think this should be re-written in the results section. If it is a major point that the authors want to make, a complementary approach would be advised - possibly human cells/mass spectrometry.
As for Figure 1, specific ubiquitylated substrates at the OMM such as the translocon subunits would be informative.
Minor points
Figure 8 model and discussion: Nice discussion. However, unless protein import/ubiquitylation of translocon factors/localisation of FBXO7 to the translocon is shown in the manuscript, I would recommend more clarity in the figure legend to emphasise what is speculation based on other papers and what are new findings from the paper.
Significance
FBXO7/ntc is clearly an important regulator of mitophagy however its mechanism of action has not been studied as intensively as Parkin and Pink1, therefore this work contains important insight into mitophagy regulators.
It will be of broad interest to many overlapping fields, and has translational impact in that mitophagy is disrupted in many diseases and FBXO7 itself is mutated in Parkinson's disease.
-
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Referee #2
Evidence, reproducibility and clarity
In this ms. Sanchez-Martinez and colleagues study the role of the ub ligase FBXO7, in regulating mitophagy - highlighting that mutations in FBXO7 associate with Parkinson's disease and defects in mitochondrial homeostasis. Using the fly as model, they carry out a series of expts. investigating ntc (Drosophila ortholog of FBX07) demonstrating that it can functionally rescue Parkin but not PINK1 deficiency. Expanding on this, they propose a model whereby ntc/FBX07 regulates basal mitophagy and also acts as a priming Ub-ligase for Parkin mediated mitophagy, finding that the dub USP30 counteracts these ntc function. Overall the data are robust and support the authors' conclusions and model, the manuscript is well written and I think can be accepted as is.
While outside the scope of this study to understand why, I find it very interesting that ntc cannot rescue the PINK1 deficient phenotype, argues that PINK1 may be having additional effects beyond regulating mitochondrial ubiquitylation.
Significance
Importance for understanding the role of FBX07 function - relevant for Parkinson's disease, also demonstrates a role for it in priming for PINK1/Parkin dependent mitophagy.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript Sanchez-Martinez et al investigated the function of ntc, a Drosophila homologue of FBXO7. The mechanisms by which mutations in this protein cause autosomal recessive PD are poorly understood. The protein has previously been implicated in PINK1/Parkin mitophagy however the mechanistic detail is lacking. The data presented here provide an important insight into the molecular functions of ntc as well as mitophagy in vivo in general. Ntc was found to promote ubiquitination of mitochondrial proteins which is counteracted by USP30. The basal ubiquitination regulated by these two enzymes is proposed to act as a permissive factor for the initiation of Pink1/Parkin mitophagy. The conclusions are based on strong data in vivo and there is a lot to like about this paper. The analyses are done rigorously, conclusions are balanced and well supported and there is a lot of conceptual novelty in the dataset. At the same time the paper raises some questions with regard to the role of mitophagy, at least in Drosophila. Not all of these could be answered during revisions but it would be useful to address the points outlined below. 1. The functional measurements such as climbing, flight and lifespan are used to complement the data on mitophagy and mitochondrial health. However, it is clear that these do not correlate. Ntc KOs and Pink1/Parkin flies have reduced climbing and flight ability, however ntc KO does not affect mitochondrial function. In case of Pink1/Parkin the assumption is that impaired fly functionality is due to damaged mitochondria. This is clearly not the case with Ntc. How relevant is climbing/flight/lifespan to the role of Ntc in mitophagy? 2. Fig 3 is somewhat patchy, mitophagy is shown for USP30 and ntc KO epistasis but climbing index used in OE setting. These data do not match, and it feels like experiments that are shown are the ones that worked. The relevance of climbing index to mitophagy is unclear as mentioned above. Does KO/OE of ntc and USP30 affect levels of mitochondria, e.g. Marf used as a maker for mitochondria in Fig. 1? And if not why not, considering that ntc/USP30 but not PINK/Parkin control basal mitophagy? 3. What is the role of mitophagy in the maintenance of mitochondrial function in Drosophila in general? Pink1/Parkin KO assumed to result in dysfunctional mitochondria due to impairment of damage-induced mitophagy which is a minor contributor to mitophagy as has previously been published by the authors and confirmed in this dataset using mitophagy reporter. At the same time ntc is clearly required for mitophagy, but mitochondria remains structurally and functionally intact in ntc KO. The most straightforward interpretation of these data is that Pink1/Parkin contribute little to mitophagy in flies and their effect on mitochondria and fly function is independent of mitophagy. Instead ntc (and USP30) strongly regulate mitophagy but mitophagy is not important for the maintenance of mitochondrial function. The effect of ntc on fly function is also independent of its role in mitophagy/mitochondria. Unless there is an alternative explanation the entire dataset would need to be reinterpreted and discussed differently.
Significance
Very strong genetic data presented; novel functions for human Park15 homologue in Drosophila; mechanistic insight into the ubiquitination of mitochondria by two opposing enzymes. Overall very interesting paper but interpretation is less clear which needs to be addressed.
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Reply to the reviewers
To the Editor,
We thank the reviewers for their generous efforts on behalf of our manuscript. We were very pleased to see that reviewer #1 considered our manuscript a “very detailed, high quality paper” that “serves as an important resource for the field.” And that Reviewer #2 concurred, writing that our manuscript is “valuable because it generates large datasets on the NK/ILC family from human blood that can be deposited in repositories”, and that it is of “special relevance to the HIV field because it examines viral infection effects on these subsets.”
We believe the revisions made in response to the reviewers suggestions have improved the presentation of our data. Our responses to each reviewer comment are listed below in bold font. References mentioned here are listed in a bibliography at the end of this document.Changes to the text are also highlighted in the manuscript.
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)):
Wang and colleagues present a very detailed, high quality paper describing phenotyping, transcriptional, epigenetic and functional differences between NK cells and ILCs in human peripheral blood. They overlay these studies which descriptions of differences in these populations in healthy and HIV infected (viremia, ART-treated, controllers), extending a their previous 2020 study.
Overall, this paper serves as an important resource for the field. There are areas in which the manuscript could be modified to improve clarity and detail regarding rigor.
My comments below are all addressable and therefore I class them all as 'major'.
- The authors describe ILCs as being 'permanently deleted' in HIV infection. As written, this can be misinterpreted to suggest complete ablation of this cell subset. This is clearly not the case. Moreover, there looks to be some restoration of ILCs in ART-treated participants. I suggest revising text to quantify the level of cell loss or replace the word deleted with reduced. The reviewer is correct that ILCs are not completely ablated. In response to this important point we have clarified the text, as follows:
- As indicated on page 5, we have changed the text to, “ILCs are decreased in the blood and intestinal lamina propria in people living with HIV-1, even after viremia has been suppressed by antiviral therapy”.
- In the Results on page 13, we have changed the text to “ILCs were decreased in all subgroups of people living with HIV-1”.
__- The text on page 18 was changed to, “The percentage of ILCs in the Lin–CD56– population decreased from 37.5% in HIV-1– controls to 7.34% in people living with HIV-1 who are viremic; the reduction in ILCs was not fully restored by ART (24.38%) or in spontaneous controllers (18.16%)” __
- As indicated on page 26 in the Discussion, we have changed the text to “HIV-1 infection permanently reduces ILCs but not NK cells”.
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The HIV EC are not clearly discussed in the paper and are not distinguished from viremic controllers. If ILCs are permanently reduced in this group, what does this suggest for the role of this cell subset in HIV control? Plasticity between ILC and NK cells is described. Is this plasticity relevant at all for HIV control, elite or otherwise? We thank the reviewer for asking us to clarify these important points in the manuscript:
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Though elite controllers suppress HIV-1 viremia to undetectable levels, ILC numbers are still decreased in these individuals. Additionally, we do not detect an inverse correlation between ILC numbers and viremia. Further, our previous publication showed that ILC reductions in HIV-1 infection correlate inversely with markers of systemic inflammation, for example sCD14 _(Wang et al_, 2020b)_. Like other people living with HIV-1 infection, elite controllers have elevated microbial translocation, suggestive of disturbed gut homeostasis (Brenchley _et al, 2006)_. Some studies have even reported higher rates of cardiovascular disease in elite controllers, presumably as a result of higher levels of systemic inflammation_ (Crowell et al. 2015; Caetano et al. 2022).____ Taken together, these observations suggest that ILCs play no direct role in control of HIV-1 replication. These points are discussed on page 26-27. __
- The fascinating question of plasticity between ILCs and NK cells is one we have explored extensively, both in our previous work and in the current manuscript. Plasticity has been reported between intraepithelial ILC1s and NK cells from tumor tissue, and between ILC3s and NK cells in tonsil _(Moreno-Nieves et al_, 2021; Raykova _et al, 2017; Cortez _et al, 2017)_. When ILC2s are cultured in vitro with IL-12, IFN-γ and TBX21 expression are upregulated to the levels of CD56hiNK cell (Lim _et al, 2016)_, indicating possible plasticity between ILC2 and CD56hiNK cells under certain inflammatory conditions. In HIV-1 infection, we do not detect correlations between the decrease in ILCs and increase in NK cells. In fact, the total NK cells did not change in HIV-1+ people who are viremic, on ART, or viremic controllers [(Figure 2A and 2B in (Wang _et al, 2020b)____]. Our transcriptome analysis indicates that, during HIV-1 infection, ILCs are likely depleted by inflammation-induced apoptosis (Figure 4I and Supplemental Table 6). However, whether blood ILCs (ILCPs or ILC2s) can upregulate TBX21 and EOMES to give rise to NK cells during HIV-1 infection is an interesting question worth further investigation. We now discuss the reviewer’s question on pages 27. __ III. The authors write that ILCs have a primary role in cytokine secretion and then distinguish the ILCs from NKs....but NKs also secrete cytokines. Can the authors please clarify their text?
__The reviewer is correct that, in this context, our statement is confusing. We have therefore deleted the sentence “Typical of cells with a primary role in secretion of cytokines…” on page 10. This change helps to focus the text on the specific genes that distinguish these subsets. __
- Discussion (an also Results) - The authors use pseudotime analysis to show that CD56+NK cells sit between the ILCs and CD56-NKs. When initially described in the Discussion they don't really interpret this in terms of their (and others' observations) that CD56-NKs are increased in disease. Other groups have suggested CD56-NKs are dysfunctional. Here you show different granzyme profiles between CD56+ and CD56- NKs. Elsewhere you distinguish CD56dim and CD56- NKs in terms of functionality in HIV+ donors, though these cells cluster on the pseudotime analysis. The IL-2 and CD4+ T cell data add another layer of complexity.
- Altogether, I am unclear on the authors' interpretation of their collective data.
- Can you please clarify whether you are suggesting that CD56dimNKs are a distinct from CD56+ NKs but functional as opposed to CD56-NKs that are dysfunctional? __It would be best to respond to these two questions together. It is important to remember that our manuscript describes the characterization of these cells using several techniques. __
- By flow cytometry, NK cells can be separated into CD56hi, CD56dim, and CD56neg populations (Figure 1F). Pseudotime analysis of our single cell RNA-Seq data showed that, at the transcriptional level, CD56dim and CD56neg NK cells are very similar to each other and cluster together (Figures 3A and 3F). Nonetheless, as compared with CD56dim NK cells, CD56neg NK cells express lower levels of GZMA and PRF1 (Supplemental Figure 4A), and produce less IFN-γ upon cytokine stimulation (Figures 8H and 8J). And when CD56neg NK cells are sorted and assessed by Bulk RNA-Seq, which gives deeper coverage than single cell RNA-Seq, metabolic gene expression is altered with respect to CD56dim NK cells (Figure 9).
__- Our pseudotime analysis based on single cell RNA-Seq showed that CD56hiNK cells form a distinct cluster, but that they share some transcriptional features with both the ILC cluster and the CD56dim/CD56–NK cell cluster (Figures 3A-3C and 3F). __
- In people living with HIV-1, as assessed by flow cytometry, CD56neg NK cells increase in number at the expense of CD56dim NK cells (Figure 7C). And yes, we show here that CD56neg NK cells expand in tissue culture if CD4+ T cells are depleted from the PBMCs, and addition of exogenous IL-2 prevents the switch from CD56dimNK cells to CD56–NK cells (Figures 8A-8C). These points are covered in the Results and Discussion on pages 11 and page 29-30.
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Are CD56-NKs end-stage or can they be rescued? IL-2 treatment of CD56–NK cells from people living with HIV-1 can be converted back to CD56dimNK cells, though function is not fully restored to the level of CD56dimNK cells ____(Mavilio ____et al_, 2005)_. ____In our manuscript, we showed that IL-2 or IL-15 treatment can prevent CD56dimNK cells from becoming dysfunctional CD56–NK cells, and that these cytokines maintain mTOR activity (Figure 8A-D, 8G, 8I and Figure 10). Taking together our data with the published data, CD56–NK cells appear to be an end-stage dysfunctional cell. Whether conditions can be found for full restorage of function is an important question that is worth pursuing. This point is now stated on page 30.
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CD8 T cell number remain high post ART and very much drive the ongoing inverted CD4:CD8 ratio. Have the authors consider how and if the need of these cells for IL-2 impact recovery of NK cell populations? __Two orthogonal experiments indicate that IL-2 secreted by CD4+ T cells, but not from CD8+ T cells, is responsible for the recovery of CD56dimNK cells after treatment with ART. In our ex vivo culture of PBMCs, depletion of CD4+ T cells , but not of CD8+ T cells, was associated with increased numbers of CD56–NK cells (Supplemental Figure 6A). Additionally, the IL-2 concentration in plasma from people living with HIV-1 correlated with CD4+ T cell numbers, but not with CD8+ T cell numbers (Figures 8N and 8O). __
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Discussion: It would be very helpful if the authors can pull this large volume of data together in a summary paragraph and possibly also a graphic. __We thank the reviewer for the suggestion. We have now summarized our data in the discussion (page 31). Additionally, we have added bullet points with a 2 sentence summary to accompany our graphic abstract (page 3). __
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"Thus, GZMK+CD8+T cells appear to be the adaptive counterpart of CD56hiNK cells, representing an intermediate state between cytokine producing CD4+T cells and cytotoxic CD8+T cells" For me, the 'cytokine-producing CD4+ T cells' comes from in from left field here. Can the authors please clarify or was the intent to write cytokine-producing CD8+ T cells? To clarify what we meant we need to discuss two points:
First, NK cells can be considered as the innate immune counterparts of CD8+T cells, in that both cell types are cytotoxic killer cells. In contrast, ILCs may be considered as the innate counterparts of non-cytotoxic CD4+ T helper cells. For example, like Th1 cells, ILC1 cells are TBX21+ producers of IFN-γ. And like Th2 cells, ILC2s are GATA3+ producers of IL-13. The relationship between ILCs and NK cells is similar to the relationship between CD4+T help cells and CD8+ cytotoxic T cells _(Vivier et al_, 2018)____. __
Second, previous studies showed that GZMK+CD8+T cells are distinguished from other CD8+T cells by higher expression of IL7R, TCF7, IFN-γ and TNF-α, and by decreased cytotoxic activity ____(Jonsson ____et al_, 2022)_. Thus, the relationship between GZMK+CD8+T cells and GZMK–CD8+T cells may be similar to the relationship between CD56hiNK cells (GZMK+, IL7R+, TCF7+, higher IFN-γ production and lower cytotoxicity) and cells from the CD56dim and CD56–NK cell cluster (GZMK–, IL7R–, TCF7–, lower IFN-γ production and higher cytotoxicity). In response to this comment we have modified the text on page 25-26 to make these points more clear.
VII. Methods: Were Pearson correlations applied because of the large 'n' or were data first tested for normality?
After checking the normality, nonparametric spearman correlation was performed for panels that failed the normality test. For panels with smaller n, the normality test may be not applicable, and Pearson correlation was performed.
VIII. Methods: Please clearly justify the use of t-tests throughout the manuscript rather than non-parametric based tests.
We tested the normality before performing parametric or nonparametric test. The t-test, Wilcoxon test or Mann-Whitney test used in our analysis was now specified for each panel in the legend. For panels that calculate cell percentage or numbers with smaller n, normality test may be not applicable, t-test was performed as done previously in these papers, Figure 7C and 7D in _(Wang et al_, 2020a)_, and in Figure 3 and 4 in (Xue _et al, 2022)____. We confirmed these analyses with two statisticians in our institute. __
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Methods: How many cells were acquired in flow cytometry? How many ILCs were acquired in healthy/HIV+ donors for these studies? Did this create limitations on interpretation of phenotypic data? ILCs constitute roughly 1,000 cells per million PBMCs. To assess ILCs, we acquired data from 500,000 PBMCs, or roughly 500 ILCs per sample. NK cells constitute roughly 100,000 cells per million PBMCs, we acquired data from 200,000 PBMCs, or roughly 20,000 NK cells per sample. For each patient group, whether HIV-1-negative, HIV-1 viremic, etc, we analyzed PBMCs from at least 19 blood donors. This information is now stated in the “Flow cytometry” section in “Methods”, on page 35.
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Methods: How was the cytokine concentrations used for in vitro assays determined? The cytokine concentrations were determined according to previous publication and our previous studies ____(Romee ____et al_, 2016, 2012; Wang _et al_, 2020b; Silverstein _et al_, 2022)_. We have added the related references to the “Stimulation conditions” section in “Method”, on page 36.
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Figure: In Figure 4A, should it be '+ILC- ' or '+ILC' (no negative symbol)? __Yes, the reviewer is correct. We have deleted the typo “-”. __
XII. It's unclear from you single cell analysis how many cells were acquired for each of the 4 subsets. I assume less ILCs were analyzed. If so, can you please clarify for the non-bioinformatician how your bioinformatic analysis took these differences into account?
Indeed, we were concerned that we might have too few ILCs and therefore set up conditions so that similar numbers of each cell type were assessed. To accumulate enough ILCs for single cell analysis, ILCs were sorted from 3 donors. ILCs, CD56hi, CD56dim and CD56–NK cells were sorted in parallel from the same 3 donors. The sorting strategy is shown in Supplemental Figure 1D. Equal numbers of ILCs, CD56hi, CD56dim and CD56–NK cells were sorted and then mixed together before library preparation. In total, libraries were generated from 5,210 single cells using 10 x genomics. 1,478 ILC2s, 897 ILCPs, 1,116 CD56hiNK cells, and 1,486 CD56dim and CD56–NK cells were shown in UMAP. We have added this information in Figure 3 legend.
Reviewer #1 (Significance (Required)):
Overall, this paper serves as an important resource for the field.
There are areas in which the manuscript could be modified to improve clarity and detail regarding rigor (see above). The overall message of this work for understanding HIV pathogenesis is unclear but can be addressed.
__We appreciate the reviewer’s efforts on behalf of our manuscript. By carefully addressing the reviewer’s questions and comments, we believe that the rigor of our manuscript is improved and that the message regarding HIV-1-induced abnormalities of ILCs and NK cells are clarified. __
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
Summary: This manuscript makes use of RNA sequencing, ATAC-Seq and single cell sequencing to compare transcriptomes and identify relationships between various ILC/NK cell subsets in blood from uninfected controls. The authors describe differences in genes and pathways between subsets and determine that CD56high NK cells are an intermediate-connecting cell type between ILC progenitors and CD56dim NK cells. The authors show how HIV infection (viremic, ART+ or controllers) effect ILC/NK cell gene expression and pathways. One of the genes enhanced in NK cells is AREG which the authors demonstrate to be upregulated in IL/NK subsets in response to PMAI/I stimulation or stimulation with IL-2 or IL-15. The authors demonstrate that TGFB1 or knockout of RUNX3 modulates the frequency of AREG+ NK cells, implicating the Wnt signaling pathway in AREG regulation. Authors show that in PLWH, the frequency of AREG+ NK cells is altered. Authors also report that with HIV infection there is an increase in CD56neg NK cells with corresponding loss of CD56dim cells. Using healthy control PBMCs, the authors suggest differentiation of CD56dim into CD56neg is prevented by CD4 T cell production of IL-2 but promoted by TGFB1. Also in healthy controls, the authors run metabolomics to describe how CD56dim are more metabolically functional than CD56neg and link this to MTOR activity.
Major:
- Which population(s) of NK cells (high, dim or negative for CD56) are responding to stimulation with IL-2 and IL-15 by upregulating AREG in Figure 5? Does this NK population have higher expression of receptors for IL-2 and IL-15 (in single cell seq data or by flow) and if so how does receptor expression change in PLWH? We thank the reviewer for these excellent questions. In response, we have added the new figure below to Supplemental Figure 4E. In general, CD56hi NK cells have higher AREG RNA and protein than do the other NK cell subsets. After IL-2 or IL-15 stimulation, all three NK cell populations upregulate AREG, though CD56hiNK cells produce significantly higher levels of AREG than do either CD56dim or CD56negNK cells.
__Consistent with the above results, the expression of IL2RB, IL2RG and IL15RA was higher in CD56hiNK cells than in CD56dimNK cells (new Supplemental Figure 4F). __
We examined IL2RA, IL2RB, IL2RG, and IL15RA expression in the different NK cell subsets from the three groups of people living with HIV-1, ART, viremic, and controllers. As compared with cells from HIV-1-negative people, the only clearly significant difference for these four genes was a reduction in IL2RB expression in CD56– and CD56dim NK cells from viremic people. These points are now mentioned on page 15.
- Does signaling through IL-2 or IL-15 converge on the TCF7/Wnt signaling pathway? For example, is it possible to knockdown TCF7 then stimulate with IL-2 or IL-15 and measured AREG+ cells with the idea that loss of TCF7 would result in reduced cytokine-induced activation of AREG if mediated through the Wnt pathway? Indeed, this question was very important to us and we attempted to answer it with lentiviral vector-mediated knockdown with shRNA and with electroporation of Cas9 ribonucleoprotein complexes (RNPs). Though we were successful in decreasing TCF7 protein, to render NK cells competent for lentiviral transduction or for electroporation with the Cas9 RNPs, NK cells must first be cultured for at least 7 days in high concentration IL-2. This treatment with IL-2 activates AREG production before TCF7 protein is decreased. These points are now discussed in the manuscript on page 29.
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In Figure 8 the authors demonstrate that CD4 T cells promote the maintenance of CD56dim NK cells likely through production of IL-2. Was AREG expression examined in these studies and if so could you conclude that CD4 T cells also promote AREG expression in this population? Yes, indeed, CD4+T cells, or IL-2, promote AREG production by CD56dimNK cells. Depletion of CD4+T cells from PBMCs decreased AREG production and addition of exogenous IL-2 was sufficient to restore AREG production by NK cells when CD4+ T cells were depleted (see figure below, left panel). Additionally, IL-2 neutralizing antibodies decreased AREG production by NK cells in total PBMC cultures (right panel). These results are now included as Supplemental Figure 6G and 6H in the revised manuscript.
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In Figure 8D, although significant, the increase in percentage from 2-4% of the CD56neg is a minimal change. Could a higher dose of IL-2 be tested to see more substantial changes? Similar comment for Figure 10D, although significant, the increase in percentage from 2-4% of the NK population to CD56neg is not a large change with rapamycin. Could a higher dose be tested (that does not kill the cells) or a different inhibitor be used to see more substantial changes? More robust changes would strengthen the conclusions. First to clarify, as concerns figure 8D, we believe the reviewer is referring to IL-2 neutralizing antibody, not IL-2. Regarding Figure 8D, which used IL-2 neutralizing antibody at 4 ug/ml, we tried a higher dose (10 ug/ml) but this caused cell death. We also tried longer culture time with 4 ug/ml IL-2 neutralizing antibody, and found the cell viability decreases after 7 days culture. Similarly, the limited in vitro culture time in the presence of anti-IL-2 antibody restricted experimental conditions in Figure 10D.
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In Figure 10, was the increase in pmTOR with IL-2/IL-15 stimulation specifically observed in CD56dim cells (rather than total NK cells or CD56neg cells)? This would strength the conclusion that CD56dim is more metabolically functional than CD56neg. Our data indicate that the mTOR response to IL2 in CD56–NK cells was similar to that in CD56+NK cells (including CD56dim and CD56hi) (see figure below). This result is consistent with a previous report showing that, when stimulated with exogenous IL-2, sorted CD56– NK cells become CD56dimNK cells ____(Mavilio ____et al_, 2005)_. Our data extend this observation by showing that upregulation of CD56 on CD56neg NK cells by IL-2 correlates with mTOR upregulation.
Minor
- Approximately how many ILC from PLWH were submitted for single cell sequencing: Since this cell population was depleted in HIV+, was there a sufficient number of cells to interpret/publish DEG results in Figure 4? In Figure 4, ILCs were sorted from HIV-1 negative donors and different groups of PLWH, and then these cells were subjected to bulk-RNA seq using CEL-Seq2. In Figure 4, for most blood donors, whether HIV-1 negative or PLWH, well over 1,000 ILCs were sorted and used to construct high quality libraries (see figure below, was included as new Supplemental Figure 3C). PCA plots also showed that all ILC libraries clustered together as a distinct population (Figure 4A), indicating the quality of all ILC libraries was comparable.
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On page 13 of text, it is a bit disconcerting to jump to Figure 7 then back to Figure 4. Would recommend reorganizing text or figure panels to flow better. __We have deleted the premature mention of Figure 7A. __
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Supplemental Figure 1 and 2: Dots for ILC population are purple in color but legend is mislabeled as pink color.
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Supplemental Figure 4: Dots for HIV+ controller are purple in color, but legend is mislabeled as pink in color. Thank you, these mistakes in the labeling of the colors have been corrected.
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Would recommend adding quantification of Figure 5A for all donors tested. In fact, the AREG production by CD56hi, CD56dim, CD56–NK cells and ILCs from HIV-1 negative donors were quantified in Figure 6A.
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Figure 5B for IFNg it appears that part of the positive population is not gated on and thus percentages are likely higher if the gate is adjusted. We thank the reviewer for the suggestion. The gating for IFN-γ has been adjusted in the revised manuscript, as suggested. The original Figure 5B and associated histogram Figure 5C were replaced accordingly. Please see the newly gated figure below:
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For Figure 5F, need to add to text and panel that PMA/I was used to stimulate as described in figure legend. Current figure and text read that the Wnt agonist alone was responsible for levels depicted in NK subsets. We now state that PMA+ionomycin was used to stimulate the cells in Figure 5F and 5G, and in the text (page 16 and 28).
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On the x-axis of Figure 6F-J does "Lin-TBX21+" refer to Total NK cells? If so then would recommend sticking with nomenclature "Total NK" as in Figure 6A-B. The x-axis of Figure 6F-J was changed to “total NK (Lin–TBX21+)”.
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Would recommend labeling gates for populations of interest in Supplemental Figure 5B-C, Supplement Figure 6A, Figure 8A. The populations of interest (CD56dimNK, CD56–NK, and ILCs) were labeled as suggested.
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Other groups have shown that CD56neg are increased in HIV, functionally impaired and correlate with loss of CD4 T cells. Would recommend citing their studies. The original manuscript had mentioned only Mavilio et al. The revised manuscript now has a more complete list of references ____(Cao ____et al_, 2021; Mavilio _et al_, 2005; Cocker _et al_, 2022; Alter _et al_, 2005; Barker _et al_, 2007)_. These references are cited in the Introduction (page 5) and in the Results (page 20).
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Would recommend adding quantification of Figure 8A for all donors tested. Also, for the 3rd flow plot does "NK+CD4" mean purified NK cells + autologous CD4 T cells? If so, then would clarify in figure legend. It may strengthen conclusion for IL-2/IL-15 to show differentiation of NK cells is not contact dependent with T cell via transwell assay. __Quantification for all donors in Figure 8A has been added to the revised manuscript (Figure 8A, right panel). The figure legend has been modified accordingly. As far as the comment about contact-dependence, the fact that CD56dimNK cells were maintained by IL-2 in the absence of CD4+ T cells demonstrates that direct contact with CD4+ T cells is not required. __
Reviewer #2 (Significance (Required)):
Significance: This study is valuable because it generates large datasets on the NK/ILC family from human blood that can be deposited in repositories and of special relevance to the HIV field because it examine show viral infection (controlled or not) effects these subsets.
The strengths of the study are the cohort of PBMC samples utilized (HIV-, HIV+ viremic, HIV+ ART+ and HIV+ controlled), the multi-omics approach for transcriptome and epigenetics and the in vitro mechanistic studies identifying key regulators of NK cell differentiation/function.
The study advances the field "mechanistically" by providing key targets that may be subject to therapeutic modulation in PLWH such as AREG, IL-2 signaling, IL-15 signaling, Wnt signaling, and mTOR activity (although more work will need to be done to examine these pathways using PBMCs from HIV+). This study advances the field "conceptually" by providing large datasets for others to mine if deposited.
The audience for this study "basic research" such as immunologists in the HIV field or immunologist interested in ILC/NK biology.
My field of expertise is infectious disease (HIV, SARS-CoV-2), basic immunology (ILC, NK, B cell) and autoimmune disease. Would recommend additional reviewers for assessment of metabolic genes/pathways in Figure 9-10.
__We were very pleased to see that the reviewer thought our manuscript makes a valuable contribution to HIV-1 immunology and ILC/NK biology, that it advances mechanistic understanding of pathogenesis in people living with HIV-1, and that it provides a valuable data resource. __
- In Figure 9, the metabolism related genes were defined as canonical targets of, or regulated by, MTOR signaling, in previous publications ____(Saxton & Sabatini, 2017; Bayeva ____et al_, 2012)_.
- In Figure 10, we used pMTOR, pAKT, p4EBP1, pS6 and CD71 to monitor MTOR pathway activation as reported previously by others ____(Marçais ____et al_, 2014)_. We have cited this paper on pages 23 and 24.
References for Response to Reviewers
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Brenchley JM, Price DA, Schacker TW, Asher TE, Silvestri G, Rao S, Kazzaz Z, Bornstein E, Lambotte O, Altmann D, et al (2006) Microbial translocation is a cause of systemic immune activation in chronic HIV infection. Nat Med 12: 1365–1371
Caetano DG, Ribeiro-Alves M, Hottz ED, Vilela LM, Cardoso SW, Hoagland B, Grinsztejn B, Veloso VG, Morgado MG, Bozza PT, et al (2022) Increased biomarkers of cardiovascular risk in HIV-1 viremic controllers and low persistent inflammation in elite controllers and art-suppressed individuals. Sci Rep 12: 6569
Cao W-J, Zhang X-C, Wan L-Y, Li Q-Y, Mu X-Y, Guo A-L, Zhou M-J, Shen L-L, Zhang C, Fan X, et al (2021) Immune Dysfunctions of CD56neg NK Cells Are Associated With HIV-1 Disease Progression. Front Immunol 12: 811091
Cocker ATH, Liu F, Djaoud Z, Guethlein LA & Parham P (2022) CD56-negative NK cells: Frequency in peripheral blood, expansion during HIV-1 infection, functional capacity, and KIR expression. Front Immunol 13: 992723
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Referee #2
Evidence, reproducibility and clarity
Summary:
This manuscript makes use of RNA sequencing, ATAC-Seq and single cell sequencing to compare transcriptomes and identify relationships between various ILC/NK cell subsets in blood from uninfected controls. The authors describe differences in genes and pathways between subsets and determine that CD56high NK cells are an intermediate-connecting cell type between ILC progenitors and CD56dim NK cells. The authors show how HIV infection (viremic, ART+ or controllers) effect ILC/NK cell gene expression and pathways. One of the genes enhanced in NK cells is AREG which the authors demonstrate to be upregulated in IL/NK subsets in response to PMAI/I stimulation or stimulation with IL-2 or IL-15. The authors demonstrate that TGFB1 or knockout of RUNX3 modulates the frequency of AREG+ NK cells, implicating the Wnt signaling pathway in AREG regulation. Authors show that in PLWH, the frequency of AREG+ NK cells is altered. Authors also report that with HIV infection there is an increase in CD56neg NK cells with corresponding loss of CD56dim cells. Using healthy control PBMCs, the authors suggest differentiation of CD56dim into CD56neg is prevented by CD4 T cell production of IL-2 but promoted by TGFB1. Also in healthy controls, the authors run metabolomics to describe how CD56dim are more metabolically functional than CD56neg and link this to MTOR activity.
Major:
- Which population(s) of NK cells (high, dim or negative for CD56) are responding to stimulation with IL-2 and IL-15 by upregulating AREG in Figure 5? Does this NK population have higher expression of receptors for IL-2 and IL-15 (in single cell seq data or by flow) and if so how does receptor expression change in PLWH?
- Does signaling through IL-2 or IL-15 converge on the TCF7/Wnt signaling pathway? For example, is it possible to knockdown TCF7 then stimulate with IL-2 or IL-15 and measured AREG+ cells with the idea that loss of TCF7 would result in reduced cytokine-induced activation of AREG if mediated through the Wnt pathway?
- In Figure 8 the authors demonstrate that CD4 T cells promote the maintenance of CD56dim NK cells likely through production of IL-2. Was AREG expression examined in these studies and if so could you conclude that CD4 T cells also promote AREG expression in this population?
- In Figure 8D, although significant, the increase in percentage from 2-4% of the CD56neg is a minimal change. Could a higher dose of IL-2 be tested to see more substantial changes? Similar comment for Figure 10D, although significant, the increase in percentage from 2-4% of the NK population to CD56neg is not a large change with rapamycin. Could a higher dose be tested (that does not kill the cells) or a different inhibitor be used to see more substantial changes? More robust changes would strengthen the conclusions.
- In Figure 10, was the increase in pmTOR with IL-2/IL-15 stimulation specifically observed in CD56dim cells (rather than total NK cells or CD56neg cells)? This would strength the conclusion that CD56dim is more metabolically functional than CD56neg.
Minor
- Approximately how many ILC from PLWH were submitted for single cell sequencing: Since this cell population was depleted in HIV+, was there a sufficient number of cells to interpret/publish DEG results in Figure 4?
- On page 13 of text, it is a bit disconcerting to jump to Figure 7 then back to Figure 4. Would recommend reorganizing text or figure panels to flow better.
- Supplemental Figure 1 and 2: Dots for ILC population are purple in color but legend is mislabeled as pink color.
- Supplemental Figure 4: Dots for HIV+ controller are purple in color, but legend is mislabeled as pink in color.
- Would recommend adding quantification of Figure 5A for all donors tested.
- Figure 5B for IFNg it appears that part of the positive population is not gated on and thus percentages are likely higher if the gate is adjusted.
- For Figure 5F, need to add to text and panel that PMA/I was used to stimulate as described in figure legend. Current figure and text read that the Wnt agonist alone was responsible for levels depicted in NK subsets.
- On the x-axis of Figure 6F-J does "Lin-TBX21+" refer to Total NK cells? If so then would recommend sticking with nomenclature "Total NK" as in Figure 6A-B.
- Would recommend labeling gates for populations of interest in Supplemental Figure 5B-C, Supplement Figure 6A, Figure 8A.
- Other groups have shown that CD56neg are increased in HIV, functionally impaired and correlate with loss of CD4 T cells. Would recommend citing their studies.
- Would recommend adding quantification of Figure 8A for all donors tested. Also, for the 3rd flow plot does "NK+CD4" mean purified NK cells + autologous CD4 T cells? If so, then would clarify in figure legend. It may strengthen conclusion for IL-2/IL-15 to show differentiation of NK cells is not contact dependent with T cell via transwell assay.
Significance
This study is valuable because it generates large datasets on the NK/ILC family from human blood that can be deposited in repositories and of special relevance to the HIV field because it examine show viral infection (controlled or not) effects these subsets.
The strengths of the study are the cohort of PBMC samples utilized (HIV-, HIV+ viremic, HIV+ ART+ and HIV+ controlled), the multi-omics approach for transcriptome and epigenetics and the in vitro mechanistic studies identifying key regulators of NK cell differentiation/function.
The study advances the field "mechanistically" by providing key targets that may be subject to therapeutic modulation in PLWH such as AREG, IL-2 signaling, IL-15 signaling, Wnt signaling, and mTOR activity (although more work will need to be done to examine these pathways using PBMCs from HIV+). This study advances the field "conceptually" by providing large datasets for others to mine if deposited.
The audience for this study "basic research" such as immunologists in the HIV field or immunologist interested in ILC/NK biology.
My field of expertise is infectious disease (HIV, SARS-CoV-2), basic immunology (ILC, NK, B cell) and autoimmune disease. Would recommend additional reviewers for assessment of metabolic genes/pathways in Figure 9-10.
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Referee #1
Evidence, reproducibility and clarity
Wang and colleagues present a very detailed, high quality paper describing phenotyping, transcriptional, epigenetic and functional differences between NK cells and ILCs in human peripheral blood. They overlay these studies which descriptions of differences in these populations in healthy and HIV infected (viremia, ART-treated, controllers), extending a their previous 2020 study.
Overall, this paper serves as an important resource for the field. There are areas in which the manuscript could be modified to improve clarity and detail regarding rigor.
My comments below are all addressable and therefore I class them all as 'major'.
- The authors describe ILCs as being 'permanently deleted' in HIV infection. As written, this can be misinterpreted to suggest complete ablation of this cell subset. This is clearly not the case. Moreover, there looks to be some restoration of ILCs in ART-treated participants. I suggest revising text to quantify the level of cell loss or replace the word deleted with reduced.
- The HIV EC are not clearly discussed in the paper and are not distinguished from viremic controllers. If ILCs are permanently reduced in this group, what does this suggest for the role of this cell subset in HIV control? Plasticity between ILC and NK cells is described. Is this plasticity relevant at all for HIV control, elite or otherwise?
- The authors write that ILCs have a primary role in cytokine secretion and then distinguish the ILCs from NKs....but NKs also secrete cytokines. Can the authors please clarify their text?
- Discussion (an also Results) - The authors use pseudotime analysis to show that CD56+NK cells sit between the ILCs and CD56-NKs. When initially described in the Discussion they don't really interpret this in terms of their (and others' observations) that CD56-NKs are increased in disease. Other groups have suggested CD56-NKs are dysfunctional. Here you show different granzyme profiles between CD56+ and CD56- NKs. Elsewhere you distinguish CD56dim and CD56- NKs in terms of functionality in HIV+ donors, though these cells cluster on the pseudotime analysis. The IL-2 and CD4+ T cell data add another layer of complexity.
- a. Altogether, I am unclear on the authors' interpretation of their collective data.
- b. Can you please clarify whether you are suggesting that CD56dimNKs are a distinct from CD56+ NKs but functional as opposed to CD56-NKs that are dysfunctional?
- c. Are CD56-NKs end-stage or can they be rescued?
- d. CD8 T cell number remain high post ART and very much drive the ongoing inverted CD4:CD8 ratio. Have the authors consider how and if the need of these cells for IL-2 impact recovery of NK cell populations?
- Discussion: It would be very helpful if the authors can pull this large volume of data together in a summary paragraph and possibly also a graphic.
- "Thus, GZMK+CD8+T cells appear to be the adaptive counterpart of CD56hiNK cells, representing an intermediate state between cytokine producing CD4+T cells and cytotoxic CD8+T cells" For me, the 'cytokine-producing CD4+ T cells' comes from in from left field here. Can the authors please clarify or was the intent to write cytokine-producing CD8+ T cells?
- Methods: Were Pearson correlations applied because of the large 'n' or were data first tested for normality?
- Methods: Please clearly justify the use of t-tests throughout the manuscript rather than non-parametric based tests.
- Methods: How many cells were acquired in flow cytometry? How many ILCs were acquired in healthy/HIV+ donors for these studies? Did this create limitations on interpretation of phenotypic data?
- Methods: How was the cytokine concentrations used for in vitro assays determined?
- Figure: In Figure 4A, should it be '+ILC- ' or '+ILC' (no negative symbol)?
- It's unclear from you single cell analysis how many cells were acquired for each of the 4 subsets. I assume less ILCs were analyzed. If so, can you please clarify for the non-bioinformatician how your bioinformatic analysis took these differences into account?
Significance
Overall, this paper serves as an important resource for the field.
There are areas in which the manuscript could be modified to improve clarity and detail regarding rigor (see above). The overall message of this work for understanding HIV pathogenesis is unclear but can be addressed.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Summary:
In this manuscript, Roberts et al. hypothesised that the 5:2 diet (a popular form of IF, a dietary strategy within the Intermittent fasting that is thought to increase adult hippocampal neurogenesis - AHN) would enhance AHN in a ghrelin-dependent manner. To do this, the Authors used immunohistochemistry to quantify new adult-born neurons and new neural stem cells in the hippocampal dentate gyrus of adolescent and adult wild-type mice and mice lacking the ghrelin receptor, following six weeks on a 5:2 diet. They report an age-related decline in neurogenic processes and identify a novel role for ghrelin-receptor in regulating the formation of new adult
born neural stem cells in an age-dependent manner. However, the 5:2 diet did not affect new neuron or neural stem cell formation in the dentate gyrus, nor did alter performance on a spatial learning and memory task. They conclude that the 5:2 diet used in their study does not increase AHN or improve associated spatial memory function.
Major comments:
One criticism might be the fact that many aspects are addressed at the same time. For instance it is not fully clear the role of ghrelin with respect to testing the DR effects on AHN. Although the link between ghrelin, CR and AHN is explained by citing several previous studies, it is difficult to identify the main focus of the study. Maybe this is due to the fact that the Authors analyse and comment throughout the paper the different experimental approaches used by different
Authors to study effect of DR to AHN. This is not bad in principle, since I think the Authors have a deep knowledge of this complex matter, but all this results in a difficulty to follow the flow of the rationale in the manuscript.
We appreciate the reviewer’s critique regarding the rationale of the studies presented in the manuscript.
The role of ghrelin in the regulation of AHN by dietary interventions such as CR and IF is a major interest of our lab and is the main focus of the study. We, and others, have shown that ghrelin mediates the beneficial effects of CR on AHN. It is often assumed that ghrelin will elicit similar effects in other DR paradigms. We selected the 5:2 diet since it is widely practiced by humans, but it has not been well tested experimentally.
We sought to empirically test how the neurogenic response to 5:2 differed between mice with functional and impaired ghrelin signaling.
Given that plasma ghrelin levels and AHN are reduced during ageing, we also wanted to determine if 5:2 diet could slow or even prevent neurogenic decline in ageing mice.
We will re-write the manuscript to ensure that our primary aim is clearly presented. We will also reanalyze the data, with genotype and 5:2 diet as key variables. To help maintain focus, the variable of age will be analyzed separately. This amendment will, we hope, help the reader follow the narrative of our manuscript.
Another major point: the Discussion is too long. The Authors analyse all the possible reasons why different studies obtained different results concerning the effectiveness of DR in stimulating adult neurogenesis. Thus, the Discussion seems more as a review article dealing with different methods/experimental approaches to evaluate DR effects. We know that sometimes different results are due to different experimental approaches, yet, when an effect is strong and clear, it occurs in different situations. Thus, I think that the Authors must be less shy in expressing their conclusions, also reducing the methodological considerations. It is also well known that sometimes different results can be due to a study not well performed, or to biases from the Authors.
In our discussion, we felt that it was particularly important to be as rigorous as possible in contextualizing our findings with other published data, whilst highlighting methodological differences. Our aim was to be as precise as possible when comparing findings across studies, however, this resulted in the narrative drifting from the key objectives of our study – namely, to determine the effect of 5:2 diet on neurogenesis and whether or not ghrelin-signalling regulated the process. We will amend the text of the discussion to ensure that the key points of our study are only compared and contrasted with relevant studies in the field. We thank the reviewer for their candid comment.
Minor comments:
- This sentence: "There is an age-related decline in adult hippocampal neurogenesis" cannot be put in the HIGHLIGHTS, since is a well known aspect of adult hippocampal neurogenesis
The reviewer is correct to state this. Our study replicates this interesting age-related phenomenon. However, we will remove it from the ‘Highlights’ section.
- Images in Figure 5 are not good quality.
We apologise for this oversight. We will review each figure and panel to ensure that high-resolution images, that are appropriately annotated, are used throughout the manuscript.
- In general, there are not a lot of images referring to microscopic/confocal photographs across the entire manuscript.
We structured the manuscript with a limited number of figures and associated microscope captured panels, with the aim of presenting representative images to illustrate the nature and quality of the IHC protocols. However, we will amend the figures for the revised manuscript to provide representative microscopy images, with each group included and clearly annotated.
- The last sentence of the Discussion "These findings suggest that distinct DR regimens differentially regulate neurogenesis in the adult hippocampus and that further studies are required to identify optimal protocols to support cognition during ageing" is meaningless in the context of the study, and in contrast with the main results. Honestly, my impression is that the Authors do not want to disappoint the conclusions of the previous studies; an alternative is that other Reviewers asked for this previously.
We do not believe that this statement is contradictory to our findings, as distinct DR paradigms do appear to regulate AHN in different ways. However, we agree that we can be more explicit with regards to our own study findings and will prioritize the conclusions of our study over those of the entire field during revision.
Reviewer #1 (Significance (Required)):
value the significance of publishing studies that will advance the field.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
In this manuscript, Roberts et al. investigate the effect of the 5:2 diet on adult hippocampal neurogenesis (AHN) in mice via the ghrelin receptor. Many studies have reported benefits of dietary restriction (DR) on the brain that include increasing neurogenesis and enhancing cognitive function. However, neither the mechanisms underlying the effects of the 5:2 diet, nor potential benefits on the brain, are well understood. The authors hypothesize that the 5:2 diet enhances AHN and cognitive function via ghrelin-receptor signaling. To test this, they placedadolescent and adult ghrelin receptor knockout or wild type mice on either the 5:2 or ad libitum (AL) diet for 6 weeks, followed by spatial memory testing using an object in place (OIP) task. The authors also assessed changes in AHN via IHC using multiple markers for cell proliferation and neural stem cells. The authors observed a decrease in AHN due to age (from adolescent to adult), but not due to diet or ghrelin-receptor signaling. While loss of the ghrelin-receptor impaired spatial memory, the 5:2 diet did not affect cognitive function. The authors conclude that the 5:2 diet does not enhance AHN or spatial memory.
We thank the reviewer for this summary. We note that there was a significant reduction in new neurones (BrdU+/NeuN+) cells in GHS-R null animals, regardless of age or diet (3 way ANOVA of age, genotype and diet (sexes pooled): Genotype P = 0.0290). These data suggest that the loss of ghrelin receptor signalling does impair AHN. However, we will re-analyse our data in light of reviewer 1 comments to remove ‘age’ as a variable. The new analyses and associated discussion will be presented in our revised manuscript.
The authors use a 5:2 diet but fail to provide a basic characterization of this dietary intervention. For example, was the food intake assessed? In addition to the time restriction of the feeding, does this intervention also represent an overall caloric restriction or not? According to the provided results, the 5:2 diet does not appear to regulate adult hippocampal neurogenesis contrary to the authors' original hypothesis. Did the authors measure the effects of the 5:2 diet on any other organ system? Do they have any evidence that the intervention itself resulted in any well documented benefits in other cell types? Such data would provide a critical positive control for their intervention.
This is an important point raised by the reviewer. Currently, we carefully quantified weight change across the duration of the study. However, we do not know whether the 5:2 diet reduced overall food intake or whether it impacted the timing of feeding events. To overcome this limitation, we will now test what impact the 5:2 dietary regime has on food intake and the timing of feeding. This study will allow us to correlate any changes with 5:2 diet. In addition, we have collected tibiae to quantify skeletal growth and have collected both liver and plasma (end point) samples which will be used to assess changes in the GH-IGF-1 axis. These additional studies will allow us to characterise the effects of the 5:2 paradigm on key indicators of physiological growth. These new data will be incorporated into the revised manuscript.
Based on the effects of ghrelin in other dietary interventions, the authors speculate that the effect of the 5:2 diet is similarly mediated through ghrelin. However, the authors do not provide any basic characterization of ghrelin signaling to warrant this strong focus on the GSH-R mice. While the GSH-R mice display changes in NSC homeostasis and neurogenesis, none of these effects appear to be modified by the 5:2 diet. Thus, the inclusion of the GSH-R mice does not seem warranted and detracts from the main 5:2 diet focus of the manuscript.
The role of ghrelin signalling via its receptor, GHSR, is a central tenet of our hypothesis. The loxTB-GHS-R null mouse is a well validated model of impaired ghrelin signalling, in which insertion of a transcriptional blocking cassette prevents expression of the ghrelin receptor (ZIgman et al.2005 JCI). We have previously shown that this mouse model is insensitive to calorie restriction (CR) mediated stimulation of AHN, in contrast to WT mice (Hornsby et al. 2016), justifying its suitability as a model for assessing the role of ghrelin signalling in response to DR interventions, such as the 5:2 paradigm. Whilst our findings do not support a role for ghrelin signalling in the context of the 5:2 diet studied, we did follow the scientific method to empirically test the stated hypothesis. While critiques of experimental design are welcome, the removal of these data may perpetuate publication bias in favour of positive outcomes and is something we wish to avoid.
Neurogenesis is highly sensitive to stress. The 5:2 diet may be associated with stress which could counteract any benefits on neurogenesis in this experimental paradigm. Did the authors assess any measures of stress in their cohorts? Were the mice group housed or single housed?
We thank the reviewer for raising this point. We have open-field recordings that will now be analysed to assess general locomotor activity, anxiety and exploration behaviour. Additionally, we will assess levels of the stress hormone, ACTH, in end point plasma samples. These datasets will be incorporated into the revised manuscript.
The authors state that the 5:2 diet led to a greater reduction in body weight (31%) in adolescent males compared to other groups. However, it appears that the cohorts were not evenly balanced and the adolescent 5:2 male mice started out with a significantly higher starting weight (Supplementary Figure 1). The difference in starting weight at such a young age is significantly confounding the conclusion that the 5:2 diet is more effective at limiting weight gain specifically in this group.
We thank the reviewer for highlighting this limitation. In the revision we will re-focus our discussion around the Δ Body weight repeated measures data, which compares the daily body weight of each group to its baseline value - thereby normalising any intergroup differences in starting weight. Furthermore, we will restructure figures 1 and S1 so that figure 1 presents only the repeated measure Δ Body weight data, while data for body weight both at baseline and on the final day of the study will be presented in figure S1.
The authors count NSCs as Sox2+S100b- cells. However, the representative S100b staining does not look very convincing. Instead, it would be more appropriate to count Sox2+GFAP+ cells with a single vertical GFAP+ projection. Alternatively, the authors could also count Nestin-positive cells. Additionally, the authors label BrdU+ Sox2+ S100B- cells as "new NSCs". However, it appears that the BrdU labeling was performed approximately 6 weeks before the tissue was collected (Figure 1A). Thus, these BrdU-positive NSCs most likely represent label retaining/quiescent NSCs that divided during the labeling 6 weeks prior but have not proliferated since. As such, the term "new NSC" is misleading and would suggest an NSC that was actively dividing at the time of tissue collection.
We apologise for presenting low-resolution images – these will be replaced by high-resolution images in the revised manuscript. In this study we have quantified the actively dividing BrdU+/Sox2+/S100B- cells that represent type II NSCs (rather than GFAP+ or Nestin+ type I NSCs) that have incorporated BrdU within the time period of the 6-week intervention. We appreciate the reviewer’s comments concerning the “new NSCs” terminology. We agree that we should be more specific in clarifying that the NSCs identified are those labelled during the 1st week of the 6-week intervention. We will amend this throughout the revised manuscript by re-naming these cells as 6-week old NSCs.
Overall, this manuscript lacks a clear focus and narrative. Due to a lack of an affect by the 5:2 diet on hippocampal neurogenesis, the authors mostly highlight already well-known effects of aging and Grehlin/GSH-R on neurogenesis. Moreover, the authors repeatedly use age-related decline and morbidities as a rational for their study. However, they assess the effects of the 5:2 diet on neurogenesis only in adolescent and young mature but not aged mice.
To provide greater clarity, and in accordance with reviewer 1’s comments, we will amend the text throughout to provide a focus on the data obtained. The objective of the changes will be to re-enforce the original study narrative. In relation to the use of the term ‘age-related decline’ or ‘age-related changes’, we think that these are appropriate to our study. Physiological ageing doesn’t begin at a specific point of chronological time, but is a process that is continuously ongoing. Indeed, our data is in agreement with previous studies reporting an age-related reduction in AHN at 6 months of age (e.g Kuhn et al.1996).
Minor Points
The authors combine the data from both male and female mice for most bar graphs. While this does not appear to matter for neurogenesis or behavioral readouts, there are very significant sexually dimorphic differences with respect to body size and weight. As such, male and female mice in Figure 1D,F should not be plotted in the same bar graph.
We agree that sexual dimorphism exists with respect to body size and weight. We used distinct male and female symbols for each individual animal on these bar graphs, but do agree with the reviewer that sexual dimorphic differences should be emphasized. To achieve this, we will include additional supplementary graphs presenting the sex differences in starting weight, final weight, and weight change versus starting weight.
The Figure legends are very brief and should be expanded to include basic information of the experimental design, statistical analyses etc.
We thank the reviewer for this comment. We will provide specific experimental detaisl in the revised figure legends.
Many figures include a representative image. However, it is often unclear if that is a representative image of a WT or mutant mouse, or a 5:2 or control group (Figure 2A, 3A, 4A, 5A).
We structured the manuscript with a limited number of figures and associated microscope captured panels, with the aim of presenting representative images to illustrate the nature and quality of the IHC protocols. However, we will amend the figures for the revised manuscript to provide representative microscopy images, with each group included and clearly annotated.
It would be helpful to provide representative images of DCX-positive cells in Figure 3A-F. Additionally, the authors should include a more extensive description of how this quantification was performed in the method section.
We will revise the manuscript to provide representative high-resolution Dcx+ images displaying cells of each category. The method will also be revised to include a detailed description of how the quantification and classification was performed.
The authors state "the hippocampal rostro-caudal axis (also known as the dorsoventral[] axis". However, the rostral-caudal and dorsal-central axis are usually considered perpendicular to one another.
We agree that the dorso-ventral and rostral-caudal axes are anatomically distinct. The terms are often used interchangeably in the literature, which can lead misinterpretations (e.g the caudal portion of dorsal hippocampus is often mislabelled as ventral hippocampus). To avoid ambiguity, mislabelling or misidentification, we will include a supplementary figure detailing our anatomical definitions of the rostral and caudal poles of the hippocampus, alongside representative images and the bregma coordinates.
Reviewer #2 (Significance (Required)):
Understanding the mechanisms of a popular form of intermittent fasting (5:2 diet) that is not well understood is an interesting topic. Moreover, examining the effect of this form of intermittent fasting on the brain is timely. Notwithstanding, while the authors use multiple markers to validate the effect of the 5:2 diet on adult hippocampal neurogenesis, concerns regarding experimental design, validation, and data analysis weaken the conclusions being drawn.
We thank reviewer 2 for this significance statement. We will revise the manuscript, as mentioned above, to clarify the experimental design, improve presentation of the data, and re-focus the narrative of the primary aims of the study.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
Summary
In this study, Roberts and colleagues used a specific paradigm of intermitted fasting, the 5:2 diet, meaning 5 days ad libitum food and 2 non-consecutive days of fasting. They exposed adolescent and adult wild-type mice and ghrelin receptor knockout mice (GHS-R-/-) for 6 weeks to this paradigm, followed by 1 week ad libitum food. They further used the "object in place task" (OIP) to assess spatial memory performance. At the end of the dietary regime, the authors quantified newborn neurons and neural stem cells (NSCs) by immunohistochemistry. Roberts
et al. show that the 5:2 diet does not change the proliferation of cells in the hippocampus, but report an increased number of immature neurons (based on DCX) in all the mice exposed to the 5:2 diet. This change however did not result in an increased number of mature adult-born neurons, as assessed by a BrdU birthdating paradigm. The authors further show diet-independent effects of the ghrelin receptor knockout, leading to less adult born neurons, but more NSCs in the adolescent mice and a lower performance in the OIP task.
Major comments:
The main conclusion of this study is that a specific type of intermitted fasting (5:2 diet) has no effects on NSC proliferation and neurogenesis. As there are several studies showing beneficial effects of intermitted fasting on adult neurogenesis, while other studies found no effects, it is important to better understand the effects of such a dietary paradigm.
The experimental approaches used in this manuscript are mostly well explained, but it is overall rather difficult to follow the results part, as the authors always show the 4 experimental groups together (adolescent vs adult and wt vs GHS-R-/-). They highlight the main effects comparing all the groups, which most of the time is the factor "age". Age is a well-known and thus not surprising negative influencer of adult neurogenesis. Instead of focusing on the main tested factor, namely the difference in diet, the authors show example images of the two age classes
(adolescent vs adult), which does not underly the major point they are making. Most of the time, they do not provide a post hoc analysis, so it is difficult to judge if the results with a significant main effect would be significant in a direct 1 to 1 comparison of the corresponding groups. The authors point out themselves that previous rodent studies did not use such a 5:2 feeding pattern, so having diet, age and genotype as factors at the same time makes the assessment of the diet effect more difficult.
The manuscript would improve if the authors restructure their data to compare first the diet groups (adolescent wt AL vs 5:2 and in a separate comparison adult wt AL vs 5:2) and only in a later part of the results check if the Ghrelin receptor plays a role or not in this paradigm.
We thank the reviewer for these comments. In line with comments from the other reviewers we will re-formulate the presentation of our datasets. We will remove ‘age’ as a key variable as age related changes are to be expected. For the revision, we will separate the adolescent and adult mouse data sets, plotting individual graphs for both. This should provide a clearer focus on 5:2 responses in both assessed genotypes.
This re-configuration will impact the data being analysed and, therefore, the statistical analysis presented. In our original manuscript post hoc analyses were performed, however, only significant post hoc comparisons were highlighted (e.g figure 5). Non-significant post hoc comparisons have not been presented. In the method section of the revised manuscript, we will clarify that we’ll report post hoc differences when they are observed.
During our study design, we decided to assess diet and genotype in parallel - as part of the same analysis. This seemed to us to be the most appropriate statistical method, so that we assessed dietary responses in both WT and GHS-R null mice.
As this 5:2 is a very specific paradigm, it is furthermore difficult to compare these results to other studies and the conclusions are only valid for this specific pattern and timing of the intervention (6 weeks). It remains unclear why the authors have not first tried to establish a study with wildtype mice and a similar duration as in previous studies observing beneficial effects of intermitted fasting on neurogenesis. Like this, it would have been possible to make a statement if the 5:2 per se does not increase neurogenesis or if the 6 weeks exposure were just too short.
The reviewer raises this relevant point which we considered during the study design period. Given that we had previously reported significant modulation of AHN with a relatively short period of 30% CR (14 days followed by 14 days AL refeeding (Hornsby et al.2016)), we predicted that a 6 week course on the 5:2 paradigm (totalling 12 days of complete food restriction over the 6 week period) would provide a similar dietary challenge. The fact that we did not observe similar changes in AHN with this 5:2 paradigm is notable.
The graphical representation of the data could also be improved. Below are a few
examples listed:
1.) Figure 1 B and C, the same symbol and colours are used for the adolescent and adult animals, which makes the graphs hard to read. One colour and symbol per group throughout the manuscript would be better.
We thank the reviewer for this comment. We will amend the presentation of the graphs throughout the manuscript to ensure that they are easier to interpret.
2.) The authors found no differences in the total number of Ki67 positive cells in the DG. However, Ki67 staining does not allow to conclude the type of cell which is proliferating. It would thus strengthen the findings if this analysis was combined with different markers, such as Sox2, GFAP and DCX.
Double labelling of Ki67 positive cells would allow for further insight into the identity of distinct proliferating cell populations. However, quantifying Ki67 immunopositive cells within the sub-granular zone of the GCL, as a single marker, is commonly used in studies of AHN. Given that studies of intermittent fasting, calorie restriction and treatment with exogenous acyl-ghrelin report no effect on NPC cell division, we decided not to pursue this line of inquiry.
3.) In Figure 3, the authors say that the diet increases the number of DCX in adolescent and adult mice, which is not clear when looking at the graph in 3B. Are there any significant differences when directly comparing the corresponding groups, for instance the WT AL vs the WT 5:2? It is further not clear how the authors distinguished the different types of DCX morphology-wise. The quantification in C and D would need to be illustrated by example images. Furthermore, the colour-code used in these graphs is not explained and remains unclear
While the 3 way ANOVA does yield a significant overall effect for diet, we agree that it is indeed difficult to see a difference on the graph, although the mean values of the adolescent 5:2 animals are more prominent than the AL counterparts. Mean +/- SEM will be provided in the supplementary section of the revised manuscript. Furthermore, we will clarify the method used to identify distinct DCX+ morphologies, include representative high-resolution images of each DCX+ cell category, and amend the colour coding to avoid misinterpretation.
4) In Figure 5, the authors show that the number of new NSCs is significantly increased in the adolescent GHS-R-/- mice, independent of the diet, but this increase does not persist in the adult mice. They conclude that "the removal of GHS-R has a detrimental effect on the regulation of new NSC number..." this claim is not substantiated and needs to be reformulated. As the GHS-R-/- mice have a transcriptional blockage of Ghrs since start of its expression, would such an effect on NSC regulation not result in an overall difference in brain development, as ghrelin is also important during embryonic development?
This is an interesting point. However, we disagree that the statement "the removal of GHS-R has a detrimental effect on the regulation of new NSC number..." is unsubstantiated, since it does not exclude any developmental deficits in these mice that may account for the differences observed. Nonetheless, we will rephrase the sentence to clarify our intended point and remove any ambiguity.
5.) In Figure 6, the authors asses spatial memory performance with a single behavioral test, the OIP. As these kind of tests are influenced by the animal's motivation to explore, it's anxiety levels, physical parameters (movement) etc., the interpretation of such a test without any additional measured parameters can be problematic. The authors claim that the loss of GHS-R expression impairs spatial memory performance. As the discrimination ratio was calculated, it is not possible to see if there is an overall difference in exploration time between genotypes. This would be a good additional information to display.
We thank the reviewer for this insight. We have open-field recordings that will now be analysed to assess general locomotor activity, anxiety and exploration behaviour. These data, alongside exploratory time of the mice during the OIP task will be incorporated into the revised manuscript.
Besides these points listed above, the methods are presented in such a way that they can be reproduced. The experiments contained 10-15 mice per group, which is a large enough group to perform statistical analyses. As mentioned above, the statistical analysis over all 4 groups with p-values for the main effects should be followed by post hoc multiple comparison tests to allow the direct comparison of the corresponding groups.
Reviewer #3 (Significance (Required)):
In the last years, growing evidences suggested that IF might have positive effect on health in general and also for neurogenesis. However, a few recent studies report no effects on neurogenesis, using different IF paradigms. This study adds another proof that not all IF paradigms influence neurogenesis and shows that more work needs to be done to better understand when and how IF can have beneficial effects. This is an important finding for the neurogenesis field, but the results are only valid for this specific paradigm used here, which limits its significance. The reporting of such negative findings is however still important, as it shows that IF is not just a universal way to increase neurogenesis. In the end, such findings might have the potential to bring the field together to come up with a more standardized dietary intervention paradigm, which would be robust enough to give similar results across laboratories and mouse strains, and would allow to test the effect of genetic mutations on dietary influences of neurogenesis.
We thank the reviewer for their insightful and thorough feedback.
1. 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.
The manuscript has not been revised at this stage.
2. 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.
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We have included in our replies to the reviewers a description of the amendments that we will make to our manuscript. Two requested revisions stand out as being unnecessary or cannot be provided within the scope of a revision.
The first was the request to perform the 5:2 study in older mice. This an interesting suggestion, however, the expense and time needed to maintain mice into old age (e.g >18 months) cannot be provided within the scope of our revision. In addition, given that we report no effect of the 5:2 paradigm on AHN in adolescent (7 week old) and adult (7 month old) mice, there is less justification for such a study in older mice.
The second request, that we disagree with, was to remove data relating to the GHS-R null mice (see reviewer 2, point 2). The role of ghrelin signalling via its receptor, GHS-R, is a central tenet of our hypothesis. Whilst our findings do not support a role for ghrelin signalling in the context of the 5:2 diet studied, we followed the scientific method to empirically test the stated hypothesis. While critiques of experimental design are welcome, the removal of such data may perpetuate publication bias in favour of positive outcomes and is something we wish to avoid.
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Referee #3
Evidence, reproducibility and clarity
In this study, Roberts and colleagues used a specific paradigm of intermitted fasting, the 5:2 diet, meaning 5 days ad libitum food and 2 non-consecutive days of fasting. They exposed adolescent and adult wildtype mice and ghrelin receptor knockout mice (GHS-R-/-) for 6 weeks to this paradigm, followed by 1 week ad libitum food. They further used the "object in place task" (OIP) to assess spatial memory performance. At the end of the dietary regime, the authors quantified newborn neurons and neural stem cells (NSCs) by immunohistochemistry. Roberts et al. show that the 5:2 diet does not change the proliferation of cells in the hippocampus, but report an increased number of immature neurons (based on DCX) in all the mice exposed to the 5:2 diet. This change however did not result in an increased number of mature adult-born neurons, as assessed by a BrdU-birthdating paradigm. The authors further show diet-independent effects of the ghrelin receptor knockout, leading to less adult born neurons, but more NSCs in the adolescent mice and a lower performance in the OIP task.
Major comments:
The main conclusion of this study is that a specific type of intermitted fasting (5:2 diet) has no effects on NSC proliferation and neurogenesis. As there are several studies showing beneficial effects of intermitted fasting on adult neurogenesis, while other studies found no effects, it is important to better understand the effects of such a dietary paradigm.
The experimental approaches used in this manuscript are mostly well explained, but it is overall rather difficult to follow the results part, as the authors always show the 4 experimental groups together (adolescent vs adult and wt vs GHS-R-/-). They highlight the main effects comparing all the groups, which most of the time is the factor "age". Age is a well-known and thus not surprising negative influencer of adult neurogenesis. Instead of focusing on the main tested factor, namely the difference in diet, the authors show example images of the two age classes (adolescent vs adult), which does not underly the major point they are making. Most of the time, they do not provide a post hoc analysis, so it is difficult to judge if the results with a significant main effect would be significant in a direct 1 to 1 comparison of the corresponding groups. The authors point out themselves that previous rodent studies did not use such a 5:2 feeding pattern, so having diet, age and genotype as factors at the same time makes the assessment of the diet effect more difficult. The manuscript would improve if the authors restructure their data to compare first the diet groups (adolescent wt AL vs 5:2 and in a separate comparison adult wt AL vs 5:2) and only in a later part of the results check if the Ghrelin receptor plays a role or not in this paradigm.
As this 5:2 is a very specific paradigm, it is furthermore difficult to compare these results to other studies and the conclusions are only valid for this specific pattern and timing of the intervention (6 weeks). It remains unclear why the authors have not first tried to establish a study with wildtype mice and a similar duration as in previous studies observing beneficial effects of intermitted fasting on neurogenesis. Like this, it would have been possible to make a statement if the 5:2 per se does not increase neurogenesis or if the 6 weeks exposure were just too short.
The graphical representation of the data could also be improved. Below are a few examples listed:
- Figure 1 B and C, the same symbol and colours are used for the adolescent and adult animals, which makes the graphs hard to read. One colour and symbol per group throughout the manuscript would be better.
- The authors found no differences in the total number of Ki67 positive cells in the DG. However, Ki67 staining does not allow to conclude the type of cell which is proliferating. It would thus strengthen the findings if this analysis was combined with different markers, such as Sox2, GFAP and DCX.
- In Figure 3, the authors say that the diet increases the number of DCX in adolescent and adult mice, which is not clear when looking at the graph in 3B. Are there any significant differences when directly comparing the corresponding groups, for instance the WT AL vs the WT 5:2? It is further not clear how the authors distinguished the different types of DCX morphology-wise. The quantification in C and D would need to be illustrated by example images. Furthermore, the colour-code used in these graphs is not explained and remains unclear.
- In Figure 5, the authors show that the number of new NSCs is significantly increased in the adolescent GHS-R-/- mice, independent of the diet, but this increase does not persist in the adult mice. They conclude that "the removal of GHS-R has a detrimental effect on the regulation of new NSC number..." this claim is not substantiated and needs to be reformulated. As the GHS-R-/- mice have a transcriptional blockage of Ghrs since start of its expression, would such an effect on NSC regulation not result in an overall difference in brain development, as ghrelin is also important during embryonic development?
- In Figure 6, the authors asses spatial memory performance with a single behavioral test, the OIP. As these kind of tests are influenced by the animal's motivation to explore, it's anxiety levels, physical parameters (movement) etc., the interpretation of such a test without any additional measured parameters can be problematic. The authors claim that the loss of GHS-R expression impairs spatial memory performance. As the discrimination ratio was calculated, it is not possible to see if there is an overall difference in exploration time between genotypes. This would be a good additional information to display.
Besides these points listed above, the methods are presented in such a way that they can be reproduced. The experiments contained 10-15 mice per group, which is a large enough group to perform statistical analyses. As mentioned above, the statistical analysis over all 4 groups with p-values for the main effects should be followed by post hoc multiple comparison tests to allow the direct comparison of the corresponding groups.
Minor comments:
The authors should provide more information in the figure legends and always show representative images of the parameters analyzed. Some of the images are also of low resolution and should be replaced with higher resolution images (for instance Fig. 5A). The significant P values of the multiple comparison between groups should be added into the figures.
Significance
In the last years, growing evidences suggested that IF might have positive effect on health in general and also for neurogenesis. However, a few recent studies report no effects on neurogenesis, using different IF paradigms. This study adds another proof that not all IF paradigms influence neurogenesis and shows that more work needs to be done to better understand when and how IF can have beneficial effects. This is an important finding for the neurogenesis field, but the results are only valid for this specific paradigm used here, which limits its significance. The reporting of such negative findings is however still important, as it shows that IF is not just a universal way to increase neurogenesis. In the end, such findings might have the potential to bring the field together to come up with a more standardized dietary intervention paradigm, which would be robust enough to give similar results across laboratories and mouse strains, and would allow to test the effect of genetic mutations on dietary influences of neurogenesis.
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Referee #2
Evidence, reproducibility and clarity
In this manuscript, Roberts et al. investigate the effect of the 5:2 diet on adult hippocampal neurogenesis (AHN) in mice via the ghrelin receptor. Many studies have reported benefits of dietary restriction (DR) on the brain that include increasing neurogenesis and enhancing cognitive function. However, neither the mechanisms underlying the effects of the 5:2 diet, nor potential benefits on the brain, are well understood. The authors hypothesize that the 5:2 diet enhances AHN and cognitive function via ghrelin-receptor signaling. To test this, they placed adolescent and adult ghrelin receptor knockout or wild type mice on either the 5:2 or ad libitum (AL) diet for 6 weeks, followed by spatial memory testing using an object in place (OIP) task. The authors also assessed changes in AHN via IHC using multiple markers for cell proliferation and neural stem cells. The authors observed a decrease in AHN due to age (from adolescent to adult), but not due to diet or ghrelin-receptor signaling. While loss of the ghrelin-receptor impaired spatial memory, the 5:2 diet did not affect cognitive function. The authors conclude that the 5:2 diet does not enhance AHN or spatial memory.
Major Points
- The authors use a 5:2 diet but fail to provide a basic characterization of this dietary intervention. For example, was the food intake assessed? In addition to the time restriction of the feeding, does this intervention also represent an overall caloric restriction or not? According to the provided results, the 5:2 diet does not appear to regulate adult hippocampal neurogenesis contrary to the authors' original hypothesis. Did the authors measure the effects of the 5:2 diet on any other organ system? Do they have any evidence that the intervention itself resulted in any well documented benefits in other cell types? Such data would provide a critical positive control for their intervention.
- Based on the effects of grehlin in other dietary interventions, the authors speculate that the effect of the 5:2 diet is similarly mediated through grehlin. However, the authors do not provide any basic characterization of grehlin signaling to warrant this strong focus on the GSH-R mice. While the GSH-R mice display changes in NSC homeostasis and neurogenesis, none of these effects appear to be modified by the 5:2 diet. Thus, the inclusion of the GSH-R mice does not seem warranted and detracts from the main 5:2 diet focus of the manuscript.
- Neurogenesis is highly sensitive to stress. The 5:2 diet may be associated with stress which could counteract any benefits on neurogenesis in this experimental paradigm. Did the authors assess any measures of stress in their cohorts? Were the mice group housed or single housed?
- The authors state that the 5:2 diet led to a greater reduction in body weight (31%) in adolescent males compared to other groups. However, it appears that the cohorts were not evenly balanced and the adolescent 5:2 male mice started out with a significantly higher starting weight (Supplementary Figure 1). The difference in starting weight at such a young age is significantly confounding the conclusion that the 5:2 diet is more effective at limiting weight gain specifically in this group.
- The authors count NSCs as Sox2+S100b- cells. However, the representative S100b staining does not look very convincing. Instead, it would be more appropriate to count Sox2+GFAP+ cells with a single vertical GFAP+ projection. Alternatively, the authors could also count Nestin-positive cells. Additionally, the authors label BrdU+ Sox2+ S100B- cells as "new NSCs". However, it appears that the BrdU labeling was performed approximately 6 weeks before the tissue was collected (Figure 1A). Thus, these BrdU-positive NSCs most likely represent label-retaining/quiescent NSCs that divided during the labeling 6 weeks prior but have not proliferated since. As such, the term "new NSC" is misleading and would suggest an NSC that was actively dividing at the time of tissue collection.
- Overall, this manuscript lacks a clear focus and narrative. Due to a lack of an affect by the 5:2 diet on hippocampal neurogenesis, the authors mostly highlight already well-known effects of aging and Grehlin/GSH-R on neurogenesis. Moreover, the authors repeatedly use age-related decline and morbidities as a rational for their study. However, they assess the effects of the 5:2 diet on neurogenesis only in adolescent and young mature but not aged mice.
Minor Points
- The authors combine the data from both male and female mice for most bar graphs. While this does not appear to matter for neurogenesis or behavioral read-outs, there are very significant sexually dimorphic differences with respect to body size and weight. As such, male and female mice in Figure 1D,F should not be plotted in the same bar graph.
- The Figure legends are very brief and should be expanded to include basic information of the experimental design, statistical analyses etc.
- Many figures include a representative image. However, it is often unclear if that is a representative image of a WT or mutant mouse, or a 5:2 or control group (Figure 2A, 3A, 4A, 5A).
- It would be helpful to provide representative images of DCX-positive cells in Figure 3A-F. Additionally, the authors should include a more extensive description of how this quantification was performed in the method section.
- The authors state "the hippocampal rostro-caudal axis (also known as the dorso-ventral [] axis". However, the rostral-caudal and dorsal-central axis are usually considered perpendicular to one another.
Significance
Understanding the mechanisms of a popular form of intermittent fasting (5:2 diet) that is not well understood is an interesting topic. Moreover, examining the effect of this form of intermittent fasting on the brain is timely. Notwithstanding, while the authors use multiple markers to validate the effect of the 5:2 diet on adult hippocampal neurogenesis, concerns regarding experimental design, validation, and data analysis weaken the conclusions being drawn.
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Referee #1
Evidence, reproducibility and clarity
In this manuscript, Roberts et al. hypothesised that the 5:2 diet (a popular form of IF, a dietary strategy within the Intermittent fasting that is thought to increase adult hippocampal neurogenesis - AHN) would enhance AHN in a ghrelin-dependent manner. To do this, the Authors used immunohistochemistry to quantify new adult-born neurons and new neural stem cells in the hippocampal dentate gyrus of adolescent and adult wild-type mice and mice lacking the ghrelin receptor, following six weeks on a 5:2 diet. They report an age-related decline in neurogenic processes and identify a novel role for ghrelin-receptor in regulating the formation of new adult born neural stem cells in an age-dependent manner. However, the 5:2 diet did not affect new neuron or neural stem cell formation in the dentate gyrus, nor did alter performance on a spatial learning and memory task. They conclude that the 5:2 diet used in their study does not increase AHN or improve associated spatial memory function.
Major comments:
I think that the key conclusions are convincing and no further experiments are required. Maybe some parts of the text should be rewritten (see below). The methods are presented in such a way that they can be reproduced, and the experiments adequately replicated with proper statistical analysis.
- One criticism might be the fact that many aspects are addressed at the same time. For instance it is not fully clear the role of ghrelin with respect to testing the DR effects on AHN. Although the link between ghrelin, CR and AHN is explained by citing several previous studies, it is difficult to identify the main focus of the study. Maybe this is due to the fact that the Authors analyse and comment throughout the paper the different experimental approaches used by different Authors to study effect of DR to AHN. This is not bad in principle, since I think the Authors have a deep knowledge of this complex matter, but all this results in a difficulty to follow the flow of the rationale in the manuscript.
- Another major point: the Discussioni is too long. The Authors analyse all the possible reasons why different studies obtained different results concerning the effectiveness of DR in stimulating adult neurogenesis. Thus, the Discussion seems more as a review article dealing with different methods/experimental approaches to evaluate DR effects. We know that sometimes different results are due to different experimental approaches, yet, when an effect is strong and clear, it occurs in different situations. Thus, I think that the Authors must be less shy in expressing their conclusions, also reducing the methodological considerations. It is also well known that sometimes different results can be due to a study not well performed, or to biases from the Authors.
Minor comments:
- This sentence: "There is an age-related decline in adult hippocampal neurogenesis" cannot be put in the HIGHLIGHTS, since is a well known aspect of adult hippocampal neurogenesis
- Images in Figure 5 are not good quality.
- In general, there are not a lot of images refferring to microscopic/confocal photographs across the entire manuscript.
- The last sentence of the Discussion "These findings suggest that distinct DR regimens differentially regulate neurogenesis in the adult hippocampus and that further studies are required to identify optimal protocols to support cognition during ageing" is meaningless in the context of the study, and in contrast with the main results.
Honestly, my impression is that the Authors do not want to disappoint the conclusions of the previous studies; an alternative is that other Reviewers asked for this previously.
Significance
The significance of this study relies on the fact that adult neurogenesis field (AN) has been often damaged by the search of "positive" results, aiming at showing that AN does occur "always and everywhere" and that most internal/external stimuli do increase it. This attitude created a bias in the field, persuading many scientists that a result in AN is worthy of publication (or of high impact factor publication) only when a positive result is found.
The Author cite in the Discussion the work by Gabarro-Solanas et al. (preprint), which share the same conclusion although analysing different aspect of neurogenesis. Both seems sound studies, substantially balanced in their conclusions.
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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
In this manuscript, Veen and colleagues investigate a role for hairy-related 6 (her6) and prospero homeobox 1 (prox1) in the regeneration of photoreceptors in the zebrafish retina. The candidate genes, her6 and prox1 were chosen for investigation based on initial analyses of genes implicated in the dedifferentiation of cells in the Drosophila brain. Using a chemogenetic approach to ablate long-wavelength cone photoreceptors (red cones), the authors investigate the role of her6 and prox1 in mediating the regenerative response of Müller glia and progenitors derived from these cells in the production of photoreceptors. They use morpholinos to identify that her6 and prox1 likely cross regulate each other.
The authors state that the loss of Her6 leads to an increase in the number of photoreceptors after injury. However, the marker they use is a Zpr1 antibody, which marks both red and green cones but no other cone type nor rods. Thus what they show is an increase in red and green cones, not all photoreceptors. More markers would be needed to make that point. It also remains possible that the loss of Her6 leads to an increase in the number of overall cells generated after red cone ablation and thus Her6 is not exclusively linked with photoreceptor regeneration. Previous work has shown that while the regenerative response is biased toward the production of cell-types lost as a result of injury, other cell-types are also generated (Powell et al., 2016). It would be important to follow up whether other retinal cell-types are also generated. While her6 and prox1 in conjunction might regenerate (some?) photoreceptors, her6 alone might have a broader effect.
The segue between the first and second sections of the results felt abrupt to me. I wonder whether the authors could instead follow this sequence:
- Identifying candidate genes that regulate de-differentiation in the Drosophila. 2.Investigating whether the candidate genes play a role in the dedifferentiation that Müller cells must go through in their regenerative response.
- To test point 2, set up an ablation paradigm - MTZ mediated red cone ablation etc. etc.<br /> The authors noted several genes as being mediators of dedifferentiation in the Drosophila. What was their reasoning for choosing the 2 they ended up pursuing in the zebrafish retina?
I do not understand why an increase in the number of PH3+ cells in Her6 MO treated retinae indicates a faster cell-cycle? Could it also mean that cells are stuck in the G2-M phase (marked by PH3) longer? There are other approaches to measure whether cell-cycle is sped up, as the authors suggest.
Minor suggestions to improve clarity:
Introduction: Noel et al., 2021, in my view, is not necessarily the reference most appropriate for a broad statement of how vision works. It appears to be specifically about zebrafish photoreceptors.
Methods:<br /> Fish husbandry and set up<br /> The authors state that the light/dark cycle in their fish facility is 12/12h. To my knowledge, this is not the standard practice; it is usually 14/10h light/dark respectively. (See Aleström et al., Laboratory Animals 2020, Vol. 54(3) 213-224).
No references are given for the Tg(lws2:nfsb-mCherry) and the Tg (her4.1:dRFP) lines. Additionally, the reference for Tg(gfap:eGFP) is incorrect. This should be Bernardos and Raymond 2006 Gene Expr Patterns 2006 Oct;6(8):1007-13. doi: 10.1016/j.modgep.2006.04.006.
Immunostaining fish samples<br /> 'The slides were covered with Parafilm and tissue was dampened.....'<br /> Here a reader may be confused by whether the authors refer to retinal tissue - presumably the authors mean paper tissue to create a humidified chamber.
Microscopy and analysis<br /> A bit more detail here would help - for example, are the 40x and 60x objective air or immersion objectives?
Analysis of zebrafish retinal sections<br /> It is unusual to quantify the percentage of cells expressing specific markers by counting voxels. Can the authors clarify why they took this approach?
Are the micrographs depicted in the figures, single confocal planes, max. intensity projections of several confocal planes?
mCherry labelled photoreceptors are sometimes difficult to appreciate in the micrographs of the main figures - eg. Fig 2C. Here it appears that mCherry is not expressed by the entire cell. It would help to show just the mCherry on its own.
Fig 4 -GHI - it would help to see the double labelled cells prox1 and zpr1 at higher magnification
Supplementary Fig 3 - PCNA, not GS is depicted in pink. GS not GFAP is in green?
Significance
This is an interesting study that pursues candidate genes derived from Drosophila screens to highlight pathways that might operate in the regeneration of cells that were previously ablated in the vertebrate CNS.
Approaches such as the ones used in this study contribute to our overall knowledge about coaxing regeneration in the context of the mammalian CNS.<br /> The work here should be of interest to biologists interested in regeneration.
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Referee #2
Evidence, reproducibility and clarity
The manuscript by Veen and colleagues assesses two transcription factors, and makes the novel conclusion that they regulate each other in a manner that is required for photoreceptor regeneration in zebrafish. The work is potentially exciting, because similar findings from zebrafish have found traction in translation to mammals, where regeneration of photoreceptors has surprising promise to treat blindness.
The authors have been ambitious in there approach to the problem by disrupting these genes in the adult retina, which is the appropriate context required to assess photoreceptor regeneration. Because technologies for conditional gene ablation are not very available in zebrafish, these authors use electroporation of morpholinos to accomplish their goals. Where most researchers have abandoned this very challenging approach, it seems these authors have found some success.
Together the technical feat and intriguing conclusions combine, in my opinion, to make this paper worthy of serious consideration for publication. I would hate to see it not be made available for public consumption. Its' merits are strong, but some shortcomings in communication and interpretation nevertheless should be addressed. I suggest Major and minor concerns below.
I suspect that doing further experiments would be asking a lot of the authors at this point, but I point out some possible experiments that would improve the manuscript if my suspicion is wrong. Without further experiments, I suggest much of the writing needs to be carefully qualified and less deterministic.
Major concerns:
- The authors need to quantify impacts of MO without MTZ (or with MTZ on wildtype fish without the nfsb Tg). Alternatively, the interpretation needs to be softened considerably. Observations made include increased proliferation and more PR, but these are not clearly connected by the data in a way that allows you to claim "more regeneration". A plausible alternative is that the MO was protective, and the MTZ did not kill as many PR cells when the genes were knocked down. Moreover, Figure 3 shows that only one of two proliferation markers is increased (how to explain?) and only at one timepoint, so this may be a fluke. I suggest softening the conclusions to state that gene knockdown increased proliferation and led to increased PR abundance, thus implying improved regeneration (and provide the alternative interpretation). E.g. the punchy titles of Figures 3, 5, 7 are not supported by the data; neither is text in Discussion bottom of page 15.
- Fig 5 quantification of proliferation is needed if the interpretation is about regeneration (see comment 1). Instead, the conclusions could be reworked to match the data.
- I'm unclear on why these experiments couldn't have been completed in mutant zebrafish. Are they not viable?
- Sequence and chemistry of the MO knockdown reagents must be provided. If they are similar to previously published MO reagents (several for both gene targets have been published) then this might be used to improve confidence of MO efficacy. Were the MOs modified to facilitate electroporation? The gene targets also must be listed with less ambiguity, e.g. when "prox1" is mentioned, do you mean prox1a? Without these details, the experiments fail to provide enough info to permit replication.
- A suggestion to improve the text [no need for new experiments]: The Discussion should address assumptions about MO knockdowns in regards to: a) efficacy, and b) specificity. E.g. (a) future experiments might challenge the efficacy by measuring the abundance of genes that are regulated by prox1 and her6. E.g. (b) future experiments should challenge the specificity of the MO reagents by testing to see if the same result is attained with disparate MO oligos, by phenocopy with CRISPR, performing the work in mutants (I assume rescuing the knockdown by replacing the target gene is not feasible by electroporation, but that would be ideal).
- The claim that Prox1 is in PR (Figure 4 title) is not convincing. Does the scRNA-Seq confirm this, and why not invoke this data to clarify more concretely? Figure 4A shows a lot of green prox1 signal, but that is very inconsistent with what is shown in Figure 4G, where no prox1 signal is observed in the PR. On page 12, which relates to this Figure, the authors instead say that Prox1 is detected in PR after injury (a big difference compared to title of Fig4!). Fig4I' shows some signal in the area of the PR, but the overlap of the signals is not convincing and it looks to mostly be adjacent to the zpr1 signal; maybe it is Muller glia or some other cone type, or rod cells. If it is Muller glia or rods, then the interpretation needs to be adjusted. Regardless, it is unclear if this is in LWS cones, which is presumably what regenerates after LWS cone ablation(?)
- Figures showing prox1 or Hes1 IHC (Fig 2, 4, 6, 7 & Supps) - how many replicates were evaluated (how many individual fish were assessed) to determine that these IHCs are representative.
- Some of the data, i.e. some photomicrographs of IHC, are used repeatedly in separate Figures. I cannot find a comment in the manuscript acknowledging this. Panel F is identical in Figures 3 and 5, and panel 7E is identical to Supp panel S5E. My opinion here is mixed: I think re-using these Figures is marginally ok if it is explicitly and repeatedly described (e.g. in Methods, Results, and Fig Legends), but I also think that if the authors have replicated the experiments sufficiently, then they will surely have some other micrographs to use. My opinion is tipped into grumpy and worried about good data integrity, because in both cases the lines that indicate retinal layers are drawn in different places between the replicated panels; that could happen out of sloppy-ness or instead could be a ploy to help hide the Figure recycling. I prefer to assume the authors are of good intent and have made an error (indeed the panels are all meant to represent the same control treatments) but I would not want the manuscript published without explicitly rectifying this issue. Minimally the replicate micrographs should be explicitly acknowledged. My search for other duplicated panels was not exhaustive.
Minor points:
- a) Page numbers and line numbers would make it less work to prepare a constructive critique of this paper. Similarly, the Figures need Figure numbers.
- b) On the histograms, does each dot represent an individual fish? (i.e. an independent biological replicate).
- c) It would be lovely to learn that left vs. right eyes were used as internal controls in each case, and then the authors could plot the difference between control & treatment within each individual. Perhaps this would allow normalizations or more powerful statistical tests, and then the PCNA data would be more aligned with the conclusions, for example.
- d) Figure 5: expected to see quantification of PH3 here, akin to Figure 3.
- e) P. 6 secondary antibodies probably did not come from ZIRC
- f) More should be done to acknowledge past papers examining Her6, Hes1 and Prox1 in vertebrate retina.
- g) I do not see how the final section of the manuscript (beginning with "Insulinoma" to the end of the Discussion is relevant to the paper. A very odd ending to this manuscript. Some sentences (especially beginning the section with a topic sentence) would be need to be added if this writing is to remain.
- h) The final two sentences of the Abstract were interesting - these ideas are unfortunately not Discussed again later in the manuscript.
- i) What is the source of the transgenic zebrafish line Tg(lws2:nfsb-mCherry) ? Is it maybe from Wang...Yan 2020 PLOS BIOL (PMID: 32168317)? If yes, it would be ideal to provide an allele number. If no, construction of this line should be described.
- j) Bottom page 4 says "Two transgenic lines used were crossed" but only one line is mentioned.
- k) Then on page 7, the text says "Zebrafish line Tg(her4.1:dRFP/gfap:GFP/lws2:nfsb-mCherry) for red cone ablation, ..." which muddies the waters even further.
- l) When the antibody zpr1 is described, it is mentioned as a "zinc finger" (many instances throughout). This is incorrect, and the words "zinc finger" can be removed.
- m) It would be useful to state in Methods, and at first occurrence in figure legends, that the antibody ZPR1 labels double cones (the red & green cones), and these make up about half of the cone photoreceptor population. (i.e. not all cones are evaluated in this work).
- n) Figure 2 desperately needs a panel describing methodological timeline, similar to Fig 1D. It is really hard to figure what happened when (e.g. when did ablation occur? When was the MO delivered?). This also should be described more explicitly in the Methods, which seem quite vague on this point: Electroporated fish went straight into MTZ?
- o) Throughout the authors refer to injury, e.g. hpi = hours post injury. I don't think this represents the methods very well at all, because they have ablated the cells, not injured them. Injured cells don't regenerate (because they are not dead). This miswording contributes to confusion interpreting the Figures, which are not decipherable as stand-alone items.
- p) There is a really weird yellow dotted line that spans between and ACROSS adjacent panels in Figure 2. It covers the white line separating panels F' & G', and then again in F" and G".
- q) Fig 2, it is evident that Hes1 protein is not eliminated so you cannot claim it is "not expressed". It is perhaps reduced in abundance, but signal is still obviously present.
- r) Title of Figure 6 needs to rewritten: LLPS may be occurring, but until you manipulate both LLPS and Prox1 together, you cannot claim that they act through one another.
- s) Figure 7 title needs to be rewritten: PR are not quantified here.
- t) Figure 6: I am deeply incredulous that applying any chemical to zebrafish for only two minutes can alter cell differentiation, except perhaps via toxicity. Perhaps examples of similar impacts can be provided from the literature to make it seem more credible that the mechanism here is LLPS in retinal cells.
The following minor comments are all captured under the notion that the Figure Legends all need to be re-written by a senior colleague. Figures+legends should be interpretable as stand-alone items. All these Figures fail this minimal standard. Below are some issues, but really I'd suggest starting with a blank slate.<br /> - u) Figure 1 must mention Drosophila. So very very confusing to read this believing it is about zebrafish.<br /> - v) Figure 1 what is "deadpan"?<br /> - w) Fig 2 title, how do you know these progenitors are MG-derived?<br /> - x) Fig 2, define abbreviation MG<br /> - y) Fig 2 title, Hes1 is less abundant, but that might be from alternative mechanisms other than "reduced expression" (e.g. altered PTMs, increased clearance, LLPS, etc)<br /> - z) Fig 3 legend is a jumble of oddity. At least three distinct signals are supposedly labelled in pink(?). separately, What about the mCherry - is it also in pink?<br /> - aa) Most Figures: we know they are micrographs, so you don't need to lead the Description saying "micrographs of...". Instead, describe the logic of the experiment and the overall interpretations.<br /> - bb) All Figures: it is really odd to list the data (averages & variances, including implausible significant digits on each) for every treatment - that is what the histograms are meant to convey.<br /> - cc) Figure 4 should send the reader to the Supplemental so they know that the no-primary control experiment is available.<br /> - dd) Fig 6B legend - explain what the chemicals are meant to do (e.g. "block LLPS").<br /> - ee) Fig 6 define "2m" = 2 minutes?<br /> - ff) Several more abbreviations are not defined: hpi, ONL, etc...
Significance
The manuscript by Veen and colleagues assesses two transcription factors, and makes the novel conclusion that they regulate each other in a manner that is required for photoreceptor regeneration in zebrafish. The work is potentially exciting, because similar findings from zebrafish have found traction in translation to mammals, where regeneration of photoreceptors has surprising promise to treat blindness.
Together the technical feat and intriguing conclusions combine, in my opinion, to make this paper worthy of serious consideration for publication. I would hate to see it not be made available for public consumption. Its' merits are strong, but some shortcomings in communication and interpretation nevertheless should be addressed
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Referee #1
Evidence, reproducibility and clarity
The authors interrogate the roles of prox1a and her6 in red/green cone photoreceptor regeneration in zebrafish. Using scRNAseq, they find evidence that her6 is expressed in MG and suggest it is downregulated in Müller glia-derived progenitor cells during retinal regeneration. Further, they show that knockdown of her6 leads to an increase in the rate of cone PR regeneration and suggest that this is due to increased proliferation of retinal progenitors. The authors then demonstrate that prox1a is expressed in differentiated PRs and that knockdown inhibits PR regeneration. An exploration of the role of Liquid-Liquid Phase<br /> Separation (LLPS) in prox1a signaling is provided. Finally, the authors show that her6 knockdown leads to increased prox1a expression and that prox1a knockdown leads to loss of her6 expression, suggesting both factors impact expression of the other to regulate the kinetics of PR regeneration in the zebrafish retina.
Major comments:
- As presented, the "downregulation" of her6 in MG-derived progenitors is not convincing due to a discrepancy between the single cell data and antibody staining. For "downregulation" to be the case, MG and/or progenitor cells would need to be expressing her6 and then lose it over time during regeneration. The single cell data are consistent with that showing expression of her6 in quiescent and proliferating MG, but the antibody staining is not. In addition, regarding the single cell data, the colors used to discriminate early PRs and PRs are nearly identical. The authors need to make clear which clusters correspond to MG-derived progenitor cells using clear labeling. Regarding antibody labeling, prior to cone PR ablation, the expression of Her6 (ie Hes1 staining) appears to be localized to interneurons and RGCs, not MG - yet the single cell data suggest this is not the case. Either the single cell data or the antibody labeling may be correct, but not both. The authors should provide a figure showing co-labeling of Her6/Hes1 and a MG marker such as GS or GFAP. In the absence of that result, the antibody data is most consistent with her6 expression either not being expressed in MG and MG-derived progenitor cells or expressed in only a subset of progenitors - both of which conflict with the single cell data.
- The her6 MO results are not convincing with respect to data interpretation. Knockdown of her6 results in more cone PRs at 72 hpi and more progenitor proliferation at the same time point (as assessed by pH3 immunostaining). For an increase in progenitor proliferation to explain the increase in cone PRs the observation would need to precede the increase in cones, not be coincident with it. Alternative hypotheses need to be explored, for instance, whether her6 downregulation alters cell fate choices in progenitor cells. The precocious increase in prox1 expression at 48 hpi (Figure 6A-E) would be consistent with that idea, leading either to precocious cone differentiation or a stronger bias toward the red/green cone PR fate.
- The connection to Liquid-liquid Phase Separation (LLPS) is the weakest component of the study given the following issues:
- a. Prox1 staining as punctate and/or liquid-like assembly associated is not convincingly demonstrated, this would require much higher magnification, quantification, and co-localization with factors known to aggregate in liquid-like assemblies.
- b. The reagents used to modulate LLPS are not specific to Prox1 and will alter all LLPS-associated signaling events.
- c. What assay was used to set "effective and consistent" outcomes at a concentration of 5% 1,6-HD anda treatment time of 2 minutes? Was toxicity or any other assay performed to assess the specificity of 1,6-HD effects in vivo at this concentration?
- d. Shouldn't the regenerated cone cells be expressing the lws2:nfsb-mCherry transgene? This is especially troubling given that the lws2:nfsb-mCherry transgene is evident at the periphery in both conditions whereas the zpr1antibody (i.e., Arr3a expression) appears to differentially label more central areas of the retina.
- e. Controls are needed to demonstrate that the expression of other transcription factors is normal following 1,6-HD treatment.
- f. Controls are needed to show that zpr1 staining / Arr3a expression is not selectively altered by 1,6-HD treatment, eg are other markers of red/cones similarly altered?
- Statistical methods are not provided for the Dros portion of the study. Please indicate which statistical tests were used and what corrections performed for multiple comparisons.
- A control is need to show that the antibody against mammalian Hes1 labels Her6 in zebrafish.
Minor Comments:
- Please provide alleles for all transgenic resources used as this will help to ensure others are able to replicate these findings and/or use equivalent resources for their own research.
- "Zebrafish injury model" section states that two transgenic lines were used to create a PR ablation line but only one line is listed? Please clarify. Also the larval ablation model should be included in the Methods.
- Montgomery et al ablated rods not cones. As cells exhibit differential sensitivity to cell ablation methods - including rods and cones - it would be preferable if a reference for NTR/Mtz-mediated cone cell ablation was cited.
- Figure S2: Since fish between 10-12 months were used, there is no need to mention the ablation results with the younger fish as it is unrelated to the study.
- 24 hpi as first observation of MG-derived progenitors (Fig. S3D-D') is very weak, data is not convincing. Please update the figure or revise the manuscript. Figure 2 is much better, simply referencing Figure 2E' would suffice.
- Edit needed: "They began proliferating at 48hpi, as indicated by clusters of PCNA+ cells across the inner nuclear cell layer (INL; Figure S3E-E'), also observed by at 72 and 96 hpi (Figure S3F-F' and G-G' EE', outlined).
- her6 has been previously implicated in retinal regeneration previously and references to these studies should be included in the intro and/or discussion. See: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8643038/<br /> https://bmcdevbiol.biomedcentral.com/articles/10.1186/1471-213X-6-36<br /> https://www.jneurosci.org/content/34/43/14403
- Please confirm her6 MO-based downregulation with a more quantitative method.
- "DamID" should be defined at the first instance (first paragraph of Results) as DNA adenine methyltransferase Identification.
- zpr-1 is an antibody not a protein and should not be capitalized (per "Zpr1+ cells").
- According to ZFIN, prox1 is now prox1a, the authors use both. It would be helpful to stay consistent and use the most recent nomenclature to refer to prox1a.
Referees cross-commenting
Reviewer #2 / Major concern #1: Unclear how one assesses the effects of gene knockdown on regeneration in the absence of cell ablation? The reviewer should clarify what "impacts" they would like quantified (e.g., developmental effects, etc) . For instance, assessing effects of gene knockdown on PR number developmentally (with egg injections of morpholino and/or sgRNAs for Crispants) would help to account for potential gene knockdown effects on progenitor differentiation (i.e., causing a fate bias toward red cones) or protection (e.g., absence of normal levels of cell death/TUNEL).
Reviewer #2 / Major concern #8: Repeated micrographs: In my view this should not be done at all. Please use different examples of control data between comparisons of her6 and prox1a knockdowns - even if these experiments were al performed in parallel there should be additional control samples from each assay and across a minimum of three biological repeats.
Reviewer #3, Paragraph 2 ("The authors state that the loss of Her6..."): Pulse-chase experiments demonstrating an increase in the number of newly generated red cones - by virtue of co-labeling with pulse marker and Lws2 transgene - would help to address this concern and clarify the degree of bias exhibited in the red cone ablation paradigm (an issue discussed by all reviewers and which the authors are familiar with, eg, DOI: 10.1186/s13064-017-0089-y)
Significance
This work is significant in interrogating the function of two classic factors associated with regulation of neurogenesis and neuronal differentiation in Drosophila in the context of cone photoreceptor regeneration in zebrafish. My expertise lies in the latter paradigm and I have restricted my evaluation to that portion of the study. The novelty of the study is diminished somewhat by recent reports of the role of Notch signaling in retinal regeneration in zebrafish - thus, it would follow that a major signaling component of the Notch pathway, Hes1/Her6, would likely be involved as well. Indeed, expression changes for her6 during regeneration have been previously reported (see refs above). However, the present study does add a functional characterization which is a significant advance. The advent of stimulation of retinal regenerative capacity in mice by Tom Reh and colleagues adds intrigue to the study of retinal regeneration in zebrafish as the insights generated are being applied in a way that suggests possible relevance to human disease. Thus defining conditions that lead to accelerated retinal regeneration is of widespread interest. However, several issues raised in the detailed review above diminish my enthusiasm for the study overall.
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Reply to the reviewers
General Statements:
We want to thank the reviewers for their time in assessing our study, their positive feedback and their constructive comments that we address here. We have carefully assessed each reviewers’ comments and address them point-by-point below. We appreciate that the reviewers consider our study to be relevant and advance the field in better understanding mitochondrial stress responses.
There is a consensus as to why we have inhibited rather than depleted PHGDH via genetic means. PHGDH knockout is developmentally lethal at embryonal day 13.5, and therefore whole-body knockout crossings were not an option (Yoshida et al. JBC 2004). Furthermore, we and colleagues have shown that mitochondrial disease induces a complex systemic response including e.g., metabokines FGF21 and GDF15, secreted by the affected muscle and heart and modifying metabolism in the whole organism, indicating that tissue-specific knockouts are not optimal to resolve mechanisms in pathophysiology. Further, potential serine supplementation from other tissues could mask the effects on the muscle. Next, the slowly progressive phenotype of the mitochondrial myopathy mouse, fully manifesting close to 2 years of age, make double-transgenic strategies resource-intensive. Therefore, a PHGDH inhibitor, the specificity of which we carefully explore, was the approach of choice.
Serine rich diet: We did consider a serine-rich diet. However, our evidence indicates that exogenous serine is not sufficient to rescue the phenotype in cultured cells. This suggests that the enzymatic intracellular localization of de novo serine synthesis is of crucial importance.
Off-target effects: We agree and are aware that using a small-molecule molecule for pharmacological inhibition bears risks of off-target effect, as Arlt et al. 2021 reported for NCT-503 neuroblastoma cells lines. In agreement with the reviewers about the relevance of our results, the observation that we do not observe any meaningful alterations in WT muscle, even at the advanced age where metabolic muscle fitness is already challenged, whilst the myopathy phenotype worsens in myopathic mice support an on-target effect of NCT-503.
Therefore, we had carefully considered the suggested experiments during the initial study and decided that PHGDH inhibitor was the best choice to answer our questions about importance of de novo serine biosynthesis.
Reviewer #1 (Evidence, reproducibility and clarity):
In this manuscript the authors describe interesting results regarding amino acid metabolism under conditions of mitochondrial stress. The authors used a selective PHGDH inhibitor (compound NCT503), and document that de novo serine synthesis is essential to sustain phospholipid biosynthesis, redox homeostasis, mitochondrial function, and mitochondrial protein synthesis in Deletor mice and in cell culture under mitochondrial stress. Interestingly, serine supplementation does not rescue those metabolic alterations, indicating a specific mitochondrial stress-dependent mechanism of serine utilization by the cells.<br /> In addition, the authors attempted to explore the role of serine in phospholipid biosynthesis under in vivo and ex vivo mitochondrial stress, and this is the weakest part of the manuscript. The specific reduction of mitochondrial PE using the PHGDH is interesting, and it can provide some clues into how mitochondrial membranes are synthetized under mitochondrial stress, but additional experimental approaches should be incorporated to generate a more robust body of evidence.
In summary, the manuscript should be improved by using additional experimental approaches. In addition, genetic intervention through PHGDH gain or loss of function can help to elucidate the molecular mechanisms.
We thank the reviewer for this proposition. As explained above in detail, knockout of PHGDH in mice is lethal in embryogenesis. Secondly, the cell culture studies show that in a mitochondrial disease background, cell-intrinsic de novo serine biosynthesis becomes essential. Therefore, the phenotype of a conditional knockout in skeletal muscle is likely to be drastic and does not reflect the situation of an adult-onset disease. Thirdly, if the gain- and loss of mutant double transgenics would live, the Deletor mice are an actual slowly progressing disease model, which manifests the phenotype at around two years. Therefore, this experiment takes three years, is not feasible and was considered to be of little informativeness. We carefully explored the specificity of PHGDH inhibition by NCT503 and found it to serve best the questions asked.
The authors could also incorporate metabolomic studies using C13 serine or C13 glucose supplemented culture medium to differentiate carbons that come from extracellular serine or from de novo synthesis.
We thank reviewer #1 for her/his comments. The exogenous serine supplementation shows minor rescue of the phenotype in cultured cells but decreases somewhat the mitochondrial integrated stress response markers in serine-containing medium, suggesting some amelioration of the PHGDH inhibition.
We have now incorporated new data of D3-serine flux in cells to the manuscript (p.14, FigS3G, p.33). These data indicate that some serine uptake occurs by the cells and that is not significantly affected by mitochondrial translation inhibition (actinonin), even if the combination of PHGDH plus actinonin is not viable.
Manuscript Figure S3G. D3-serine uptake in C2C12 cells with and without actinonin. Normal non-labelled serine was used as a negative control for D3-serine contamination. D3-serine amounts were measured in culture media and in cells; biological replicates (n=3). In media, fold change (FC) was calculated relative to the sample with normal serine media without actinonin. In cells, FC was determined against cells in D3-serine without actinonin. No traces of D3 label were detected in normal serine samples. ACT = actinonin.
Additional questions: Is PHDGH subcellular localization modulated under mitochondrial stress conditions?
This is an interesting question. The insufficient resolution in muscle sections did not give a conclusive answer. We have, however, performed new immunofluorescence experiments in cells to investigate this potential mechanism and used a newly generated PHGDHKO cell line as a negative control (Rev Fig.1). The conclusions have been added to the manuscript (page 14, FigS4E,F, p.34). In essence, no altered localization of PHGDH in cells is observed – the localization appears to be cytoplasmic. The increasing PHGDH amount in increasing actinonin concentration is apparent, however.
Revision Figure 1. Immunofluorescent staining of HEK293 and C2C12 cells. WT and PHGDHKO HEK293 cells were used as controls for the PHGDH antibody. (Hoechst staining of nucleus, blue; anti-PHGDH, green; mitochondrial outer membrane protein TOM20, red. EtOH = ethanol; ACT = actinonin; INH = PHGDH inhibitor.
Is the extracellular serine uptake impaired under mitochondrial stress?
As explained above, we have now incorporated data of D3-labeled serine uptake in cells to the manuscript, quantifying the uptake from the media and the levels in the cells. Mitochondrial translation inhibition by actinonin does not affect uptake, indicating that the uptake per se is not impaired. However, the de novo synthesis being essential in metabolic stress strongly points to the intracellular site to be important.
While the extracellular serine can only little compensate for de novo synthesis, our new data, qPCR analysis on muscle of all mouse groups to quantify serine tRNA levels (MTTS1) indicates the levels to be increased, suggesting insufficient charging of the tRNA (MTTL1 as negative control; Rev Fig. 2). In addition, the presumed mitochondrial serine transporter SFXN1 is upregulated on protein level (p.11, Fig S2H, p.32). These data suggest that cell-intrinsic serine synthesis supports mitochondrial translation in metabolic stress situations.
Revision Figure 2. RNA expression of mitochondrial tRNAs for leucine (MTTL1) and serine (MTTS1) in skeletal muscles of wild type (WT) and Deletor (DEL) mice; RT-qPCR. WT VEH n=6, DEL VEH n=5, WT INH n=7, DEL INH n=8. VEH = vehicle; INH = PHGDH inhibitor; FC = fold change.
ATF4 is a transcription factor that regulates amino acid transport. In this connection, is ATF4-dependent serine transporters modulated under mitochondrial stress or under PHGDH treatment?
As explained above, SFXN1 transporter was upregulated in protein level. In postmitotic skeletal muscle, the responses are under ATF5, as shown in Forsström, Jackson et al. Cell Metab 2019.
Regarding the alteration in redox homeostasis, mitochondrial function and mitochondrial protein synthesis. Is the alteration of phospholipid synthesis upstream of all of those mitochondrial alterations?
The authors are unclear of what the reviewer means by “all those mitochondrial alterations”. The disease in the Deletor mice is caused by dominant patient-homologous mutation of mitochondrial DNA helicase Twinkle, and in the cell culture model we block mitochondrial protein synthesis with actinonin. Therefore, the primary defect in both mice and cells is intramitochondrial, in mtDNA replication and protein synthesis, and the stress responses are a consequence of the primary mitochondrial dysfunction. The consequent secondary stagewise mitochondrial integrated stress response, ISRmt, affects both mitochondria and rest of the cell, with effects in metabolism and nuclear genome transcription. We have pioneered the discovery of ISRmt in mice and humans with mitochondrial defects/diseases in several studies (e.g., Cell Metab 2016, 2017, 2019, 2020). This response includes a remarkable remodeling of one-carbon metabolism, with major changes in methyl cycle, transsulfuration and nucleotide synthesis of the whole cell. PS synthesis is dependent of methyl groups deriving from the one-carbon cycle -driven methyl cycle. Therefore, the original mitochondrial replisome dysfunction causes a stagewise, progressive disease process, which is upstream of all the other responses. Phospholipid synthesis alteration, however, has high potential to modify mitochondrial membranes that can aggravate disease during its progression.
The temporal metabolomics of cultured cells did show PE accumulation at later time points than on mitochondrial translation or other crucial cellular metabolites, suggesting its alterations to be a consequence rather than upstream. Indeed, further studies are needed to dig deeper into the dynamics of phospholipid synthesis in mitochondrial dysfunction.
Additionally, in my opinion the results should be reorganized, because in the current format the manuscript is fragmented, and several panels lose the symmetry.
The authors are unclear what the reviewer means by the panels losing symmetry. Without suggestions it is hard to make changes, but we have carefully reviewed the clarity of the presentation.
Major concerns.
Figure 1
The authors should incorporate the Deletor mice amino acid levels in muscle. How does the PHGDH inhibitor treatment modulate the other non-essential amino acids?
We have quantified all 11 non-essential amino acids from Deletor muscle by targeted metabolomics in combination or individually and added the new graphs (p.10, Figure S2D,E, p.32).
Manuscript Figure S2D. Total non-essential amino acid quantification (NEAAs) from targeted metabolomics of skeletal muscles of WT and DEL mice. WT VEH n=6, DEL VEH n=5, WT INH n=7, DEL INH n=8. VEH = vehicle; INH = PHGDH inhibitor. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001.
Manuscript Figure S2E. Individual NEAAs from targeted metabolomics of skeletal muscles of WT and DEL mice. WT VEH n=6, DEL VEH n=5, WT INH n=7, DEL INH n=8. VEH = vehicle; INH = PHGDH inhibitor. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001.2. The authors should incorporate the data of WT + vehicle and wt + NCT503 mice in figures 1C, 1D, 1F and 1G, in order to compare properly the effects of PHGDH inhibitorThe authors should incorporate the data of WT + vehicle and wt + NCT503 mice in figures 1C, 1D, 1F and 1G, in order to compare properly the effects of PHGDH inhibitor.The authors should incorporate the data of WT + vehicle and wt + NCT503 mice in figures 1C, 1D, 1F and 1G, in order to compare properly the effects of PHGDH inhibitor.
The authors should incorporate the data of WT + vehicle and wt + NCT503 mice in figures 1C, 1D, 1F and 1G, in order to compare properly the effects of PHGDH inhibitor.
We agree with the reviewer`s notion to depict all groups. No COX- fibres exist in our vehicle or inhibitor-treated WT mice and we have added this data into the manuscript in p.31, commented on in p.6, Figure S1B, also below).
Manuscript Figure S1B. Histochemical analysis of combined cytochrome-c-oxidase (COX) and succinate dehydrogenase (SDH) activity in muscles of treated WT mice. (Brown fibres indicate high COX activity, translucent – low COX activity). Lower panel shows immunohistochemical detection of the mTORC1 downstream target - phosphorylated ribosomal S6 (p-S6). INH = PHDGH inhibitor.
Figure 1H. Are there any effect of PHGDH in the mtDNA of WT mice? The authors might incorporate this information, to show properly that mitochondrial stress led to dependence of serine to sustain muscle homeostasis.
In addition to the mtDNA deletion analysis, we have assessed mtDNA copy number via qPCR (p.27, Figure S1D). No mtDNA deletions exist in WTs and their mtDNA copy number raised slightly. These new data are included in p. 6 and Figure S1D, p.31.
Manuscript Figure S1D. Mitochondrial DNA copy number analysis in muscles of WT and DEL mice. Measured with qPCR (n=5-8/group). VEH = vehicle; INH = PHGDH inhibitor. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001.
Figure 2.<br /> Interestingly the authors observe a decrease in total mitochondrial lipids content, and an increase in mitochondrial PE content in Deletor mice compared to WT mice. These results suggest an alteration in the phospholipids flux between mitochondria and endoplasmic reticulum in this model of mitochondrial disease. Moreover, PHGDH treatment appears to be able to rescue this alteration. Some question related this issue: What is the expression of genes involved in the balance PC, PE, PS? Are the PSS1, PSS2, PSD and PEMT expression altered?
Previous Deletor muscle studies cohorts showed non-altered PEMT in diseased mice of similar age nor was PEMT and PSD significantly altered RNAseq data from patients in contrast to PHGDH (Forsstrom et al., 2019; Rev Fig.3). 20-months old Deletor do not show any alteration in PEMT (qPCR quantification below) when analysed from total muscle. Whether these are changed in single fibers (mosaic manifestation of the disease) we cannot exclude.
Revision Figure 3. Left: RNA expression of PEMT in skeletal muscles of 20-months-old WT and DEL mice. Measured with qPCR; n=9. Right: Gene expression of PEMT, PSD, and PHGDH enzymes in muscles of mitochondrial myopathy patients. Measured with RNA-Seq; n=8 in control; n=4 in patients. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001.
Regarding the phospholipid synthesis. Is mitochondria or endoplasmic reticulum ultrastructure altered in Deletor mice muscle? The authors should explain the possible mechanisms.
We have extensively characterized the pathology in Deletor muscle in publications previously (Tyynismaa et al. PNAS 2005; Tyynismaa Hum Mol Genet 2010 for morphology, especially, but also as a part of the physiology studies Nikkanen et al. Cell Metab 2016; Khan et al. Cell Metab 2017; Forsström, Jackson et al. Cell Metab 2019 and Mito et al. Cell Metab 2022). The morphological changes in mitochondria are quite extensive, and these are comparable to those found in patients with similar mutations: enlarged mitochondria with distorted and few cristae, various inclusions. We presume the reviewer means sarcoplasmic reticulum in skeletal muscle. The extent of the muscle pathology in vivo suggests that ER structure is changed as everything else is: the diseased muscle fibers are full of abnormal mitochondria in the Deletors, with only few traces of myofibers or fibrils. These fibers become more prevalent after PHGDH inhibition. Furthermore, the mice – WT and Deletors – show age-induced prevalence of non-pathology-related accumulation of sacroplasmic aggregates (so called tubular aggregates) as a known feature of C57Bl6 mice.
New Figure S1 C, p.31 and below (Rev Fig.4): Ultrastructure of Deletor muscle shows enlarged mitochondria both inside the fibers (Fig S1C left panel, arrows) and subsarcolemmally, further aggravated by PHGDH inhibition. Tubular aggregates, as shown in the inhibitor treated Deletor in the Figure S1C seen in the light-microscopic image on the right (arrows), are part of the mouse substrain characteristics, not disease associated. These changes are also, as white aggregates inside the fibers in all genotypes and treatment groups We now added the light and electron microscopic image analysis to Figure S1 C. We now added the electron microscopic images to the manuscript as S1C (commented on p.6), indicating the aggravated phenotype of PHGDH inhibitor.
Revision Figure 4. Left: Panel from the Manuscript Fig. S1C. Representative images of transmission electron microscopy (TEM) in skeletal muscles of WT and DEL mice. Black arrows – enlarged mitochondria. Right: Representative images from light microscopy (LM) of muscles of the same groups as in Left. Black arrows – tubular aggregates. VEH = vehicle; INH = PHGDH inhibitor.
We have also performed analysis of mitochondrial ultrastructure in cells (see below) showing specific lipid accumulation. As mentioned above the alterations in PE levels are detected metabolically at later time points and after substantial loss of mitochondrial translation.
We added this new data as Figure S3E, p.33, commented on p.6.
Manuscript Figure S3E. Representative images of TEM analysis of 12h-treated C2C12 cells. The cells were incubated in media with or without serine and treated with either actinonin, PHGDH inhibitor or a combination of both. White arrow – myelinosome-like membranous lipid aggregates; M = mitochondria. INH = PHGDH inhibitor; ACT = actinonin; Ser = serine.
Supplementary figure 3D<br /> Based on the metabolomic studies, the authors propose a time-dependent decrease in PSAT1 and phosphoserine in cells under mitochondrial stress (Figure S3D). To elucidate the direct role of PHGDH, the authors should analyze the phosphoserine and different phospholipid (described in figure 2E) in presence of PHGDH inhibitor. This will help to understand the link between the endogenous serine synthesis and mitochondrial PE accumulation.
The temporal metabolomics show a time-dependent decrease of the metabolite phosphoserine (not PSAT1). Here, we show the PE and PC dynamics at 6 and 24 hours. These data have now been added to the manuscript, figure S3I, p.33, commented on page 14.
Manuscript Figure S3I. Normalised PC and PE pools in C2C12 cells measured with untargeted metabolomics after treatments with actinonin, PHGDH inhibitor, or a combination of two for 6 and 24 hours. n=6-11/group; ACT = actinonin; INH = PHGDH inhibitor.
Figure 3H shows a decrease in phosphoserine in the presence of PHGDH inhibitor but this figure is asymmetric compared to figure 3I. Can the authors use another experimental approach to detect the specific mitochondria phospholipid levels (used in Figure 2 for instance)?
Figure 3H shows a decrease in phosphoserine in the presence of mitochondrial dysfunction induced through actinonin alone. Figure 3I shows a further decrease in phosphoserine when actinonin-treated cells are treated with the PHGDH inhibitor (phosphoserine is marked now also in our genetic model of mtDNA depletion, Figure 3I). The data are from untargeted metabolomics, parallel analysed samples, and therefore are comparable for the levels.
We have now grouped the time-wise dynamics of the annotated phospholipids from the untargeted metabolomics decreasing at a late stage of the temporal treatment, suggesting that the consequences on of mitochondrial dysfunction by translation inhibition clearly precede phospholipid alterations in cells. (Figure below, also added to the manuscript as Figure S3D, p.33, and commented in the text in p. 13)
Manuscript Figure S3D. Heatmap of selected top significantly altered metabolites in primary human myoblasts temporally treated with actinonin; untargeted metabolomics (n=5-6, run in technical duplicates). ACT = actinonin.
The authors should incorporate mitochondrial PE analysis in figure 3 to link the cellular studies described in this figure with the studies done in Deletor mice muscle.
Figure 3 I-K. The authors suggest an alteration in glutathione redox state and a further increase in mitochondrial superoxide production in cells treated with the PHGDH inhibition under mitochondrial stress. What are the total glutathione levels under these conditions? Could GSH regeneration improve the mitochondrial function and mitochondrial protein synthesis? Is extracellular serine able to rescue the reduced glutathione levels?
We have previously shown in vivo (Nikkanen et al. Cell Metab 2016), in Deletors, that in the skeletal muscle and the heart glucose carbons show flux via serine to glutathione, without changes in steady-state levels of glutathione, indicating high usage. In our targeted metabolomics assay from muscle, the steady-state glutathione amount was below the limit of quantitation. The levels of glutathione oxidized vs reduced are dynamic, however. Our untargeted set shows a trend towards an increase. The GSSG/GSH data (Rev Fig.5 Right) was included already in the original manuscript, as Figure S2C, and the time-wise dynamics is here shown for the reviewer (Rev Fig.5 Left).
Revision Figure 5. Left: Ratio between oxidized (GSSG) and reduced (GSH) glutathione temporally measured in primary human myoblasts with untargeted metabolomics; n=10-16/group. Right: Ratio between glutathione forms in muscles of WT and DEL mice. Measured by targeted metabolomics; WT VEH n=6, DEL VEH n=5, WT INH n=7, DEL INH n=8; VEH = vehicle; INH = inhibitor. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001.
Minor concerns. Figure 3B,C does not show the statistical analysis so please incorporate this information.<br /> Include quantification of figure 3 E and supplementary figure S3E.
We have added this information to both figures.
Figure S3E. Improve flow cytometry histogram, the cell population data values cannot be observed.
We have improved the resolution.
Some methods and primers included in the material and methods section are not used in the manuscript.
We have carefully edited the materials and methods sections for any unnecessary data.
Reviewer #1 (Significance):
In this manuscript the authors describe interesting results regarding amino acid metabolism under conditions of mitochondrial stress. The authors used a selective PHGDH inhibitor (compound NCT503), and document that de novo serine synthesis is essential to sustain phospholipid biosynthesis, redox homeostasis, mitochondrial function, and mitochondrial protein synthesis in Deletor mice and in cell culture under mitochondrial stress. Interestingly, serine supplementation does not rescue those metabolic alterations, indicating a specific mitochondrial stress-dependent mechanism of serine utilization by the cells.<br /> This data will be relevant to better understand the connection between alterations in mitochondrial function and amino acid metabolism in cells, and in organisms.
We thank the reviewer #1 for the constructive comments and acknowledgement of interesting results and significance.
Reviewer #2 (Evidence, reproducibility and clarity):
Experiments reported in this manuscript indicate that NCT-530- an inhibitor of the de novo serine biosynthetic enzyme PHGDH- worsens mitochondrial pathology.<br /> Systemic administration of NCT-503 decreased serine levels only in Deletor mice- ubiquitously expressing a homologous dominant patient mutation in mitochondrial twinkle helicase.<br /> NCT-503 treatment induced a further increase of the mitochondrial integrated stress response in Deletor mice. Moreover, the metabolic profile and lipid balance was further modified by NCT-503 administration to Deletor mice. The relevance of NCT-503 treatment was finally evaluated in cellular systems exposed with different treatments inducing mitochondrial insults.
COMMENTS:
NCT-530 specificity should be confirmed by reducing PHGDH levels by either siRNA or even better by CRISPR-Cas9-mediated gene deletion.
Firstly, we find clear results in Deletor mice but no pathology in WT mice treated with NCT-530. We interpret the reviewer to mean our cellular model, because in vivo siRNA or CRISPR-Cas9 approach is not feasible in mice that manifest the disease at 2 years of age. The compound is inhibiting the activity of PHGDH. The specificity has been described in the paper of Pacoult et al. (2016) previously, and as we find decreased serine and response of increased PHGDH transcript, the results are well consistent to what has previously been described. However, to respond to this reviewer, we have now added new data on a PHGDHKO in HEK293 cells (Figure S4E,F,p34 and below, commented on page 14).
Manuscript Figure S4F. Quantification of population doublings of WT and PHGDHKO cells treated with actinonin, PHDGH inhibitor or a combination of both. Immunofluorescence images are presented in Rev Fig 1. The data is presented as average values of three independent experiments; VEH = vehicle; INH = inhibitor; ACT = actinonin; KO = knockout; EtOH = ethanol. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001; **** p ≤0.0001.
If the serine biosynthetic pathway is causally relevant to worsen the mitochondrial pathology, supplementing Deletor mice with a serine-rich diet or intraperitoneal injection of serine is expected to improve pathology.
This is an exciting suggestion which we did consider. However, based on our cell experiments, we show that in the context of mitochondrial disease, the de novo serine synthesis becomes essential for cellular viability, and this cannot be compensated by extracellular serine supplementation alone. This suggests that the intracellular localization of serine synthesis is essentially important, which is an interesting finding and warrants further investigation, not in the scope of this paper.
Reviewer #2 (Significance):
Limited significance in the field.
Reviewer #3 (Evidence, reproducibility and clarity):
This study concludes that de novo serine biosynthesis fueled by PHGDH activity is an adaptive mechanism counteracting defects in mitochondrial function observed in mitochondrial myopathies, while being dispensable for mitochondrial function of healthy muscle. By using a mouse model of mitochondrial myopathies, as well as cells treated with different mitochondrial poisons, authors show that de novo serine biosynthesis is specifically needed to preserve phospholipid synthesis, some degree of mitochondrial function, and mitigate mitochondrial ROS production. These conclusions are drawn mostly from the data obtained from experiments treating cells and mutant mice with NCT-503, an inhibitor of PHGDH. The main limitation is that the approach does not allow us to discern whether the phenotypes observed are explained by on-target and muscle autonomous actions of NCT-503. The list of major concerns are as follows:
We thank reviewer #3 for her/his comments.
1) The authors do not cite the study by Vandekeere et al. Cell Metabolism 2018 that define the KO of PHGDH in endothelial cells. This study demonstrates that serine derived from PHGDH is required to synthesize heme to preserve mitochondrial function in endothelial cells. In addition, they demonstrate that the absence of PHGDH increases mitochondrial ROS and decreases electron transport chain function. These previous studies can indicate that the worsening of the muscle phenotype in the mice treated with NCT-503 might be driven by its actions in endothelial cells, and not in muscle. In addition, it raises the question on why NCT-503 has no effect on muscle of 24-month-old mice, which have a decline in metabolic fitness.
This is an interesting comment, and we indeed have now included the missing reference. Firstly, we find it interesting as well that NCT-503 has no significant health-related effect in WT background in the tissues that we analysed but shows harmful effects upon mitochondrial dysfunction. Our aged WT mice, even at the age of 24 months, show no signs of respiratory chain deficiency in skeletal muscle and this is consistent with numerous other studies on old mice. Therefore, the metabolic fitness decline that the reviewer mentions does not make PHGDH induction essential in normal aging.
Secondly, we are aware of the Vandekeere et al. study on endothelial cells. Our mouse is a constitutive transgenic mouse, and therefore isolated changes in single tissues as in the endothelial KO mouse, because of metabolite signaling between cell types, is hard to compare with ours. In our mice, expressing a dominant patient mutation in the mitochondrial replicative helicase Twinkle, PHGDH induction in the skeletal muscle is a key component of the mitochondrial integrated stress response (ISRmt) as we described in e.g., in Tyynismaa et al. 2010 and Forsström, Jackson et al. Cell Metab 2019. Similar findings have been reported by Kuhl et al. ELife 2017 and other groups. We have also shown that PHGDH expression is dependent on prior induction of FGF21 in the skeletal muscle (Cell Metab 2019). We cannot fully exclude a contribution of endothelial cells in the Deletor phenotype, but the upregulation of PHGDH is robust exactly in the Deletor muscle, and endothelial cells show no phenotype in ultrastructural analysis of these mice. Therefore, our strong view is that in order to study the effect of PHGDH induction caused by primary mitochondrial disease in the skeletal muscle, the use of an inhibitor is the first choice.
Hence, we find that the Vandekeere et al. study supports our findings in that increasing PHGDH could represent an adaptive response to support electron transport chain function and decreasing mitochondrial ROS in a tissue where PHGDH is induced.
In this respect, we would also like to emphasize that a 1-month treatment of old mice, as in our study, differs from a life-long tissue-specific knockout, which is not a natural disease presentation nor an avenue to understand whether the opposite – increasing PHGDH activity – could represent a viable treatment option.
2) No experiments with PHGDH knockdown are performed in vitro (or ideally in vivo using muscle electroporation if possible) to confirm the specificity of NCT-503. This is validation is key in muscle, as the on-target actions of NCT-503 were mostly shown in different cancers with low and high PGHDH expression (Pacold et al). Therefore, whether there are no off-target effects of NCT-503 in muscle is still unknown and should be defined.
Firstly, we find effects in serine levels and also response to PHGDH expression, and effects on ISRmt. As argued, full-body genetic ablation is associated with lethality in early embryogenesis and is not an option. Muscle-specific PHGDH-KO was considered, but with a late-manifesting mouse is a several-year experiment and therefore was not considered to be in the scope of this article. In an addition to the arguments, we raised above, muscle electroporation or intramuscular AAV infection would represent the only option, but with limited spreading in adult aged mice (our own and colleagues’ experience), and in a mosaic disease would offer low information.
We have however, now added data on a PHGDHKO HEK293 cell line with and without pharmacologically inducing mitochondrial dysfunction, p.14, Fig S4E,F.
3) The data showing that exogenous serine supplementation cannot override the effects of NCT-503 treatment on mitochondria could also be compatible with an off-target effect of NCT-503 in models of mitochondrial dysfunction (see point 2). If the experiments suggested in point number 2 demonstrate on-target action of NCT-503, authors should then decrease the expression of the mitochondrial transporter of serine (SFXN1) to demonstrate that specific intracellular pools of serine are needed to mitigate mitochondrial dysfunction. If the authors' conclusion is conclusive, knock-down of SFXN1 should be highly toxic in in vitro and in vivo models of mitochondrial myopathies, while having barely any effect in controls (similarly to serine deprivation in vitro being almost harmless).
Thank you for the comment. To our knowledge and based on our own experience elsewhere, the role of SFXN1 as the only serine transporter is still somewhat unclear (Kory et al, Science 2018; see also below). Therefore, the relevant metabolomic serine-dependent changes, PHGDH response and effects on the relevant stress response to our opinion are strong evidence of on-target-effects.
4) The authors list SFXN1 in the antibodies used in the paper, but I could not find any data. Are the protein levels of SFXN1 changed in mice with mitochondrial myopathies? Do they strongly correlate with PHGDH expression?
We actually had probed SFXN1 ab in the muscle but because of the extent of the data in the paper, had decided to omit the data – but accidentally left it in the methods. We do see an increase in the abundance of SFXN1 in treated Deletors. However, as also explained above, although SFXN1 has been described as a serine transporter, it is not fully characterized, also transports other amino acids, and has some redundancy with other SFXN family members requiring multiple KDs to get the required effect (Kory et al., Science 2018).
These data are now included to Figure S2H (p.32 and below) and commented in page 11.
Manuscript Figure S2H. Evaluation of SFXN1 protein expression in muscles of WT and DEL mice with Western Blotting. Left: image of the SFXN1 bands and the total protein lanes. Right: quantification of the band intensities. n=5/group; VEH = vehicle; INH = inhibitor. Significance levels: n.s. = p > 0.05; * p ≤ 0.05; ** p ≤ 0.01; *** p ≤0.001.
4) Serine tracing experiments would be required to conclude that serine is needed for phospholipid synthesis. Otherwise, the defects observed can just be downstream of mitochondrial dysfunction and ISRmt activation.
Thank you for the point. Our study aims to characterize the role of PHGDH in skeletal muscle, in a mitochondrial disease. In vivo tracing experiments would be out of the scope for this study. We have modified our conclusions in respect to this in page 11.
5) Authors use isolated mitochondria from muscle to determine whether OPA1 processing is changed in mice with mitochondrial myopathy and treated with NCT-503. The blots show higher total OPA1 content per mitochondria in the group with the greatest mitochondrial dysfunction, depolarization, and ROS production (myopathy + NCT-503). These data strongly suggest that dysfunctional mitochondrial from dysfunctional fibers do not survive the isolation procedure, showing just OPA1 content of resilient mitochondria surviving isolation. Indeed, heme depletion (as expected from PHGDH inhibition Vadekeere et al. Cell Metabolism 2018) and OPA1 processing catalyzed by OMA1 activation by ROS and depolarization can both activate the mitochondria ISR, via HRI. Therefore, authors should analyze OPA1 processing in total lysates to include mitochondria from dysfunctional fibers. Maybe increased OMA1 activity as a result of increased mitochondrial ROS and depolarization could explain the exacerbation of the mitochondrial ISR induced by NCT-503 treatment.
The notion that stress-induced OPA1 processing present in mitochondrial myopathy is a valid one, which we did ask in a previous study in the Deletor mouse (Forsstrom et al., Cell Metabolism 2019). Surprisingly, we did not detect any significant levels of OPA1 processing in the Deletors, in the total cell lysates in that paper, nor in a previous paper of mitochondrial myopathy treated with Atkins diet (Ahola et al. EMBO Mol Med, 2016). The differential centrifugation protocol is unlikely to induce selection bias at the high centrifugation forces used (10000xg). We have previously described the increase in stress-related proteins in mitochondria-enriched fractions (Forsstrom et al., Cell Metabolism, 2019) and Rev Fig.6, below from the current study.
Revision Figure 6. Immunoblot analysis of mitochondria-enriched fractions from skeletal muscles of all treatment groups from this study. n=5/group; VEH = vehicle; INH = inhibitor.
Reviewer #3 (Significance):
This study is significant, as it aims to understand the pathways that mediate adaptation to mitochondrial myopathies and such knowledge is necessary to find novel therapeutic targets. It could be of high interest to basic researchers studying metabolism and mitochondrial regulation, as well as to clinicians treating mitochondrial diseases.
We appreciate the reviewer noting its importance and emphasizing the significance of this pathway for its clinical relevance.
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Referee #3
Evidence, reproducibility and clarity
This study concludes that de novo serine biosynthesis fueled by PHGDH activity is an adaptive mechanism counteracting defects in mitochondrial function observed in mitochondrial myopathies, while being dispensable for mitochondrial function of healthy muscle. By using a mouse model of mitochondrial myopathies, as well as cells treated with different mitochondrial poisons, authors show that de novo serine biosynthesis is specifically needed to preserve phospholipid synthesis, some degree of mitochondrial function, and mitigate mitochondrial ROS production. These conclusions are drawn mostly from the data obtained from experiments treating cells and mutant mice with NCT-503, an inhibitor of PHGDH. The main limitation is that the approach does not allow us to discern whether the phenotypes observed are explained by on-target and muscle autonomous actions of NCT-503. The list of major concerns are as follows:
- The authors do not cite the study by Vadekeere et al. Cell Metabolism 2018 that define the KO of PHGDH in endothelial cells. This study demonstrates that serine derived from PHGDH is required to synthesize heme to preserve mitochondrial function in endothelial cells. In addition, they demonstrate that the absence of PHGDH increases mitochondrial ROS and decreases electron transport chain function. These previous studies can indicate that the worsening of the muscle phenotype in the mice treated with NCT-503 might be driven by its actions in endothelial cells, and not in muscle. In addition, it raises the question on why NCT-503 has no effect on muscle of 24-month-old mice, which have a decline in metabolic fitness.
- No experiments with PHGDH knockdown are performed in vitro (or ideally in vivo using muscle electroporation if possible) to confirm the specificity of NCT-503. This is validation is key in muscle, as the on-target actions of NCT-503 were mostly shown in different cancers with low and high PGHDH expression (Pacold et al). Therefore, whether there are no off-target effects of NCT-503 in muscle is still unknown and should be defined.
- The data showing that exogenous serine supplementation cannot override the effects of NCT-503 treatment on mitochondria could also be compatible with an off-target effect of NCT-503 in models of mitochondrial dysfunction (see point 2). If the experiments suggested in point number 2 demonstrate on-target action of NCT-502, authors should then decrease the expression of the mitochondrial transporter of serine (SFXN1) to demonstrate that specific intracellular pools of serine are needed to mitigate mitochondrial dysfunction. If the authors' conclusion is conclusion, knock-down of SFXN1 should be highly toxic in in vitro and in vivo models of mitochondrial myopathies, while having barely any effect in controls (similarly to serine deprivation in vitro being almost harmless).
- The authors list SFXN1 in the antibodies used in the paper, but I could not find any data. Are the protein levels of SFXN1 changed in mice with mitochondrial myopathies? Do they strongly correlate with PHGDH expression?
- Serine tracing experiments would be required to conclude that serine is needed for phospholipid synthesis. Otherwise, the defects observed can just be downstream of mitochondrial dysfunction and ISRmt activation.
- Authors use isolated mitochondria from muscle to determine whether OPA1 processing is changed in mice with mitochondrial myopathy and treated with NCT-503. The blots show higher total OPA1 content per mitochondria in the group with the greatest mitochondrial dysfunction, depolarization, and ROS production (myopathy + NCT-503). These data strongly suggest that dysfunctional mitochondrial from dysfunctional fibers do not survive the isolation procedure, showing just OPA1 content of resilient mitochondria surviving isolation. Indeed, heme depletion (as expected from PHGDH inhibition Vadekeere et al. Cell Metabolism 2018) and OPA1 processing catalyzed by OMA1 activation by ROS and depolarization can both activate the mitochondria ISR, via HRI. Therefore, authors should analyze OPA1 processing in total lysates to include mitochondria from dysfunctional fibers. Maybe increased OMA1 activity as a result of increased mitochondrial ROS and depolarization could explain the exacerbation of the mitochondrial ISR induced by NCT-503 treatment.
Significance
This study is significant, as it aims to understand the pathways that mediate adaptation to mitochondrial myopathies and such knowledge is necessary to find novel therapeutic targets. It could be of high interest to basic researchers studying metabolism and mitochondrial regulation, as well as to clinicians treating mitochondrial diseases.
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Referee #2
Evidence, reproducibility and clarity
Experiments reported in this manuscript indicate that NCT-530- an inhibitor of the de novo serine biosynthetic enzyme PHGDH- worsens mitochondrial pathology.
Systemic administration of NCT-503 decreased serine levels only in Deletor mice- ubiquitously expressing a homologous dominant patient mutation in mitochondrial twinkle helicase.
NCT-503 treatment induced a further increase of the mitochondrial integrated stress response in Deletor mice. Moreover, the metabolic profile and lipid balance was further modified by NCT-503 administration to Deletor mice. The relevance of NCT-503 treatment was finally evaluated in cellular systems exposed with different treatments inducing mitochondrial insults.
Comments:
- NCT-530 specificity should be confirmed by reducing PHGDH levels by either siRNA or even better by CRISPR-Cas9-mediated gene deletion.
- If the serine biosynthetic pathway is causally relevant to worsen the mitochondrial pathology, supplementing Deletor mice with a serine-rich diet or intraperitoneal injection of serine is expected to improve pathology.
Significance
Limited significance in the field.
-
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Referee #1
Evidence, reproducibility and clarity
In this manuscript the authors describe interesting results regarding amino acid metabolism under conditions of mitochondrial stress. The authors used a selective PHGDH inhibitor (compound NCT503), and document that de novo serine synthesis is essential to sustain phospholipid biosynthesis, redox homeostasis, mitochondrial function, and mitochondrial protein synthesis in Deletor mice and in cell culture under mitochondrial stress. Interestingly, serine supplementation does not rescue those metabolic alterations, indicating a specific mitochondrial stress-dependent mechanism of serine utilization by the cells.<br /> In addition, the authors attempted to explore the role of serine in phospholipid biosynthesis under in vivo and ex vivo mitochondrial stress, and this is the weakest part of the manuscript. The specific reduction of mitochondrial PE using the PHGDH is interesting, and it can provide some clues into how mitochondrial membranes are synthetized under mitochondrial stress, but additional experimental approaches should be incorporated to generate a more robust body of evidence.<br /> In summary, the manuscript should be improved by using additional experimental approaches. In addition, genetic intervention through PHGDH gain or loss of function can help to elucidate the molecular mechanisms. The authors could also incorporate metabolomic studies using C13 serine or C13 glucose supplemented culture medium in order to differentiate carbons that come from extracellular serine or from de novo synthesis.
Additional questions:
Is PHDG subcellular localization modulated under mitochondrial stress conditions?
Is the extracellular serine uptake impaired under mitochondrial stress?
ATF4 is a transcription factor that regulates amino acid transport. In this connection, is ATF4-dependent serine transporters modulated under mitochondrial stress or under PHGDH treatment?
Regarding the alteration in redox homeostasis, mitochondrial function and mitochondrial protein synthesis. Is the alteration of phospholipid synthesis upstream of all of those mitochondrial alterations?
Additionally, in my opinion the results should be reorganized, because in the current format the manuscript is fragmented, and several panels lose the symmetry.
Major concerns.
Figure 1<br /> 1. The authors should incorporate the Deletor mice amino acid levels in muscle. How does the PHGDH inhibitor treatment modulate the other non-essential amino acids?<br /> 2. The authors should incorporate the data of WT + vehicle and wt + NCT503 mice in figures 1C, 1D, 1F and 1G, in order to compare properly the effects of PHGDH inhibitor<br /> 3. Figure 1D is mislabeled<br /> 4. Figure 1H. Are there any effect of PHGDH in the mtDNA of WT mice?
The author might incorporate this information, to show properly that mitochondrial stress led to dependence of serine to sustain muscle homeostasis
Figure 2
Interestingly the authors observe a decrease in total mitochondrial lipids content, and an increase in mitochondrial PE content in Deletor mice compared to WT mice. These results suggest an alteration in the phospholipids flux between mitochondria and endoplasmic reticulum in this model of mitochondrial disease. Moreover, PHGDH treatment appears to be able to rescue this alteration. Some question related this issue:<br /> What is the expression of genes involved in the balance PC, PE, PS?, Are the PSS1, PSS2, PSD and PEMT expression altered?<br /> Regarding the phospholipid synthesis. Is mitochondria or endoplasmic reticulum ultrastructure altered in Deletor mice muscle?<br /> The authors should explain the possible mechanisms.
Figure 3
Based on the metabolomic studies, the authors propose a time-dependent decrease in PSTA1 and phosphoserine in cells under mitochondrial stress (Figure 3D). To elucidated the direct role of PHGDH, the authors should analyze the phosphoserine and different phospholipid (described in figure 2E) in presence of PHGDH inhibitor. This will help to understand the link between the endogenous serine synthesis and mitochondrial PE accumulation.<br /> Figure 3H shows a decrease in phosphoserine in the presence of PHGDH inhibitor but this figure is asymmetric compared to figure 3I. Can the authors use another experimental approach to detect the specific mitochondria phospholipid levels (used in Figure 2 for instance)?<br /> The authors should incorporate mitochondrial PE analysis in figure 3 to link the cellular studies described in this figure with the studies done in Deletor mice muscle.<br /> Figure 3 I-K. The authors suggest an alteration in glutathione redox state and a further increase in mitochondrial superoxide production in cells treated with the PHGDH inhibition under mitochondrial stress. What are the total glutathione levels under these conditions? Could GSH regeneration improves the mitochondrial function and mitochondrial protein synthesis? Is extracellular serine able to rescue the reduced glutathione levels?
Minor concerns.
Figure 3B,C does not show the statistical analysis so please incorporate this information.
Include quantification of figure 3 E and supplementary figure S3E.
figure S3E. Improve flow cytometry histogram, the cell population data values cannot be observed.
Some methods and primers included in the material and methods section are no used in the manuscript.
Significance
In this manuscript the authors describe interesting results regarding amino acid metabolism under conditions of mitochondrial stress. The authors used a selective PHGDH inhibitor (compound NCT503), and document that de novo serine synthesis is essential to sustain phospholipid biosynthesis, redox homeostasis, mitochondrial function, and mitochondrial protein synthesis in Deletor mice and in cell culture under mitochondrial stress. Interestingly, serine supplementation does not rescue those metabolic alterations, indicating a specific mitochondrial stress-dependent mechanism of serine utilization by the cells.
This data will be relevant to better understand the connection between alterations in mitochondrial function and amino acid metabolism in cells, and in organisms.
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Reply to the reviewers
Reviewer #1:
Major comments:
- In figure 4 and throughout the text they refer to AVP neurons as being "directly" inhibited by glucose but they do not show this. They do show membrane depolarization in response to decreased glucose form 2.5 to 0.1 mM; however this could easily be an indirect effect. To demonstrate that they directly sense glucose, it is necessary to block presynaptic input (generally done with the sodium channel blocker tetrodotoxin). In addition, the example recordings are not very good. The neurons seem to just decrease action potential frequency throughout the recording, despite the membrane depolarization. In the methods section, they state that cell resistance was measured but they do not report it. Looking at the traces, it appears that resistance does not change in response to decreased glucose which further supports a presynaptic action. In order to characterize these neurons as directly glucose sensing, they must use a blocker of presynaptic activity such as tetrodotoxin and the resistance values should be reported. They should also choose better representative traces.
Answer: By “directly inhibited” we do not refer to a cell-autonomous effect but to a direct glucose responsiveness. Our cFOS experiments (Fig 3) and preexisting in vivo fiber photometry data (Kim et al., PMID: 34787082; Mandelblat-Cerf et al., PMID: 27989461) reported activation of AVP neurons in conditions of hypoglycemia. We further wanted to verify that the activation was triggered directly by the decreased glucose levels and not by accompanying systemic signals (for example insulin levels, stress response, etc). Furthermore, we aimed at identifying if inactivation of Tmem117 in AVP neurons affects their glucose responsiveness (at the circuit level). Therefore, we decided to take into account the synaptic inputs. Of course, this approach provides information at the circuit level (that we consider essential for CRR characterization) but is also accompanied with highly variable firing patterns. We focused our analysis on the membrane potential, as an indicator of cell excitability state that based on our previous experience was proven to be consistently affected in glucose sensing neurons regardless of cell-type, inputs or topology (Strembitska et al., PMID: 36180454; Kessler et al., PMID: 34622169; Quenneville et al., PMID: 32839348; Quenneville et al., PMID: 32839348; Labouèbe et al., PMID: 29218531; Steinbusch et al., PMID: 27422385; Labouèbe et al., PMID: 27322418; Lamy et al., PMID: 24606905). We used membrane resistance as an indicator of our patch-clamp quality. As specified in the Materials and Methods section (pages 33, lines 702-704), neurons with an access resistance >25 MΩ or changing by >20% during the recording were excluded from the analysis.
We understand that the term “directly affected” has created some confusion since it could be interpreted as cell-autonomous effect. Therefore, we have exchanged the term as follows:
- Results section (page 14, line 281): “To determine whether AVP neurons were directly sensitive to hypoglycemia and whether Tmem117 would modify this sensitivity” was converted to “To determine whether AVP neurons were sensitive to the decreased glucose availability and whether Tmem117 would modify this sensitivity”
- Discussion section (page 27, lines 548-553): “Thus, AVP neurons can directly respond to hypoglycemia. Interestingly, a recent study reported that hypoglycemia can also activate AVP neurons indirectly, through afferent connections arising from GI neurons of the basolateral medulla (Kim et al., 2021). Thus, AVP neurons are part of a brainstem-hypothalamus neuronal circuit where hypoglycemia can be sensed by neurons located at multiple sites to activate the secretion of AVP leading to increased secretion of GCG.” was converted to “Thus, AVP neurons can respond to decreased glucose levels. Interestingly, a recent study reported that hypoglycemia can also activate AVP neurons through afferent connections arising from GI neurons of the basolateral medulla (Kim et al., 2021). Thus, AVP neurons are part of a brainstem-hypothalamus neuronal circuit where hypoglycemia can be sensed by neurons located at multiple sites to activate the secretion of AVP leading to increased secretion of GCG.”
Regarding the membrane resistance measurements, 6 out of 7 AVPTM117KO GI cells and 6 out of 9 AVPTM117WT GI cells show a decrease in conditions of low glucose suggesting a cell autonomous effect, at least in a subpopulation of AVP GI neurons. We realized, based on the reviewer’s comment, that not including these data can lead to misinterpretation of the results, therefore we included the membrane resistance measurements in figure 4 and added the corresponding explanation in the Results section (page 15, lines 295-298).
Regarding the representative traces, those included in the figure clearly show the increase in membrane potential that was consistent in all our GI cells. Choosing a representative trace for firing patterns is unrealistic given the high variability observed without the use of synaptic blockers.
- The relationship between the AVP/Tmem117 knockout and glucagon secretion is also not very convincing - especially in terms of the data showing that the effect seen at 1-week reverses by 3 weeks post knockdown in males when the neurons have died. First, the effect is very slight to begin with. Second, and more of a concern, the over secretion is still evident at the later time point, it just did not reach significance. This could have been due to the difference in sample size. Sample size in the early timepoint is 15-16 and in the late time point is reported as 8-9 (almost half the size), and in fact when I try to count data points, it really looks like the WT sample size is only 5. To make the conclusion that the effect disappears at the later time it is necessary to increase sample size so that the studies are equivalent. This is very important because these data are what is supporting the hypothesis that Tmem117 in AVP neurons regulates (inhibits) glucagon secretion. It is also concerning that the increased glucagon secretion in the knockout did not translate into differences in the depth of hypoglycemia raising concerns about physiological relevance.
Answer: The sample size required based on our power calculations for these traits (plasma glucagon and copeptin) in male mice is 8 animals per group. Figure 2 consists of data merged from two individual experiments, both of which showed a significant effect. Figure 6 is the 3rd replication of our phenotypic observations with the addition of a later timepoint measurement. The number of animals included is 9 AVPTM117WT and 8 AVPTM117KO. Only for copeptin levels (panel F), as stated in the figure legend, the n is 8 mice per group, since for one of the AVPTM117WT mice the baseline levels of copeptin were undetectable by ELISA. Counting the datapoints in a 2D graph can cause misinterpretation since similar values can be depicted as overlapping points. We had decided to present in Fig 6 only the later timepoint that corresponds to the IF results reporting AVP cell death. We now realize based on the reviewer’s comment that this can cause misinterpretation of the phenotypic outcome, therefore we have exchanged graphs E-G (containing 2 timepoints) for the corresponding graphs that contain all 3 timepoints. We believe that with this addition the concern will be addressed since with the same sample size there is a significant increase in glucagon and copeptin secretion in AVPTM117KO mice at the early timepoint that is no longer evident at the later timepoint.
Regarding the concern of effect size, we acknowledge the fact that we are reporting a small effect. But the CRR is controlled by a highly complex network of hypoglycemia activated neurons, which are located in different brain regions and act in an integrated manner to induce glucagon secretion through autonomic control, the HPA axis, and the secretion of AVP (reviewed in Steinbush et al., PMID: 26163755; Thorens, PMID: 34989155). Therefore, in this highly redundant and robust system, suppressing only one hypoglycemia sensing node, cannot be expected to have major consequence on the glucagon secretion. Nevertheless, we provide solid evidence that inactivation of Tmem117 in AVP neurons leads to a slight upregulation of AVP secretion that is accompanied by a subsequent increase in the glucose-stimulating hormone glucagon. To further highlight this observation, we added in figure 6 the correlation analysis between glucagon and copeptin levels of each tested sample that is reporting a significant positive correlation in both genotypes.
Regarding the concern for physiological relevance, we would like to clarify that in this model we have not followed the reestablishment of normoglycemia over time. The timepoint of blood collection and glycemic measurement was selected based on our previous experience. We have performed multiple times full insulin tolerance tests in various mouse models, and we selected here (and in other papers: Picard et al., PMID: 35339728; Strembitska et al., PMID: 36180454) the one-hour time point because this is always the nadir of the glycemic curves, where CRR has the strongest effect in stimulating the secretion of CRR hormones. Glycemia at this time point depends on the insulin sensitivity of the animal. Thus, finding similar glycemia at 60 minutes after insulin injection indicates similar insulin sensitivity in AVPTM117WT and AVPTM117KO mice, further supporting that the increased glucagon secretion is directly correlated to the increased AVP secretion.
- It is also curious that the females in proestrus were similar to males but that females in other stages showed no effect. If, as mentioned in the discussion, estradiol was involved one would expect that males would be more similar to females in stages with low estradiol. The sex difference should be discussed more fully since it does seem to be one of the strong conclusions in the study
Answer: We acknowledge that the discussion of the sex-specific phenotype was minimal in the initial version of our manuscript. We consider this finding very important for the general understanding of sex-differences in CRR, therefore we have included it in our main figures. But given that our observations remain in the phenotypic level our intention was to keep the discussion minimal and not add a lot of speculations that would not be supported by experimental data. We have performed all our further mechanistic analysis only in male mice and therefore we are not able to comment about this sex specific effect with evidence on the underlying mechanism. Of course, we have our literature-based explanation/hypothesis for the observed phenotype and given that this point was raised by all 3 reviewers, we have expanded this section of the discussion (pages 26, lines 520-542).
- The discussion needs to be adjusted in line with the findings.
Answer: Several adjustments both in the Results and Discussion sessions have been incorporated based on the reviewers’ comments. Details on the adjustments for each point raised can be found in the corresponding answer.
Minor comments:
The BXD mice should be defined and the reason for their use explained
Answer: We did not include further information in the first place because all the details and rational for the use of BXD mice were included in the original publication of this genetic screen (Picard et al., PMID: 35339728). We have now added further details on the origin of the BXD mouse lines accompanied with the corresponding reference (page 4, lines 83-85).
The abbreviation cQTL needs to be defined at first use in the text of the results
Answer: We added the abbreviation (page 5, line 102).
Reviewer #2:
Minor comments:
- Page 5, line 111: Fig1 shows Tmem117 expression in the hypothalamus. Tmem117 expression in AVP neurons in the PVN and SON are highlighted, however, AVP is not only expressed in these areas in the hypothalamus and in extra-hypothalamic areas. Was Tmem117 also expressed in AVP neurons beyond these areas?
Answer: Based on our immunofluorescent detection Tmem117 is only observed in AVP neurons of the PVN and SON. This pattern (Fig 1A), the percentage of AVP-Tmem117 co-positive cells in these two areas (Fig 1H, I) and the presence of strong positive staining in the neurohypophysis (Fig 1B) points towards specific expression in magnocellular neurosecretory AVP cells. We do not observe staining in other AVP positive neurons. An example can be found in Fig 1A where Tmem117 staining is localized at the PVN and SON, but not at the Suprachiasmatic nucleus.
- Page 10, line 219: Fig2 shows CRR responses after conditional Tmem117 ko in AVP neurons. A sex-dependent difference was observed in the increased CRR after Tmem117 inactivation. A similar pattern between males and females during pro-estrus in copeptin and glucagon was observed. Was AVP expression and AVP neuron response to hypoglycemia also analyzed in both sexes, and in the case of females, were the results analyzed during the pro-estrus phase?
Answer: Unfortunately, a detailed analysis of the mechanistic underpins of the estrus phase-dependent phenotype in female mice would exceed the spectrum of this initial characterization. We do believe that this finding is of great importance for the general understanding of sex-differences in CRR, therefore we have included it in our main figures. But our observations remain at the phenotypic level. We have performed all our further mechanistic analysis only in male mice. Of course, we have our literature-based explanation/hypothesis for the observed phenotype and given that this point was raised by all 3 reviewers, we have expanded this section of the discussion (pages 26, lines 520-542).
- Many of the experiments performed after Fig 3 (glucose responsiveness of AVP neurons, ER stress and ROS production, Ca2+ imaging) are mainly analyzed in the SON, but not the PVN. What is the rationale for analyzing only the SON in some experiments? Analyzing the PVN is of relevance due to its known role in CRR triggering.
Answer: The reason for focusing our single-cell level analysis only in SON is its homogeneous population of AVP-Tmem117 double positive cells (Fig 1I). In the PVN about 10% of AVP neurons are negative for Tmem117 (Fig 1H). Therefore, we would be unable to distinguish between the cells with Tmem117 inactivation and those that did not express it at the first place. We agree with the reviewer that PVN is of great relevance for CRR induction, and this is why for all our in vivo phenotyping experiments we aimed at targeting both areas. Our AVPTM117KO mouse model is generated by injection of the AAV6-AVP-icre virus in the posterior pituitary and is targeting both regions (Fig S2E). This model was used for all our phenotypic analyses (Fig 2, 6) and for the fiber photometry recordings (Fig 5H-M). The Ca2+ signal we obtain is a collective output of AVP magnocellular terminals in the posterior pituitary deriving from both PVN and SON. But when it comes to the analysis of responses at the single-cell level, not having the ability to identify the subpopulation of Tmem117 negative cells could have a big impact on the results and their interpretation.
- Page 16, line 346: Again here, only BIP expression in AVP neurons is shown in the SON. I would be interested in looking at expression in AVP neurons in the PVN. Same goes for activation of these neurons (measured by Ca2+) after insulin administration.
Answer: As mentioned above, we did not quantify these single-cell events in AVP neurons of the PVN due to the inability of effectively distinguishing between cells with Tmem117 inactivation and those that do not express Tmem117. But based on our supporting data (activation of PVN AVP cells in Fig 3 and decreased number of AVP PVN cells upon Tmem117 inactivation in Fig 6) we believe that the effect of Tmem117 inactivation is comparable between the Tmem117-positive AVP cells of both areas.
- What would be the role of Tmem117 in CRR triggering after hypoglycemia? Would its expression change during hypoglycemic conditions versus normoglycemia? Would that be different in models of pathology, like diabetes? Speculation of its physiological role in the discussion might be of help to visualize its role beyond inactivation.
Answer: We focused our discussion strictly on the acquired results, but we agree with the reviewer than including speculations regarding the physiological role of Tmem117 would enhance the communication of our results. We have incorporated some extra points focusing on the possible role of Tmem117 expression in physiological conditions and pathological states in the Discussion section (pages 27-28, lines 562-571). Furthermore, we have included some extra data from microdissected PVN and SON tissue reporting downregulation of Tmem117 in the SON as a physiological response to insulin-induced hypoglycemia (Fig 3G-I).
Reviewer #3:
Major comments:
1) The in vivo calcium data is not convincing (e.g. Figure 5j). Why is the activity not similar to that normally seen from populations of neurons (and in particular AVP neurons) in vivo - bursting/spikes. This is just a background increase in calcium... not an increase in activity?
Answer: Our aim with the fiber photometry experiments was not to detect the activity of AVP neurons but to evaluate the Ca2+ fluctuations in AVP neuronal terminals, directly at the site of AVP exocytosis. The activity of AVP neurons in conditions of hypoglycemia has been previously detected with similar techniques at the level of cell bodies in the SON (Kim et al., PMID: 34787082; Mandelblat-Cerf et al., PMID: 27989461) and was further supported by our cFOS and ephys experiments (Fig 3, 4). These experiments showed that inactivation of Tmem117 did not affect the activation of AVP neurons in conditions of hypoglycemia. But our phenotypic characterization revealed higher secretion of AVP (Fig 2) and our in vitro (Fig S3) and in vivo (Fig 5A-G) data demonstrated increased ER stress and ROS in AVPTM117KO cells. Therefore, we wanted to assess if this increased stress is associated with increased Ca2+ at the level of neuronal terminals which would enhance AVP exocytosis. The acquired signal is a collective output of AVP magnocellular neurons from PVN and SON and although it is not resembling the pattern observed from cell body recordings, we believe it provides important information for the output of this circuit in conditions of hypoglycemia. Our results do not only report that Tmem117 inactivation is accompanied by an increase in intracellular Ca2+ at the level of nerve terminals/exocytosis, but further demonstrate (for the first time to our knowledge) that the activity reported in conditions of hypoglycemia is linked, as expected, to an increase in local Ca2+ levels at the posterior pituitary. All the essential controls for normalization and interpretation have been taken into account as mentioned in the methods section (page 31, lines 655-668). GCaMP7 signal recordings are corrected for artifacts and photobleaching. The isosbestic channel is subtracted to correct for non-GCaMP7 related signal artifacts and then at a second stage (during the DF/F0 normalization) the traces are corrected for photobleaching by the running average algorithm. Furthermore, 60min recordings of mice injected with saline are used as control for determining the increased signal after insulin injection. We have now added a clarification on the origin of the recorded signal in the Results section (page 18, line 368).
2) Why would this response be oestrus cycle dependent? This is given very little thought in the manuscript.
Answer: We acknowledge that the sex-specific phenotype observed was not thoroughly discussed in the initial version of our manuscript. We included the data in a main figure since we consider them as an important piece of information supporting the crucial role of sex hormones in the regulation of CRR. On the other hand, since our observations remain in the phenotypic level, we thought it would be better to keep the discussion on the topic short and not include various literature-based hypothesis that would not be supported by experimental data. We have performed all our further mechanistic analysis only in male mice and therefore we are not able to comment about this sex specific effect with evidence on the underlying mechanism. We have now realized based on the reviewers’ comments that further discussion on the topic is needed, therefore we have expanded this section of the Discussion (page 26, lines 520-542).
Minor comments:
1) How does the regulation make sense in the context of AVPs normal role in whole body physiology?
Answer: We focused our discussion strictly on the acquired results, but it has become evident based on the reviewers’ comments that a discussion of the broad picture regarding the role of AVP and Tmem117 in physiological and pathological conditions would strengthen the interpretation of our results. We have now incorporated some extra points focusing on the possible role of Tmem117 expression in physiological conditions and pathological states in the Discussion section (pages 27-28, lines 562-571).
2) What do the authors think about the role of AVP in islets, some authors suggest it actually has the opposite effect.
Answer: The literature on the role of AVP on pancreatic islets shows indeed some controversies. A couple of studies suggest an action on beta cells and insulin secretion without any effect on glucagon secretion. On the other hand, the evidence on the stimulation of glucagon secretion is supported by numerous studies over the years and has been convincingly demonstrated with various ex vivo and in vivo models. Our study, in line with these findings, verifies the increased AVP secretion in conditions of hypoglycemia and reports a positive correlation between the levels of circulating copeptin and glucagon (Fig 6H).
3) Why have the authors left the recent study by Kim, Rorsman and colleagues et al. 2022 (eLife) to the discussion? This manuscript is an important piece in this field and should be introduced in the introduction.
Answer: We have now added the AVP induced glucagon secretion, accompanied by the supporting references (including the reference mentioned by the reviewer) as integral part of the CRR in our Introduction section (pages 3-4, lines 68-71).
4) The intro should also mention that islets also can intrinsically regulate glucagon release.
Answer: We focused our introduction exclusively to the brain triggered glucagon secretion, but in accordance with the reviewer’s comment we have now incorporated the intra-islet regulation and supporting literature in the Introduction (page3, line 55).
5) Has tmem117 shown up in any human screens of hypogylcaemia risk? Do tmem117 variants show in any osmoregulation or insipidus risk?
Answer: Not to our knowledge.
6) Please clarify what N= is? What is a statistical unit in each case in the graphs. It is not clear when it is a mouse, cell or experiment. This should be justified in each case.
Answer: We have now justified the corresponding values in all figure legends.
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Referee #3
Evidence, reproducibility and clarity
Glucagon secretion counters hypogylcaemia, and this is in part regulated by the CNS.
The authors investigated the role of hypothalamic Tmem117, which was previously identified in a genetic screen as a regulator of the counter-regulatory response to hypoglycaemia. They show that Tmem117 is expressed in vasopressin neurons and that inactivation of Tmem117 in AVP neurons increases hypoglycemia-induced vasopressin secretion leading to higher glucagon secretion. They show this is oestrus cycle phase-dependent.
The manuscript is generally well written and the results of good quality. The findings are important.
I have some comments:
Major:
- The in vivo calcium data is not convincing (e.g. Figure 5j). Why is the activity not similar to that normally seen from populations of neurons (and in particular AVP neurons) in vivo - bursting/spikes. This is just a background increase in calcium... not an increase in activity?
- Why would this response be oestrus cycle dependent? This is given very little thought in the manuscript.
Minor:
- How does the regulation make sense in the context of AVPs normal role in whole body physiology?
- What do the authors think about the role of AVP in islets, some authors suggest it actually has the opposite effect.
- Why have the authors left the recent study by Kim, Rorsman and colleagues et al. 2022 (eLife) to the discussion? This manuscript is an important piece in this field and should be introduced in the introduction.
- The intro should also mention that islets also can intrinsically regulate glucagon release.
- Has tmem117 shown up in any human screens of hypogylcaemia risk? Do tmem117 variants show in any osmoregulation or insipidus risk?
- Please clarify what N= is? What is a statistical unit in each case in the graphs. It is not clear when it is a mouse, cell or experiment. This should be justified in each case.
Significance
This is important, but some of the in vivo calcium data is weak. The manuscript is also riddled with self-citations and doesn't really put the results into a broader context. In addition, the finding is in a sense piggybacking off a recent revelation in the field (AVP neuron importance) using a technique that is available to the authors (Tmem117 manipulation) rather than trying to address the hypothesis/question with THE BEST approach to answer the question. The question feels like: "how can we use our mouse model to probe this AVP neuron hypothesis ourselves". Strange. The finding that the results are only relevant during a particular phase of the oestrus cycle feels a bit random and lacks adequate explanation. I still like the manuscript very much, the experiments are very technically challenging, the results are very interest, the data (mostly) of excellent quality, and the relevance to the field highly important, but I feel there is still room for improvement (unlikely more experiments, definitely some thinking and rewritting).
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Referee #2
Evidence, reproducibility and clarity
The present study led by Gaspari, et al shows a new role for Tmem117 as a major regulator in the CRR. The authors used a variety of techniques to demonstrate that Tmem117 innactivation modulates hypoglycemia-induced responses by regulating AVP action in the hypothalamus. I found the rationale of the study interesting, the results seem to support the author's claims and conclusions seem to be proper. However there are some minor issues that needs to addressed:
- Page 5, line 111: Fig1 shows Tmem117 expression in the hypothalamus. Tmem117 expression in AVP neurons in the PVN and SON are highlighted, however, AVP is not only expressed in these areas in the hypothalamus and in extra-hypothalamic areas. Was Tmem117 also expressed in AVP neurons beyond these areas?
- Page 10, line 219: Fig2 shows CRR responses after conditional Tmem117 ko in AVP neurons. A sex-dependent difference was observed in the increased CRR after Tmem117 inactivation. A similar pattern between males and females during pro-estrus in co-peptin and glucagon was observed. Was AVP expression and AVP neuron response to hypoglycemia also analyzed in both sexes, and in the case of females, were the results analyzed during the pro-estrus phase?
- Many of the experiments performed after Fig 3 (glucose responsiveness of AVP neurons, ER stress and ROS production, Ca2+ imaging) are mainly analyzed in the SON, but not the PVN. What is the rationale for analyzing only the SON in some experiments? Analyzing the PVN is of relevance due to its known role in CRR triggering.
- Page 16, line 346: Again here, only BIP expression in AVP neurons is shown in the SON. I would be interested in looking at expression in AVP neurons in the PVN. Same goes for activation of these neurons (measured by Ca2+) after insulin administration.
- What would be the role of Tmem117 in CRR triggering after hypoglycemia? Would its expression change during hypoglycemic conditions versus normoglycemia? Would that be different in models of pathology, like diabetes? Speculation of its physiological role in the discussion might be of help to visualize its role beyond inactivation.
Significance
The study of Gaspari, et al proposes a new player in the hypoglycemia-induced CRR, specially affecting AVP modulation of CRR. The results and conclusions are of relevance to the field, as the mechanisms mediating hypoglycemia-induced CRR and how these are affected during pathology are not completely understood. The study is relevant in the metabolic field and for a neuroendocrinology public.
Field of expertise: Neuroendocrinology, hypoglycemia, diabetes.
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Referee #1
Evidence, reproducibility and clarity
In this study the authors convincingly demonstrate that the hypothalamic protein Tmem117 protects against elevated ROS and cell death in AVP neurons, and that knocking out Tmem117 in these neurons leads to cell death. However, the major thrust of this paper was to demonstrate that Tmem117, in AVP neurons plays a role in hypoglycemia counter regulation (per the title). The data supporting this hypothesis are much less convincing.
Major comments
There are 2 major findings of this study that are problematic (#1 and 2 below). Further experiments are needed to support their conclusions.
- In figure 4 and throughout the text they refer to AVP neurons as being "directly" inhibited by glucose but they do not show this. They do show membrane depolarization in response to decreased glucose form 2.5 to 0.1 mM; however this could easily be an indirect effect. To demonstrate that they directly sense glucose, it is necessary to block presynaptic input (generally done with the sodium channel blocker tetrodotoxin). In addition, the example recordings are not very good. The neurons seem to just decrease action potential frequency throughout the recording, despite the membrane depolarization. In the methods section, they state that cell resistance was measured but they do not report it. Looking at the traces, it appears that resistance does not change in response to decreased glucose which further supports a presynaptic action. In order to characterize these neurons as directly glucose sensing, they must use a blocker of presynaptic activity such as tetrodotoxin and the resistance values should be reported. They should also choose better representative traces.
- The relationship between the AVP/Tmem117 knockout and glucagon secretion is also not very convincing - especially in terms of the data showing that the effect seen at 1-week reverses by 3 weeks post knockdown in males when the neurons have died. First, the effect is very slight to begin with. Second, and more of a concern, the over secretion is still evident at the later time point, it just did not reach significance. This could have been due to the difference in sample size. Sample size in the early timepoint is 15-16 and in the late time point is reported as 8-9 (almost half the size), and in fact when I try to count data points, it really looks like the WT sample size is only 5. To make the conclusion that the effect disappears at the later time it is necessary to increase sample size so that the studies are equivalent. This is very important because these data are what is supporting the hypothesis that Tmem117 in AVP neurons regulates (inhibits) glucagon secretion. It is also concerning that the increased glucagon secretion in the knockout did not translate into differences in the depth of hypoglycemia raising concerns about physiological relevance.
- It is also curious that the females in proestrus were similar to males but that females in other stages showed no effect. If, as mentioned in the discussion, estradiol was involved one would expect that males would be more similar to females in stages with low estradiol. The sex difference should be discussed more fully since it does seem to be one of the strong conclusions in the study
- The discussion needs to be adjusted in line with the findings.
Minor comments:
The BXD mice should be defined and the reason for their use explained<br /> The abbreviation cQTL needs to be defined at first use in the text of the results
Significance
The observation that Tmem117 is protective against ROS and cell death is interesting. However, the other conclusions are not supported by the data which decreases the overall significance of the study
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Reply to the reviewers
Thank you for the rapid and favorable reviews of our manuscript entitled “Long-Read Genome Assembly and Gene Model Annotations for the Rodent Malaria Parasite Plasmodium yoelii 17XNL.” We particularly appreciated that both reviewers had substantial, detailed expertise with the sequencing and assembly of Plasmodium genomes, and valued their questions and suggestions to ensure high rigor of our work. We have addressed all of the reviewers’ comments in the revised manuscript, and have provided a point-by-point response to each below.
Response to Reviewers
Note: Point-by-point responses are provided in italics below each reviewer comment below. Line numbers referenced in our responses refer to their final line position in the Track Changes version of the manuscript.
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
The manuscript entitled "Long-Read Genome Assembly and Gene Model annotation for the Rodent Malaria Parasite P. yoelii 17XNL" is a well-written manuscript providing updates and important observations about the genome assembly and annotation of this specific non-lethal isolate. The group overall did a great job showing how the application of newer technologies such as long-read DNA and direct RNA sequencing to generate top-quality genomes to be used as a reference for the community. Here are some comments about the work presented:
Response: Thank you for your positive feedback and suggestions on how to clarify these findings. We have improved the revised manuscript based on your feedback and suggestions below.
Major comments: - The authors added several result information across the methods section. Making the text repetitive, since the same is also presented in the results section. Please revise the method section to remove results from this section.
Response: We agree and have streamlined both the Results and Methods sections to remove redundancy in these descriptions.
- Some methods are also redundant in the Result section. For example, in line 141-142, the group describe which DNA extraction kit they used (again this is correctly mentioned in the methods section).
Response*: We agree and have removed minutiae such as these from the Results section. These details remain in the Methods section to ensure reproducibility. *
- Besides important, the group added several information about method comparison between base call accuracy and sequencing methods. I agree that having this information in the supplemental material is great, but I would be careful to not focus too much on those, since most of the observations are already well-known by the community and focus more in the biological relevance of what is being generated with the newly updated genome.
Response: The advances in base calling algorithms do make substantial improvements to the Nanopore reads. We have only included a short description of this in the main manuscript and feel this is an appropriate amount of context for the typical reader. Those that love these details and want to dig further can find this content in our supplemental information.
- The group did a great job generating two versions of the genome, and an updated gene annotation set using long-read sequencing. But the major question is, how about alternative splicing? They mention the use of it (line 350) but I don't see any result about how many alternative transcripts were observed, and if they were differentially detected in different life stages of the sets used for the RNA sequencing. This is a very important result to be added since one of the key pieces of information that long-read RNA sequencing brings for Genome annotation.
Response: We have now expanded this description in the manuscript to note that 866 genes are predicted to have multiple transcript isoforms (Lines 240-241). Moreover, we have now generated a Supplemental Table 4 that lists these isoforms in the revised manuscript. As we have not conducted further validation of this large number of transcript isoforms, we have left the description at this level.
- Same observation as above for potential long ncRNAs.
Response: We agree that lncRNAs are a fascinating aspect of the biology of the parasite, but a proper analysis of this class of RNA is far outside of the scope of this current study. Automatic identification approaches with Nanopore data will likely yield high numbers of false positives, which require manual curation for rigorous annotation. We hope others can use these data to accelerate such studies as well.
- From what I understand the Hifi run was able to generate a gapless genome assembly and the ONT run did not. What was the final coverage for each? From my experience with P. falciparum genomes, ONT even with the rapid kit was able to generate chromosomal level assemblies if the coverage was >100x (but again, this is not a rule). Add those valuable observations about the depth so the reader can check if other variables in the comparison should be made.
Response: This is a particularly interesting aspect of not only our datasets, but of other Plasmodium genomes as well. This issue occurs at least in part due to the presence of many repeated elements in the subtelomeric regions. It is important to note that these repeated elements do not resolve into a single haplotype in an assembly due to conflicting information, not due to lack of coverage. For instance, regions may differ by only a few nucleotides that each have significant read support. We are particularly interested in a recent preprint that concludes that P. falciparum harbors extrachromosomal plasmids with these var sequences present (doi.org/10.1101/2023.02.02.526885). *If this observation is supported via peer review, this interpretation could also begin to explain our results with P. yoelii 17XNL as well. *
- Also be sure that the structural comparisons between the genomes are not the ones used after running ragtag.py. If so, there is a high chance of structural bias in the scaffolded contigs.
Response: We apologize for the confusion. We did not use ragtag for the PacBio assembly, and all structural and variant comparisons were done using the PacBio assembly. However, we did use ragtag for the Nanopore assembly that is included in this study as an additional resource to our community. These data were not used for variant calling though.
- How Prokka differed from Braker2 for the Mitochondria/API annotation? This needs to be very well described since prokka is made for prokaryotic organisms and not for eukaryotic ones. And Braker2 uses a custom build dataset for training, which I believe contains known information about MIT/API for Plasmodium species.
Response: We first applied Braker2 to the organellar genomes and identified only 6 genes in the apicoplast genome and only 2 genes in the mitochondrial genome. Due to their prokaryotic origin, we then tested if Prokka could alleviate this issue. To do so, we applied Prokka to the 17X reference genome and found that it detected all of its annotated organellar genes. Therefore, we also applied Prokka to our Py17XNL genome to annotate the genes found on the apicoplast and mitochondrial genomes. As a final validation check, the gene annotations on these two organellar genomes are effectively identical between 17X and 17XNL. This is consistent with the sequencing results and assemblies that show that the apicoplast genome is identical and the mitochondrial genome differs in a single, notable deletion in 17XNL.
- Figure 5B, what is the peak observed in the mitochondria? What genes? Repeats?
Response: What appears to be an inward pointed trough actually reflects the deletion of bases in 17XNL compared to the 17X assembly. We have clarified this in the manuscript on Lines 296-297 and in the legend of Figure 5.
Minor comments: - For Oxford nanopore sequencing using the ligation kit, did the group check for potential chimeric reads generated by the protocol?
Response*: We did. We used the adapter trimming software, Porechop, to identify and bin chimeric reads that were eliminated from the dataset. This method is described in the Makefile associated with the manuscript. *
- Check if all species are italicized (for example, line 187 P. yoelii is not)
Response: We have italicized this instance of P. yoelii and have reviewed the document to search for any other words that should be italicized.
- In methods add the parameters for minimap2 for the direct RNA alignment
Response*: We would encourage readers to view our MakeFile that has all of the commands and parameters used for the bioinformatic work reported here. *
- For variant calling, I would use a minimum of 10x coverage to make a variant call instead of 5x. Besides looking well reproducible between all checks, I would be careful mainly with the single bp deletions with a such low threshold.
Response: Read counts for the called variants were generally greater than 20. Moreover, we took these validations a step further and manually curated these variants using the data from multiple sequencing platforms used in this study to ensure high rigor in making these variant calls. We have further clarified this in the revised manuscript.
- In some parts of the methods, the authors mentioned slight modifications in some protocols (for example, lines 443 and 454), besides well described in the text, could you highlight what were the modifications in the text? This will facilitate many other researchers to understand why those modifications were needed.
Response: We have clarified these modifications in the revised manuscript. In short, these modifications consisted of: 1) For the HMW gDNA prep kit, an agitation speed of 1500 rpm was used as opposed to the recommended 2000 rpm due to limitations of our instruments. 2) A slow end over end mixing by hand was preferred over using a vertical rotating mixer as yield was consistently greater with this change. 3) For the RNeasy kit, the lysate was passed through a 20-gauge needle for homogenization of the sample. Instead of an on-column DNaseI treatment, the RNA was treated with DNaseI off of the column to promote complete DNA digestion. 4) A second elution from the RNeasy column was performed in order to improve yield.
- As mentioned in the major, the data analysis method section needs rework to remove results from the text.
Response: We have revised the manuscript accordingly.
- The group mentioned that small contigs not mapping to Py17X were discarded. What are those? Repeats? Contamination?
Response: These contigs were of mouse origin, as P. yoelii was grown in Swiss webster mice in this work. We have clarified this in the revised manuscript on Lines 183-184.
Reviewer #1 (Significance (Required)):
This work generated a strong method and resource for a better genome assessment of P. yoelii for the community. As I mentioned in my comments, some more details about the findings such as alternative splicing and lncRNAs may strengthen them even more the publication. I know that comparative analysis between Py17X and XNL is not in the scope here, but more information about it, such as a synteny plot would be great for the community to understand that they can rely on this new reference genome. I've been working with eukaryotic and prokaryotic genomes for more than a decade and I have a lot of experience with all the methods presented. I believe that potentially the depth generated for the ONT data may be one of the factors for not reaching the chromosomal level of this isolate, since HiFI was. The group did a great job on the method description, and I believe that the community will be very happy to incorporate this genome as one of the references for this organism.
Response: We are thrilled that you value the data and the rigor of our approaches. We also believed that a direct comparison between 17X and 17XNL strains is critical. Because of this, we provided details of this comparison in Figures 5 and 6, as well as in supplemental files. Because our colleagues often use these strains interchangeably, it is important for our community to know what differences are present between the parental 17X and the cloned 17XNL line. While substantial identity exists between the 17X and 17XNL strains, there are many variants between them, including many that affect genes that are known to have essential functions for the parasite. For this reason and more, we believe the true 17XNL genome assembly will be a preferred reference once it is fully integrated into PlasmoDB.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
The paper has three distinct parts, 1. Assembly of the P. yoelii yoelii 17XNL 2 Annotation of the genome and adding UTR regions 3. Comparing the sequence of 17XNL with 17X .
Assembly: The authors present a novel assembly for the P. yoelii yoelii 17XNL genome. They used two different approaches, comparing Oxford Nanopore (ONT) long reads + Illumina DNA with PacBio Hifi. None of the approaches generated a telomer to telomer assembly so sequences from the 17X reference was used to fill in the mssing sequence.
Response: Please also see the comment from Reviewer 1 and our response. The presence of many repeated elements in the subtelomeric regions leads to the challenges noted here about a telomere-to-telomere assembly, as well. The presence of these elements means that the sequences do not resolve into a single haplotype in an assembly due to conflicting information, not due to lack of coverage. Because of this, we have chosen to harmonize the selected haplotype at these subtelomeric regions with that of 17X, while still acknowledging and providing the complex data associated with the subtelomeric regions.
Annotation Next, they generated long reads (ONT)and Illumina RNA-Seq to improve the annotation. Although, their annotation is not better than the current P. yoelii 17X reference genome in PlasmoDB, they could predict the UTR regions and alternative splice sites due to the 3' capturing approach and long reads. Having the UTR annotated and potentially having alternative splice sides is useful for the field.
Response: We agree that the additional gene model annotations for both UTRs and alternative transcript isoforms is a valuable resource to our community. We are working with PlasmoDB currently to make these data readily accessible.
17XNL - 17X comparison The author compared the 17XNL with the 17X reference. Both genomes were done with Pacbio, and it should be noted that P. yoelii has a GC content of probably ~23% with several homopolymer tracks. Further, the 17XNL genotype was obtained from a 17X culture, so the genomes are expected to be very similar as the author noted in the introduction. The authors found ~2000 differences; some are in genes, but many are indels, which very well could be sequencing errors. Finally, the authors claim that this genome could become relevant for the community as new reference to perform analysis. As their genome is so similar to 17X and they have to show that their annotation is at least as good as the current 17X reference genome (manual curated) and the difference are not due to sequence error in 17X or 17XNL.
Response: As we describe below, we have taken multiple steps to inspect the quality of the 17X genome assembly (it is very robust), to call variants between strains, and to validate them using our data across multiple sequencing platforms and via manual curation. Because of this, we view these as true variants between the 17X and 17XNL genomes
Major comments Overall I struggle to see the need for a "NEW" P. yoelii reference. It would be good to state how similar these genomes are - they are basically identical. As the 17XNL is curated manually, it would have made more sense to me to start from that one and then generate the UTR annotation and include splice sides. This could be easily loaded into an alternative Web-apollo track and then merged to the current annotation to be useful to the community.
Response*: We chose to generate a new reference assembly for 17XNL because the current one is from 2002, remains in >5000 contigs, has gene identifiers that do not align with other current Plasmodium gene models (e.g., PY00204 vs. PY17X_0502200), and historically has had problematic gene models attributed to individual genes. This clean start ensures that users can know the provenance of the underlying data that created the genome assembly and gene models. *
I wonder if many of the differences the authors found between 17X and the 17XNL reference are true. The authors are correct that some differences between 17X and 17XNL are true. I could not find any evidence of genome polishing with tools like Pilon or ICORN to correct sequencing errors, I wonder if these differences are sequencing errors.
Response: The PacBio-based assembly received no error correction or polishing. It should be noted that all variants that were called automatically were also manually verified using data from multiple sequencing platforms generated in this study. Moreover, for coding sequences, we imposed a threshold that 80% of all reads at the variant’s location needed to support the variant in order to be considered true. Through these strict thresholds, we eliminated many potential variants that only had support from one sequencing platform. We highlight several variants that were confirmed through multiple datasets in Table 2.
Did the authors look into the reads of the NCBI - GCA_900002385.2 - assembly? Maybe they could use the underlying Illumina reads if theirs don't have enough coverage. Also, the differences between 17X and 17XNL could be that the reference is wrong. How many pseudo genes did they obtain? Are there more or less than in the current reference?
To confirm the calls, could you also map the 17XNL reads against the 17X reference and see if they are still true. As the same time, map the 17X illumina reads to see if the reference is correct at this state. When looking at the alignments, it can be seen that many different are in low complexity/repetitive regions.
Response: We analyzed both their raw and assembled data to compare them with our results, and we determined that the 17X data and assembly were robust and that these difference likely reflect true variance between the strains. The 17X reference has 57 pseudogenes that are annotated as pir, fam-a/c, or others. Overall, there were 1057 pir genes annotated in the 17X genome, whereas we annotated 1048 for our Py17XNL genome. There were 302 fam-a/b genes annotated in the 17X genome, whereas we annotated 301 for our Py17XNL genome. As noted above, we confirmed variant calls using data from multiple sequencing platforms in this study as well as through manual curation.
The authors sequence their genome with a HiFi Pacbio run and also ONG + DNASeq... but why did they not get 16 chomromes out? For example the current P. yoelii reference was assembled directly into far less pieces than theirs [P. chabaudi assembles into 16 pieces]. Could it be a different read depth or is it the fragment length? Could the authors please comment on that. Also, if there were contigs, why did they fill the sequence with 17X sequence, rather than keeping gaps? So in the end, their sequence is a hybrid, of 17X and 17XNL, right?
Response: Please see our responses above to both Reviewer 1 and 2 regarding the heterogeneity of the subtelomeric regions that indicate that a single haplotype is not readily called. This is not due to insufficient read depth, but rather we believe it reflects something fascinating about Plasmodium genomes in these regions. A recent preprint (doi.org/10.1101/2023.02.02.526885) provides one possible interpretation for this observation.
Why do you think you had less coverage of CCS read around the telomer ends? Do you think it is a systematic issue of the PacBio Hifi? Did you see any evidence of Illumina or ONT reads - or could it be that while culturing the telomer ends dropped off?
Response: See our response above about the challenging nature of the subtelomeric regions of Plasmodium genomes. As above, this is not an issue of coverage per se, but rather of heterogeneous related sequences that are not readily resolved into a single haplotype. In order to minimize the risk of sequencing a genome of a mixture of heterogeneous parasites, we sequenced “Pass 0” parasites received directly from BEI Resources to ensure this genome reflects the established P. yoelii 17XNL clone.
I realised that the authors used a lot of primary tools. I wonder why they chose that path, as there are several tools to do automatic finishing for long read assemblies: Assemblosis, ARAMIS, MpGAP or ILRA. Especially the last one focuses on Plasmodium genomes. Please comment.
Response: We initially started our bioinformatic analyses using established tools such as these. Specifically, we first tried Companion and ILRA, but the results were not superior to those we achieved with the workflow we describe in this manuscript, which also provided greater parameter control.
Also, for the annotation, could it not be better to transfer the manually curated genome annotation with LIFT off or RATT? All these tools are widely used in the generation of reference genomes in the parasitology field. I annotated their sequence with Companion, and although their gene models are good and some of the Companion calls might need improvement, overall, the Companion results look more exact to me.
Response: Companion was the original tool we used for the generation of gene models. While we found that for a pre-package software platform it performed excellently, we found it to be insufficiently customizable and the results were not sufficiently accurate from our assessment. Additionally, lifting over information always raises the risk of imposing a different perspective on what is truly present. We believe that a high quality, de novo assembly is always preferable, and therefore chose this workflow.
The code is very well organised, and it was easy to follow. Are you planning to put it on a GitHub repository?
Response: We appreciate this recognition. We believe clear reporting of the bioinformatics work is critical for rigor and reproducibility. Yes, all of this will also be provided in GitHub to benefit the wider community.
For the annotation in the attachment, there were two files. I had a look at them and they were quite different. As 17X and this genome are basically identical (Response: The two gff files represent either a Nanopore only or hybrid Nanopore+Illumina-based model. The latter produced a more comprehensive annotation of gene models, which is what we have proceeded with. However, we provided both in case end users find value in the Nanopore only annotation which has a 3’ bias due to the mechanism of how sequencing occurs via this approach.
We have found meaningful variations in genome sequence that potentially impact biological function (see Discussion). Therefore, we maintain that these genomes are not basically identical and are useful to the malaria research community for these reasons and more.
It is excellent that the genome is submitted to NCBI. Why are there 18k proteins? Are these the alternative spliced forms?
Response*: We are not certain how this interpretation might have arisen, as we only have reported 7047 potential transcript isoforms to NCBI based upon our data. *
Minor The current Py 17X genome in PlasmoDB is a Pacbio assembly (https://plasmodb.org/plasmo/app/record/dataset/TMPTX_pyoeyoelii17X), but not part of the 2014 paper. It was submitted later to NCBI than the paper the authors cite. Also, the current P. berghei Pacbio genome is from Fougère et al. PLoS Pathog 2016;12(11):e1005917.
Response: We have now made a detailed note about the Py17X PacBio dataset in our revised manuscript on Lines 186-187. Mentions of the current P. berghei genome assembly had already cited the Foug’ere et al. publication.
I tried to open the supplemental tables, but they were all in pdf rather than excel and split over several pages. Two had missing information, e.g. UTR per gene. From the name of the tables, I had an idea of what they should contain, but for a re-submission, it would be good to have them in the correct format.
Response: We agree that provision of the PDFs of the supplemental files is not the ideal way to review these analyses. The complete data was also provided in the Excel files provided to Review Commons. We will ensure that the affiliate journal receives the Excel files for completion’s sake.
To me, the beginning of the results reads a bit like an introduction (the part which sequencing technology to use)
Response: We agree, and as noted to Reviewer 1 above, we have streamlined this section of the revised manuscript.
Could you add to the tables: Sequence Coverage of the three technology, how many contigs you had before ordering the contigs and the number of pseudogenes in the annotation?
Response: This information is now provided in Supplemental Table 3 in the revised manuscript.
I struggle with the section header line 229-230 that the new sequence is more complete as it is a hybrid assembly with 17X. Alternatively, please explain how the consensus was built.
Response: We agree and have revised this section header for accuracy.
The authors correctly state that ONG is great, lines 333ff, but why does it not generate telomer-to-telomer chromosomes in this case? Please discusss.
Response: Please see our response to this above for remarks made by both Reviewer 1 and 2. We have also added clarifying text in our revised manuscript discussing why this may have occurred.
Reviewer #2 (Significance (Required)):
General assessment As mentioned above, I struggle to see this as a strong leap for the malaria community to use this genome, as it is so similar to the current 17X genome, which is manually curated in plasmodb. Response: We agree that it is important to know how similar the genomes of 17X and the cloned 17XNL strain are. It is perhaps even more important to know what the key differences are as well. In this study, we have asked and answered these questions, and identified 2000+ variants between the strains. We have manually curated several of the variants that impact the expression of essential/important genes, and found that biologically meaningful differences exist (see Discussion). Finally, we have also provided additional information on the gene models of 17XNL, including an experimental definition of UTRs and transcript isoforms. Together, we hold that these data will not only match those currently available for 17X, but will exceed them. We are currently working with PlasmoDB to make these data readily accessible to our community.
Advance The authors should make the comparison of ONT and PacBio HiFi clearer and discuss why the technologies still don't generate telomer-to-telomer sequences. From the biological side, none of the found differences were related to the different phenotype between 17X and 17XNL.
Response: We have provided these comparisons and all related data to the reader in this manuscript, as well as through public depositories. Please see above for our responses as to why a true telomere-to-telomere assembly is challenging with Plasmodium parasites, and for a recent preprint that might provide an explanation for this. Finally, the phenotypic differences between 17X and 17XNL are variable, which might reflect differences in individual parasite stocks as has been historically seen in the spontaneous development of lethality in multiple laboratories. While we do not find any particular genetic difference correlates with a specific phenotype, these data using the cloned 17XNL parasite available from BEI provides a robust reference with a defined parasite stock.
Audience: I do agree that adding the UTR sequence will be useful for those working with P. yoelii as a model, or who want to do comparative UTR analysis across species.
Response: We agree that this additional gene model information will be valuable. We are working with PlasmoDB to make this information readily available and are already integrating it into our ongoing studies.
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Referee #2
Evidence, reproducibility and clarity
The paper has three distinct parts,
- Assembly of the P. yoelii yoelii 17XNL 2 Annotation of the genome and adding UTR regions
- Comparing the sequence of 17XNL with 17X .
Assembly: The authors present a novel assembly for the P. yoelii yoelii 17XNL genome. They used two different approaches, comparing Oxford Nanopore (ONT) long reads + Illumina DNA with PacBio Hifi. None of the approaches generated a telomer to telomer assembly so sequences from the 17X reference was used to fill in the mssing sequence.
Annotation Next, they generated long reads (ONT)and Illumina RNA-Seq to improve the annotation. Although, their annotation is not better than the current P. yoelii 17X reference genome in PlasmoDB, they could predict the UTR regions and alternative splice sites due to the 3' capturing approach and long reads. Having the UTR annotated and potentially having alternative splice sides is useful for the field.
17XNL - 17X comparison The author compared the 17XNL with the 17X reference. Both genomes were done with Pacbio, and it should be noted that P. yoelii has a GC content of probably ~23% with several homopolymer tracks. Further, the 17XNL genotype was obtained from a 17X culture, so the genomes are expected to be very similar as the author noted in the introduction. The authors found ~2000 differences; some are in genes, but many are indels, which very well could be sequencing errors.
Finally, the authors claim that this genome could become relevant for the community as new reference to perform analysis. As their genome is so similar to 17X and they have to show that their annotation is at least as good as the current 17X reference genome (manual curated) and the difference are not due to sequence error in 17X or 17XNL.
Major comments
Overall I struggle to see the need for a "NEW" P. yoelii reference. It would be good to state how similar these genomes are - they are basically identical. As the 17XNL is curated manually, it would have made more sense to me to start from that one and then generate the UTR annotation and include splice sides. This could be easily loaded into an alternative Web-apollo track and then merged to the current annotation to be useful to the community.
I wonder if many of the differences the authors found between 17X and the 17XNL reference are true. The authors are correct that some differences between 17X and 17XNL are true. I could not find any evidence of genome polishing with tools like Pilon or ICORN to correct sequencing errors, I wonder if these differences are sequencing errors. Did the authors look into the reads of the NCBI - GCA_900002385.2 - assembly? Maybe they could use the underlying Illumina reads if theirs don't have enough coverage. Also, the differences between 17X and 17XNL could be that the reference is wrong. How many pseudo genes did they obtain? Are there more or less than in the current reference?
To confirm the calls, could you also map the 17XNL reads against the 17X reference and see if they are still true. As the same time, map the 17X illumina reads to see if the reference is correct at this state. When looking at the alignments, it can be seen that many different are in low complexity/repetitive regions. The authors sequence their genome with a HiFi Pacbio run and also ONG + DNASeq... but why did they not get 16 chomromes out? For example the current P. yoelii reference was assembled directly into far less pieces than theirs [P. chabaudi assembles into 16 pieces]. Could it be a different read depth or is it the fragment length? Could the authors please comment on that. Also, if there were contigs, why did they fill the sequence with 17X sequence, rather than keeping gaps? So in the end, their sequence is a hybrid, of 17X and 17XNL, right?
Why do you think you had less coverage of CCS read around the telomer ends? Do you think it is a systematic issue of the PacBio Hifi? Did you see any evidence of Illumina or ONT reads - or could it be that while culturing the telomer ends dropped off?
I realised that the authors used a lot of primary tools. I wonder why they chose that path, as there are several tools to do automatic finishing for long read assemblies: Assemblosis, ARAMIS, MpGAP or ILRA. Especially the last one focuses on Plasmodium genomes. Please comment.
Also, for the annotation, could it not be better to transfer the manually curated genome annotation with LIFT off or RATT? All these tools are widely used in the generation of reference genomes in the parasitology field. I annotated their sequence with Companion, and although their gene models are good and some of the Companion calls might need improvement, overall, the Companion results look more exact to me. The code is very well organised, and it was easy to follow. Are you planning to put it on a GitHub repository? For the annotation in the attachment, there were two files. I had a look at them and they were quite different.
As 17X and this genome are basically identical (<2k variants), would it not be better to transfer the genes from the 17X genome and then add the UTR (see comment before)? The 17X is manually curated. Table 1 and figure 4 show that it is far better. I doubt that the community would use this genome, if the annotation is not lifted over.
There are two gff files in the supplemental. Which one is better? It is excellent that the genome is submitted to NCBI. Why are there 18k proteins? Are these the alternative spliced forms?
Minor
The current Py 17X genome in PlasmoDB is a Pacbio assembly (https://plasmodb.org/plasmo/app/record/dataset/TMPTX_pyoeyoelii17X), but not part of the 2014 paper. It was submitted later to NCBI than the paper the authors cite. Also, the current P. berghei Pacbio genome is from Fougère et al. PLoS Pathog 2016;12(11):e1005917. I tried to open the supplemental tables, but they were all in pdf rather than excel and split over several pages. Two had missing information, e.g. UTR per gene. From the name of the tables, I had an idea of what they should contain, but for a re-submission, it would be good to have them in the correct format. To me, the beginning of the results reads a bit like an introduction (the part which sequencing technology to use) Could you add to the tables: Sequence Coverage of the three technology, how many contigs you had before ordering the contigs and the number of pseudogenes in the annotation? I struggle with the section header line 229-230 that the new sequence is more complete as it is a hybrid assembly with 17X. Alternatively, please explain how the consensus was built. The authors correctly state that ONG is great, lines 333ff, but why does it not generate telomer-to-telomer chromosomes in this case? Please discusss.
Significance
General assessment As mentioned above, I struggle to see this as a strong leap for the malaria community to use this genome, as it is so similar to the current 17X genome, which is manually curated in plasmodb.
Advance The authors should make the comparison of ONT and PacBio HiFi clearer and discuss why the technologies still don't generate telomer-to-telomer sequences. From the biological side, none of the found differences were related to the different phenotype between 17X and 17XNL.
Audience: I do agree that adding the UTR sequence will be useful for those working with P. yoelii as a model, or who want to do comparative UTR analysis across species.
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Referee #1
Evidence, reproducibility and clarity
The manuscript entitled "Long-Read Genome Assembly and Gene Model annotation for the Rodent Malaria Parasite P. yoelii 17XNL" is a well-written manuscript providing updates and important observations about the genome assembly and annotation of this specific non-lethal isolate. The group overall did a great job showing how the application of newer technologies such as long-read DNA and direct RNA sequencing to generate top-quality genomes to be used as a reference for the community. Here are some comments about the work presented:
Major comments:
- The authors added several result information across the methods section. Making the text repetitive, since the same is also presented in the results section. Please revise the method section to remove results from this section.
- Some methods are also redundant in the Result section. For example, in line 141-142, the group describe which DNA extraction kit they used (again this is correctly mentioned in the methods section).
- Besides important, the group added several information about method comparison between base call accuracy and sequencing methods. I agree that having this information in the supplemental material is great, but I would be careful to not focus too much on those, since most of the observations are already well-known by the community and focus more in the biological relevance of what is being generated with the newly updated genome.
- The group did a great job generating two versions of the genome, and an updated gene annotation set using long-read sequencing. But the major question is, how about alternative splicing? They mention the use of it (line 350) but I don't see any result about how many alternative transcripts were observed, and if they were differentially detected in different life stages of the sets used for the RNA sequencing. This is a very important result to be added since one of the key pieces of information that long-read RNA sequencing brings for Genome annotation.
- Same observation as above for potential long ncRNAs.
- From what I understand the Hifi run was able to generate a gapless genome assembly and the ONT run did not. What was the final coverage for each? From my experience with P. falciparum genomes, ONT even with the rapid kit was able to generate chromosomal level assemblies if the coverage was >100x (but again, this is not a rule). Add those valuable observations about the depth so the reader can check if other variables in the comparison should be made.
- Also be sure that the structural comparisons between the genomes are not the ones used after running ragtag.py. If so, there is a high chance of structural bias in the scaffolded contigs.
- How Prokka differed from Braker2 for the Mitochondria/API annotation? This needs to be very well described since prokka is made for prokaryotic organisms and not for eukaryotic ones. And Braker2 uses a custom build dataset for training, which I believe contains known information about MIT/API for Plasmodium species.
- Figure 5B, what is the peak observed in the mitochondria? What genes? Repeats?
Minor comments:
- For Oxford nanopore sequencing using the ligation kit, did the group check for potential chimeric reads generated by the protocol?
- Check if all species are italicized (for example, line 187 P. yoelii is not)
- In methods add the parameters for minimap2 for the direct RNA alignment
- For variant calling, I would use a minimum of 10x coverage to make a variant call instead of 5x. Besides looking well reproducible between all checks, I would be careful mainly with the single bp deletions with a such low threshold.
- In some parts of the methods, the authors mentioned slight modifications in some protocols (for example, lines 443 and 454), besides well described in the text, could you highlight what were the modifications in the text? This will facilitate many other researchers to understand why those modifications were needed.
- As mentioned in the major, the data analysis method section needs rework to remove results from the text.
- The group mentioned that small contigs not mapping to Py17X were discarded. What are those? Repeats? Contamination?
Significance
This work generated a strong method and resource for a better genome assessment of P. yoelii for the community. As I mentioned in my comments, some more details about the findings such as alternative splicing and lncRNAs may strengthen them even more the publication. I know that comparative analysis between Py17X and XNL is not in the scope here, but more information about it, such as a synteny plot would be great for the community to understand that they can rely on this new reference genome.
I've been working with eukaryotic and prokaryotic genomes for more than a decade and I have a lot of experience with all the methods presented. I believe that potentially the depth generated for the ONT data may be one of the factors for not reaching the chromosomal level of this isolate, since HiFI was. The group did a great job on the method description, and I believe that the community will be very happy to incorporate this genome as one of the references for this organism.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
Banerji and colleagues measure DUX4 and target gene expression over a time course in doxycycline-inducible myoblasts to estimate kinetic parameters and rates underlying the transition of non-expressing cells through DUX4-expressing cells to cell death. They then use these parameters to model the rate of appearance of DUX4+ cells, DUX4 target gene expression, etc. in cells from FSHD patients, and derive a model that predicts that over 100 days around one fourth of cells die while less than 1% of cells express DUX4 or its target genes at any given time. This is somewhat similar to what is seen in FSHD patients, where DUX4 expression is infrequent in cultured cells, while patients eventually have substantial muscle loss. The experiments are well-designed and explained clearly.
We thank the reviewer for their kind comments on our manuscript and for acknowledging the similarity between our model simulation and both cell biological and clinical features of FSHD.
Reviewer #1 (Significance (Required)):
The primary significance of this study is that the field has a sense that the damage seen in patient muscle is not congruent with the low expression of DUX4 in patients, and the model showing many cells dying with only a few cells expressing DUX4 at any given time suggests that overall damage can be greater than that observed in any particular snapshot.
However, it is important not to conflate low frequencies of DUX4+ nuclei in cultured myoblasts with "DUX4 being difficult to detect" as in p 12, Discussion. DUX4 is difficult to detect, indeed basically not detected, in muscle biopsy specimens, but in cells in vitro, DUX4 is fairly easy to detect, albeit in quite low numbers of cells. Since the study evaluates cells in vitro, it is important to make clear that the situation in vivo is qualitatively different from that seen in vitro, namely DUX4 not being detected, and the authors should clarify this importance difference.
We appreciate this important point that DUX4 detection is extremely challenging in FSHD patient muscle biopsies, compared to in vitro cell culture of FSHD myoblasts and myotubes, a topic we considered at length in our recent review (Banerji and Zammit 2021, https://doi.org/10.15252/emmm.202013695).
Detection of DUX4 mRNA in muscle biopsies is highly variable requiring nested RT-qPCR, and protein detection is even less robust, though this has been achieved via western blot in less affected FSHD muscle (Tassin et al., 2013, DOI: 10.1111/j.1582-4934.2012.01647.x) and using a proximity ligation assay (Beermann et al. 2022, doi: 10.1186/s13104-022-06054-8). DUX4 target gene expression is detected in inflamed FSHD muscle but less robustly in non-inflamed muscle, indicating the recent presence of DUX4 protein, and also implying that a systemic component may activate DUX4 expression in vivo.
Conversely in cell culture of FSHD muscle cells, DUX4 mRNA is typically found in 0.5-3.8% of myonuclei (van den Heuvel et al., 2019, https://doi.org/10.1093/hmg/ddy400) and protein in around 1/1000 myonuclei (Snider et al., 2010, https://doi.org/10.1371/journal.pgen.1001181). Arguably these levels are still very low and DUX4 is still ‘difficult to detect’ in vitro, for example DUX4 expression is never seen above the limit of detection in bulk RNA-seq of FSHD patient cultured myoblasts. However, we fully appreciate that DUX4 is ‘easier to detect’ in vitro versus in vivo.
Regardless, anti-DUX4 therapy is currently the most heavily funded approach to FSHD treatment, and all anti-DUX4 therapies currently under consideration were first investigated in the myoblast in vitro setting. Thus, the aim of our model is to provide an additional level of in silico screening for anti-DUX4 therapy, before progressing to in vitro investigation.
Full consideration of DUX4 expression in vivo (while an exciting prospect), would require significantly more data than is currently available (relating to inflammation, vascularity and other systemic factors) and a highly complex model which is beyond the remit of this investigation.
We will clarify in the manuscript that our model applies in vitro, highlighting differences with in vivo and emphasising that the model is limited for understanding DUX4 expression in FSHD muscle biopsies.
We will also change the title to emphasise this point to: ‘In silico FSHD muscle cell culture for modelling DUX4 dynamics and predicting the impact of therapy’.
A second reason for caution in extrapolating correlates from the in vitro model to the disease process in muscle tissue is that in vivo there is a continual source of replacement cells, as the authors have shown in a previous study. Have the authors attempted to model a situation in which new cells are provided into the system at some rate, related to the amount of death occurring at different times? Although the authors mention that the static cell number is a limitation of the model, it would be valuable to revisit or explore this idea in the Discussion section, if only to provide the reader with a more pragmatic perspective.
We are focused specifically on modelling the in vitro differentiated myogenic cell setting to provide an in silico pre-screening tool for assessing anti-DUX4 therapy, rather than attempting to model the full pathology in vivo, which given data limitations, is beyond the scope of our study. As the reviewer notes, we highlight this limitation relating to proliferation when we introduce the model in the results stating: ‘Cells are assumed not to proliferate over the evolution of the model. We restrict applications to differentiating cells which have exited the cell cycle.’
As the reviewer likely appreciates, DUX4 expression in proliferating cells differs significantly from differentiated cells. The single nuclear and single cell RNA-seq data we employ to derive the parameters underlying DUX4 and DUX4 target transcription rates are from non-proliferating myocytes differentiated for 3 days. Hence it is not appropriate to include proliferation in this model, as the transcription rates we use will not be accurate for proliferating cells.
Introducing proliferation will also require us to estimate the proliferation rate of FSHD myoblasts, and how it is impacted by DUX4 expression, as well as how DUX4/target transcription rates change as the proliferating cells differentiate. Though this is an interesting application there is not sufficient data available to produce this wider scale model at present.
We thus restrict application of our model to the non-proliferating differentiated setting, which can be easily accessed in vitro to screen anti-DUX4 therapy.
We appreciate the observation that in vivo, there will be addition of new cells during muscle regeneration, and will include this in discussion in the updated manuscript. We will also expand on our discussion of what data would be required to include proliferation in our model in the revised manuscript.
The second part of the paper models presence of DUX4 in nuclei based on diffusion from expressing to non-expressing nuclei, and characterizes this as the activity of "an infectious agent, able to spread from one nucleus to another by adapting epidemiological compartment models". The relationship to an infection process is probably not the ideal way to characterize this process, because an infection implies the setting up of new sites of production of the agent, DUX4, where what is really happening is that DUX4 diffusing into these other nuclei isn't leading to more DUX4 production, it is just diffusing into nearby nuclei and accumulating there. Unless I am misunderstanding, the authors are simply showing that a larger number of nuclei will be positive in a system in which cells are fusion products having many nuclei than in a system in which all nuclei are isolated within their own cells.
The term ‘infectious agent’ is only an analogy and implies some preconceptions. The reviewer interprets our infectious agent model as: ‘an infection implies the setting up of new sites of production of the agent, DUX4, where what is really happening is that DUX4 diffusing into these other nuclei isn't leading to more DUX4 production, it is just diffusing into nearby nuclei and accumulating there. Our bespoke model is not based on a direct mapping of e.g., viral infection to our setting. In our case, the ‘infectious agent’ DUX4 causes harm but does not replicate. DUX4 protein is a transcription factor and thus activates the expression of target genes (not including DUX4). In our model, DUX4 can be seen as the ‘infectious agent’, and expression of DUX4 target genes can be seen as the ‘infection’, which leads to cell death. DUX4 can either stay in the ‘infected’ cell until it dies or diffuse to another cell to spread the ‘infection’.
The reviewer interprets the results of our model as ‘simply showing that a larger number of nuclei will be [DUX4] positive in a system in which cells are fusion products having many nuclei than in a system in which all nuclei are isolated within their own cells’.
In fact, we make several observations: firstly we compare single cell RNA-seq of unfused myocytes to single nuclear RNA-seq of fused muti-nucleated myotubes and find that the latter has a greater proportion of cells expressing DUX4 target genes (i.e. more infection). The proportion of DUX4 positive cells (i.e. the amount of infectious agent produced) is similar in the two settings. We posit that this difference in DUX4 target gene positive cells (infection) may be due to DUX4 protein diffusing between cells in the myotube syncytium and activating the targets in neighbouring nuclei (i.e., greater mobility of the infectious agent/loss of quarantine). Note that there are many other possibilities, such as fusion causing an increase in DUX4 transcription/mRNA stability etc.
We find that by introducing a DUX4 protein diffusion term (loss of quarantine) into our model we can completely explain the difference between DUX4 target gene expression (infection) in real data of unfused versus fused myonuclei, despite identical levels of DUX4 (infectious agent). This is a novel finding providing evidence for DUX4 protein diffusion in syncytial myonuclei, which represents an often overlooked therapeutic target/consideration in FSHD. We also provide the first explicit quantification of this diffusion rate via our model as well as a framework for investigators to understand how modifying this parameter can impact DUX4 induced myotoxicity.
We will better define our ‘infectious agent’ analogy and clarify our interpretation in the updated manuscript.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
An in silico FSHD muscle fibre for modelling DUX4 dynamics
Summary
This paper studies and mathematically models the stochastic process of presence or absence of DUX4 expression in individual myocytes in FSHD, which underlies the very small proportion of individual cells which do express DUX4. The paper is valuable in providing a mathematical basis for modelling this, and hence a basis by which to study the effects of other factors or potential therapeutic interventions which may influence the overall proportion of cells which do express.
We thank the reviewer for the kind comments on our manuscript and recognition of its value to design/screening of potential therapeutics for FSHD.
To understand the paper fully, requires a familiarity with mathematical and statistical reasoning which will be beyond many potential readers, including this reviewer, but I hope that the following specific comments may still be helpful.
We appreciate the reviewer’s candour regarding their understanding of the more advanced mathematical aspects the paper. Interdisciplinary work such as ours may introduce concepts which are unfamiliar to some readers.
As the reviewer will appreciate, understanding a complex process like DUX4 expression requires new and more sophisticated approaches, having largely eluded the conventional approaches to date. The main mathematical tools employed in our work derive from the well-established stochastic gene expression and epidemiological compartment models. We have endeavoured to make the mathematics self-contained to facilitate understanding and will edit to further improve accessibility.
Major Comments
- A potential major concern is that the modelling seems to be based largely on combined data from 27 DUX-4 positive myocytes out of 5133 myocytes from 4 FSHD patients described by Van Den Heuvel et al, 2019 (ref 17), but with 2 being FSHD1 and 2 FSHD2, and without the 2 patients within each FSHD type being matched for D4Z4 fragment length (RU = 'residual units'), which can be expected to be a major influencing factor on the threshold for expression in any one myocyte upon which the stochastic process acts. Thus, one can expect lower RU number to show a greater proportion of expressing cells within FSHD1, and to some extent similarly within FSHD2 (although in FSHD2, different SMCHD1 mutations will also have different 'strengths'). The 4 patients were : 2x FSHD1 (3RU ; 6RU); 2x FSHD2 (12RU ; 18 RU). In the paper of Den Heuvel et al it is evident that the DUX4-positive cell count differs between these 4 cell lines very much as might be anticipated from their D4Z4 RU number. Thus (Figure 2 in that paper) patient 1.1 (3RU) has 12 positive cells, whereas patient 1.2 (6RU) has only 2 positive cells. Patient 2.1 (SMCHD1 exon 37 mutation, and 12 RU) has 11 positive cells, whereas Patient 2.2 (SMCHD1 exon 10 mutation, and 18 RU) has only 2 positive cells. Therefore, if the validity and accuracy of the modelling here would be affected by genetic heterogeneity, the authors should present their calculations and analyses based only on the 2 patients who account for 23/27 of the positive cells, and furthermore, that the calculations and modelling are performed and presented for those 2 patients separately.
The reviewer raises the important point that 2/5 of the parameters of our model were derived from the single cell RNA-seq data set of van den Heuvel et al., which comprises 4 FSHD patients of various genotype. The reviewer remarks that the number of DUX4 positive cells reported for each patient in the van den Heuvel data, differs according to genotype, in line with the known inverse association between DUX4 expression and D4Z4 short allele length. Figure 2E in van den Heuvel et al., to which the reviewer refers, does not present absolute DUX4+ cell counts, but rather ‘DUX4 affected’ cell counts, based on the expression of 67 DUX4 target genes. The numbers in that figure thus differ from ours. We caution that the number of ‘DUX4 affected’ cell counts must be normalised by the total number of cells assayed per patient, to obtain a ‘DUX4 affected’ proportion for each patient. However, we appreciate the reviewers point.
A concern is raised that we have pooled all 4 FSHD patients to derive our parameter estimates, essentially averaging over genotypes. The two parameters we derived from this data are ‘the average DUX4 transcription rate, and ‘the average DUX4 target gene transcription rate.
The average DUX4 target gene transcription rate was derived from consideration of DUX4 target gene expression in the 27 FSHD cells already expressing DUX4 mRNA. Since the capacity of DUX4 to activate its target genes is not known to depend on genotype, we feel it is appropriate to pool the patients to estimate this parameter.
For the average DUX4 transcription rate however, we do appreciate the reviewer’s concern that patient genotype may impact the estimate. The reason for pooling all patients is partly statistical. As there are so few cells expressing DUX4 in each patient, the gradient descent algorithm we employed to estimate the 3 rate parameters for the promoter switching model of DUX4, may fail to converge for every patient separately. By pooling patients, we obtained an estimate that may not be true for an individual but represented the ‘average’ transcription rate of DUX4 in these 4 FSHD patients, hence our careful use of wording when defining the average DUX4 transcription rate parameter.
Our in silico model of DUX4 expression is proposed as a pre- in vitro screening tool to guide anti-DUX4 therapy for the general population, not a digital twin of a single FSHD patient, and so an average DUX4 transcription rate derived from pooling available data is optimal.
This average measure is not irrelevant in light of genetic variation and in fact may be more informative for anti-DUX4 therapeutics intended for a general population, but less informative for genotype stratified therapeutic design. Genotypic stratification by D4Z4 repeat length was not performed in recent FSHD clinical trials for anti-DUX4 therapy (e.g., losmapimod: NCT04003974), which recruited patients with all pathogenic D4Z4 repeat lengths, motivating an average over genotype design in the first instance.
We will elaborate in detail on the reasons for patient pooling throughout the manuscript.
We will attempt the analysis the reviewer suggests i.e. ‘the authors should present their calculations and analyses based only on the 2 patients who account for 23/27 of the positive cells…separately’. However, this is conditional on algorithm convergence given the smaller number of cells, and we must caveat that in doing so we will have eliminated 2 patients purely on the basis of low DUX4 expression and so will over-estimate the average DUX4 transcription rate for FSHD patients in general.
In order to be of value for assessing potential interventions more widely in FSHD, the authors would then need, in further publications, to extend their analysis similarly to genetically homogeneous myocyte sets with other RU number.
We agree with the reviewer that for genotypically stratified therapeutic design, based on D4Z4 short allele length, personalised or genotype specific estimates of the DUX4 transcription rate should be calculated. However, as the reviewer clearly appreciates, developing such FSHD digital twins, though exciting, would require a much larger library of single cell RNA-seq datasets describing FSHD patients of various genotypes than is currently available.
We will explore this in an updated discussion.
Specific points.
Introduction 4th paragraph: - 'Single cell and single nuclear transcriptomic studies find only 0.5-3.8% of in vitro differentiated FSHD myonuclei express DUX4 transcript16,17. Immunolabelling studies only detect DUX4 protein in between 0.1-5% of FSHD myonuclei18,19.' The authors should comment whether there is any evidence from the data in these references, or from other publications, regarding differences in these proportions by FSHD diagnosis (I or II) or by D4Z4 residual number?.
We will expand discussion in the updated manuscript of the result (explained by the reviewer) that the number of DUX4 affected cells found in the single cell RNA-seq dataset of van den Heuvel may correlate with genotype. We will contrast this with the observation that immortalised isogenic FSHD myoblast clones isolated from a single FSHD patient can also have a very wide range of DUX4 expression (e.g., Krom et al., doi: 10.1016/j.ajpath.2012.07.007). This will highlight the mix of poorly understood genetic and epigenetic factors impacting DUX4 expression and further motivate an average model in the first instance.
Introduction 5th paragraph: - Importantly, a recent phase 2b clinical trial of the DUX4 inhibitor losmapimod failed to reach its primary endpoint of reduced DUX4 target gene expression in patient muscle, despite improvement in functional outcomes23. Please state here whether or not there was any evidence that DUX4 expression itself was reduced in this trial. It would help if the authors could also add here an interpretive comment as to whether this indicates that the current presumed target genes for DUX4 are not in fact the ones important for FSHD, or whether their expression might be retained from compensatory upregulation by other upstream regulators. The authors should expand briefly also in the introduction on the evidence for toxicity of target gene expression.
We are very happy to include a discussion of these points, which we explore in considerable detail in our recent review of DUX4 in FSHD (Banerji and Zammit 2021, https://doi.org/10.15252/emmm.202013695). Briefly, the losmapimod trial did not publish data showing they measured DUX4, as Reviewer #1 pointed out DUX4 is highly difficult to detect in patient muscle biopsies and dynamic change following anti-DUX4 therapy has certainly never been observed. Expression of four DUX4 target genes was intended as a surrogate measure of DUX4 activity, reasons for its lack of change in this trial is very much a topic of open debate, which we will outline in an updated manuscript.
Results 2nd paragraph: - We first describe the compartment model. FSHD single myocytes can express DUX4 and therefore DUX4 target genes; DUX4 target gene expression leads to cell death19,27,28. Please indicate whether the evidence in these studies is independent of DUX4. Ie. Is there independent evidence that it is definitely the target gene expression, rather than DUX4 expression per se, that leads to cell death, especially if losmapimod improves function by inhibiting DUX4, but has no impact on these target genes.
This is an important point raised by the reviewer and one that we have rigorously investigated (Knopp et al., 2016, https://doi.org/10.1242/jcs.180372).
The c-terminus of DUX4 is a potent transcriptional activator and is required for DUX4 target gene activation, while an inverted centromeric D4Z4 repeat unit encodes a version of DUX4 lacking the c-terminus, named DUX4c. We constructed a library of DUX4 expression constructs encoding: DUX4, DUX4c, tMALDUX4 (DUX4 with the c-terminus removed), DUX4-VP16 (DUX4 with the c-terminus replaced by the VP16 transactivation domain) and DUX4-ERD (DUX4 with the c-terminus replaced by the engrailed repressor domain). In a series of experiments outlined in Knopp et al., we clearly demonstrated that only DUX4 and DUX4-VP16 could activate DUX4 targets in C2C12 murine myoblasts and that only these constructs could induce apoptosis. Our prior work provides this clear link between DUX4 target gene expression and cell death. We will include discussion of this point in the updated manuscript.
Results 2nd paragraph Item 4 : - 𝑅(𝑡) - a resigned state where the cell expresses no DUX4 mRNA but does express DUX4 target mRNA (DUX4 -ve/Target gene +ve: i.e. a historically DUX4 mRNA expressing cell) Since the mRNA is from the target genes, why should it be produced only in response to DUX4 expression ? ie. Please indicate the evidence to say that these must be 'historically DUX4 mRNA expressing cells', rather than target gene expression in response to other factors, or even autonomously.
The reviewer raises the point that the 8 DUX4 target genes we investigate may be expressed in a DUX4 independent manner, making DUX4 target gene +ve, DUX4 -ve cells, potentially not historic DUX4 expressing cells. We selected these 8 genes as they are confirmed DUX4 targets by ChIP-seq and have been identified as upregulated by DUX4 in every transcriptomic analysis of DUX4 over-expressing human myoblasts (Banerji and Zammit 2021, https://doi.org/10.15252/emmm.202013695). We provide further evidence for these genes indicating historic DUX4 in these cells: first, we never find a single transcript for any of these 8 target genes in 1914 single myocytes and 77 single nuclei from control individuals, suggesting that their expression requires an FSHD genotype (and thus likely DUX4 expression). Second, our investigation of these genes in the single cell RNA-seq data set of van den Heuvel demonstrated that in the presence of DUX4, expression of all 8 genes significantly increase (Figure 3D), indicating activation by DUX4.
While this is evidence that the 8 targets are specific to DUX4, we accept that it is not 100% conclusive and these genes may also be induced by some other factor related to the FSHD genotype. We will thus highlight this possibility of other modes of expression in the discussion.
Results - Estimating the kinetics of DUX4 mRNA - 2nd paragraph: - DUX4 expression was induced with 250 ng/ml doxycycline for 7 hours .... Might some of the laboratory detail here be better placed in the 'Methods' section ?
We will move some methodological detail to the methods as suggested.
Results - Estimating the kinetics of DUX4 mRNA - 4th paragraph: - '...from 4 FSHD patients (2 FSHD1 and 2 FSHD2).' Please give additional information about these patients - ie. Age, sex, severity (or age-onset), and genetic results - perhaps best done as a Table in this paper rather than only by reference back to the Van den Heuvel et al. paper (see main comment 1 above).
We will provide this information in a table as the reviewer suggests.
Results - Estimating kinetics of DUX4 target activation - 2nd paragraph: - '8 DUX4 target genes......expression was restricted to FSHD cells/nuclei and never observed in controls.' So are these genes normally only expressed in the zygote , rather than post-birth (except perhaps the testis)? The authors should comment on this.
The 8 DUX4 target genes are not well characterised in terms of their expression pattern in other tissues. We are confident that in our data sets they are not expressed in healthy myocytes and myotubes, but it is difficult to expand confidently on other tissues due to lack of data. We will include comment on what is known about their expression pattern during zygotic genome activation and in testicular tissue, but this cannot be an exhaustive description of their expression. For example, DUX4 has been detected in keratinocytes, osteoblasts and lymphocytes, but the target genes have not been characterised in such settings. We still have much to learn about the expression of these genes outside of the muscle setting.
Results - Estimating kinetics of DUX4 target activation - 4nd paragraph: - In the presence of DUX4 mRNA the proportion of time the promoters of the 8 DUX4 target genes remained in the active state,....significantly increased. It would be interesting to know if any of these temporal dynamic descriptors of DUX4 target promoters differ consistently between sample II-2 and II-1 and in the same direction between I-2 and I-1. ie. Might the same factors (eg. D4Z4 copy number) which may affect presence/absence of DUX4 also affect other cellular measures of DUX 4 ?
The reviewer raises an interesting point about genetic modifiers of DUX4 transcriptional activation. As discussed in response to point 1, the DUX4 target gene transcription rate is derived from the 27 cells expressing DUX4. As there are so few cells expressing DUX4 in each patient (sometimes We will attempt analysis of the two patients which provide the majority of DUX4 positive cells separately, as the reviewer requested in point 1. If successful, we will investigate whether the derived DUX4 target gene expression parameters differ between these two patients as the reviewer suggests. While this limited data will not permit anything definitive about impact of D4Z4 repeat length on DUX4 target gene expression, it may highlight the existence of inter-individual differences in such parameters.
Results - Compartment model simulation - 4th paragraph: - '...so that after 10 days 26.3% of cells had died.' The authors need to give data here also for controls. Ie. What proportion of cells die after 10 days in controls ?
As mentioned in the introduction of our model, we only model DUX4 dependent cell death. As control cells do not express DUX4 they cannot experience cell death by this mechanism. The reviewer can therefore interpret this result as excess death due to DUX4, i.e., the 26.3% of FSHD cells die which would not have died in control cells. We will clarify this point in an updated manuscript.
Discussion - 1st paragraph: - ' However, DUX4 expression in FSHD muscle demonstrates a complex dynamic with DUX4 mRNA, protein and target gene accumulation all difficult to detect2,21. Understanding this complex dynamic is essential to the construction of optimal therapy' So, it presumably follows that comparison by known genetic or demographic modifiers of disease severity (such as D4Z4 copy number) could be of fundamental importance in interpreting this dynamic and hence the results of clinical trials) (see Main point 1, and point 7).
This point appears to generally be a reiteration of the reviewer’s initial concerns on genotypic variation in the van den Heuvel et al., data set. We have addressed these concerns in response to points 1, 2 and 9.
Discussion - 6th paragraph: - 'Our model predicts
We will update the manuscript to amend to ‘DUX4 target gene mRNA positive’. The reviewer again raises the concern of genotypic variability, we will of course discuss this and perform additional analysis as detailed above (points 1, 2, 9 and 11).
Minor comments
Methods - scRNAseq and snRNAseq data - 2nd paragraph: - '..2 sperate patients...' Typo. to correct.
We thank the reviewer and will address this typo.
Methods - Hypothetical scenarios for raising 𝑬[𝒎] under the promoter-switching model- 1st paragraph: - '...constant in the second...' needs punctuation.
We thank the reviewer and will address this typo.
Methods - Cellular Automaton Model - 3rd paragraph: - '...according the non-syncytial...' Typo : '...according to...'
We thank the reviewer and will address this typo.
Methods - Genetic algorithms - 3rd paragraph: - '...elitism of 5%, mutation probability 0.1, crossover probability 0.8,...' Should these parameters be given in the same format to avoid any confusion - ie. all as probability, or all as percentages ?
We thank the reviewer and will change all parameters and probabilities.
Reviewer #2 (Significance (Required)):
Please see comments in the 'Evidence, reproducibility and clarity' box above.
This paper is valuable in providing a mathematical basis for modelling the stochastic process of presence or absence of DUX4 expression in individual myocytes in FSHD (facioscapulohumeral muscular dystrophy), and hence a basis by which to study the effects of other factors or potential therapeutic interventions which may influence the overall proportion of muscle cells which do express DUX4, and hence succumb to its toxicity.
This is a specialist field and the nature of presentation of the mathematical modelling in the paper will restrict accessibility to only a very few researchers in this field.
We appreciate that introducing concepts from different fields such as mathematics can present a challenge to some readers. However, new methods and interdisciplinary science are essential to understand complex disorders and this is even more so in complex rare diseases such as FSHD, where diversity in expertise is important. ‘Stochastic’ has been used to describe DUX4’s expression pattern for many years and is commonly used in many FSHD papers and conferences. We have introduced concepts from the well established field of ‘stochastic gene expression’ to understand DUX4 expression in FSHD. The methods are different from conventional approaches used in FSHD, but are arguably the most natural framework in which to understand DUX4.
We have provided user-friendly programs that can be used to estimate the effects on DUX4 parameters of multiple variables to make the paper useful, even if some of the more advanced mathematics is challenging. We will also further edit to increase accessibility.
There appears to be a possible major problem in the way that the paper has combined data from patients with different genetic forms of FSHD, and different likely genetic severities. It would seem better to analyse the data separately for each of these to allow a more homogenous platform on which to construct a model.
That we pooled data from 4 FSHD patients, to derive estimates of 2 of the 5 parameters of our model is the major (non-editorial) comment about our study, and is raised in various versions in points 1, 2, 9, 11 and 12 of reviewer 2’s response. We have explained above that the reason for pooling is partly statistical, due to dataset size limitation. Considering each patient separately may prevent convergence of a gradient descent algorithm for parameter estimation. We again emphasise that pooling 4 FSHD patients, while less personalised, does not make our estimate of the average DUX4 transcription rate in FSHD patients invalid. It is simply an average level across our 4 patients, perhaps higher than for some patients but lower than for others.
As commented, we will repeat the analysis separately for the 2 patients who have larger numbers of DUX4 positive cells and report the findings, with the caveat that these estimates will, by definition, be over-estimates of the true value of the average DUX4 transcription rate for the FSHD population.
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Referee #2
Evidence, reproducibility and clarity
An in silico FSHD muscle fibre for modelling DUX4 dynamics
Summary
This paper studies and mathematically models the stochastic process of presence or absence of DUX4 expression in individual myocytes in FSHD, which underlies the very small proportion of individual cells which do express DUX4. The paper is valuable in providing a mathematical basis for modelling this, and hence a basis by which to study the effects of other factors or potential therapeutic interventions which may influence the overall proportion of cells which do express. To understand the paper fully, requires a familiarity with mathematical and statistical reasoning which will be beyond many potential readers, including this reviewer, but I hope that the following specific comments may still be helpful.
Major Comments
- A potential major concern is that the modelling seems to be based largely on combined data from 27 DUX-4 positive myocytes out of 5133 myocytes from 4 FSHD patients described by Van Den Heuvel et al, 2019 (ref 17), but with 2 being FSHD1 and 2 FSHD2, and without the 2 patients within each FSHD type being matched for D4Z4 fragment length (RU = 'residual units'), which can be expected to be a major influencing factor on the threshold for expression in any one myocyte upon which the stochastic process acts. Thus, one can expect lower RU number to show a greater proportion of expressing cells within FSHD1, and to some extent similarly within FSHD2 (although in FSHD2, different SMCHD1 mutations will also have different 'strengths'). The 4 patients were : 2x FSHD1 (3RU ; 6RU); 2x FSHD2 (12RU ; 18 RU). In the paper of Den Heuvel et al it is evident that the DUX4-positive cell count differs between these 4 cell lines very much as might be anticipated from their D4Z4 RU number. Thus (Figure 2 in that paper) patient 1.1 (3RU) has 12 positive cells, whereas patient 1.2 (6RU) has only 2 positive cells. Patient 2.1 (SMCHD1 exon 37 mutation, and 12 RU) has 11 positive cells, whereas Patient 2.2 (SMCHD1 exon 10 mutation, and 18 RU) has only 2 positive cells. Therefore, if the validity and accuracy of the modelling here would be affected by genetic heterogeneity, the authors should present their calculations and analyses based only on the 2 patients who account for 23/27 of the positive cells, and furthermore, that the calculations and modelling are performed and presented for those 2 patients separately. In order to be of value for assessing potential interventions more widely in FSHD, the authors would then need, in further publications, to extend their analysis similarly to genetically homogeneous myocyte sets with other RU number.
Specific points.
- Introduction 4th paragraph: - 'Single cell and single nuclear transcriptomic studies find only 0.5-3.8% of in vitro differentiated FSHD myonuclei express DUX4 transcript16,17. Immunolabelling studies only detect DUX4 protein in between 0.1-5% of FSHD myonuclei18,19.' The authors should comment whether there is any evidence from the data in these references, or from other publications, regarding differences in these proportions by FSHD diagnosis (I or II) or by D4Z4 residual number?.
- Introduction 5th paragraph: - Importantly, a recent phase 2b clinical trial of the DUX4 inhibitor losmapimod failed to reach its primary endpoint of reduced DUX4 target gene expression in patient muscle, despite improvement in functional outcomes23. Please state here whether or not there was any evidence that DUX4 expression itself was reduced in this trial. It would help if the authors could also add here an interpretive comment as to whether this indicates that the current presumed target genes for DUX4 are not in fact the ones important for FSHD, or whether their expression might be retained from compensatory upregulation by other upstream regulators. The authors should expand briefly also in the introduction on the evidence for toxicity of target gene expression.
- Results 2nd paragraph: - We first describe the compartment model. FSHD single myocytes can express DUX4 and therefore DUX4 target genes; DUX4 target gene expression leads to cell death19,27,28. Please indicate whether the evidence in these studies is independent of DUX4. Ie. Is there independent evidence that it is definitely the target gene expression, rather than DUX4 expression per se, that leads to cell death, especially if losmapimod improves function by inhibiting DUX4, but has no impact on these target genes.
- Results 2nd paragraph Item 4 : - 𝑅(𝑡) - a resigned state where the cell expresses no DUX4 mRNA but does express DUX4 target mRNA (DUX4 -ve/Target gene +ve: i.e. a historically DUX4 mRNA expressing cell) Since the mRNA is from the target genes, why should it be produced only in response to DUX4 expression ? ie. Please indicate the evidence to say that these must be 'historically DUX4 mRNA expressing cells', rather than target gene expression in response to other factors, or even autonomously.
- Results - Estimating the kinetics of DUX4 mRNA - 2nd paragraph: - DUX4 expression was induced with 250 ng/ml doxycycline for 7 hours .... Might some of the laboratory detail here be better placed in the 'Methods' section ?
- Results - Estimating the kinetics of DUX4 mRNA - 4th paragraph: - '...from 4 FSHD patients (2 FSHD1 and 2 FSHD2).' Please give additional information about these patients - ie. Age, sex, severity (or age-onset), and genetic results - perhaps best done as a Table in this paper rather than only by reference back to the Van den Heuvel et al. paper (see main comment 1 above).
- Results - Estimating kinetics of DUX4 target activation - 2nd paragraph: - '8 DUX4 target genes......expression was restricted to FSHD cells/nuclei and never observed in controls.' So are these genes normally only expressed in the zygote , rather than post-birth (except perhaps the testis)? The authors should comment on this.
- Results - Estimating kinetics of DUX4 target activation - 4nd paragraph: - In the presence of DUX4 mRNA the proportion of time the promoters of the 8 DUX4 target genes remained in the active state,....significantly increased. It would be interesting to know if any of these temporal dynamic descriptors of DUX4 target promoters differ consistently between sample II-2 and II-1 and in the same direction between I-2 and I-1. ie. Might the same factors (eg. D4Z4 copy number) which may affect presence/absence of DUX4 also affect other cellular measures of DUX 4 ?
- Results - Compartment model simulation - 4th paragraph: - '...so that after 10 days 26.3% of cells had died.' The authors need to give data here also for controls. Ie. What proportion of cells die after 10 days in controls ?
- Discussion - 1st paragraph: - ' However, DUX4 expression in FSHD muscle demonstrates a complex dynamic with DUX4 mRNA, protein and target gene accumulation all difficult to detect2,21. Understanding this complex dynamic is essential to the construction of optimal therapy' So, it presumably follows that comparison by known genetic or demographic modifiers of disease severity (such as D4Z4 copy number) could be of fundamental importance in interpreting this dynamic and hence the results of clinical trials) (see Main point 1, and point 7).
- Discussion - 6th paragraph: - 'Our model predicts <2.9% of single FSHD myocytes will be DUX4 target gene positive at any given time...' Should this be: '...DUX4 target gene-mRNA positive' . Also, does this 2.9%-figure differ between individual patients, and therefore might generally differ between FSHD1 and 2, and between different D4Z4 genetic categories ?; as this will matter for different individual patients.
Minor comments
- Methods - scRNAseq and snRNAseq data - 2nd paragraph: - '..2 sperate patients...' Typo. to correct.
- Methods - Hypothetical scenarios for raising 𝑬[𝒎] under the promoter-switching model- 1st paragraph: - '...constant in the second...' needs punctuation.
- Methods - Cellular Automaton Model - 3rd paragraph: - '...according the non-syncytial...' Typo : '...according to...'
- Methods - Genetic algorithms - 3rd paragraph: - '...elitism of 5%, mutation probability 0.1, crossover probability 0.8,...' Should these parameters be given in the same format to avoid any confusion - ie. all as probability, or all as percentages ?
Significance
Please see comments in the 'Evidence, reproducibility and clarity' box above.
This paper is valuable in providing a mathematical basis for modelling the stochastic process of presence or absence of DUX4 expression in individual myocytes in FSHD (facioscapulohumeral muscular dystrophy), and hence a basis by which to study the effects of other factors or potential therapeutic interventions which may influence the overall proportion of muscle cells which do express DUX4, and hence succumb to its toxicity.
This is a specialist field and the nature of presentation of the mathematical modelling in the paper will restrict accessibility to only a very few researchers in this field. There appears to be a possible major problem in the way that the paper has combined data from patients with different genetic forms of FSHD, and different likely genetic severities. It would seem better to analyse the data separately for each of these to allow a more homogenous platform on which to construct a model.
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Referee #1
Evidence, reproducibility and clarity
Banerji and colleagues measure DUX4 and target gene expression over a time course in doxycycline-inducible myoblasts to estimate kinetic parameters and rates underlying the transition of non-expressing cells through DUX4-expressing cells to cell death. They then use these parameters to model the rate of appearance of DUX4+ cells, DUX4 target gene expression, etc. in cells from FSHD patients, and derive a model that predicts that over 100 days around one fourth of cells die while less than 1% of cells express DUX4 or its target genes at any given time. This is somewhat similar to what is seen in FSHD patients, where DUX4 expression is infrequent in cultured cells, while patients eventually have substantial muscle loss. The experiments are well-designed and explained clearly.
Significance
The primary significance of this study is that the field has a sense that the damage seen in patient muscle is not congruent with the low expression of DUX4 in patients, and the model showing many cells dying with only a few cells expressing DUX4 at any given time suggests that overall damage can be greater than that observed in any particular snapshot.
However, it is important not to conflate low frequencies of DUX4+ nuclei in cultured myoblasts with "DUX4 being difficult to detect" as in p 12, Discussion. DUX4 is difficult to detect, indeed basically not detected, in muscle biopsy specimens, but in cells in vitro, DUX4 is fairly easy to detect, albeit in quite low numbers of cells. Since the study evaluates cells in vitro, it is important to make clear that the situation in vivo is qualitatively different from that seen in vitro, namely DUX4 not being detected, and the authors should clarify this importance difference.
A second reason for caution in extrapolating correlates from the in vitro model to the disease process in muscle tissue is that in vivo there is a continual source of replacement cells, as the authors have shown in a previous study. Have the authors attempted to model a situation in which new cells are provided into the system at some rate, related to the amount of death occurring at different times? Although the authors mention that the static cell number is a limitation of the model, it would be valuable to revisit or explore this idea in the Discussion section, if only to provide the reader with a more pragmatic perspective.
The second part of the paper models presence of DUX4 in nuclei based on diffusion from expressing to non-expressing nuclei, and characterizes this as the activity of "an infectious agent, able to spread from one nucleus to another by adapting epidemiological compartment models". The relationship to an infection process is probably not the ideal way to characterize this process, because an infection implies the setting up of new sites of production of the agent, DUX4, where what is really happening is that DUX4 diffusing into these other nuclei isn't leading to more DUX4 production, it is just diffusing into nearby nuclei and accumulating there. Unless I am misunderstanding, the authors are simply showing that a larger number of nuclei will be positive in a system in which cells are fusion products having many nuclei than in a system in which all nuclei are isolated within their own cells.
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Referee #2
Evidence, reproducibility and clarity
In the manuscript "Compaction of Drosophila histoblasts in a crowded epidermis is driven by buckling of their apical junctions", Rigato et al. study the behaviour of histoblasts during the third larval stage of Drosophila. Histoblasts are the progenitor cells of the adult abdominal epidermis. They are produced in the embryo and lie between the larval epithelial cells (LECs) in the larva before abdominal morphogenesis takes place during metamorphosis. The authors use this system to explore the role of forces during epithelial development.
The authors show that histoblasts undergo a dramatic change in morphology between 90 and 115 h AEL (after egg laying), with adherens junctions changing from a straight to a highly folded appearance. They also show that, during this time, histoblast volume is increasing. Furthermore, both junctional actin and junctional myosin II levels decrease over time. Interestingly, reduction of contractility (Rok-RNAi) and increase of contractility (overexpression of Rok constitutively active) in both histoblasts or LECs has no significant effect on histoblast behaviour.
The authors hypothesise that growth of histoblasts and LECs lead to a compression of the histoblasts, which causes the buckling of the histoblast junctions. To test this hypothesis, they perform three experiments and show that (1) overexpression of a dominant negative form of insulin receptor in LECs leads to a non-autonomous effect on histoblast cell size, (2) overexpression of a dominant negative Rab11 in histoblasts interferes with histoblast buckling, and (3) overexpression of String in histoblasts induces histoblast division and reduces histoblasts buckling.
Major comments
As mentioned in the significance box below, a major weakness of the manuscript is that the presented data does not sufficiently support the hypothesis that histoblasts are compressed by the LECs: Firstly, the manuscript does not provide evidence that the LECs expand and compress the histoblasts. Such an analysis needs to be included.
Secondly, the authors present two pieces of evidence to support their hypothesis, which are not very convincing:
- In line 147ff, the authors imply that their experiments in Fig. S3D (Rok alterations in LECs) support a 'mechanical tug of war'. However, the authors point out that their analysis is not statistically significant, so their data does not actually support their hypothesis.
- The authors show that overexpression of a dominant negative form of insulin receptor results in a non-autonomous increase in apical histoblast cell area. Here, I wonder to which extent the change in histoblast cell size might be due to a change in histoblast cell number per nest rather than a change in LEC pressure. Furthermore, they state that junctions are straighter, however, it would be good to see a statistical analysis here. Importantly, the conclusion of the experiment is not very convincing as it has not been shown that LECs are smaller, or grow slower, or exert less pressure on the histoblasts due to the performed genetic manipulation. So, the reason for the observed histoblast phenotype is unclear. This needs to be explored further.
Thirdly, there are a few observations, which further challenge the author's hypothesis:
- Buckling appears to happen in the plane of the tissue, but should it not happen orthogonal to it, as shown in the scheme in Fig. 2J, if LEC compression was the cause of buckling?
- In Fig. 1D, one can see buckling at interfaces between histoblasts and LECs - does this not suggest that histoblasts push against LECs (and that in that area LECs are not pushing against histoblasts)? I think this observation is very interesting and a more detailed analysis of this phenomenon at histoblast-LEC junctions could be included in the manuscript.
Based on the above point, there are various sections of the manuscript that need to be adjusted in my opinion, for example:
- Line 190ff. 'Combined, these perturbation experiments provide strong evidence that junctional buckling of the histoblasts is the result of a imbalance between the addition of junctional material in the histoblasts and mechanical constraints from the overcrowding of the epidermis.' - There is not sufficient evidence for this statement with respect to overcrowding. The presented data does however show convincingly that junctional remodelling is needed for buckling.
- Line 201 ff. 'This experiments confirms that junctional buckling is a result of the combined overcrowding and absence of divisions.' - The presented experiments do not provide sufficient evidence for this statement. The presented data does however show convincingly that inducing cell division leads to less buckling. I wonder whether this result is counterintuitive with respect to the authors' compression hypothesis, as if increased compression from LECs would lead to buckling would then not also increased pushing by neighbouring histoblast lead to buckling?
- Line 235 ff. 'We investigated the formation of histoblast junctional folding and found that it is a non-autonomous transition originated by the competition for space of the two cell populations.' - This needs to be rephrased are there is not sufficient evidence for this hypothesis.
Further major comments
Line 56: More details about which histoblasts were imaged would help the reader understanding the experiments better. - Which abdominal segment was imaged? - The authors state that they have imaged the "dorsal posterior nest, which has the largest number of cells (15-17)" - is this correct? In later stages, the anterior dorsal nest is larger than the posterior dorsal nest. - Do the different abdominal segments have different histoblast numbers/ histoblast nest sizes? - I think that it would be helpful to show the behaviour of the ventral nest - the authors' hypothesis suggests that all histoblasts behave similarly and the buckling should be observed in all nests.
In the figures, the authors do not clearly present the statistics done. Here, giving the p-values in the graphs would be very helpful. There are instances where it is not sufficiently clear whether the authors present a significant finding or merely a non-significant tendency (e.g. in Fig. 6).
Fig. 4CD. I do not agree with the authors' interpretation that Sqh::GFP is lost from the junctions. The figure shows that levels are reduced. Also, in line 157, it might be better to use 'reduction of junctional myosin' rather than 'loss of junctional myosin'.
With a few exceptions, the authors do not show the fluorescent marker used in their experiments to report where and how strong the Gal4 is expressed, which they use to drive their RNAi or dominant negative constructs. For example, in Fig. 5, they say that they have co-expressed a cytosolic GFP, but they do not show it. To have this kind of information would be very useful when interpreting the data.
In line 171 and in other places the authors talk about 'plastic remodelling'. It would be helpful if the authors could explain in more detail what they mean by this.
Minor comments
In my opinion, the paragraph about the 'Qualitative model of junctional buckling' would be better placed in the discussion.
Fig. 6. Why was the insulin receptor experiment done in white pupa and not in wandering L3 larvae? This makes comparison of data more difficult.
I wonder when are histoblasts stopping to show the buckling? I assume that it must be before the beginning of abdominal morphogenesis, as at the beginning of LEC replacement, the junctions are straight again?
What is the morphology of histoblasts in late L1- and late L2-stage larvae? Potentially there might also be crowding during those stages?
Significance
The observations by Rigato et al. are very interesting. They present a novel model system that enables the study of the interaction of two epithelial cell types, which do not divide. The fact that the presented data suggests that neither histoblasts nor LECs are under tension, makes this an extremely interesting novel system to explore the forces involved. The presented results provide some interesting insights into histoblast biology. However, a major weakness of the manuscript is that the proposed hypothesis of histoblast compression by larval epithelial cells is not sufficiently supported by the results. So apart from the very interesting observations, the manuscript lacks insight into the mechanistical basis of junctional buckling.
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Referee #1
Evidence, reproducibility and clarity
The manuscript by Rigato and colleagues uses live imaging of Drosophila larvae to describe the transition of histoblasts from a configuration where junctions are straight to a configuration where junctions are folded. The emergence of folded junctions is concomitant with a decreasing apical area, an increasing cell height and decreasing junctional Myosin. Expression of Rab11-DN (reducing apical junctional trafficking) or Cdc25 (inducing proliferation) in histoblasts abolishes the emergence of folded junctions. Expression of InRdn (impairing insulin receptor pathway) in surrounding larval epidermal cells (LEC) is claimed to also reduce folding (but see comment below). Finally, laser ablation of folded junctions reveals little or no relaxation, indicating that these junctions are not under tension. The authors propose a model in which growth mediated cellular crowding generates mechanical constrain on histoblasts which, in conjunction with decreased junctional Myosin II, leads to the buckling of junctions.
- The authors convincingly show that histoblast junctions buckle/fold during late larval stages. They also convincingly show that junctional folding requires Rab11 and is counteracted by cell proliferation. The conclusion that folded junctions are not under tension is less well supported. Ablation of folded junction results in little/no relaxation (Fig. 5), however, the positive control (late pupal histoblasts) did not show obvious relaxation either (in absence of quantification).
- The key conclusion that growth mediated crowding drives junctional folding is not well supported. The authors claim that InRdn expression in LECs leads to straight junctions of histoblast, but that is not obvious from Fig. 6F. Additional experiments will be required to further test the role of growth mediated crowding in junctional folding. For example, the authors should further attempt to modulate growth of LECs and/or test whether overgrowth of larvae to increase epidermal surface (e.g. lgl mutants) would influence junctional folding. These experiments will likely require several months.
- Moreover, the authors provide a 'qualitative model' (Fig. 7). The paper would be strengthened by providing a model based simulation (best based on quantitative data derived from experiment (e.g. growth rates of histoblasts, LECs, etc.) of the transition of straight to folded junctions. This simulation would test whether the authors' hypothesized mechanism is feasible. This work will likely require several months.
- Statistical analysis to reveal significances between datasets is missing throughout the manuscript. The number of biological replicates (i.e. larvae) for each experiment are not provided. The authors should provide statistical analysis.
- Fig. 3/S3. The authors observe a correlation between junctional folding and a decrease in F-actin and Myosin on junctions. However, changes in Rok activity do not alter junctional folding. It is therefore unclear whether the decrease of F-actin and Myosin is a cause or consequence of junctional folding. The authors should tune down their conclusion that junctions 'soften' through a loss of cytoskeletal components.
- Fig. 5. The laser ablation experiments require a quantitative analysis.
- Fig. 6. A control image (Cad;mKate without perturbation) is missing.
- Fig. 7. The junctional buckling model is a hypothesis by the authors to explain their observation; it is not data and therefore should be removed from the 'results' section of the manuscript.
Significance
The manuscript describes an interesting behaviour of cells to change their junctional morphology from straight to folded during development. Previous work has mainly described epithelia as networks of cell junctions under tension. This work advances our understanding by providing evidence that epithelia can also be in a configuration that is not based on tension. The authors provide evidence that this cell configuration requires the absence of cell proliferation and trafficking of junctional material. However, beyond this, the mechanisms that drive epithelia into this configuration remain somewhat unclear. The manuscript would therefore likely target a specialist audience
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the answers and strategy plans are details in the "revision plan" document attached to this submission
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Referee #3
Evidence, reproducibility and clarity
This study used metabolomic, lipidomic and proteomic approaches to analyze the metabolic changes induced by the p.S59L CHCHD10 mutation in mice. Altered metabolism in plasma and heart of Chchd10S59L/+ mice was seen compared to their wild type littermate. In plasma, levels of phospholipids were decreased while those of carnitine derivatives and most of amino acids were increased. In cardiac tissue, Chchd10S59L/+ mice showed a decreased Oxidative Phosphorylation (OXPHOS) and -oxidation proteins levels as well as tricarboxylic acid cycle (TCA) intermediates and carnitine pathway metabolism. In parallel, lipidomics analysis revealed changes in the lipidome, including triglycerides, cardiolipin and phospholipids. Consistent with this energetic deficiency in cardiac tissue, the authors show that L-acetylcarnitine supplementation improved the mitochondrial network length in IPS-derived cardiomyocytes from a patient carrying the CHCHD10S59L/+ mutation. It is concluded that L-acetylcarnitine may restore mitochondrial function in CHCHD10-related disease, due to the reduction in energy deficit that could be compensated by carnitine metabolic pathways.
General Comments:
The authors had already generated knock-in (KI) mice (Chchd10S59L/+) that developed cardiomyopathy associated with morphological abnormalities of mitochondria, severe oxidative phosphorylation (OXPHOS) deficiency and multiple defects of respiratory chain (RC) complexes activity in several tissues in the late stage. Other authors have seen similar results (see reference 5) As a result, the insights provided by this further metabolomic, lipidomic and proteomic analysis are not that novel. The data is very descriptive and often the authors misinterpret the meaning of the results. Addionally the alterations in either metabolites or proteins have in their mutant CHCHD10S59L/+ mice are often not accurately represented.
The administration of acetylcarnitine to reverse the metabolic defects in iPSC cardiomyoctytes derived from a from a patient carrying the CHCHD10S59L/+ mutation is interesting, although the authors did not determine if similar benefits of acetylcarnitine were seen in the CHCHD10S59L/+ mice. They msy also misinterprete the role of acetylcarnitine in the mitochondria.
Specific Comments:
- The authors point out that in vitro and in vivo studies have shown that CHCHD10 mutants cause disease by a toxic gain-of-function mechanism rather than by loss of function. It would be helpful to better define what the effects of the CHCHD10S59L/+ mutation represent.
- An aim of this study is to understand how mitochondria dysfunction associated with CHCHD10 mutations triggers altered global metabolism. This aim has not really be accomplished in this study.
- Figure 3C: The authors put FABP3 in the ß-oxidation pathwayt. This is incorrect. The figure also does not highlight the ketothiolase (ACAT1)? It is also not clear why CPT1 and CPT2 are place together. There is a carnitine translocase situation in between these enzymes. It should also be pointed out that CACT also has role in long chain acylcarnitine translocation.
- The main direction of CrAT in heart mitochondria is the conversion of acetyl CoA to acetylcarnitine. This is not recognized by the authors, and has important implications on interpreting acetylcarnitine therapy.
- Figure 3C: Why is just palmitate and linoeate shown as fatty acids?
- The authors state that "In cells, long-chain fatty acids dependent on esterification with L-carnitine to form acetyl-carnitine for transport from the cytoplasm to the mitochondrial matrix for oxidation and energy production." This sentence should be re-written and broken down into clearer statements.
- The authors state that "In lipid biosynthesis pathway, protein levels of long-chain- fatty-acid-CoA ligase 1 (Acsl1; as well as mRNA expression) and mitochondrial short-chain specific acyl-CoA dehydrogenase (Acads) in the hearts of symptomatic Chchd10S59L/+ mice were significantly lower than those of age-matched wild-type mice (with adjusted p < 0.05) (Fig. 3A-B). Please clarify and re-write this sentence. ACSl1 is primarily producing acyl CoA for CPT1. ACADs is involved in ß-oxidation of short chain fatty acids. Not lipid biosynthesis.
- The authors state that "With respect to the lipid oxidation, protein levels of carnitine-O-Acetyltransferase (Crat; as well as mRNA expression)...". Crat is not involved in fatty acid oxidation.
- It is stated that "Interestingly, a significant decrease in fatty acid biosynthesis intermediates, such as malonate and ethyl-malonate, was also observed in the hearts of symptomatic Chchd10S59L/+ mice (Fig. 3C). I do no not see this data. Where is this?
- Figure 3G.; Data is incomplete
- The authors state that: Altogether, those results suggest that CHCHD10S59L mutation induces branched-chain amino acids catabolic defects and increased non-essential amino acids synthesis which may contribute to the elevated levels of amino acids metabolites observed in plasma and heart of Chchd10S59L/+ mice (Fig.1D, Fig. 3D)." It should be recognized that the heart is a small contributor to plasma amino acid changes.
- The IPSC-derived cardiomyocytes seem to involve one single patient.
- The authors state that "As highlighted by our study, Chchd10S59L/+ mice displayed markedly elevated levels of cholesteryl esters, some glycerophospholipids and reduced concentrations of triglycerides species in heart at the symptomatic stage. Changes in cholesteryl ester metabolism were not reflected in changes in plasma total cholesterol pools (Table 1). In other words, it appears that cholesterol synthesis is upregulated but does not result in accumulation of free cholesterol." It should be recognized that the heart is not really involved in the synthesis of cholesterol.
- The authors state that "Increased plasma concentrations of acylcarnitines (which formed from carnitine and acyl-CoAs) are suggested as a marker of metabolism disorders related to cardiovascular diseases [43, 44]. Based on our data and the literature, we suggested that targeting carnitine metabolism pathway could counterbalance the metabolic disturbances, ameliorate mitochondrial functions, and therefore delay CHCHD10-related disease progression." This statement is not supported by data. There are also inaccuracies with the discussion of metabolism.
Significance
The authors had already generated knock-in (KI) mice (Chchd10S59L/+) that developed cardiomyopathy associated with morphological abnormalities of mitochondria, severe oxidative phosphorylation (OXPHOS) deficiency and multiple defects of respiratory chain (RC) complexes activity. Other authors have seen similar results (see reference 5) As a result, the insights provided by this further metabolomic, lipidomic and proteomic analysis are not that novel. The data is very descriptive and often the authors misinterpret the meaning of the results. They often misrepresent the significance of the observed alterations in metabolites and proteins in their mutant CHCHD10S59L/+ mice.
The administration of acetylcarnitine to reverse the metabolic defects in iPSC cardiomyoctytes derived from a from a patient carrying the CHCHD10S59L/+ mutation is interesting, although the authors did not determine if similar benefits of acetylcarnitine were seen in the CHCHD10S59L/+ mice.
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Referee #2
Evidence, reproducibility and clarity
This manuscript by Madji Hounoum et al presents a study of the metabolic changes associated with the p.S59L CHCHD10 mutation that underlies a toxic gain-of-function in a number of disease phenotypes, including ALS and mitochondrial myopathy. The authors have used a multi-omics approach in their mouse model to demonstrate significant decreases in proteins required for oxidative phosphorylation (OXPHOS) and -oxidation, as well as metabolites involved in the Kreb's cycle and carnitine metabolism, along with significant changes in lipid profiles. The authors also provide evidence that L-acetylcarnitine appears to ameliorate mitochondrial function.
Major comments:
The manuscript is, in general, well-written and 1. The conclusions drawn are mostly justified on the basis of the data presented (see comment 2). 2. The authors have used a multi-omics approach, which is very powerful in allowing a cell-(or organism-) wide analysis of multiple systems. However, the key drawback for the proteomics approach is that low abundance proteins, such as the OXPHOS proteins, are often not accurately assessed. In this regard, it seems critical that the authors provide further evidence for the changes suggested by the heatmaps - or justify that the technical approach they have taken can account for low abundance. Western blotting would fit the bill nicely - there are antibodies available to many of the OXPHOS complex subunits. 3. There is a very rich and deep literature, particularly from the '80s and '90s, regarding the metabolic disturbances identified in mitochondrial disease patients, both for OXPHOS and fatty acid oxidation defects, that should be cited. In addition, the literature delineating the mitochondrial 'cofactor cocktail' should at least be mentioned.
Minor comments:
- Some attention to grammar would help clarify the meaning for the reader. Some sentences are incomplete.
- The authors are encouraged to check their references, as a number are incomplete.
- Adding the scale to the scale bar for the MitoTracker Red confocal images would be handy. The right-most micrographs of the S59L/+ cells (Fig 4C) are not nearly as convincing as the middle pair of micrographs - and detract from the message. In addition, it would be nice to have the authors comment on the very intense staining of the mitochondria in the S59L/+ cardiomyocytes in panel A of Figure 4.
- The final paragraph of the Discussion is not as impactful as it could be. Specifically, referencing the mitochondrial disease literature would aloow a more fulsome discussion as to the mechanism underlying the action of ALCAR i.e. is the anti-oxidant function most important? Or is it simply it's action as a metabolite?
Significance
This study is an important contribution to the literature examining neurodegenerative diseases, such as ALS, that remain poorly understood. While the advance seems incremental, especially in light of the many studies in recent years that have document mitochondrial dysfunction in the mutant mice, the ALCAR treatment is novel and worthy of dissemination. The audience that this manuscript would interest would span from neurologists and other clinicians, such as medical geneticists, to basic biomedical researchers in both academic and industry.
Reviewer area of expertise: mitochondrial function in health and disease; insufficient expertise to evaluate the details of the 'omics' methodologies.
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Referee #1
Evidence, reproducibility and clarity
Summary
In the manuscript titled "Multiomics study of CHCHD10 S59L -related disease reveals energy metabolism downregulation: OXPHOS and beta-oxidation deficiencies associated with lipids alterations," Hounoum et al. performed metabolomics, lipidomics, and proteomics analyses of symptomatic and presymptomatic CHCHD10 S59L murine hearts. The results are largely descriptive. Levels of carnitine acyltransferases and carnitine palmitoyltransferase 2 are lower in S59L hearts. Many proteins of lipid biosynthesis and beta-oxidation pathways are also reduced. Authors concluded that utilization of fatty acids for energy production is deficient in the mutants. They treated CHCHD10 S59L iPS-derived cardiomyocytes with acetyl-L-carnitine and observed a rescue of mitochondrial length and cristae organization in vitro. This paper contains a few grammatical, structural, and organizational issues. The paper confirms several findings recently published by Sayles et al. (Cell Reports, 2022) while providing some additional information through lipidomics analysis in the hearts and metabolomics analysis in the plasma. Overall, it is largely descriptive apart from an experiment in the figure 3 in which the authors use iPSC-derived cardiomyocytes to show partial rescue of a mitochondrial morphology defect following acetyl-L-carnitine supplementation. However, these data seem preliminary and the correlation between the iPSC and mouse model is not established. Overall, these data are likely to be of interest to the immediate field but lack novelty for a general audience.
Major comments
- In Figure 3, authors treated CHCHD10 S59L iPSC-derived cardiomyocytes with acetyl-L-carnitine for 72 hours and observed a rescue of mitochondrial length and cristae organization. However, it is not established that the defect in mitochondrial length is important to the pathology in the mouse heart. A rescue of the mitochondrial functional defects would have greater relevance. Thus, the relevance of rescuing this phenotype is not clear. It is not clear a priori whether increasing acetyl-L-carnitine levels would be protective. While certainly there is evidence for downregulation of fatty acid beta-oxidation as well as carnitine-related metabolites, if this a compensatory response to an OXPHOS defect, increasing acetyl-L-carnitine levels could make the cardiomyopathy worse. Supporting this alternative interpretation, levels of carnitine derivatives are already higher in mutant plasma. Thus, it is important to demonstrate this rigorously and in the most appropriate model. For instance, showing rescue of cardiomyopathy in the in vivo mouse model would be stronger than showing rescue of a minor defect in mitochondrial morphology in iPSC derived cardiomyocytes. Additionally, the EM images provided in the paper are in low magnification, and cristae structures are not clear. Quantifications of the cristae defects are not provided. Authors also do not provide any information regarding how they quantify mitochondrial length. Mitochondria is a 3D structure. The length of mitochondria on a 2D transmission EM image may not represent the true length of the mitochondria.
Minor comments
- Title. Recommend changing "lipids alterations" to "lipid alterations."
- Page 7, line 13, 14, and 23. Some characters appear as squares.
- Page 12, line 8. Recommend changing "After 72 treated with Acetyl-L-carnitine" to "After treated with acetyl-L-carnitine for 72 hours."
- Page 14. It is unclear what the significance of the electrolyte measurements is. A brief discussion of the implications should be added.
- Page 15, last sentence. Consider rephrasing the sentence "Very interestingly, most of the amino acids detected in the plasma were increased in CHCHD10 S59L/+ mice at both stages, as well as carnitine, O-acetyl-L-carnitine and deoxycarnitine increased at symptomatic stage."
- Page 16, line 10. "Longitudinal proteomics" implies that the pre-symptomatic and symptomatic heart samples came from the same subjects. If this is not the case, I would recommend deleting the word "longitudinal."
- Page 17, line 14. Authors show changes in levels of proteins and metabolites in beta-oxidation, but there is no evidence presented to show that beta-oxidation is impaired in CHCHD10 S59L/+ hearts.
- Page 17, line 19. Please indicate where Cyb5r1 levels are shown.
- Page 18, line 15. Please indicate where Acss1 levels are shown.
- Page 18, line 10. Abbreviation Plaa has already been spelled out in line 2.
- Page 18, line 10, it is stated here that Plaa levels are lower in the CHCHD10 S59L KO mice but 3 sentences earlier and on the figure they are higher. Please resolve this discrepancy.
- Page 18, line 18. Recommend changing "lipids alterations" to "lipid alterations."
- Are enzymes involved in amino acid metabolism (PHGDH, PSAT1, and ASNS) upregulated in your proteomics analysis?
- Page 20, line 6. Recommend changing "Catabolic enzymes are mainly located in the mitochondrial matrix such as the branched-chain alpha-keto dehydrogenase complex (Bckdha, Bckdhb) and branched-chain-amino-acid aminotransferase (Bcat2)" to "Catabolic enzymes, such as the branched-chain alpha-keto dehydrogenase complex (Bckdha, Bckdhb) and branched-chain-amino-acid aminotransferase (Bcat2), are mainly located in the mitochondrial matrix."
- Page 20, line 12. The authors interpret the increase in non-essential amino acid synthesis as a consequence of the changes in branch-chain amino acids. An alternative interpretation is that this is a consequence of the mitochondrial integrated stress response, which has been demonstrated to be upregulated in symptomatic CHCHCD10 S59L hearts. Specifically, expression of proline synthesis, serine metabolism, and asparagine synthesis enzymes is increased in a manner that depends on the OMA1-DELE1-eIF2alpha signaling axis. This alternative explanation for these results should be discussed and the relevant studies cited (PMID: 35700042 and 32338760).
- Page 22, line 12. An alternative explanation for lower creatinine levels is decreased body weight in the CHCHD10 S59L mice. This should be discussed in addition to noting changes in creatinine in ALS. Additionally, it seems more likely that these changes in the CHCHD10 S59L mouse relate more to the myopathy/cardiomyopathy in this model than motor neuron disease, which is not a prominent feature in the model.
- Page 23, line 10. Recommend showing Uchl1 levels in Results and/or Figures.
- Page 23, line 15. Myh6 levels are unchanged or decreased not increased in cardiomyopathy.
- Page 24, line 17. Recommend changing "mitochondrial dysfunctional" to "mitochondrial dysfunction."
- Page 27, line 10. Recommend changing "ameliorate mitochondrial function" to "ameliorate mitochondrial dysfunction."
- Page 31, line 22. Formatting error.
- Figure and Figure legend 3D. Recommend changing "not regulated" and "not modulated" to "unchanged" or "not significantly different."
- Figure 4C and 4D. Please provide images of higher magnification to clearly show mitochondrial network and cristae. Please provide quantification for 4C.
Significance
This paper contains a few grammatical, structural, and organizational issues. The paper confirms several findings recently published by Sayles et al. (Cell Reports, 2022) while providing some additional information through lipidomics analysis in the hearts and metabolomics analysis in the plasma. Overall, it is largely descriptive apart from an experiment in the figure 3 in which the authors use iPSC-derived cardiomyocytes to show partial rescue of a mitochondrial morphology defect following acetyl-L-carnitine supplementation. However, these data seem preliminary and the correlation between the iPSC and mouse model is not established. Overall, these data are likely to be of interest to the immediate field but lack novelty for a general audience.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
The study "Mesenchymal stem cell models reveal critical role of Myc as early molecular event in osteosarcomagenesis" by Akkawi et al shows that BM-MSCs are a foundational tool for study of osteosarcoma. And authors identified Myc and its targets as early molecular events in osteosarcoma formation, using BM-MSCs knocked out of both p53 and Wwox. Although the quality and validity of the data presented in this manuscript are not in question, this reviewer has doubts about the novelty of the findings in this current version of manuscript. It does not clearly indicate what is different from previous findings.
Response: We thank the reviewer for the kind words regarding our manuscript. Our study revealed that combined deletion of WWOX and p53, two known tumor suppressors in OS, results in early transformation of BM-MSCs that mediates upregulation of Myc. We believe that this notion is original and has not been described before. In addition, we provide evidence that this genetic manipulation has an advantage over p53 deletion alone. More details are provided below.
- It has already been reported that p53-/- BM-MSCs are the cells of origin in osteosarcoma development (ref. 21).
Response: We agree with the reviewer about this notion/fact and we indeed cited this reference. It should be noted that in this study the cell of origin of osteosarcoma was proposed to be BM-MSCs-derived osteogenic progenitors when p53 and Rb are co-deleted. Interestingly, this study did not show whether p53-/- BM-MSCs-derived osteogenic progenitors are able to form osteosarcoma or any other type of sarcomas. In our model BM-MSCs p53-KO alone were not able to develop osteosarcoma tumors as well, even when injected intratibially. Moreover, we showed that co-deletion of Wwox and p53 in BM-MSCs-derived osteogenic progenitors have the ability to form OS at earlier stages at the time point when deletion of p53 alone is still not enough to induce osteosarcomagenesis. Based on our findings and those in the literature, we believe that this combined genetic perturbation is critical for initiation of OS.
- Indispensability of Myc in osteosarcomagenesis was revealed (PMID: 12098700).
Response: It is well known that Myc is a potent oncogene and overexpressed in osteosarcoma (ref. 12, 13, 28 and ref. 29) as well as in many other human malignancies. The referred study (PMID: 12098700; ref 32) which expressed Myc in lymphocytes based their analysis of Myc contribution at the tumor stage (at the time of tumor detection). Our study, on the contrary, shows that upregulation of Myc is an early event in osteogenic-committed BM-MSCs deficient for Wwox and p53 in tumor-free mice. This notion indicates that combined deletion of two important tumor suppressors, WWOX and p53, promotes osteosarcoma through early changes in Myc levels. Our data further show that p53 deletion alone is dispensable for this change to happen at early stages further highlighting the significance of our findings. The referred paper was cited and discussed in the discussion section (ref 32).
Our data further shed light on WWOX as a key determinant of Myc function placing it as an upstream regulator. To further proof this, we propose in our revision plan to knockout WWOX in yBM SKO cells and/or restore WWOX in yBM DKO cells and determine consequences on Myc levels and activity as well as on tumorigenesis. In addition, we shall perform a ChIP-seq assay for Myc in yBM DKO and compare it to yBM SKO cells to show whether WWOX deletion is indeed results in enhanced chromatin accessibility of Myc.
- Osteosarcoma formation of p53flox-OsxCre mice was rescued by Myc-depletion and BM-MSCs from p53flox-OsxCre was shown to upregulate Myc (PMID: 34803166).
Response: This is a very relevant new study that we regrettably missed to cite so we are grateful for the reviewer to bring this up. In our revised version, we will be citing this important reference and discussing it (ref 33). Although this article shows that p53 deficiency promotes osteosarcomagenesis mediated through oncogenic Myc, which we also showed in our study (figure 6C, D), but the authors did not validate the tumorigenic ability of these cells at this earlier stage of osteosarcomagenesis. The later was showed in our study by injecting yBM-MSCs deficient for p53 intratibially into immunocompromised mice and showed that they lack tumorigenic ability although they display a mild upregulation of Myc (figure S5). On the other hand, co-deletion of Wwox and p53 at this earlier stage resulted in even higher levels of Myc and inducing osteosarcomagenesis at this earlier stage. Therefore, our study provides unforeseen effect of genetic perturbation that promotes OS initiation.
First of all, the authors need to cite the above papers and compare their findings with them to better clarify the value of their findings.
Response: Thank you for this comment, we will cite and discuss these valuable studies in our revised version.
The only one clear finding would be that Wwox functions as a tumor suppressor by repressing Myc function in the absence of p53, but unfortunately, no data have been presented on the mechanism Some additional analysis would be needed to mention it
Response: As addressed above, our revision plan will include:
- Depleting WWOX in yBM SKO and/or restoring WWOX in yBM DKO cells to further prove the tumor suppressor function of WWOX.
- Performing ChIP-seq assay for Myc in yBM DKO and compare it to yBM SKO cells to show whether WWOX deletion is indeed results in enhanced chromatin accessibility of Myc.
In the first place, Myc is upregulated in the absence of both p53 and Wwox, compared in only p53-null situation? Western blotting would be better to show it
Response: In our revised version we will add a western blotting showing the upregulation of Myc in DKO (WWOX, p53) compared to SKO (p53) yBM cells; This is already added in new Figure 5S C.
- In Figure 1D, should separate each panel so that it is clearly visible. What is the blue-colored fluorescence, DAPI? If so, why don't tdTomato positive cells overlap with blue (Figs, 1D, 2C, 4C, 4E?
Response: In our revised version we added more precise images in all Figures indicating the overlap between DAPI (blue) and tdTomato (Red).
- Why was MCM7 chosen among the Myc targets (S Figure 3)? What is the rationale for this?
Response: Thank you for this important notion. MCM7 is part of the MCMs protein family, that plays and essential role as a helicase and organizing center in DNA replication initiation. Moreover, several studies show the upregulation of MCM7 in several types of cancers among which is osteosarcoma, as cited in our manuscript (Ref. 14, 15, 16). MCM7 is also a direct target of Myc and has been shown to be a druggable target, by SVA as has been presented in Fig 7. Altogether, these facts and observations made us exploring its significance in our mode. In our revision plan, we will also explore other Myc targets through performing ChIP-seq on DKO cells.
In Figure 5 legend, what does "yBM cells (1.5, 4-months) (n=6)" mean? yBM cells (1.5-months) (n=3) and yBM cells (4-months) (n=3)?
Response: Thank you for this notion. yBM, at age of 1.5 months or 4-months were collected from tumor free mice and analyzed. In our revised paper, we updated and clarified this in the Figure 5 legend.
- In Figure 7B, is there a correlation between MCM7 and Myc protein expression levels?
Response: Thank you for this comment. In our revised version we added a western blot analysis showing the upregulation of both Myc and MCM7 in yBM-DKO compared to SKO cells; new Figure S5 C. (did the mean 7B upper panne, if so, we have to add this in the updated version).
Also, do MCM7 and Myc immunopositivites overlap in Figure 7G?
Response: In our revised version we will perform Myc IHC on same tumor sections. In the meanwhile, we added a western blot analysis showing the inhibitory effect of Simvastatin on both MCM7 and Myc in vitro (new Fig 7B, lower panel, re-blotted for Myc).
In S Figure 4C, what is 'PC'? What sample was loaded?
Response: PC refers to positive control for p53 that was used which was in this case HEPG2 cells treated with Nutlin to stabilize p53. p53 antibody used in this plot (IC12-Cell signaling) detects both human and mouse p53. A note was added to Figure legend.
- In S Figure 2A, what does 'US' (BM-US) mean? In S Figure 4F, what does 'US' and 'S' (Direct US and Direct S) mean?
Response: Thank you for this notion. We apologize for not clearly defined these symbols. In our revised version we added clarifications in the legends of these figures. The symbols are as follow: US: unstained BM-control, S: stained BM, Direct: directly collected BM and checked with FACS before culturing.
- Overall, this manuscript, there are too many symbols and it is cumbersome. Ex, in S Figure 3, yBM_DKO, Tum_DKO, DKOT, DKO-BMT, etc. All figures should be consistent with the same notation.
Response: We apologize for this in consistency in using too many symbols. In our revised version we will provide a table with all the symbols that should be consistent all over the manuscript
Reviewer #1 (Significance):
Although the quality and validity of the data presented in this manuscript are not in question, this reviewer has doubts about the novelty of the findings in this current version of manuscript. It does not clearly indicate what is different from previous findings, such as;
- It has already been reported that p53-/- BM-MSCs are the cells of origin in osteosarcoma development (ref.21).
- Indispensability of Myc in osteosarcomagenesis was revealed (PMID: 12098700).
- Osteosarcoma formation of p53flox-OsxCre mice was rescued by Myc-depletion and BM-MSCs from p53flox-OsxCre was shown to upregulate Myc (PMID: 34803166).
First of all, the authors need to cite the above papers and compare their findings with them to better clarify the value of their findings.
Response: Thank you for your valuable comments, and as we mentioned these important studies were and will be cited and discussed properly in our revised version.
The only one clear finding would be that Wwox functions as a tumor suppressor by repressing Myc function in the absence of p53, but unfortunately, no data have been presented on the mechanism.
Response: As stated in our response above, we argue that our observations showing very early transformation of BM-MSCs in combined genetic perturbation of WWOX and p53 is novel. In our revision plan we propose to perform additional ex vivo experiments to prove this notion by performing WWOX deletion in SKO-yBM cells and WWOX restoration in DKO-yBM cells and test consequences on Myc levels/activity and tumorigenicity. To further shed light on the mechanistic outcome of WWOX action in this context, we shall perform Myc ChIP and ChIP seq assays in yBM DKO and compare it to yBM SKO cells to show whether WWOX deletion is indeed results in enhanced chromatin accessibility of Myc [follow up of Fig-I shown above]. These experiments should further strengthen our findings.
Reviewer #2 (Evidence, reproducibility and clarity):
In current study, the authors established a mouse model with tdTomato expression under the OSX-controlled double deletions of Wwox and Trp53. Such mouse strain gives a great platform to study the OS development and therapeutic potential. Experiments are clear and convincing. Results are well presented.
Response: We thank the reviewer for the kind words regarding our manuscript and acknowledging its clarity and validity.
To better improve this study, few minor suggestions regarding the data are as following:
- Some of the legends on figures are too small to read, or in low quality. please change these labels.
Response: We thank the reviewer for this notion. We apologize for the low quality and inconvenience. In our revised version, we shall provide an improved resolution of legends.
- For Figure 7C and D, from 7C, the control WT BM showed clear resistance to the SVA treatment, but in 7D, there is almost no cells in the WT BM group. Data of this group might be missed?
Response: Thank you for this comment. Cre+WT BM cells (shown in 7D) were unable to form colonies as shown previously in figures 2B and 4B. Fig 7C refers to sensitivity to SVA using MTT assay.
- For figure 7G, the difference among MCM7 IHC staining of two groups didn't show as much as the statistical analysis in the right panel. Authors may consider using MCM7 western blot to check its levels after SVA treat.
Response: Thank you for this notion. We updated the Figure showing a more representative image (new Figure 7G).
Reviewer #2 (Significance):
This study uses a transgenic mouse model with tdTomato expressed in combination of loss of p53 and Wwox under the OSX lineage to study early initiation of OS. They found only DKO bone marrow cells can form OS in a subsequent orthotopic mouse model, but not the p53 single KO cells. After compare the RNA-seq from these different cell population, they identified the Myc pathway is the key player to promote OS development, especially the MCM7. Moreover, they tested SVA in treating these BM cells and reveal a therapeutic potential. This animal model is a good platform to study OS, especially at the early stage. Most results are clear and convincing. With the identification of Myc pathway, they further tested the SVA effects on treating these DKO BM. This is an important study and provided meaningful information to the OS, even broad cancer research community.
Response: We thank the reviewer for his/her supporting comments, and acknowledging the importance of our study.
However, the significance, or novelty of this work is not sufficient. For instance, SKO BM won't form tumor in the IT injection assays compare to the DKO BM groups, therefore, the involvement of Wwox during the OS tumorigenesis is clear. However, authors didn't explore any potential mechanisms of Wwox function or related signaling behind this observation
Response: We thank the reviewer for this very important comment. As mentioned previously, response to reviewer 1, our results indicate that combined deletion of two important known tumor suppressors, WWOX and p53, promotes osteosarcoma through early changes in Myc levels. Our data further show that p53 deletion alone is dispensable for this change to happen at early stages further highlighting the significance of our findings. In our revision plan we will do knockout of WWOX in yBM SKO and restore WWOX in yBM DKO cells. In addition, we are currently working to perform ChIP assay for Myc in yBM DKO and compare it to yBM SKO cells to show whether WWOX deletion is indeed results in enhanced chromatin accessibility of Myc.
And the RNA-seq analysis mostly focus on c-Myc pathway and its downstream targets. Given the well-known relationship of p53, c-myc even RB in the OS, it will be more interesting and attractive to see a clear mechanism of Wwox in this context.
Response: We thank the reviewer for this suggestion. Indeed, combined deletion of WWOX and p53 resulted in alteration of key cellular pathways involved in OS development. Due to the capacity of the work, we focused here on this important notion showing very early upregulation of Myc in BM-MSCs isolated from DKO cells, but not from SKO cells. Future work can expand use of this model to address relationship with other key pathways and genes.
Second, since authors took effort to generate this Tomato-DKO mice, it could be clearer if they isolate tdTomato positive cells instead of a mixture of BM, culture them, differentiate them, and perform more assays using these cells. In this way, it will give better clean background for all assays, and may be able to find novel effectors during this OS progression process.
Response: Thank you for this important suggestion. BM-MSCs cells collected directly from the mouse (Tom+, Sca1+, CD45-) represents a very small and minute population and was used to be cultured for enrichment as was done in previous studies (ref. 33 and 34). So direct collecting this small population and injecting directly to immunocompromised mice is not feasible. Moreover, further validation of the cultured cells used in our study confirmed their mesenchymal identity. We however, propose to try performing in vitro tumorigenic assays on these sorted cells. In our revision plan we suggest performing colony formation assays and soft agar assays to address tumorigenicity of these cells.
Third, within the text, authors tried to use OB differentiation and some other assays to discuss the OS origin cells, MSC or OB; but didn't get a preferred conclusion. It could be possible to better understand this process with the single cell RNA-seq using these BM from different mice or at different ages
Response: Thank you for this important point. According to our results we can conclude that BM-MSCs committed to the osteoblast lineage are supposed to be the cell of origin for OS and will be clearly emphasized in our revised version. Preforming a single cell RNA-seq is beyond the scope of this study and can be explored in future studies.
In general, this is a clean, straightforward study, and they established a very useful model to study OS. But the mechanisms merit is somewhere short
Response: Thank you for the kind words, as proposed previously our plan to further investigate the mechanism of WWOX regulatory effect on Myc will be addressed using the in vitro assays of WWOX deletion/restoration to SKO/DKO-yBM cells respectively. Moreover, ChIP-seq assay for Myc in yBM DKO and compare it to yBM SKO cells to show whether WWOX deletion is indeed results in enhanced chromatin accessibility of Myc.
Reviewer #3 (Evidence, reproducibility and clarity):
Summary: The work describes analysis of an Osx1-Cre p53fl/fl Wwoxfl/fl mouse model compared to an Osx1-Cre p53fl/fl model. The authors have assessed the osteosarcoma inducing potential of cells within the bone marrow by including a tdTom reporter of Cre expression. They conclude that bone marrow mesenchymal cells can give rise to osteosarcoma when transplanted. Based on transcriptomics they contend that upregulation of Myc is important and its target MCM7 can be targeted with simvastatin.
Major comments: -
Are the key conclusions convincing?
The authors can generate tumors in immunocompromised mice upon injecting cells derived from bone marrow flushed. This is not surprising given the data available now about expression of Osx1-Cre
Response: Thank you for this notion. In our study we showed that yBM cells harboring the deletion of two known important tumor suppressor genes WWOX and p53 collected from tumor free mice are tumorigenic compared to SKO p53 at this earlier stage. This is a novel notion that has not been presented previously. In our revised version, we propose to further study the mechanism of WWOX action on Myc accessibility.
The analysis of MSCs lacks detail and needs significant more improvement and assessment by FACS using the well-defined criteria for mesenchymal cells that have been developed
Response: Thank you for this comment. In our revised version we will add another marker (CD11b), in addition to the used markers (CD45/Sca-1 and CD29) which are all well known to define MSCs as mentioned in Ref. 21, 33, 34.
It is not clear to me from the available information if the authors have used bone marrow cells that were flushed and immediately transplanted or if all cells transplanted have been placed in culture first, adherent cells expanded in culture media favoring survival and proliferation of non-hematopoietic cells and then transplanted- this is important to clarify explicitly as it is important to the significance of the study. If these cells are all used after culture, then the novelty of these studies are questionable as it was demonstrated previously that similar types of cells give rise to OS when transplanted (PMID: 18697945).
Response: Thank you for this important point. In the referred reference (PMID: 18697945, ref 34) authors used p53/Rb Cre- stromal cells that were cultured in vitro then infected with Ad-Cre and then injected subcutaneously in immunocompromised mice. In our study, we provide evidence that genetically manipulated young BM-MSCs (for Wwox/p53) are tumorigenic when injected intratibially, a more relevant niche for these cells, and this involved upregulation of Myc. In our revised version, we shall provide more mechanistic insights on the functional relationship of WWOX and Myc. Using BM-MSCs cells that are directly collected from the mouse (Tom+, Sca1+, CD45-) is not feasible due to very low percentage of cells which has been also previously reported by many groups (Ref 34). In our revision plan, we also propose to try performing in vitro tumorigenic assays on sorted cells.
Moreover, in our study we validated that the deletion of p53 alone at this earlier stage is not enough to induce osteosarcomagenesis (which was not shown previously) suggesting additional hits are required for OS formation. Importantly, co-deletion of Wwox and p53 using the same Cre line resulted in the upregulation/higher levels of Myc that promotes osteosarcomagenesis at this earlier stage.
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
I think overall the authors are appropriately cautious in interpretation. The points raised above regarding the nature of the cells would need clarification and then the claims reassessed however.
Response: Thank you for this acknowledgment. According to our results we can conclude that BM-MSCs committed to the osteoblast lineage could be the cell of origin for OS and this will be clearly emphasized in the discussion of our revised version.
Claims re "metastatic potential" should be significantly reconsidered - the authors present (motility assays) which should be referred to as motility assays. The injection of cells intravenously is a lodgment assay of cells in the venous circulation and does not equate to the process a cancer cell must undergo and survive to metastasis from a primary tumor in an immune competent environment. The claims around these assays should be significantly reconsidered.
Response: Thank you for this important comment. In our revision plan we will check the lungs of IT injected mice for the presence of lung metastatic nodules (tdTomato positive cells in the lungs).
- 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.
It is not explained or justified what the control cohort in Fig 7F is significantly smaller than the treated cohort. This will affect the statistical analysis and interpretation. There is no statement regarding blinding/randomization (or not) in the in vivo simvastatin experiment - this needs to be added.
Response: In our revised version we clarified in the materials and methods section clearly the randomization of the mice selection for each group and number of mice in each group.
The authors should include discussion that these are relatively long latency OS models compared to p53/pRb compound mutants and contrast with previous data from these models where in vitro cultured cells did give rise to OS in vivo after Cre treatment.
Response: Thank you for this suggestion. In our revised paper, we will include the latency of OS in our model and compare them to p53/Rb, and emphasize that our model tested the tumorigenic ability of SKO yBM cells and showed that they are unable to form osteosarcoma tumors at this early stage compared to DKO yBM 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.
If a patient could to be treated based on these data, then the extra experiments to provide a robust preclinical dataset should be provided otherwise significant caution should be stated.
Response: Our study provides a proof-of-concept showing that our model can be used to screen for drugs that could inhibit OS development. The inhibitory potential of SVA affecting the progression of OS for clinical assessment would certainly need further investigation that goes beyond the scope of this paper.
- Are the data and the methods presented in such a way that they can be reproduced?
See comments regarding cells used for injection and blinding. Need to more clearly describe the cells being injected and what was done to them from isolation to injection.
Response: Thank you for this comment. In our revised version we will add clearly in the materials and methods section the protocol of cell isolation and injection, randomization of the mice selection for each group and number of mice in each group.
- Are the experiments adequately replicated and statistical analysis adequate? Unclear if appropriate experiment completed in Fig 7F as no justification of different sample sizes is provided nor a statement reblinding/randomization.
Response: Thank you for this point. In our revised version we will add clearly in the materials and methods section the randomization of the mice selection for each group and number of mice in each group.
Minor comments:
- Specific experimental issues that are easily addressable.
The Osx1-Cre expresses a Cre:GFP fusion - the authors should correlate the GFP and tomato signal.
Response: We thank the reviewer for this point. We shall perform validation analysis in our revised plan.
Fig 2A- if 50% of the bone marrow is tdTom positive this is not evident in the image in Fig 1D. Quantify the images in Fig 1D. The tumor images in Fig 2C appear to have only sporadic tdTom positive cells - the authors should explain this further.
Response: Thank you for this notion, Figure 2A represents BM collected from a tumor bearing mouse which has a higher percentage of tomato positive BM cells compared to tumor free mouse (Fig 1D). Fig 2C is updated
Need statistics added to all GSEA plots.
Response: Thank you for this comment, statistics will be added in our revised version.
4C is very different than 2C - 4C is more consistent with the levels of tomato stated
Response: Thank you for this notion, the images were updated in our revised version
- Are prior studies referenced appropriately?
This seems appropriate
Response: Thank you for this comment.
- Are the text and figures clear and accurate?
Figures are not ideal and could be improved in terms of >clarity and text size
Response: We apologize for the low quality. In our revised version, we shall provide an improved resolution and accuracy.
Several sections of text are either contradictory or questionably accurate:
page 3: Molecular studies of OS are significantly hindered by its genetic complexity and chromosomal instability, which precludes the identification of a single recurrent event associated with OS. Contrasts with the following text: Page 18 - p53 has been extensively shown to play a central role in OS development in both human and mouse models. The data from sequencing of human OS and mouse models and canine data all point to p53 loss as being a central event in OS.
Response: We apologize for this inaccurate statement. In our revised paper, we revised this statement to reflect the common event of p53 deletion in OS and its significance in osteosarcomagenesis.
Page 18: High genetic heterogeneity and chromosomal instability limit the early diagnosis of OS and lead to lung metastases and a worse prognosis. I don't understand this statement given that intratumor characteristics are not a determinant of early diagnosis - the patient being aware they have an issue and the clinical follow up determine the rate of diagnosis (and access to healthcare).
Response: We shall revise this statement to reflect the genetic heterogeneity of OS tumors.
Page 21: Consistent with their roles as tumor suppressor genes, the combined deletion of WWOX and p53 in Osx1-positive progenitor cells resulted in their transformation and growth advantage. Didn't the authors reach this conclusion from their previous work published in 2016? –
Response: Thank you for this notion. In our previous paper, we provided evidence that WWOX and p53 loss contributes to more aggressive OS tumor formation. In the current study, we provide evidence about early events contributes to osteosarcomagenesis using our Wwox/p53 model.
Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
improve figure clarity and text sizes
Response: We thank the reviewer for this notion; in our revised version, we shall provide an improved resolution, accuracy and clarity.
Reviewer #3 (Significance):
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
I think this is largely an incremental study which largely confirms previous studies.
Response: Although our results are consistent with some previously noted observations, we clearly provide unforeseen evidence that links Wwox/p53 in early osteosarcomagenesis and suggest that p53 deletion alone is not enough at this stage; other hits are required as in Wwox/p53 or Rb/p53. The mechanism of how DKO cells (Wwox/p53) results in Myc upregulation is also novel and will be further tested in our revised submission.
- Place the work in the context of the existing literature (provide references, where appropriate).
The study is a modest advance over the existing literature.
Response: We believe that with our revision plan, our paper will provide a significant advancement in the research in osteosarcomagenesis.
- State what audience might be interested in and influenced by the reported findings.
This would be relevant to basic sarcoma researchers.
- 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.
Generated multiple murine models of OS and characterized and applied them for biological understanding and preclinical studies.
-
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Referee #3
Evidence, reproducibility and clarity
Summary: The work describes analysis of an Osx1-Cre p53fl/fl Wwoxfl/fl mouse model compared to an Osx1-Cre p53fl/fl model. The authors have assessed the osteosarcoma inducing potential of cells within the bone marrow by including a tdTom reporter of Cre expression. The conclude that bone marrow mesenchymal cells can give rise to osteosarcoma when transplanted. Based on transcriptomics they contend that upregulation of Myc is important and its target MCM7 can be targeted with simvastatin.
Major comments:
- Are the key conclusions convincing?
The authors can generate tumors in immunocompromised mice upon injecting cells derived from bone marrow flushed. This is not surprising given the data available now about expression of Osx1-Cre. The analysis of MSCs lacks detail and needs significant more improvement and assessment by FACS using the well-defined criteria for mesenchymal cells that have been developed.
It is not clear to me from the available information if the authors have used bone marrow cells that were flushed and immediately transplanted or if all cells transplanted have been placed in culture first, adherent cells expanded in culture media favouring survival and proliferation of non-hematopoietic cells and then transplanted - this is important to clarify explicitly as it is important to the significance of the study. If these cells are all used after culture then the novelty of these studies are questionable as it was demonstrated previously that similar types of cells give rise to OS when transplanted (PMID: 18697945).<br /> - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?
I think overall the authors are appropriately cautious in interpretation. The points raised above regarding the nature of the cells would need clarification and then the claims reassessed however.
Claims re "metastatic potential" should be significantly reconsidered - the authors present motility assays which should be referred to as motility assays. The injection of cells intravenously is a lodgement assay of cells in the venous circulation and does not equate to the process a cancer cell must undergo and survive to metastasise from a primary tumour in an immune competent environment. The claims around these assays should be significantly reconsidered.<br /> - 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.
It is not explained or justified what the control cohort in Fig 7F is significantly smaller than the treated cohort. This will affect the statistical analysis and interpretation. There is no statement regarding blinding/randomisation (or not) in the in vivo simvastatin experiment - this needs to be added.
The authors should include discussion that these are relatively long latency OS models compared to p53/pRb compound mutants and contrast with previous data from these models where in vitro cultured cells did give rise to OS in vivo after Cre treatment.<br /> - 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.
If a patient could to be treated based on these data then the extra experiments to provide a robust preclinical dataset should be provided otherwise significant caution should be stated.<br /> - Are the data and the methods presented in such a way that they can be reproduced?
See comments regarding cells used for injection and blinding.
Need to more clearly describe the cells being injected and what was done to them from isolation to injection.<br /> - Are the experiments adequately replicated and statistical analysis adequate?
Unclear if appropriate experiment completed in Fig 7F as no justification of different sample sizes is provided nor a statement re blinding/randomisation.
Minor comments:
- Specific experimental issues that are easily addressable.
The Osx1-Cre expresses a Cre:GFP fusion - the authors should correlate the GFP and tomato signal.
Fig 2A- if 50% of the bone marrow is tdTom positive this is not evident in the image in Fig 1D. Quantify the images in Fig 1D.
The tumor images in Fig 2C appear to have only sporadic tdTom positive cells - the authors should explain this further.
Need statistics added to all GSEA plots
Panel 4C is very different than 2C - 4C is more consistent with the levels of tomato stated<br /> - Are prior studies referenced appropriately?
This seems appropriate<br /> - Are the text and figures clear and accurate?
Figures are not ideal and could be improved in terms of clarity and text sizes
Several sections of text are either contradictory or questionably accurate:<br /> page 3: Molecular studies of OS are significantly hindered by its genetic complexity and chromosomal instability, which precludes the identification of a single recurrent event associated with OS.<br /> Contrasts with the following text:<br /> Page 18 - p53 has been extensively shown to play a central role in OS development in both human and mouse models.
The data from sequencing of human OS and mouse models and canine data all point to p53 loss as being a central event in OS.
Page 18: High genetic heterogeneity and chromosomal instability limit the early diagnosis of<br /> OS and lead to lung metastases and a worse prognosis.<br /> I don't understand this statement given that intratumor characteristics are not a determinant of early diagnosis - the patient being aware they have an issue and the clinical follow up determine the rate of diagnosis (and access to healthcare).
Page 21: Consistent with their roles as tumor suppressor genes, the combined deletion of<br /> WWOX and p53 in Osx1-positive progenitor cells resulted in their transformation<br /> and growth advantage.
Didn't the authors reach this conclusion from their previous work published in 2016?<br /> - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
improve figure clarity and text sizes
Significance
- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
I think this is largely an incremental study which largely confirms previous studies.<br /> - Place the work in the context of the existing literature (provide references, where appropriate).
The study is a modest advance over the existing literature.<br /> - State what audience might be interested in and influenced by the reported findings.
This would be relevant to basic sarcoma researchers.<br /> - 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.
Generated multiple murine models of OS and characterized and applied them for biological understanding and preclinical studies.
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Referee #2
Evidence, reproducibility and clarity
In current study, the authors established a mouse model with tdTomato expression under the OSX-controlled double deletions of Wwox and Trp53. Such mouse strain gives a great platform to study the OS development and therapeutic potential. Experiments are clear and convincing. Results are well presented.
To better improve this study, few minor suggestions regarding the data are as following,
- Some of the legends on figures are too small to read, or in low quality. please change these labels.
- For Figure 7C and D, from 7C, The control WT BM showed clear resistance to the SVA treatment, but in 7D, there is almost no cells in the WT BM group. Data of this group might be missed?
- For figure 7G, the difference among MCM7 IHC staining of two groups didn't show as much as the statistic analysis in the right panel. Authors may consider using MCM7 western blot to check its levels after SVA treat.
Significance
This study use a transgenic mouse model with tdTomato expressed in combination of loss of p53 and Wwox under the OSX lineage to study early initiation of OS. They found only DKO bone marrow cells can form OS in a subsequent orthotopic mouse model, but not the p53 single KO cells. After compare the RNA-seq from these different cell population, they identified the Myc pathway is the key player to promote OS development, especially the MCM7. Moreover, they tested SVA in treating these BM cells and reveal a therapeutic potential.
This animal model is a good platform to study OS, especially at the early stage. Most results are clear and convincing. With the identification of Myc pathway, they further tested the SVA effects on treating these DKO BM. This is an important study and provided meaningful information to the OS, even broad cancer research community. However, the significance, or novelty of this work is not sufficient.
For instance, SKO BM won't form tumor in the IT injection assays compare to the DKO BM groups, therefore, the involvement of Wwox during the OS tumorigenesis is clear. However, authors didn't explore any potential mechanisms of Wwox function or related signaling behind this observation. And the RNA-seq analysis mostly focus on c-Myc pathway and its downstream targets. Given the well known relationship of p53, c-myc even RB in the OS, it will be more interesting and attractive to see a clear mechanisms of Wwox in this context.
Second, since authors took effort to generate this Tomato-DKO mice, it could be more clear if they isolate tdTomato positive cells instead of a mixture of BM, culture them, differentiate them, and perform more assays using these cells. In this way, it will give better clean background for all assays, and may be able to find novel effectors during this OS progression process.
Third, within the text, authors tried to use OB differentiation and some other assays to discuss the OS origin cells, MSC or OB; but didn't get a preferred conclusion. It could be possible to better understand this process with the single cell RNA-seq using these BM from different mice or at different ages.
In general, this is a clean, straightforward study, and they established a very useful model to study OS. But the mechanisms merit is somewhere short.
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Referee #1
Evidence, reproducibility and clarity
The study "Mesenchymal stem cell models reveal critical role of Myc as early molecular event in osteosarcomagenesis" by Akkawi et al shows that BM-MSCs are a foundational tool for study of osteosarcoma. And authors identified Myc and its targets as early molecular events in osteosarcoma formation, using BM-MSCs knocked out of both p53 and Wwox. Although the quality and validity of the data presented in this manuscript are not in question, this reviewer has doubts about the novelty of the findings in this current version of manuscript. It does not clearly indicate what is different from previous findings, such as;
- It has already been reported that p53-/- BM-MSCs are the cells of origin in osteosarcoma development (ref.19).
- Indispensability of Myc in osteosarcomagenesis was revealed (PMID: 12098700).
- Osteosarcoma formation of p53flox-OsxCre mice was rescued by Myc-depletion and BM-MSCs from p53flox-OsxCre was shown to upregulate Myc (PMID: 34803166).<br /> First of all, the authors need to cite the above papers and compare their findings with them to better clarify the value of their findings.
The only one clear finding would be that Wwox functions as a tumor suppressor by repressing Myc function in the absence of p53, but unfortunately, no data have been presented on the mechanism. Some additional analysis would be needed to mention it. In the first place, Myc is upregulated in the absence of both p53 and Wwox, compared in only p53-null situation? Western blotting would be better to show it.
- In Figure 1D, should separate each panel so that it is clearly visible. What is the blue-colored fluorescence, DAPI? If so, why don't tdTomoto positive cells overlap with blue (Figs, 1D, 2C, 4C, 4E?
- Why was MCM7 chosen among the Myc targets (S Figure 3)? What is the rationale for this?
- In Figure 5 legend, what does "yBM cells (1.5, 4-months)(n=6)" mean? yBM cells (1.5-months)(n=3) and yBM cells (4-months)(n=3)?
- In Figure 7B, is there a correlation between MCM7 and Myc protein expression levels? Also, do MCM7 and Myc immunopositivites overlap in Figure 7G?
- In S Figure 4C, what is 'PC'? What sample was loaded?
- In S Figure 2A, what does 'US' (BM-US) mean? In S Figure 4F, what does 'US' and 'S' (Direct US and Direct S) mean?
- Overall this manuscript, there are too many symbols and it is cumbersome. Ex, in S Figure 3, yBM_DKO, Tum_DKO, DKOT, DKO-BMT, etc. All figures should be consistent with the same notation.
Significance
Although the quality and validity of the data presented in this manuscript are not in question, this reviewer has doubts about the novelty of the findings in this current version of manuscript. It does not clearly indicate what is different from previous findings, such as;
- It has already been reported that p53-/- BM-MSCs are the cells of origin in osteosarcoma development (ref.19).
- Indispensability of Myc in osteosarcomagenesis was revealed (PMID: 12098700).
- Osteosarcoma formation of p53flox-OsxCre mice was rescued by Myc-depletion and BM-MSCs from p53flox-OsxCre was shown to upregulate Myc (PMID: 34803166).<br /> First of all, the authors need to cite the above papers and compare their findings with them to better clarify the value of their findings.<br /> The only one clear finding would be that Wwox functions as a tumor suppressor by repressing Myc function in the absence of p53, but unfortunately, no data have been presented on the mechanism.
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Reply to the reviewers
Reviewer #1 (Evidence, reproducibility and clarity):
Summary:<br /> Plasmodium sporozoites rely on gliding motility to invade the salivary glands of the mosquito vector where they reside until being inoculated into the vertebrate host. Once in the vertebrate host, sporozoites again have to glide to pass through liver cells and reach the final host cell before exo-erythrocytic replication occurs. In sporozoites, thrombospondin-related anonymous protein (TRAP) is the key adhesin, linking the molecular motor to the substrate. TRAP and TRAP-like proteins contain on the extracellular side an inserted (I) domain that is responsible for substrate binding. The I domain can be in an open or closed state which can be fixed by mutating specific amino acids. Braumann et al. then assessed the effect of these states on gliding motility and infection. Whilst no effect was seen for both mutants with closed or open states until the production of haemolymph sporozoites, the number of salivary gland sporozoites were highly reduced in both mutants. The closed mutant was not able to be transmitted from mosquitoes to mice whilst the open mutant is severely impacted in transmission. Gliding of both mutant is highly impaired. Some of these phenotypes could be reverse by adding a reducing agent.
Major comments:<br /> This is an elegant study with exhaustive experiments to address the research questions. One of the things I wondered about is the effect of exchanging amino acids. As far as I understood, structural information of integrins from other organisms informed the authors about positions that should be mutated and about the impact (or loss of it) on the 3D structure of the domain. Would it not be useful to run a structure prediction programme such as Alphafold on all the mutants to at least confirm stability of the domain structure upon mutation in silico?_
A: Thanks for this suggestion, we added the crystal structure models of P. falciparum and P. vivax as well as the Alphafold models of the open and closed state of P. berghei TRAP as new panels in Figure 1, added some corresponding text to the results, materials and methods, and the figure legend.
Some of the concentrations of reducing agents tested are very high. Can the authors be sure that the parasites are not dead?
A: We used sporozoites expressing GFP in the cytosol and did not see loss of fluorescence. While this does not rule out that the parasites are not alive anymore, it shows that the plasma membrane was not compromised. Importantly, when using the more moderate concentrations that rescued motility, wild type parasites were also moving, showing that the parasites were alive.
Minor comments:<br /> -Please make sure that punctuation is correct (e.g. missing commas) and that there are no other typing errors.
A: We carefully read and edited the manuscript again and hopefully corrected all those errors.
- Line 50: This sentence may imply mechanical rupture of oocysts rather than active egress of the sporozoite. Please re-phrase.
A: rephrased, it now reads “egress” instead of “burst”. (now line 53)
- Line 82: Do you mean a complexed Mg2+ ion?
A: Yes, this sentence was revised. (now line 99)
- The introduction stops rather abruptly. Maybe a sentence of the significance of this study could be added.
A: we added the following: “Our results suggest that active change between the open and closed conformation of the TRAP I domain is essential for sporozoite invasion of salivary glands and transmission from mosquitoes to mammals.” (line 122-125).
- Line 361: 20 million parasites each? Please re-phrase to make it clearer.
A: done, it now reads: “…into each of two naïve mice…”.(now line 517)
- Line 363: Field of view needs to defined: What is the magnification used to observe exflagellation?
A: done, it now reads: “as observed with a Zeiss Axiostar using a 100x objective lens – revealing 300-400 red blood cells per field of view) – now line 519-521.”
- Materials and Methods: Please write out reagent names for the first time.
A: done, e.g. “phosphate buffered saline” for PBS; line 540; Roswell Park Memorial Institute medium 1640 for RPMI; line 420; as well as for DTT and TCEP (lines 560, 561), BSA (line 565), etc
Figures:<br /> - Figure 1A is very small. The label font of the whole figure 1 is often too small.
A: We intentionally kept Figure 1A small as most readers will be familiar with the life cycle but increased font size as much as possible throughout the figure including Figure 1B, which we needed to shrink in the new design to accommodate the Alphafold structures.
- Figure 1D: Please list the components in the figure legend, e.g. blue: substrate etc.
A: done, now lines 722-725
- Figure 3: The figure title should be changed as there is no complete failure of sporozoites with fixed I-domains to invade salivary glands.
A: done, it now reads: “…show strong reduction in salivary gland invasion”, line 790-791
- Figure 5: for clarity, it would be easier if Figure C would not be squeezed into the legends of A and B.
A: We agree this is a tricky arrangement, but when composing the figure, we tried many different ways, which were all unsatisfactory too, leading to either too awkward an arrangement or too much white between the panels. We hence, despite anticipating this critique, decided on this arrangement and would hence like to keep it. However, we changed the color of the box around C so that it is marked more differently.
Reviewer #1 (Significance):
This study addresses in detail the mechanism of Plasmodium TRAP I domain in gliding motility and transmission. It builds on work from many years and groups including their own and contributes to deepen our understanding of TRAP-family proteins, gliding motility in Plasmodium sporozoites and maybe even in other Plasmodium stages or other Apicomplexan parasites.
This work is of interest to researchers in the field of Plasmodium mosquito stages and transmission as well as scientist who work on apicomplexan gliding motility and transmission.
I have previously worked on Plasmodium mosquito stages, but currently work on Toxoplasma_ gondii.
A: Thank you for your appreciation of our study, the mechanistic insights it gives into gliding and transmission, and the helpful critique.
Reviewer #2 (Evidence, reproducibility and clarity):
This work seeks to investigate the effects on sporozoite motility of hypothesized conformational changes in TRAP's integrin domain. Previous structural studies suggested that the Integrin-like domain of TRAP assumes 'open' and 'closed' conformations induced by ligand binding. Here the authors hypothesize that TRAP's ability to dynamically switch between these states is crucial for sporozoite motility. The hypothesis is interesting and the authors elected to test it by 'fixing' TRAP in constitutively 'open' and 'closed' conformations by introducing Cys residues that are presumed to form disulphide bonds resulting in these states.
Major Comments<br /> The approach is creative. The data that are presented are of high quality with adequate reproducibility. However, as written the manuscript does not provide a rationale for the specific substitutions they chose, how these substitutions are expected to lead to 'open' and 'closed' states, and how they mimic the natural route of TRAP transitioning between the 'open' and 'closed' conformations._
A: We now add a more detailed rationale at the very start of the results section, which now reads: “We used closed and open structures of TRAP from P. falciparum and P. vivax, respectively (Song et al., 2012), to design cysteine mutations in P. berghei (Fig. 1E-J). The TRAP I domain of P. berghei is 42 and 48% identical in sequence to those of P. vivax and P. falciparum, respectively; lower identity was used for successful introduction of a disulfide into integrin αI domains (Shimaoka et al., 2001; Shimaoka et al., 2003). Between the open and closed TRAP I domain conformations, the I domain α7-helix pistons 9 Å relative to the neighboring β6-strand; therefore, disulfides introduced between these two structural elements can stabilize one state over the other, as previously pioneered in integrin I domains. β6-strand and α7-helix residues with Cβ atoms within 5 Å of one another in structures of the two states were chosen for mutation to cysteine (Fig. 1G&H). P. falciparum TRAP-Fc fusions with homologous cysteine mutations were well expressed in mammalian cells (Koksal et al,, 2013). Using the TRAP sequence alignment (Fig. 1F), homologous residues in P. berghei TRAP were mutated to cysteine to stabilize the closed conformation (Ser-210 and Phe-224 in the S210C/F224C mutation) and the open conformation (Ser-210 and Gln-216 in the S210C/Q216C mutation). AlphaFold (Mirdita et al 2022) predicted that the P. berghei TRAP I domains were well folded and assumed the desired conformations with formation of the mutationally introduced disulfide bonds (Fig. 1I&J). The I domain of P. berghei is 42 and 48% identical in sequence to those of P. vivax and P. falciparum in which the open and closed conformations are defined, assuring highly confident modeling (Song et al., 2012). Cysteines were substituted in positions that were sufficiently close in one conformation to form a disulfide but not in the alternative conformation..” lines 130-202 and also provided a detailed view of the structures in Figure 1.
Furthermore, there is no biochemical, biophysical or modeling data demonstrating that the introduced mutations impact the folding/unfolding of TRAP's I domain in the manner hypothesized. Therefore, it is difficult to interpret subsequent phenotypic data from the two mutant lines. While mutant parasites display defects in gliding motility, these defects are unexpected, perhaps pointing to alternative explanations - such as aberrant inter- or intra-molecular disulphide bonding in TRAP's extracellular domain.
A: The ability of such mutations to give biologically meaningful results has already been demonstrated in integrin I domains, where ligand-binding affinity was measured. We now describe the rationale in more detail, and demonstrate that the cysteines are recognized by Alphafold to yield well-folded domains that are stabilized in the desired conformations. These are presented as new panels in Figure 1.
About 10% of mutant sporozoites assumed to be in a constitutively 'closed' conformation display gliding motility and they move faster that WT. Yet this mutant did not cause patency in mice when introduced either via mosquito bite or IV injection. In contrast, the mutant assumed to be in an 'open' conformation displayed no motility in vitro but was able to infect mice (albeit at a significantly reduced rate compared to controls). Presumably, these data suggest that the in vitro gliding motility assays used are insufficient for testing the effect of these mutations on motility that is relevant in vivo. The model is that TRAP's interaction with extracellular ligands stabilizes its 'open' position. This suggests that motility assays conducted with extracellular matrix eg Matrigel are a more appropriate test of motility.
A: The reviewer raises interesting points. There are several types of sporozoite motility assays available, 2D on glass, 2D on ligands (e.g. Matrigel), 3D in polyacrylamide gels or Matrigel, and 3D in the skin. All of these have a number of advantages and disadvantages. 2D on glass is clearly the easiest, 3D in skin, clearly the most complex one. The advantage of the 2D on glass assay is that it reveals even tiny defects on motility that cannot be revealed in 3D assays as the enclosure of the parasite in a 3D matrix compensates for several defects, especially those in adhesion that are most relevant for our study here (see also e.g. Bane et al. Plos Path 2016, Ripp et al., EMBO Mol Med 2021). Hence, we believe that for understanding the role of adhesion in motility the 2D assay is highly valuable because it represents a minimal system. In contrast, the complex 3D environments, are closer to the natural situation but are less useful in our specific case. The fact that the mutants are severely limited in vivo (in the mosquito where they are blocked at the 2D surface of the salivary gland) suggests that the assays are highly relevant. We take this comment as a motivation to write a review/opinion like paper in the near future but feel it would distract if added here to e.g. the discussion.
Experiments with DTT are difficult to interpret since there is once again no biochemical evidence that this treatment leads to a change in conformation of TRAP. DTT's effect on motility of the mutant could be non-specific. Overall, conclusions that are presented need to be supported by more data.
A: We are aware of this and hence already discussed these potential shortcomings of our study in the discussion. Importantly: there is no known specific ligand to the TRAP I domain. Hence, we believe that biochemical tests would not justify the effort it would take to express the different domains.
Reviewer #2 (Significance):
Sporozoite motility is a prerequisite for infection by Plasmodium of the liver. A better mechanistic understanding of this process is significant for our understanding of the first step of malaria infection. TRAP is the major adhesin on the sporozoite surface and its loss abrogates sporozoite motility. The authors are to be commended for undertaking a challenging study.
A: We thank the reviewer for appreciating our efforts, the advance provided, and for the constructive critique.
Reviewer #3 (Evidence, reproducibility and clarity):
This paper builds on previous structural studies from the Springer lab, which show that the I-domain of the malaria sporozoite surface protein TRAP can switch between two conformations ("open" and "closed"), similar to what happens with the I domain of integrins. In the current study the authors explore whether the open and closed conformations of TRAP are important for sporozoite migration and infectivity by generating parasites expressing each form locked in place using introduced disulfides. Locking TRAP into either form inhibits sporozoite gliding, invasion of the mosquito salivary glands and transmission from mosquito to mouse. The addition of low levels of a reducing agent can partially rescue these effects with the open form, which the authors suggest points to a requirement for TRAP to undergo a switch between its open and closed states to support these key processes in the parasite's life cycle.
The paper is well written and the data and methods are clearly presented.
Major Comments:
Lines 109-115: The entire paper relies on the premise that the introduced disulfides lock the I domain of TRAP in either the open or closed conformation. In the absence of experimental proof that this is the case, it would be helpful to the reader to have more detail on how this can be confidently inferred from the previous work on integrins -- perhaps as a supplementary figure._
A: We now added a statement on how the positions for the cysteines were selected and also a figure on structures and Alphafold prediction as also suggested by reviewers 1 and 2 as panels in Figure 1.
The partial rescue of motility in the S210C/Q216C parasites by 50-100mM DTT is a VERY indirect approach to testing whether the conformational switch between the open and closed states is functionally important. The authors are appropriately reserved in their conclusions, but wildtype parasites are ultimately a better (less confounded) comparator; the authors may want to stress this more._
A: Thanks for appreciating our efforts to navigate the limitations of our experimental system. We have changed our wording (e.g. replaced “fixed state” with “stabilized state” in the discussion) and added cautionary statements, which now read “While DTT clearly does not only act on TRAP, these data nevertheless suggest that…” (lines 353-354); “While not providing final proof, this phenotype indicates…” (lines 371); “…antibodies that stabilize… could contribute to stopping parasite migration” (line 415)
The implications of the current results for the authors' previous stick-and-slip model of sporozoite motility should be discussed.
A: We added a few sentences including two references on this in the discussion: “Sporozoites glide in a stick-slip fashion…” (lines 417-422)
Minor Comments:
The authors are experienced in the use reflection interference contrast microscopy to visualize attachment of the parasite to the substrate. Did they do any RICM on the mutants? Although not necessary for the paper, this would be a good way to support the interpretation of some of their results (eg, lines 185-190)._
A: We indeed hoped that the mutants would allow us to exploit these techniques as this would give much insight into the mode of migration. However, all our previous work on RICM was done with salivary gland derived sporozoites, which are robustly gliding. In contrast, those derived from the hemolymph or oocysts do not glide very well. While we can quantitatively image them at low magnification (large field of view) settings, we have consistently failed to get sufficient data on most of our advanced assays that require single sporozoite imaging such as RICM, TIRFM, and laser tweezer experiments. This, unfortunately, is a real limitation of the system as most interesting mutants (see also e.g. recent paper by Yee et al., Plos Pathogens 2022) are not entering the salivary glands.
Line 127: Figure 2A does not show "no growth difference to wild type mice"
A: we split the sentence in two with Figure 2A now only referring to mosquito infections (now line 212)
Line 154: "higher, but not significantly higher" - if the data don't meet the significance threshold being used, they cannot be called higher
A: Yes, the thing here is that we always got more from the open mutant and hence could do experiments but indeed the stats showed it not to be significant. We changed the sentence to read “…was not significantly higher…” (line 242)
Line 186: "showed nearly no floating parasites compared to the controls S210C and cFluo" - cFluo and S210C/Q216C show the same amount of floaters in Fig 5B. Also, S210C/Q216C HLS show similar levels of floaters to both controls in 2A.
A: Thanks for spotting this mixup, we changed it to: “Interestingly, hemolymph sporozoites expressing the closed I domain (S210CF224C) showed more floating parasites suggesting reduced adhesion. Intriguingly, the few moving sporozoites of this mutant were also significantly faster than the corresponding controls.” (lines 296-299). We also pick up on this observation in the discussion in the new paragraph on stick-slip motility, lines 414-422) which links back to the Munter et al paper cited in line 303. This is in line with observations in mammalian cells where reduced ligand density also leads to less adhesion and faster migration.
Fig S2 defines unproductive gliding to include waving, but Figs. 5 and S3 scores waving as a separate category
A: We define it as unproductive motility, which we now changed into “unproductive movement” in the hope to be less misleading, clearly “lazy gliding” is motility while waving is no motility but some type of movement.
Fig S3B and Fig 5D,E appear to be the same data presented twice
A: Correct, we now state this explicitly in the figure legend to Figure S3B (lines 958-960) where they are reproduced together with the matching controls
Line 304: "the inability of sporozoites with the TRAP I domain to migrate" (?)
A: “conformationally stabilized” was missing and has now been included (line 453)
Line 226: please explain what the + > ++++ qualitative descriptors signify in the tables and how they were scored
A: Now added in the legends to the table, lines 885-887 and 892, respectively.
Lines 282, 312: the authors should mention here the extensive work that has been done on efficacy of viral vaccines directed against a particular conformational state of the immunogen
A: We were naturally tempted to do this but feel that this could hype the study more than is justified by our data.
Fig 2B: The labels above the lanes are incomplete and therefore confusing; suggest sticking to the same nomenclature as in 2A
A: Modified as suggested
Typographical errors on lines: 58 (space missing), 80-81 (parentheses), 155 (Figure misspelled), 188 (expressing the closed (S210C/F224C)), 306 (comma after both)
A: Thanks, these were corrected.
CROSS-CONSULTATION COMMENTS<br /> Since all three reviewers questioned whether the introduced disulfides would have the assumed effects on I domain structure, the authors should provide a stronger rationale for this assumption or -- as suggested by reviewer 2 -- some actual data to support it. Reviewer 2's comment about the extracellular ligands available for the parasite to bind to in the gliding assay and whether this could influence the outcome (and relevance to what occurs in vivo) also deserves consideration.
A: We have now added Alphafold predictions of the mutants (Figure 1) and also described better how we selected the mutations based on extensive work by the Springer lab (see newly added lines 130-202). We appreciate the idea of using extracellular ligands, however, all our previous assays (e.g. Klug et al. eLife 2020 and Perschmann et al., Nano Letter 2011) suggest that the parasites move on a large variety of surfaces at the same rate.
Reviewer #3 (Significance):
This is an elegant study that contributes important new information to our understanding of apicomplexan parasite motility and the function of the TRAP protein. The results will be of significant interest to those who study parasite motility, and likely also to those who study the role of integrins in cellular adhesion and signaling. The data nicely connect what was previously known about conformational changes in integrins with parasite adhesion to the substrate and motility.
I have expertise in the area of parasite motility._
A: We thank the reviewer for the constructive comments and appreciation of our work
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Referee #3
Evidence, reproducibility and clarity
This paper builds on previous structural studies from the Springer lab, which show that the I-domain of the malaria sporozoite surface protein TRAP can switch between two conformations ("open" and "closed"), similar to what happens with the I domain of integrins. In the current study the authors explore whether the open and closed conformations of TRAP are important for sporozoite migration and infectivity by generating parasites expressing each form locked in place using introduced disulfides. Locking TRAP into either form inhibits sporozoite gliding, invasion of the mosquito salivary glands and transmission from mosquito to mouse. The addition of low levels of a reducing agent can partially rescue these effects with the open form, which the authors suggest points to a requirement for TRAP to undergo a switch between its open and closed states to support these key processes in the parasite's life cycle.
The paper is well written and the data and methods are clearly presented.
Major Comments:
Lines 109-115: The entire paper relies on the premise that the introduced disulfides lock the I domain of TRAP in either the open or closed conformation. In the absence of experimental proof that this is the case, it would be helpful to the reader to have more detail on how this can be confidently inferred from the previous work on integrins -- perhaps as a supplementary figure.
The partial rescue of motility in the S210C/Q216C parasites by 50-100mM DTT is a VERY indirect approach to testing whether the conformational switch between the open and closed states is functionally important. The authors are appropriately reserved in their conclusions, but wildtype parasites are ultimately a better (less confounded) comparator; the authors may want to stress this more.
The implications of the current results for the authors' previous stick-and-slip model of sporozoite motility should be discussed.
Minor Comments:
The authors are experienced in the use reflection interference contrast microscopy to visualize attachment of the parasite to the substrate. Did they do any RICM on the mutants? Although not necessary for the paper, this would be a good way to support the interpretation of some of their results (eg, lines 185-190).
Line 127: Figure 2A does not show "no growth difference to wild type mice"
Line 154: "higher, but not significantly higher" - if the data don't meet the significance threshold being used, they cannot be called higher
Line 186: "showed nearly no floating parasites compared to the controls S210C and cFluo" - cFluo and S210C/Q216C show the same amount of floaters in Fig 5B. Also, S210C/Q216C HLS show similar levels of floaters to both controls in 2A.
Fig S2 defines unproductive gliding to include waving, but Figs. 5 and S3 scores waving as a separate category
Fig S3B and Fig 5D,E appear to be the same data presented twice
Line 304: "the inability of sporozoites with the TRAP I domain to migrate" (?)
Line 226: please explain what the + > ++++ qualitative descriptors signify in the tables and how they were scored
Lines 282, 312: the authors should mention here the extensive work that has been done on efficacy of viral vaccines directed against a particular conformational state of the immunogen
Fig 2B: The labels above the lanes are incomplete and therefore confusing; suggest sticking to the same nomenclature as in 2A
Typographical errors on lines: 58 (space missing), 80-81 (parentheses), 155 (Figure misspelled), 188 (expressing the closed (S210C/F224C)), 306 (comma after both)
Referees cross-commenting
Since all three reviewers questioned whether the introduced disulfides would have the assumed effects on I domain structure, the authors should provide a stronger rationale for this assumption or -- as suggested by reviewer 2 -- some actual data to support it. Reviewer 2's comment about the extracellular ligands available for the parasite to bind to in the gliding assay and whether this could influence the outcome (and relevance to what occurs in vivo) also deserves consideration.
Significance
This is an elegant study that contributes important new information to our understanding of apicomplexan parasite motility and the function of the TRAP protein. The results will be of significant interest to those who study parasite motility, and likely also to those who study the role of integrins in cellular adhesion and signaling. The data nicely connect what was previously known about conformational changes in integrins with parasite adhesion to the substrate and motility.
I have expertise in the area of parasite motility.
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Referee #2
Evidence, reproducibility and clarity
This work seeks to investigate the effects on sporozoite motility of hypothesized conformational changes in TRAP's integrin domain. Previous structural studies suggested that the Integrin-like domain of TRAP assumes 'open' and 'closed' conformations induced by ligand binding. Here the authors hypothesize that TRAP's ability to dynamically switch between these states is crucial for sporozoite motility. The hypothesis is interesting and the authors elected to test it by 'fixing' TRAP in constitutively 'open' and 'closed' conformations by introducing Cys residues that are presumed to form disulphide bonds resulting in these states.
Major Comments
The approach is creative. The data that are presented are of high quality with adequate reproducibility. However, as written the manuscript does not provide a rationale for the specific substitutions they chose, how these substitutions are expected to lead to 'open' and 'closed' states, and how they mimic the natural route of TRAP transitioning between the 'open' and 'closed' conformations.
Furthermore, there is no biochemical, biophysical or modeling data demonstrating that the introduced mutations impact the folding/unfolding of TRAP's I domain in the manner hypothesized. Therefore, it is difficult to interpret subsequent phenotypic data from the two mutant lines. While mutant parasites display defects in gliding motility, these defects are unexpected, perhaps pointing to alternative explanations - such as aberrant inter- or intra-molecular disulphide bonding in TRAP's extracellular domain.
About 10% of mutant sporozoites assumed to be in a constitutively 'closed' conformation display gliding motility and they move faster that WT. Yet this mutant did not cause patency in mice when introduced either via mosquito bite or IV injection. In contrast, the mutant assumed to be in an 'open' conformation displayed no motility in vitro but was able to infect mice (albeit at significantly reduced compared to controls). Presumably these data suggest that the in vitro gliding motility assays used are insufficient for testing the effect of these mutations on motility that is relevant in vivo. The model is that TRAP's interaction with extracellular ligands stabilizes its 'open' position. This suggests that motility assays conducted with extracellular matrix eg Matrigel are a more appropriate test of motility.
Experiments with DTT are difficult to interpret since there is once again no biochemical evidence that this treatment leads to a change in conformation of TRAP. DTT's effect on motility of the mutant could be non-specific. Overall, conclusions that are presented need to be supported by more data.
Significance
Sporozoite motility is a prerequisite for infection by Plasmodium of the liver. A better mechanistic understanding of this process is significant for our understanding of the first step of malaria infection. TRAP is the major adhesin on the sporozoite surface and its loss abrogates sporozoite motility. The authors are to be commended for undertaking a challenging study.
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Referee #1
Evidence, reproducibility and clarity
Summary:
Plasmodium sporozoites rely on gliding motility to invade the salivary glands of the mosquito vector where they reside until being inoculated into the vertebrate host. Once in the vertebrate host, sporozoites again have to glide to pass through liver cells and reach the final host cell before exo-erythrocytic replication occurs. In sporozoites, thrombospondin-related anonymous protein (TRAP) is the key adhesin, linking the molecular motor to the substrate. TRAP and TRAP-like proteins contain on the extracellular side an inserted (I) domain that is responsible for substrate binding. The I domain can be in an open or closed state which can be fixed by mutating specific amino acids. Baumann et al. then assessed the effect of these states on gliding motility and infection. Whilst no effect was seen for both mutants with closed or open states until the production of haemolymph sporozoites, the number of salivary gland sporozoites were highly reduced in both mutants. The closed mutant was not able to be transmitted from mosquitoes to mice whilst the open mutant is severely impacted in transmission. Gliding of both mutant is highly impaired. Some of these phenotypes could be reverse by adding a reducing agent.
Major comments:
This is an elegant study with exhaustive experiments to address the research questions. One of the things I wondered about is the effect of exchanging amino acids. As far as I understood, structural information of integrins from other organisms informed the authors about positions that should be mutated and about the impact (or loss of it) on the 3D structure of the domain. Would it not be useful to run a structure prediction programme such as Alphafold on all the mutants to at least confirm stability of the domain structure upon mutation in silico?
Some of the concentrations of reducing agents tested are very high. Can the authors be sure that the parasites are not dead?
Minor comments:
- Please make sure that punctuation is correct (e.g. missing commas) and that there are no other typing errors.
- Line 50: This sentence may imply mechanical rupture of oocysts rather than active egress of the sporozoite. Please re-phrase.
- Line 82: Do you mean a complexed Mg2+ ion?
- The introduction stops rather abruptly. Maybe a sentence of the significance of this study could be added.
- Line 361: 20 million parasites each? Please re-phrase to make it clearer.
- Line 363: Field of view needs to defined: What is the magnification used to observe exflagellation?
- Materials and Methods: Please write out reagent names for the first time.
Figures:
- Figure 1A is very small. The label font of the whole figure 1 is often too small.
- Figure 1D: Please list the components in the figure legend, e.g. blue: substrate etc.
- Figure 3: The figure title should be changed as there is no complete failure of sporozoites with fixed I-domains to invade salivary glands.
- Figure 5: for clarity, it would be easier if Figure C would not be squeezed into the legends of A and B.
Significance
This study addresses in detail the mechanism of Plasmodium TRAP I domain in gliding motility and transmission. It builds on work from many years and groups including their own and contributes to deepen our understanding of TRAP-family proteins, gliding motility in Plasmodium sporozoites and maybe even in other Plasmodium stages or other Apicomplexan parasites.
This work is of interest to researchers in the field of Plasmodium mosquito stages and transmission as well as scientist who work on apicomplexan gliding motility and transmission.
I have previously worked on Plasmodium mosquito stages, but currently work on Toxoplasma gondii.
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