Author response:

Reviewer #1 (Evidence, reproducibility and clarity):

Summary:

This manuscript reports the identification of putative orthologues of mitochondrial contact site and cristae organizing system (MICOS) proteins in Plasmodium falciparum - an organism that unusually shows an acristate mitochondrion during the asexual part of its life cycle and then this develops cristae as it enters the sexual stage of its life cycle and beyond into the mosquito. The authors identify PfMIC60 and PfMIC19 as putative members and study these in detail. The authors at HA tags to both proteins and look for timing of expression during the parasite life cycle and attempt (unsuccessfully) to localise them within the parasite. They also genetically deleted both gene singly and in parallel and phenotyped the effect on parasite development. They show that both proteins are expressed in gametocytes and not asexuals, suggesting they are present at the same time as cristae development. They also show that the proteins are dispensible for the entire parasite life cycle investigated (asexuals through to sporozoites), however there is some reduction in mosquito transmission. Using EM techniques they show that the morphology of gametocyte mitochondria is abnormal in the knockout lines, although there is great variation.

Major comments:

The manuscript is interesting and is an intriguing use of a well studied organism of medical importance to answer fundamental biological questions. My main comments are that there should be greater detail in areas around methodology and statistical tests used. Also, the mosquito transmission assays (which are notoriously difficult to perform) show substantial variation between replicates and the statistical tests and data presentation are not clear enough to conclude the reduction in transmission that is claimed. Perhaps this could be improved with clearer text?

We would like to thank the reviewer for taking the time to review our manuscript. We are happy to hear the reviewer thinks the manuscript is interesting and thank the reviewer for their constructive feedback.

To clarify the statistical analyses used, we included a new supplementary dataset with all statistical analyses and p-values indicated per graph. Furthermore, figure legends now include the information on the exact statistical test used in each case.

Regarding mosquito experiments, while we indeed reported a reduction in transmission and oocysts numbers, we are aware that this effect might be due to the high variability in mosquito feeding assays. To highlight this point, we deleted the sentence “with the transmission reduction of [numbers]….” and we included the sentence “The high variability encountered in the standard membrane feeding assays, though, partially obstructs a clear conclusion on the biological relevance of the observed reduction in oocyst numbers“

More specific comments to address:

Line 101/Fig1E (and figure legend) - What is this heatmap showing. It would be helpful to have a sentence or two linking it to a specific methodology. I could not find details in the M+M section and "specialized, high molecular mass gels" does not adequately explain what experiments were performed. The reference to Supplementary Information 1 also did not provide information.

We added the information “high molecular mass gels with lower acrylamide percentage” to clarify methodology in the text. Furthermore, we extended the figure legend to include all relevant information. Further experimental details can be found in the study cited in this context, where the dataset originates from (Evers et al., 2021).

Line 115 and Supplementary Figure 2C + D - The main text says that the transgenic parasites contained a mitochondrially localized mScarlet for visualization and localization, but in the supplementary figure 2 it shows mitotracker labelling rather than mScarlet. This is very confusing. The figure legend also mentions both mScarlet and MitoTracker. I assume that mScarlet was used to view in regular IFAs (Fig S2C) and the MitoTracker was used for the expansion microscopy (Fig S2D)?

Please clarify.

We thank the reviewer for pointing this out – this was indeed incorrectly annotated. We used the endogenous mito-mScarlet signal in IFA and mitoTracker in U-ExM. The figure annotation has now been corrected.

Figure 2C - what is the statistical test being used (the methods say "Mean oocysts per midgut and statistical significance were calculated using a generalized linear mixed effect model with a random experiment effect under a negative binomial distribution." but what test is this?)?

The statistic test is now included in the material and method section with the sentence “The fitted model was used to obtain estimated means and contrasts and were evaluated using Wald Statistics”. The test is now also mentioned in the figure legend.

Also the choice of a log10 scale for oocyst intensity is an unusual choice - how are the mosquitoes with 0 oocysts being represented on this graph? It looks like they are being plotted at 10^-1 (which would be 0.1 oocysts in a mosquito which would be impossible).

As the data spans three orders of magnitude with low values being biologically meaningful, we decided that a log scale would best facilitate readability of the graph. As the 0 values are also important to show, we went with a standard approach to handle 0s in log transformed data and substituted the 0s with a small value (0.001). We apologize for not mentioning this transformation in the manuscript. To make this transformation transparent, we added a break at the lower end of the log-scaled y-axis and relabelled the lowest tick as ‘0’. This ensures that mosquitoes with zero oocysts are shown along the x-axis without being assigned an artificial value on the log scale. We would furthermore like to highlight that for statistics we used the true value 0 and not 0.001.

Figure 2D - it is great that the data from all feeding replicates has been shared, however it is difficult to conclude any meaningful impact in transmission with the knock-out lines when there is so much variation and so few mosquitoes dissected for some datapoints (10 mosquitoes are very small sample sizes). For example, Exp1 shows a clear decrease in mic19- transmission, but then Exp2 does not really show as great effect. Similarly, why does the double knock out have better transmission than the single knockouts? Sure there would be a greater effect?

We agree with the reviewer and with the new sentence added, as per major point, we hope we clarified the concept. Note that original Figure 2D has been moved to the supplementary information, as per minor comment of another reviewer.

Figure 3 legend - Please add which statistical test was used and the number of replicates.

Done

Figure 4 legend - Please add which statistical test was used and the number of replicates.

Done. Regarding replicates, note that while we measured over 100 cristae from over 30 mitochondria, these all stem from the same parasite culture.

Figure 5C - the 3D reconstructions are very nice, but what does the red and yellow coloring show?

Indeed, the information was missing. We added it to the figure legend.

Line 352 - "Still, it is striking that, despite the pronounced morphological phenotype, and the possibly high mitochondrial stress levels, the parasites appeared mostly unaffected in life cycle propagation, raising questions about the functional relevance of mitochondria at these stages."

How do the authors reconcile this statement with the proven fact that mitochondria-targeted antimalarials (such as atovaquone) are very potent inhibitors of parasite mosquito transmission?

Our original sentence was reductive. What we wanted to state was related to the functional relevance of crista architecture and overall mitochondrial morphology rather than the general functional relevance of the mitochondria. We changed the sentence accordingly.

Furthermore, even though we do not discuss this in the article, we are aware of mitochondria targeting drugs that are known to block mosquito transmission. We want to point out that it is difficult to discern the disruption of ETC and therefore an impact on energy conversion with the impact on the essential pathway of pyrimidine synthesis, highly relevant in microgamete formation. Still, a recent paper from Sparkes et al. 2024 showed the essentiality of mitochondrial ATP synthesis during gametogenesis so it is very likely that the mitochondrial energy conversion is highly relevant for transmission to the mosquito.

Reviewer #1 (Significance):

This manuscript is a novel approach to studying mitochondrial biology and does open a lot of unanswered questions for further research directions. Currently there are limitations in the use of statistical tests and detail of methodology, but these could be easily be addressed with a bit more analysis/better explanation in the text.

This manuscript could be of interest to readers with a general interest in mitochondrial cell biology and those within the specific field of Plasmodium research.

My expertise is in Plasmodium cell biology.

We thank the reviewer for the praise.

Reviewer #2 (Evidence, reproducibility and clarity):

Major comments:

(1) In my opinion, the authors tend to sensationalize or overinterpret their results. The title of the manuscript is very misleading. While MICOS is certainly important for crista formation, it is not the only factor, as ATP synthase dimer rows make a highly significant contribution to crista morphology. Thus, one can argue with equal validity that ATP synthase should be considered the 'architect', as it's the conformation of the dimers and rows modulate positive curvature. Secondly, while cristae are still formed upon mic60/mic19 gene knockout (KO), they are severely deformed, and likely dysfunctional (see below). Thus, I do not agree with the title that MICOS is dispensable for crista formation, because the authors results show that it clearly is essential. So, the title should be changed.

We thank the reviewer for taking the time to review our manuscript.

Based on the reviewers’ interpretation we conclude the title does not come across as intended. We have changed the title to: “The role of MICOS in organizing mitochondrial cristae in malaria parasites”

The Discussion section starting from line 373 also suffers from overinterpretation as well as being repetitive and hard to understand. The authors infer that MICOS stability is compromised less in the single KOs (sKO) in compared to the mic60/mic19 double KO (dKO). MICOS stability was never directly addressed here and the composition of the MICOS complex is unaddressed, so it does not make sense to speculate by such tenuous connections. The data suggest to me that mic60 and mic19 are equally important for crista formation and crista junction (CJ) stabilization, and the dKO has a more severe phenotype than either KO, further demonstrating neither is epistatic.

We do agree with the reviewer’s notion that we did not address complex stability, and our wording did not make this sufficiently clear. We shortened and rephrased the paragraph in question.

The following paragraphs (line 387 to 422) continues with such unnecessary overinterpretation to the point that it is confusing and contradictory. Line 387 mentions an 'almost complete loss of CJs' and then line 411 mentions an increase in CJ diameter, both upon Mic60 ablation. I do not think this discussion brings any added value to the manuscript and should be shortened. Yes, maybe there are other putative MICOS subunits that may linger in the KOS that are further destabilized in the dKO, or maybe Mic60 remains in the mic19 KO (and vice versa) to somehow salvage more CJs, which is not possible in the dKO. It is impossible to say with confidence how ATP synthase behaves in the KOs with the current data.

We shortened this paragraph.

(2) While the authors went through impressive lengths to detect any effect on lifecycle progression, none was found except for a reduction in oocyte count. However, the authors did not address any direct effect on mitochondria, such as OXPHOS complex assembly, respiration, membrane potential. This seems like a missed opportunity, given the team's previous and very nice work mapping these complexes by complexome profiling. However, I think there are some experiments the authors can still do to address any mitochondrial defects using what they have and not resorting to complexome profiling (although this would be definitive if it is feasible):

i) Quantification of MitoTracker Red staining in WT and KOs. The authors used this dye to visualize mitochondria to assay their gross morphology, but unfortunately not to assay membrane potential in the mutants. The authors can compare relative intensities of the different mitochondria types they categorized in Fig. 3A in 20-30 cells to determine if membrane potential is affected when the cristae are deformed in the mutants. One would predict they are affected.

Interesting suggestion. As our staining and imaging conditions are suitable for such analysis (as demonstrated by Sarazin et al., 2025, https://www.biorxiv.org/content/10.1101/2025.11.27.690934v1), we performed the measurements on the same dataset which we collected for Figure 3. We did, however, not detect any difference in mitotracker intensity between the different lines. The result of this analysis is included in the new version of Supplementary figure S6.

ii) Sporozoites are shown in Fig S5. The authors can use the same set up to track their motion, with the hypothesis that they will be slower in the mutants compared to WT due to less ATP. This assumes that sporozoite mitochondria are active as in gametocytes.

While theoretically plausible and informative, we currently do not know the relevance of mitochondrial energy conversion for general sporozoite biology or specifically features of sporozoite movement. Given the required resources and time to set this experiment up and the uncertainty whether it is a relevant proxy for mitochondrial functioning, we argue it is out of scope for this manuscript.

iii) Shotgun proteomics to compare protein levels in mutants compared to WT, with the hypothesis that OXPHOS complex subunits will be destabilized in the mutants with deformed cristae. This could be indirect evidence that OXPHOS assembly is affected, resulting in destabilized subunits that fail to incorporate into their respective complexes.

While this experiment could potentially further our understanding of the interaction between MICOS and levels of OXPHOS complex subunits we argue that the indirect nature of the evidence does not justify the required investments.

To expedite resubmission, the authors can restrict the cell lines to WT and the dKO, as the latter has a stronger phenotype that the individual KOs and conclusions from this cell line are valid for overall conclusions about Plasmodium MICOS.

I will also conclude that complexome/shotgun proteomics may be a useful tool also for identifying other putative MICOS subunits by determining if proteins sharing the same complexome profile as PfMic60 and Mic19 are affected. This would address the overinterpretation problem of point 1.

(3) I am aware of the authors previous work in which they were not able to detect cristae in ABS, and thus have concluded that these are truly acristate. This can very well be true, or there can be immature cristae forms that evaded detection at the resolution they used in their volumetric EM acquisitions. The mitochondria and gametocyte cristae are pretty small anyway, so it not unreasonable to assume that putative rudimentary cristae in ABS may be even smaller still. Minute levels of sampled complex III and IV plus complex V dimers in ABS that were detected previously by the authors by complexome profiling would argue for the presence of miniscule and/or very few cristae.

I think that authors should hedge their claim that ABS is acristate by briefly stating that there still is a possibility that miniscule cristae may have been overlooked previously.

We acknowledge that we cannot demonstrate the absolute absence of any membrane irregularities along the inner mitochondrial membrane. At the same time, if such structures were present, they would be extremely small and unlikely to contain the full set of proteins characteristic of mature cristae. For this reason, we consider it appropriate to classify ABS mitochondria as acristate. To reflect the reviewer’s point while maintaining clarity for readers, we have slightly adjusted our wording in the manuscript, changing ‘fully acristate’ to ‘acristate’.

This brings me to the claim that Mic19 and Mic60 proteins are not expressed in ABS. This is based on the lack of signal from the epitope tag; a weak signal is detected in gametocytes. Thus, one can counter that Mic19 and Mic60 are also expressed, but below the expression limits of the assay, as the protein exhibits low expression levels when mitochondrial activity is upregulated.

We agree with the reviewer that the absence of a detectable epitope-tag signal does not definitively exclude low-level expression, and we have therefore replaced the term ‘absent’ with ‘undetectable’ throughout the manuscript. In context with previous findings of low-level transcripts of the proteins in a study by Lopez-Berragan et al. and Otto et al., we also added the sentence “The apparent absence could indicate that transcripts are not translated in ABS or that the proteins’ expression was below detection limits of western blot analysis.” to the discussion. At the same time, we would like to clarify that transcript levels for both genes fall within the <25th percentile, suggesting that these low values likely represent background signal rather than biologically meaningful expression. This interpretation is further supported by proteomic datasets in PlasmoDB, which report PfMIC19 and PfMIC60 expression in gametocyte and mosquito stages, but not in asexual blood stages.”

To address this point, the authors should determine of mature mic60 and mic19 mRNAs are detected in ABS in comparison to the dKO, which will lack either transcript. RT-qPCR using polyT primers can be employed to detect these transcripts. If the level of these mRNAs are equivalent to dKO in WT ABS, the authors can make a pretty strong case for the absence of cristae in ABS.

We appreciate the reviewer’s suggestion. As noted in the Discussion, existing transcriptomic datasets already show detectable MIC19 and MIC60 mRNAs in ABS. For this reason, we expect RT-qPCR to reveal low (but not absent) levels of both transcripts, unlike the true loss expected to be observed in the dKO. Because such residual signals have been reported previously and their biological relevance remains uncertain, we do not believe transcript levels alone can serve as a definitive indicator of cristae absence in ABS.

They should highlight the twin CX9C motifs that are a hallmark of Mic19 and other proteins that undergo oxidative folding via the MIA pathway. Interestingly, the Mia40 oxidoreductase that is central to MIA in yeast and animals, is absent in apicomplexans (DOI: 10.1080/19420889.2015.1094593).

Searching for the CX9C motifs is a valuable suggestion. In response to the reviewer´s suggestion we analysed the conservation of the motif in PfMIC19 and included this in a new figure panel (Figure 1 F).

Did the authors try to align Plasmodium Mic19 orthologs with conventional Mic19s? This may reveal some conserved residues within and outside of the CHCH domain.

In response to this comment we made Figure 1 F, where we show conserved residues within the CHCH domains of a broad range of MIC19 annotated sequences across the opisthokonts, and show that the Cx9C motifs are conserved also in PfMIC19. Outside the CHCH domain, we did not find any meaningful conservation, as PfMIC19 heavily diverges from opisthokont MIC19.

(5) Statistical significance. Sometimes my eyes see population differences that are considered insignificant by the statistical methods employed by the authors, eg Fig. 4E, mutants compared to WT, especially the dKO. Have the authors considered using other methods such as student t-test for pairwise comparisons?

The graphs in figures 3, 4 and 5 got a makeover, such that they now are in linear scale and violin plots (also following a suggestion from further down in the reviewer’s comments). We believe that this improves interpretability. ANOVA was kept as statistical testing to assure the correction for multiple comparisons that cannot be performed with standard t-test. A full overview of statistics and exact pvalues can also be found in the newly added supplementary information 2.

Minor comments:

Line 33. Anaerobes (eg Giardia) have mitochondria that do produce ATP, unlike aerobic mitochondria

We acknowledge that producing ATP via OXPHOS is not a characteristic of all mitochondria-like organelles (e.g. mitosomes), which is why these are typically classified separately from canonical mitochondria. When not considering mitochondria-like organelles, energy conversion is the function that the mitochondrion is most well-known for and the one associated with cristae.

Line 56: Unclear what authors mean by "canonical model of mitochondria"

To clarify we changed this to “yeast or human” model of mitochondria.

Lines 75-76: This applies to Mic10 only

We removed the “high degree of conservation in other cristate eukaryotes” statement.

Line 80: Cite DOI: 10.1016/j.cub.2020.02.053

Done

Fig 2D: I find this table difficult to read. If authors keep table format, at least get rid of 'mean' column' as this data is better depicted in 2C. I suggest depicted this data either like in 3B depicting portion of infected vs unaffected flies in all experiments, then move modified Table to supplement. Important to point out experiment 5 appears to be an outlier with reduced infectivity across all cell lines, including WT.

To clarify: the mean reported in the table indicates the mean per replicate while the mean reported in figure 2C is the overall mean for a given genotype that corrects for variability within experiments. We agree that moving the table to the supplementary data is a good idea. We decided to not include a graph for infected and non-infected mosquitoes as this information would be partially misleading, highlighting a phenotype we argue to be influenced by the strong variability.

Fig. 3C-G: I feel like these data repeatedly lead to same conclusions. These are all different ways of showing what is depicted in Fig 2B: mitochondria gross morphology is affected upon ablation of MICOS. I suggest that these graphs be moved to supplement and replaced by the beautiful images.

Thank you for the nice comment on our images. We have now moved part of the graphs to supplementary figure 6 and only kept the Relative Frequency, Sphericity and total mitochondria volume per cell in the main figure.

Line 180: Be more specific with which tubulin isoform is used as a male marker and state why this marker was used in supplemental Fig S6.

We have now specified the exact tubulin isoform used as the male gametocyte marker, both in the main text and in Supplementary Fig. S6. This is a commercial antibody previously known to work as an effective male marker, which is why we selected it for this experiment. This is now clearly stated in the manuscript.

Line 196 and Fig 3C: the word 'intensities' in this context is very ambiguous. Please choose a different term (puncta, elements, parts?). This is related to major point 2i above.

To clarify the biological effect that we can conclude form the measurement, we added an explanation about it in the respective section of the results, and we decided to replace the raw results of the plug-in readout with the deduced relative dispersion.

Line 222: Report male/female crista measurements

We added Supplementary information 2, which contains exact statistical test and outcomes on all presented quantifications as well as a per-sex statistical analysis of the data from figure 4. Correspondingly, we extended supplementary information 2 by a per-sex colour code for the thin section TEM data.

Fig. 4B-E: depict data as violin plots or scatter plots like Fig. 2C to get a better grasp of how the crista coverage is distributed. It seems like the data spread is wider in the double KO. This would also solve the problem with the standard deviation extending beyond 0%.

We changed this accordingly.

Lines 331-333: Please clarify that this applies for some, but not all MICOS subunits. Please also see major point 1 above. Also, the authors should point out that despite their structural divergence, trypanosomal cryptic mitofilins Mic34 and Mic40 are essential for parasite growth, in contrast to their findings with PfMic60 (DOI: https://doi.org/10.1101/2025.01.31.635831).

This has been changed accordingly.

Line 320: incorrect citation. Related to point 1above.

Correct citation is now included in the text.

Lines 333-335. This is related to the above. Again, some subunits appear to affect cell growth under lab conditions, and some do not. This and the previous sentence should be rewritten to reflect this.

This has been changed accordingly.

Line 343-345: The sentence and citation 45 are strange. Regarding the former, it is about CHCHD10, whose status as a bona fide MICOS subunit is very tenuous, so I would omit this. About the phenomenon observed, I think it makes more sense to write that Mic60 ablation results in partially fragmented mitochondria in yeast (Rabl et al., 2009 J Cell Biol. 185: 1047-63). A fragmented mitochondria is often a physiological response to stress. I would just rewrite as not to imply that mitochondrial fission (or fusion) is impaired in these KOs, or at least this could be one of several possibilities.

The sentence has been substituted following the indication of the reviewer. Though we still include the data of the human cells as this has also been shown in Stephens et al. 2020.

Line 373: 'This indicates' is too strong. I would say 'may suggest' as you have no proof that any of the KOs disrupts MICOS. This hypothesis can be tested by other means, but not by penetrance of a phenotype.

Done

Line 376-377; 'deplete functionality' does not make sense, especially in the context of talking about MICOS subunit stability. In my opinion, this paragraph overinterprets the KO effects on MICOS stability. None of the experiments address this phenomenon, and thus the authors should not try to interpret their results in this context. See major point 1.

We removed the sentence. Also, the entire paragraph has been shortened, restructured and wording was changed to address major point 1.

Other suggestions for added value

(1) Does Plasmodium Sam50 co-fractionate with Mic60 and Mic19 in BN PAGE (Fig. 1E)

While we did identify SAMM50 in our BN PAGE, the protein does not co-migrate with the MICOS components but instead comigrates with other components of a putative sorting and assembly machinery (SAM) complex. As SAMM50, the SAM complex and the overarching putative mitochondrial membrane space bridging (MIB) complex are not mentioned in the manuscript, we decided to not include the information in Author response image 1.

Author response image 1.

Reviewer #2 (Significance):

The manuscript by Tassan-Lugrezin is predicated on the idea that Plasmodium represents the only system in which de novo crista formation can be studied. They leverage this system to ask the question whether MICOS is essential for this process. They conclude based on their data that the answer is no, which the authors consider unprecedented. But even if their claim is true that ABS is acristate, this supposed advantage does not really bring any meaningful insight into how MICOS works in Plasmodium.

First the positives of this manuscript. As has been the case with this research team, the manuscript is very sophisticated in the experimental approaches that are made. The highlights are the beautiful and often conclusive microscopy performed by the authors. Only the localization of Mic60 and Mic19 was inconclusive due to their very low expression unfortunately.

The examination of the MICOS mutants during in vitro life cycle of Plasmodium falciparum is extremely impressive and yields convincing results. Mitochondrial deformation is tolerated by life cycle stage differentiation, with a modest but significant reduction of oocyte production, being observed.

However, despite the herculean efforts of the authors, the manuscript as it currently stands represents only a minor advance in our understanding of the evolution of MICOS, which from the title and focus of the manuscript, is the main goal of the authors.

In its current form, the manuscript reports some potentially important findings:

(1) Mic60 is verified to play a role in crista formation, as is predicted by its orthology to other characterized Mic60 orthologs.

(2) The discovery of a novel Mic19 analog (since the authors maintain there is no significant sequence homology), which exhibits a similar (or the same?) complexome profile with Mic60. This protein was upregulated in gametocytes like Mic60 and phenocopies Mic60 KO.

(3) Both of these MICOS subunits are essential (not dispensable) for proper crista formation

(4) Surprisingly, neither MICOS subunit is essential for in vitro growth or differentiation from ABS to sexual stages, and from the latter to sporozoites. This says more about the biology of plasmodium itself than anything about the essentiality of Mic60, i.e. plasmodium life cycle progression tolerates defects to mitochondrial morphology. But yes, I agree with the authors that Mic60's apparent insignificance for cell growth in examined conditions does differ with its essentiality in other eukaryotes. But fitness costs were not assayed (e.g. by competition between mutants and WT in infection of mosquitoes)

(5) Decreased fitness of the mutants is implied by a reduction of oocyte formation.

While interesting in their own way, collectively they do not represent a major advance in our understanding of MICOS evolution. Furthermore, the findings bifurcate into categories informing MICOS or Plasmodium biology. Both aspects are somewhat underdeveloped in their current form.

This is unfortunate because there seem to be many missed opportunities in the manuscript that could, with additional experiments, lead to a manuscript with much wider impact. For me, what is remarkable about Plasmodium MICOS that sets it apart from other iterations is the apparent absence of the Mic10 subunit. Purification of plasmodium MICOS via the epitope tagged Mic60 and Mic19 could have verified that MICOS is assembled without this core subunit. Perhaps Mic60 and Mic19 are the vestiges of the complex, and thus operate alone in shaping cristae. Such a reduction may also suggest the declining importance of mitochondria in plasmodium.

Another missed opportunity was to assay the impact of MICOS-depletion of OXPHOS in plasmodium.

This is a salient issue as maybe crista morphology is decoupled from OXPHOS capacity in Plasmodium, which links to the apparent tolerance of mitochondrial morphology in cell growth and differentiation. I suggested in section A experiments to address this deficit.

Finally, the authors could assay fitness costs of MICOS-ablation and associated phenotypes by assaying whether mosquito infectivity is reduced in the mutants when they are directly competing with WT plasmodium. Like the authors, I am also surprised that MICOS mutants can pass population bottlenecks represented by differentiation events. Perhaps the apparent robustness of differentiation may contribute plasmodium's remarkable ability to adapt.

I realize that the authors put a lot of efforts into their study and again, I am very impressed by the sophistication of the methods employed. Nevertheless, I think there is still better ways to increase the impact of the study aside from overinterpreting the conclusions from the data. But this would require more experiments along the lines I suggest in Section A and here.

We thank the reviewer for their extensive analysis of the significance of our findings, including the compliments on our microscopy images and the sophisticated experimental approaches. We hope we have convincingly argued why we could or could not include some of the additional analyses suggested by the reviewer in section 1 above.

With regard to the significance statement, we want to point out that our finding that PfMICOS is not needed for initial formation of cristae (as opposed to organization thereof), is a confirmation of something that has been assumed by the field, without being the actual focus of studies. We argue that the distinction between formation and organization of cristae is important and deserves some attention within the manuscript. The result of MICOS not being involved in the initial formation of cristae, we argue to be relevant in Plasmodium biology and beyond. As for the insights into how MICOS works in Plasmodium we have confirmed that the previously annotated PfMIC60 is indeed involved in the organization of cristae. Furthermore, we have identified and characterized PfMIC19. These findings, we argue, are indeed meaningful insights into PfMICOS.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

MICOS is a conserved mitochondrial protein complex responsible for organising the mitochondrial inner membrane and the maintenance of cristae junctions. This study sheds first light on the role of two MICOS subunits (Mic60 and the newly annotated Mic19) in the malaria parasite Plasmodium falciparum, which forms cristae de novo during sexual development, as demonstrated by EM of thin section and electron tomography. By generating knockout lines (including a double knockout), the authors demonstrate that knockout of both MICOS subunits leads to defects in cristae morphology and a partial loss of cristae junctions. With a formidable set of parasitological assays, the authors show that despite the metabolically important role of mitochondria for gametocytes, the knockout lines can progress through the life stages and form sporozoites, albeit with diminished infection efficiency.

We thank the reviewer for their time and compliment.

Major comments:

(1) The authors should improve to present their findings in the right context, in particular by:

i) giving a clearer description in the introduction of what is already known about the role of MICOS. This starts in the introduction, where one main finding is missing: loss of MICOS leads to loss of cristae junctions and the detachment of cristae membranes, which are nevertheless formed, but become membrane vesicles. This needs to be clearly stated in the introduction to allow the reader to understand the consistency of the authors' findings in P. falciparum with previous reports in the literature.

We extended the introduction to include this information.

iii) at the end to the introduction, the motivating hypothesis is formulated ad hoc "conclusive evidence about its involvement in the initial formation of cristae is still lacking" (line 83). If there is evidence in the literature that MICOS is strictly required for cristae formation in any organism, then this should be explained, because the bona fide role of MICOS is maintenance of cristae junctions (the hypothesis is still plausible and its testing important).

To clarify we rephrased the sentence to: “Although MICOS has been described as an organizer of crista junctions, its role during the initial formation of nascent cristae has not been investigated.”

(2) Line 96-97: "Interestingly, PfMIC60 is much larger than the human MICOS counterpart, with a large, poorly predicted N-terminal extension." This statement is lacking a reference and presumably refers to annotated ORFs. The authors should clarify if the true N-terminus is definitely known - a 120kDa size is shown for the P. falciparum but this is not compared to the expected length or the size in S. cerevisiae.

To solve the reference issue, we added the uniprot IDs we compared to see that the annotated ORF is bigger in Plasmodium. We also changed the comparison to yeast instead of human, because we realized it is confusing to compare to yeast all throughout the figure, but then talk about human in this specific sentence.

Regarding whether the true N-terminus is known. Short answer: No, not exactly.

However, we do know that the Pf version is about double the size of the yeast protein.

As the reviewer correctly states, we show the size of 120kDa for the tagged protein in Figure 1G. Considering that we tagged the protein C-terminally, and observed a 120kDa product on western blot, it is safe to conclude that the true N-terminus does not deviate massively from the annotated ORF, and hence, that there is a considerable extension of the protein beyond a 60kDa protein. We do not directly compare to yeast MIC60 on our western blots, however, that comparison can be drawn from literature: Tarasenko et al., 2017 showed that purified MIC60 running at ~60kDa on SDS-PAGE actively bends membranes, suggesting that in its active form, the monomer of yeast MIC60 is indeed 60kDa in size.

To clarify, we now emphasize that we ran the Alphafold prediction on the annotated open reading frame (annotated and sequenced by Bohme et al. and Chapell et al. now cited in the manuscript), and revised the wording to make clear what we are comparing in which sentence.

(3) lines 244-245: "Furthermore, our data indicates the effect size increases with simultaneous ablation of both proteins?". The authors should explain which data they are referring to, as some of the data in Fig 3 and 4 look similar and all significance tests relate to the wild type, not between the different mutants, so it is not clear if any overserved differences are significant. The authors repeat this claim in the discussion in lines 368-369 without referring to a specific significance test. This needs to be clarified.

As a reply to this and other comments from the reviewers we added the multiple testing within all samples. In addition, to clarify statistics used we included a supplementary dataset with all p-values and statistical tests used.

(4) lines 304-306: "Though well established as the cristae organizing system, the role of MICOS in initial formation of cristae remains hidden in model organisms that constitutively display cristae.". This sentence is misleading since even in organisms that display numerous cristae throughout their life cycle, new cristae are being formed as the cells proliferate. Thus, failure to produce cristae in MICOS knockout lines would have been observable but has apparently not been reported in the literature. Thus, the concerted process in P. falciparum makes it a great model organism, but not fundamentally different to what has been studied before in other organisms.

We deleted this statement.

(5) lines 373-378. "where ablation of just MIC60 is sufficient to deplete functionality of the entire MICOS (11, 15),". The authors' claim appears to be contrary to what is actually stated in ref 15, which they cite:

"MICOS subunits have non-redundant functions as the absence of both MICOS subcomplexes results in more severe morphological and respiratory growth defects than deletion of single MICOS subunits or subcomplexes."

This seems in line with what the authors show, rather than "different".

This sentence has been removed.

(6) lines 380-385: "... thus suggesting that membrane invaginations still arise, but are not properly arranged in these knockout lines. This suggests that MICOS either isn't fully depleted,...". These conclusions are incompatible with findings from ref. 15, which the authors cite. In that study, the authors generated a ∆MICOS line which still forms membrane invaginations, showing that MICOS is not required at all for this process in yeast. Hence the authors' implication that MICOS needs to be fully depleted before membrane invaginations cease to occur is not supported by the literature.

This sentence has been deleted in the revised version of the manuscript.

Minor comments:

(1) The authors should consider if the first part of their title could be seen as misleading: It suggests that MICOS is "the architect" in cristae formation, but this is not consistent with the literature nor their own findings.

Title is changed accordingly

- Line 43, of the three seminal papers describing the discovery of MICOS in 2011, the authors only cite two (refs 6 and 7), but miss the third paper, Hoppins et al, PMID: 21987634, which should probably be corrected.

Done, the paper is now cited

- Page 2, line 58: for a more complete picture the authors should also cite the work of others here which shows that although at very low levels, e.g. complex III (a drug target) and ATP synthase do assemble (Nina et al, 2011, JBC).

Done

- Page 3, line 80: "Irrespective of the shape of an organism's cristae, the crista junctions have been described as tubular channels that connect the cristae membrane to the inner boundary membrane (22, 24)." This omits the slit-shaped cristae junctions found in yeast (Davies et al, 2011, PNAS), which the authors should include.

The paper and concept have been added to the manuscript, though the sentence has been moved up in the introduction, when crista junctions are first introduced.

- Line 97: "poorly predicted N-terminal extension", as there is no experimental structure, we don't know if the prediction is poor. Presumably the authors mean either poorly ordered or the absence of secondary structure elements, or the poor confidence score for that region in the prediction? This should be clarified or corrected.

We were referring to the poor confidence score. To address this comment as well as major point 2, we rewrote the respective paragraph. It now clearly states that confidence of the prediction is low, and we mention the tool that was used to identify conserved domains (Topology-based Evolutionary Domains).

- Line 98: "an antiparallel array of ten β-sheets". They are actually two parallel beta-sheets stacked together. The authors could find out the name of this fold, but the confidence of the prediction is marked a low/very low. So, its existence is unknown, not just its "function".

We adapted the domain description to “a stack of two parallel beta-sheets" and replaced the statement on unknown function by the statement “Because this domain is predicted solely from computational analysis, both its actual existence in the native protein and its biological function remain unknown.”

- Fig 1B: The authors show two alphafold predictions of S. cerevisiae and P. falciparum Mic60 structures. There is however an experimental Mic60/19 (fragment) structure from the former organism (PMID: 36044574), which should be included if possible.

We appreciate the reviewer’s suggestion and note that the available structural data indeed provides valuable insight into how MIC60 and MIC19 interact. However, these structures represent fusion constructs of limited protein fragments and therefore capture only a small portion of each protein, specifically the interaction interface. Because our aim in Fig. 1B is to compare the overall domain architecture of the full-length proteins, we believe that including fragment-based structures would be less informative in this context.

- Line: 318-321: "The same trend was observed for PfMIC19 and PfMIC60. Although transcriptomic data suggested that low-level transcripts of PfMIC19 and PfMIC60 are present in ABS (38), we did not detect either of the proteins in ABS by western blot analysis. While this statement is true, the authors should comment on the sensitivity of the respective methods - how well was the antibody working in their hands and how do they interpret the absence of a WB band compared to transcriptomics data?

The HA antibody used in our experiments is a standard commercial reagent that performs reliably in both WB and IFA, although it shows a low background signal in gametocytes. We agree that the sensitivity of the method and the interpretation of weak or absent bands should be addressed explicitly. Transcript levels for both PfMIC19 and PfMIC60 in asexual blood stages fall within the <25 percentile, suggesting that these signals likely represent background. Nevertheless, we acknowledge that low-level protein expression below the detection limit of western blot analysis cannot be excluded. To reflect these considerations, we added the sentence: ‘The apparent absence could indicate that transcripts are not translated in ABS or that the proteins’ expression was below detection limits of western blot analysis.

- Lines 322-323: would the authors not typically have expected an IFA signal given the strength of the band in Western blot? If possible, the authors should comment if the negative fluorescence outcome can indeed be explained with the low abundance or if technical challenges are an equally good explanation.

Considering the nature of the investigated proteins (embedded in the IMM and spread throughout the mitochondria) difficulties in achieving a clear signal in IFA or U-ExM are not very surprizing. While epitopes may remain buried in IFA, U-ExM usually increases accessibility for the antibodies. However, U-ExM comes at the cost of being prone to dotty background signals, therefore potentially hiding low abundance, naturally dotty signals such as the signal of MICOS proteins that localize to distinct foci (at the CJ) along the mitochondrion. Current literature suggests that, in both human and yeast, STED is the preferred method for accurate spatial resolution of MICOS proteins (https://www.ncbi.nlm.nih.gov/pubmed/32567732,https://www.ncbi.nlm.nih.gov/pubmed/3206734 4). Unfortunately, we do not have experience with, nor access to, this particular technique/method.

- Lines 357-365: the authors describe limitations of the applied methods adequately. Perhaps it would be helpful to make a similar statement about the analysis of 3D objects like mitochondria and cristae from 2D sections. E.g. the apparent cristae length depends on whether cristae are straight (e.g. coiled structures do not display long cross sections despite their true length in 3D).

The limitations of other methods are described in the respective results section.

We added a clarifying sentence in the results section of Figure 4:

“Note that such measurements do not indicate the true total length or width of cristae, as the data is two-dimensional. The recorded values are to be considered indicative of possible trends, rather than absolute dimensions of cristae.“

This statement refers to the length/width measurements of cristae.

In the context of Figure 4D we mention the following (see preprint lines 229 – 230): “We expect this effect to translate into the third dimension and thus conclude that the mean crista volume increases with the loss of either PfMIC19, PfMIC60, or both.”

For Figure 5, we included a clarifying statement in the results section of the preprint (lines 269 – 273): “Note that these mitochondrial volumes are not full mitochondria, but large segments thereof. As a result of the incompleteness of the mitochondria within the section, and the tomography specific artefact of the missing wedge, we were unable to confirm whether cristae were in fact fully detached from the boundary membrane, or just too long to fit within the observable z-range.”

- Line 404: perhaps undetected or similar would be a better description than "hidden"?

The sentence does not exist in the revised manuscript.

Reviewer #3 (Significance):

The main strength of the study is that it provides the first characterisation of the MICOS complex in P. falciparum, a human parasite in which the mitochondrion has been shown to be a drug target. Mic60 and the newly annotated Mic19 are confirmed to be essential for proper cristae formation and morphology, as well as overall mitochondrial morphology. Furthermore, the mutant lines are characterised for their ability to complete the parasite life cycle and defects in infection effectivity are observed. This work is an important first step for deciphering the role of MICOS in the malaria parasite and the composition and function of this complex in this organism. The limitation of the study stems from what is already known about MICOS and its subunits in great detail in yeast and humans with similar findings regarding loss of cristae and cristae defects. The findings of this study do not provide dramatic new insight on MICOS function or go substantially beyond the vast existing literature in terms of the extent of the study, which focuses on parasitological assays and morphological analysis. Exploring the role of MICOS in an early-divergent organism and human parasite is however important given the divergence found in mitochondrial biology and P. falciparum is a uniquely suited model system. One aspect that would increase the impact of the paper would be if the authors could mechanistically link the observed morphological defects to the decreased infection efficiency, e.g. by probing effects on mitochondrial function. This will likely be challenging as the morphological defects are diverse and the fitness defects appear moderate/mild.

As suggested by Reviewer 2, we examined mitochondrial membrane potential in gametocytes using MitoTracker staining and did not observe any obvious differences associated with the morphological defects. At present, additional assays to probe mitochondrial function in P. falciparum gametocytes are not sufficiently established, and developing and validating such methods would require substantial work before they could be applied to our mutant lines. For these reasons, a more detailed mechanistic link between the observed morphological changes and the reduced infection efficiency is currently beyond reach.

The advance presented in this study is to pioneer the study of MICOS in P. falciparum, thus widening our understanding of the role of this complex to different model organism. This study will likely be mainly of interest for specialised audiences such as basic research parasitologists and mitochondrial biologists. My own field of expertise is mitochondrial biology and structural biology.

Nope. You could just use the traditional approach where most tokenizers only have a generic tag/discriminant for all number tokens. The every-non-text-token-is-one-character constraint is arbitrary and unnecessary.

(Perceivable Principle) I noticed this big promotional banner right away, but it made me wonder how it translates for someone using a screen reader. According to the Perceivable principle, the image next to this text needs a concise <alt> tag of 125 characters or less so visually impaired users don't miss out on the information. If it is just named something random like "IMG_098.jpg" in the code, the site is failing to make this content truly presentable to everyone.

IPFS Desktop release v0.49.0

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Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

This study investigates the roles of Rab32 and Rab38 in hepatic lipid droplet metabolism. The authors propose that Rab32/38-positive lysosome-related organelles (LROs) mediate lipid droplet degradation through a mechanism independent of conventional macroautophagy. While the study addresses an interesting question, several conceptual and technical issues need to be addressed before the conclusions can be fully supported.

Major Concerns

1.The authors primarily define the Rab32/38-positive ring-like structures as "lysosome-related organelles (LROs)" based on their morphological characteristics and co-localization with LAMP1. However, this classification lacks biochemical validation. Would it be more appropriate to include a Lyso-IP assay to provide additional supporting evidence? 2.In hepatocytes, what is the operational definition of LROs? Beyond being "larger in size," how are these structures functionally distinguished from conventional lysosomes? If Rab32/38 defines LRO identity, why does GFP-Rab32/38 not co-localize with all LAMP1-positive structures (Figure S1A)? 3.In Figure 2A, the dextran pulse-chase experiment shows fluid-phase uptake into large vacuoles; however, dextran can enter any endocytic compartment after prolonged chase periods. What evidence supports that these structures are bona fide LROs rather than enlarged late endosomes or lysosomes resulting from long-term culture? What determines why only certain lysosomes become Rab32/38-positive? This heterogeneity is not explained. Does it imply that pre-existing lysosomes convert into LROs, or that LROs are newly formed under high-density stress? The developmental trajectory of these structures has not been explored. 4.The authors propose a microautophagy mechanism based on the "invagination-like" structures observed by light microscopy (Figure 3A). However, the resolution of light microscopy is insufficient to distinguish true membrane invaginations from lipid droplets that are closely apposed to, or partially wrapped by, the outer membrane of LROs in three-dimensional space. Would a CLEM experiment be necessary to confirm that lipid droplets are indeed located within the lumen of LROs, rather than in deep invaginations that remain connected to the cytosol? In addition, multilamellar membrane structures were observed after Bafilomycin A1 treatment (Figure 3A). Have these structures been validated by electron microscopy, or could they simply represent complex membrane infoldings within swollen lysosomes? The conclusions drawn from light microscopy alone appear somewhat insufficient. 5.The authors use ATG4B C74A overexpression to claim macroautophagy independence. However, while this mutant blocks LC3 lipidation, the study still lacks genetic evidence, such as ATG knockouts. In Figure S2B, the authors state that the "majority" of Rab38-positive LRO-associated lipid droplets are LC3-negative, but no quantitative data are provided. 6.The manuscript does not clearly distinguish the functions of Rab32 and Rab38. Although the authors describe these proteins as paralogs with overlapping roles, multiple data points indicate that they have differential effects on lipid droplet (LD) metabolism. Notably, Rab38-but not Rab32-significantly affects LD delivery to acidic compartments, exerts a stronger influence on LRO size, and responds more robustly to VPS4B perturbation. These observations suggest that Rab32 and Rab38 regulate distinct steps of LD metabolism rather than functioning redundantly. However, the manuscript does not clearly highlight these functional differences and lacks mechanistic validation. 7.Figure 5A shows that the PI3P probe (2×FYVE) forms ring-like structures inside or near the LRO membrane. However, LROs themselves are Rab5-negative (Figures 1C-E), and PI3P is typically generated by Vps34 on early endosomes. Where do these PI3P signals originate? Are they transported from other organelles, or is there a local PI3P-generating mechanism on the LRO membrane? If the latter, which kinase is responsible, and is Vps34 recruited to the LRO membrane? This issue is not discussed. If PI3P is indeed locally generated on LROs, it could represent a key feature distinguishing LROs from classical lysosomes.

Minor Concerns

1.The double-knockout mice exhibit obesity and fatty liver; however, Rab32 and Rab38 are expressed in multiple tissues. A whole-body knockout model cannot distinguish whether these effects are hepatocyte-autonomous or arise from contributions by adipose tissue or macrophages, emphasizing the need for liver-specific knockout animals or cell models. Serum TAG levels were unchanged, and the authors speculate that VLDL secretion may be impaired, but this was not directly tested. Furthermore, the authors do not address the observed sex-specific effects, which appear to be male-specific. 2.The concentration of Orlistat used is relatively high (50-200 μM) and may cause non-specific effects. Have dose-response experiments been performed, or have other LAL inhibitors (e.g., Lalistat) been tested? 3.LysoTracker reflects acidity rather than lysosome identity, and reduced acidification in DKD cells may affect co-localization analysis.

Significance

Assessment of Significance Overall Assessment

Strengths:

Conceptual novelty: Introduces lysosome-related organelles (LROs) into hepatic lipid metabolism, expanding the functional repertoire of Rab32/38 beyond pigment cells and macrophages.

Mechanistic exploration: Links LD uptake to PI3P/PI(3,5)P2 signaling and VPS4B, providing molecular handles for future studies.

In vivo validation: DKO mice show age-dependent obesity and HFD sensitivity, establishing physiological relevance.

Weaknesses:

Rab32 vs. Rab38 functions remain blurred: Data suggest differential roles (Rab38 in LD delivery, Rab32 in LD size regulation), but authors default to "redundancy" narrative.

Microautophagy evidence incomplete: Relies on light microscopy; EM/CLEM needed to confirm true internalization.

Model relevance unclear: High-confluence AML12 vacuoles lack clear physiological correlate in healthy liver.

Audience

Primary:

Lysosome biologists

Autophagy researchers

Lipid metabolism researchers

Secondary:

Cell biologists

Metabolic disease researchers

Geneticists

这个7250亿美元的AI投资规模数据表明AI领域正在经历前所未有的资本投入。这一数字相当于许多中等规模国家的GDP，反映了市场对AI技术的极高期望。然而，文章质疑这种巨额投资是否能获得相应回报，暗示可能存在AI泡沫风险。

reply to https://www.facebook.com/groups/TypewriterCollectors/posts/10161712887224678/

to Steve Clancy Zach Hubbird Jean Brunet

I'm curious what the sourcing is on your differentiation of the two models? Are there manuals, advertising, or other details to back up the differences? From what I can see, the phrase "Rhythm Touch" seems to have been an advertising tag for the Underwood SS which started a few months after production of the SS began and there wasn't any difference in them other than the advertising tag.

Robert Messenger has some scant history on the machine and the differences, primarily due to a redesign at the time, at https://oztypewriter.blogspot.com/2012/11/on-this-day-in-typewriter-history_25.html. The primary change from the S to the SS seems to have been a move from a carriage shift to a basket shift and so it seems somewhat fitting that Underwood uses the phrase "Rhythm Touch" as an advertising gimmick much like Smith-Corona were doing with their "Floating Shift" marketing.

Generally standards at the time were not differentiated by different trim lines as standards had all the bells and whistles for office use (potentially aside from custom use cases like decimal tabulators or extra wide carriage). Meanwhile all the trim variations were generally seen in the portable market geared toward home use rather than office. This would seem to support the idea that there's only the SS and "Rhythm Touch" is only an advertising tag line as the SS was newly introduced in January of '46 and "Rhythm Touch" appears around July '46.

There's also some discussion on the TWdB in the commentary at https://typewriterdatabase.com/1950-underwood-ss.23202.typewriter which may add to the question.

I'm curious to hear everyone's thoughts on the idea/thesis that the only model is the Underwood SS which is being marketed as the "Rhythm Touch" or evidence to the contrary to refute the claim.

Is it just me or are there only two of them visible on the picture?

Differentiating between an Underwood SS and the Underwood Rhythm Touch:

comment to James Grooms at https://typewriterdatabase.com/show.23202.typewriter

James, perhaps it's hiding somewhere else in the comments on the database, but I'm curious if you've come across definitive differences between the Underwood SS and the Underwood Rhythm Touch models which have separate pages within the database:<br /> - SS https://typewriterdatabase.com/Underwood.SS.4.bmys - Rhythm Touch https://typewriterdatabase.com/Underwood.Rhythm+Touch.4.bmys

Most of my Google searches don't return anything definitive or with actual sourcing of any sort.

The main page has the SS starting in May 1946 and the Rhythm Touch beginning in July of that year, but doesn't seem to specify between the two in any substantive way. Neither of the two models seems to have had a name printed on it.

Your description here uses both designators, but knowing your penchant for newspaper and magazine advertisements, I would suspect you may have seen specific differentiators.

This Facebook post has some handwaving differentiators: https://www.facebook.com/groups/TypewriterCollectors/posts/10161712887224678/ but none seem definitive or sourced. It also uses the phrase carriage shift, though presumably with these models Underwood had moved to a segment/basket shift on their standards.

Other than the chrome side detailing moving from 3 strips to 5 as you've noted, one of the few differentiators I can see in this era is the shift from the shorter carriage return lever to the longer armed version around 1948 which Robert Messenger notes in https://oztypewriter.blogspot.com/2012/11/on-this-day-in-typewriter-history_25.html. However that same page also has an advertisement on it with the words Rhythm Touch featuring a short armed (older style) carriage return.

Is there really a difference between the SS and the Rhythm Touch or are they the same model with the phrase "Rhythm Touch" used as a marketing tag to compete potentially with Smith-Corona's "Floating Shift"?

Thanks!

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Zacharia and colleagues investigate the role of the C-terminus of IFT172 (IFT172c), a component of the IFT-B subcomplex. IFT172 is required for proper ciliary trafficking and mutations in its C-terminus are associated with skeletal ciliopathies. The authors begin by performing a pull-down to identify binding partners of His-tagged CrIFT172968-C in Chlamydomonas reinhardtii flagella. Interactions with three candidates (IFT140, IFT144, and a UBX-domain containing protein) are validated by AlphaFold Multimer with the IFT140 and IFT144 predictions in agreement with published cryo-ET structures of anterograde and retrograde IFT trains. They present a crystal structure of IFT172c and find that a part of the C-terminal domain of IFT172 resembles the fold of a non-canonical U-box domain. As U-box domains typically function to bind ubiquitin-loaded E2 enzymes, this discovery stimulates the authors to investigate the ubiquitin-binding and ubiquitination properties of IFT172c. Using in vitro ubiquitination assays with truncated IFT172c constructs, the authors demonstrate partial ubiquitination of IFT172c in the presence of the E2 enzyme UBCH5A. The authors also show a direct interaction of IFT172c with ubiquitin chains in vitro. Finally, the authors demonstrate that deletion of the U-box-like subdomain of IFT172 impairs ciliogenesis and TGFbeta signaling in RPE1 cells.

However, some of the conclusions of this paper are only partially supported by the data, and presented analyses are potentially governed by in vitro artifacts. In particular, the data supporting autoubiquitination and ubiquitin-binding are inconclusive. Without further evidence supporting a ubiquitin-binding role for the C-terminus, the title is potentially misleading.

Strengths:

(1) The pull-down with IFT172 C-terminus from C. reinhardtii cilia lysates is well performed and provides valuable insights into its potential roles.

(2) The crystal structure of the IFT172 C-terminus is of high quality.

(3) The presented AlphaFold-multimer predictions of IFT172c:IFT140 and IFT172c:IFT144 are convincing and agree with experimental cryo-ET data.

Weaknesses:

(1) The crystal structure of HsIFT172c reveals a single globular domain formed by the last three TPR repeats and C-terminal residues of IFT172. However, the authors subdivide this globular domain into TPR, linker, and U-box-like regions that they treat as separate entities throughout the manuscript. This is potentially misleading as the U-box surface that is proposed to bind ubiquitin or E2 is not surface accessible but instead interacts with the TPR motifs. They justify this approach by speculating that the presented IFT172c structure represents an autoinhibited state and that the U-box-like domain can become accessible following phosphorylation. However, additional evidence supporting the proposed autoinhibited state and the potential accessibility of the U-box surface following phosphorylation is needed, as it is not tested or supported by the current data.

We thank the reviewer for this comment. IFT172C contains TPR region and Ubox-like region, which are admittedly tightly bound to each other. While there is a possibility that this region functions and exists as one domain, below are the reasons why we chose to classify these regions as two different domains.

(1) TPR and Ubox-like regions are two different structural classes

(2) TPR region is linked to Ubox-like region via a long linker which seems poised to regulate the relative movement between these regions.

(3) Many ciliopathy mutations are mapped to the interface of TPR region and the Ubox region hinting at a regulatory mechanism governed by this interface.

That said, we agree that the proposed autoinhibited state and its potential relief by phosphorylation remains a hypothesis that requires experimental validation. We have revised the manuscript to present this more clearly as a speculative model rather than an established mechanism. We clearly acknowledge this limitation on pg. 16-17 of the revised discussion: ‘The IFT172 U-box domain appears to be in an auto-inhibited state in our crystal structure of HsIFT172C2 (Fig. 2E), potentially explaining the absence of a robust auto-ubiquitination activity in-vitro. This structural inhibition is reminiscent of the RING ubiquitin ligase CBL [59], where phosphorylation and substrate binding trigger a conformational change that activates ligase activity [59,75]. Intriguingly, the phosphosite database [76] lists four residues (T1533, S1549, T1689, Y1691) at the U-box/TPR interface as phosphorylation sites (Fig. S2D). Phosphorylation of these residues could potentially alleviate the auto-inhibited state, suggesting a possible regulatory mechanism. Furthermore, a 30-residue linker connects the U-box domain to the last TPR of IFT172, likely providing significant conformational flexibility (Fig. 2A-B). This flexibility may be functionally crucial for the U-box domain, allowing it to adopt different conformations as needed for its various roles. However, we note that the proposed autoinhibition model and its potential regulation by phosphorylation remain hypothetical and require future experimental validation.

(2) While in vitro ubiquitination of IFT172 has been demonstrated, in vivo evidence of this process is necessary to support its physiological relevance.

We thank the reviewer for this important point. We agree that in vivo evidence of IFT172 ubiquitination would strengthen the physiological relevance of our findings. While our current study focuses on the in vitro characterization of this activity, we have revised the manuscript to more clearly state that demonstration of IFT172 ubiquitination activity in cells, including identification of bona fide substrates, is required to establish its physiological significance (p. 16). We consider this an important direction for future studies.

(3) The authors describe IFT172 as being autoubiquitinated. However, the identified E2 enzymes UBCH5A and UBCH5B can both function in E3-independent ubiquitination (as pointed out by the authors) and mediate ubiquitin chain formation in an E3-independent manner in vitro (see ubiquitin chain ladder formation in Figure 3A). In addition, point mutation of known E3-binding sites in UBCH5A or TPR/U-box interface residues in IFT172 has no effect on the mono-ubiquitination of IFT172c1. Together, these data suggest that IFT172 is an E3-independent substrate of UBCH5A in vitro. The authors should state this possibility more clearly and avoid terminology such as "autoubiquitination" as it implies that IFT172 is an E3 ligase, which is misleading. Similarly, statements on page 10 and elsewhere are not supported by the data (e.g. "the low in vitro ubiquitination activity exhibited by IFT172" and "ubiquitin conjugation occurring on HsIFT172C1 in the presence of UBCH5A, possibly in coordination with the IFT172 U-box domain").

We now consider this possibility and tone down our statements about the autoubiquitination activity of IFT172 in both the abstract and results/discussion parts of the revised version of the manuscript. We no longer refer to IFT172 as having auto-ubiquitination activity in the manuscript.

(4) Related to the above point, the conclusion on page 11, that mono-ubiquitination of IFT172 is U-box-independent while polyubiquitination of IFT172 is U-box-dependent appears implausible. The authors should consider that UBCH5A is known to form free ubiquitin chains in vitro and structural rearrangements in F1715A/C1725R variants could render additional ubiquitination sites or the monoubiquitinated form of IFT172 inaccessible/unfavorable for further processing by UBCH5A.

We agree and the conclusion on pg. 11 has now been changed to: Therefore, while mutations in the IFT172 U-box domain affect the formation of higher molecular weight ubiquitin conjugates, the prominent mono-ubiquitination of IFT172 is likely attributable to the E3-independent activity of UbcH5a, as this event is not impacted by these U-box mutations, rather than indicating an intrinsic auto-ubiquitination capacity of IFT172 itself.

(5) Identification of the specific ubiquitination site(s) within IFT172 would be valuable as it would allow targeted mutation to determine whether the ubiquitination of IFT172 is physiologically relevant. Ubiquitination of the C1 but not the C2 or C3 constructs suggests that the ubiquitination site is located in TPRs ranging from residues 969-1470. Could this region of TPR repeats (lacking the IFT172C3 part) suffice as a substrate for UBCH5A in ubiquitination assays?

We thank the reviewer for raising this important point about ubiquitination site identification. While not included in our manuscript, we did perform mass spectrometry analysis of ubiquitination sites using wild-type IFT172 and several mutants (P1725A, C1727R, and F1715A). As shown in Author response image 1, we detected multiple ubiquitination sites across these constructs. The wild-type protein showed ubiquitination at positions K1022, K1237, K1271, and K1551, while the mutants displayed slightly different patterns of modification. However, we should note that the MS intensity signals for these ubiquitinated peptides were relatively low compared to unmodified peptides, making it difficult to draw strong conclusions about site specificity or physiological relevance.

Author response image 1.

Consistent with the reviewer's suggestion, all detected ubiquitination sites fall within the TPR-containing region (residues 1022-1551), which is present in the C1 construct but absent from C2 and C3, explaining the construct-dependent ubiquitination pattern. We did not test the TPR region alone as a UBCH5A substrate, but this would be an informative experiment for future studies.

(6) The discrepancy between the molecular weight shifts observed in anti-ubiquitin Western blots and Coomassie-stained gels is noteworthy. The authors show the appearance of a mono-ubiquitinated protein of ~108 kDa in anti-ubiquitin Western blots. However, this molecular weight shift is not observed for total IFT172 in the corresponding Coomassie-stained gels (Figures 3B, D, F). Surprisingly, this MW shift is visible in an anti-His Western blot of a ubiquitination assay (Fig 3C). Together, this raises the concern that only a small fraction of IFT172 is being modified with ubiquitin. Quantification of the percentage of ubiquitinated IFT172 in the in vitro experiments could provide helpful context.

We acknowledge that the ubiquitin conjugation of IFT172 in vitro is weak, as stated in the manuscript (p. 16). The discrepancy between anti-ubiquitin Western blots and Coomassie-stained gels is consistent with only a small fraction of IFT172 being modified, which is expected given that the reaction likely reflects E3-independent ubiquitination by UBCH5A rather than a robust enzymatic activity of IFT172 itself. The anti-His Western blot (Fig. 3C) is more sensitive than Coomassie staining, explaining why the shift is visible there but not on Coomassie. We have not performed formal quantification of the ubiquitinated fraction, but based on the Coomassie data, we estimate it to be a minor proportion of total IFT172, consistent with the toned-down conclusions in our revised manuscript. The identification of physiological substrates and in vivo validation will be important future directions to establish the biological relevance of these observations.

(7) The authors propose that IFT172 binds ubiquitin and demonstrate that GST-tagged HsIFT172C2 or HsIFT172C3 can pull down tetra-ubiquitin chains. However, ubiquitin is known to be "sticky" and to have a tendency for weak, nonspecific interactions with exposed hydrophobic surfaces. Given that only a small proportion of the ubiquitin chains bind in the pull-down, specific point mutations that identify the ubiquitin-binding site are required to convincingly show the ubiquitin binding of IFT172.

We appreciate the reviewer's point regarding the potential for non-specific ubiquitin interactions and the value of mutational analysis for confirming specificity. While further mutagenesis of the predicted ubiquitin-binding interface was not performed for this revision, we note that our data show comparable tetra-ubiquitin pull-down by both the larger HsIFT172C2 construct and, importantly, the isolated HsIFT172C3 U-box domain itself (Fig. 4D). This localization of binding to the smaller U-box domain, coupled with our AlphaFold model predicting a specific interface with ubiquitin (Fig. 4E-F) and the observation that a mutation elsewhere (D1605R, Fig. 4C) does not abrogate this binding, collectively suggest a degree of specificity. We have revised the manuscript to more cautiously present these findings and acknowledge the need for future studies to definitively map the binding site. Specifically, we have now toned down the conclusion in the section on pg. 12-13 of the revised manuscript including a toned down heading: “IFT172 U-box domain pulls down ubiquitin in vitro”.

(8) The authors generated structure-guided mutations based on the predicted Ub-interface and on the TPR/U-box interface and used these for the ubiquitination assays in Fig 3. These same mutations could provide valuable insights into ubiquitin binding assays as they may disrupt or enhance ubiquitin binding (by relieving "autoinhibition"), respectively. Surprisingly, two of these sites are highlighted in the predicted ubiquitin-binding interface (F1715, I1688; Figure 4E) but not analyzed in the accompanying ubiquitin-binding assays in Figure 4.

We thank the reviewer for emphasizing the importance of mutational analysis to confirm the specificity of ubiquitin binding and for specifically inquiring about residues like F1715 and I1688 at the predicted ubiquitin interface. We tested purified HsIFT172C1 constructs containing the F1715A mutation (along with P1725A and C1727R variants) in pull-down assays with GST-Ubiquitin, see Author response image 2.

Author response image 2.

However, these experiments did not reveal a conclusive difference in ubiquitin binding for any of the tested variants compared to wild-type IFT172. The I1688A mutant, unfortunately, yielded insoluble protein and could not be evaluated. It is conceivable that the F1715A mutation was not disruptive enough to significantly alter binding, and future studies with different substitutions might be more informative. Nevertheless, our observations that the isolated HsIFT172C3 U-box domain itself pulls down tetra-ubiquitin (Fig. 4D), that our AlphaFold model predicts a specific interface (Fig. 4E-F), and that a mutation elsewhere (D1605R, Fig. 4C) does not abrogate this binding, collectively suggest a degree of specificity. We have revised the manuscript to present these ubiquitin binding findings cautiously, acknowledging the need for further investigation to definitively map the binding site and its functional relevance.

(9) If IFT172 is a ubiquitin-binding protein, it might be expected that the pull-down experiments in Figure S1 would identify ubiquitin, ubiquitinated proteins, or E2 enzymes. These were not observed, raising doubt that IFT172 is a ubiquitin-binding protein.

We acknowledge that the absence of ubiquitin or ubiquitinated proteins in our pull-down/MS experiment (Fig. S1) could raise questions about the ubiquitin-binding capacity of IFT172. However, several technical factors likely explain this. First, IFT172 appears to bind ubiquitin with low affinity, as indicated by our in vitro pull-downs and the AF-predicted interface. Second, we used extensive washes to remove non-specific interactors, which would also remove weak but potentially genuine ubiquitin interactions. Third, we did not include ubiquitination-preserving reagents such as NEM in our pull-down buffers, exposing ubiquitinated proteins to DUB-mediated deubiquitination during the experiment. These factors combined would strongly select against the detection of ubiquitin-related interactors under our experimental conditions.

(10) The cell-based experiments demonstrate that the U-box-like region is important for the stability of IFT172 but does not demonstrate that the effect on the TGFb pathway is due to the loss of ubiquitin-binding or ubiquitination activity of IFT172.

We acknowledge that our current data cannot definitively distinguish whether the TGFβ pathway defects arise from reduced IFT172 protein stability or from specific loss of ubiquitin-related functions of the U-box domain. Our experiments demonstrate that the U-box region is required for both IFT172 stability and proper TGFβ signaling, but we agree that establishing a direct mechanistic link between ubiquitin-binding/conjugation and signaling would require additional experiments such as point mutations that selectively disrupt ubiquitin-related activity without affecting protein stability. We have revised the discussion (p. 18-19) to more clearly acknowledge this limitation. Addition to text: “However, we note that our current experiments cannot distinguish whether these signaling effects result specifically from loss of ubiquitin-related functions of the U-box domain or from the reduced levels of functional IFT172 protein in the heterozygous U-box deleted cells. Targeted point mutations that selectively disrupt ubiquitin binding without affecting protein stability would be required to resolve this question.”

(11) The challenges in experimentally validating the interaction between IFT172 and the UBX-domain-containing protein are understandable. Alternative approaches, such as using single domains from the UBX protein, implementing solubilizing tags, or disrupting the predicted binding interface in Chlamydomonas flagella pull-downs, could be considered. In this context, the conclusion on page 7 that "The uncharacterized UBX-domain-containing protein was validated by AF-M as a direct IFT172 interactor" is incorrect as a prediction of an interaction interface with AF-M does not validate a direct interaction per se.

We agree with the reviewer that our AlphaFold-Multimer (AF-M) predictions alone do not constitute experimental validation of a direct interaction. We appreciate the reviewer's understanding of the technical challenges in validating this interaction experimentally. We have revised our text (p. 7) to state that "The uncharacterized UBX-domain-containing protein was predicted by AF-M as a potential direct IFT172 interactor" and discuss the AF-M predictions as computational evidence that suggests, but does not prove, a direct interaction.

Reviewer #2 (Public review):

Summary:

Cilia are antenna-like extensions projecting from the surface of most vertebrate cells. Protein transport along the ciliary axoneme is enabled by motor protein complexes with multimeric so-called IFT-A and IFT-B complexes attached. While the components of these IFT complexes have been known for a while, precise interactions between different complex members, especially how IFT-A and IFT-B subcomplexes interact, are still not entirely clear. Likewise, the precise underlying molecular mechanism in human ciliopathies resulting from IFT dysfunction has remained elusive.

Here, the authors investigated the structure and putative function of the to-date poorly characterised C-terminus of IFT-B complex member IFT172 using alpha-fold predictions, crystallography and biochemical analyses including proteomics analyses followed by mass spectrometry, pull-down assays, and TGFbeta signalling analyses using chlamydomonas flagellae and RPE cells. The authors hereby provide novel insights into the crystal structure of IFT172 and identify novel interaction sites between IFT172 and the IFT-A complex members IFT140/IFT144. They suggest a U-box-like domain within the IFT172 C-terminus could play a role in IFT172 auto-ubiquitination as well as for TGFbeta signalling regulation.

As a number of disease-causing IFT72 sequence variants resulting in mammalian ciliopathy phenotypes in IFT172 have been previously identified in the IFT172 C-terminus, the authors also investigate the effects of such variants on auto-ubiquitination. This revealed no mutational effect on mono-ubiquitination which the authors suggest could be independent of the U-box-like domain but reduced overall IFT172 ubiquitination.

Strengths:

The manuscript is clear and well written and experimental data is of high quality. The findings provide novel insights into IFT172 function, IFT complex-A and B interactions, and they offer novel potential mechanisms that could contribute to the phenotypes associated with IFT172 C-terminal ciliopathy variants.

Weaknesses:

Some suggestions/questions are included in the comments to the authors below.

Reviewer #3 (Public review):

Summary:

Zacharia et al report on the molecular function of the C-terminal domain of the intraflagellar transport IFT-B complex component IFT172 by structure determination and biochemical in vitro and cell culture-based assays. The authors identify an IFT-A binding site that mediates a mutually exclusive interaction to two different IFT-A subunits, IFT144 and IFT140, consistent with interactions suggested in anterograde and retrograde IFT trains by previous cryo-electron tomography studies. Additionally, the authors identify a U-box-like domain that binds ubiquitin and conveys ubiquitin conjugation activity in the presence of the UbcH5a E2 enzyme in vitro. RPE1 cell lines that lack the U-box domain show a reduction in ciliation rate with shorter cilia, and heterozygous cells manifest TGF-beta signaling defects, suggesting an involvement of the U-box domain in cilium-dependent signaling.

Strengths:

(1) The structural analyses of the C-terminal domain of IFT172 combine crystallography with structure prediction using state-of-the-art algorithms, which gives high confidence in the presented protein structures. The structure-based predictions of protein interactions are validated by further biochemical experiments to assess the specific binding of the IFT172 C-terminal domains with other proteins.

(2) The finding that the IFT172 C-terminus interactions with the IFT-A components IFT140 and IFT144 appear mutually exclusive confirm a suggested role in mediating the binding of IFT-B to IFT-A in anterograde and retrograde IFT trains, which is of very high scientific value.

(3) The suggested molecular mechanism of IFT train coordination explains previous findings in Chlamydomonas IFT172 mutants, in particular an IFT172 mutant that appeared defective in retrograde IFT, as well as mutations identified in ciliopathy patients.

(4) The identification of other IFT172 interactors by unbiased mass spectrometry-based proteomics is very exciting. Analysis of stoichiometries between IFT components suggests that these interactors could be part of IFT trains, either as cargos or additional components that may fulfill interesting functions in cilia and flagella.

(5) The authors unexpectedly identify a U-box-like fold in the IFT172 C-terminus and thoroughly dissect it by sequence and mutational analyses to reveal unexpected ubiquitin binding and potential intrinsic ubiquitination activity.

(6) The overall data quality is very high. The use of IFT172 proteins from different organisms suggests a conserved function.

Weaknesses:

(1) Interaction studies were carried out by pulldown experiments, which identified more IFT172 interaction partners. Whether these interactions can be seen in living cells remains to be elucidated in subsequent studies.

We agree with the reviewer that validation of protein-protein interactions in living cells provides important physiological context. While our pulldown experiments have identified several promising interaction partners and the AF-M predictions provide computational support for these interactions, we acknowledge that demonstrating these interactions in vivo would strengthen our findings. However, we believe our current biochemical and structural analyses provide valuable insights into the molecular basis of IFT172's interactions, laying important groundwork for future cell-based studies.

(2) The cell culture-based experiments in the IFT172 mutants are exciting and show that the U-box domain is important for protein stability and point towards involvement of the U-box domain in cellular signaling processes. However, the characterization of the generated cell lines falls behind the very rigorous analysis of other aspects of this work.

We thank the reviewer for noting that the characterization of our cell lines could be more rigorous. In the revised version of the manuscript, we have addressed this by providing additional validation data for all four engineered RPE1 cell lines. First, we performed Sanger sequencing to confirm precise in-frame integration of the GFP tag at the targeted loci and to exclude unintended insertions or deletions (indels), both for the full-length IFT172-eGFP lines (Fig. S6) and for the IFT172∆U-box-eGFP lines (Fig. S7). Second, we performed anti-IFT172 immunoblotting on all four cell lines alongside parental RPE1 cells, confirming expression of both the full-length and U-box-truncated IFT172 proteins (Fig. S8). Notably, the immunoblot revealed reduced steady-state levels of the IFT172∆U-box protein compared to full-length IFT172, providing direct biochemical evidence that loss of the U-box domain compromises IFT172 protein stability consistent with the ciliogenesis phenotype described in the main text. Together, these data verify the integrity of the edited loci at both the genomic and protein levels, and strengthen the validation of the cellular models used in this study.

Overall, the authors achieved to characterize an understudied protein domain of the ciliary intraflagellar transport machinery and gained important molecular insights into its role in primary cilia biology, beyond IFT. By identifying an unexpected functional protein domain and novel interaction partners the work makes an important contribution to further our understanding of how ciliary processes might be regulated by ubiquitination on a molecular level. Based on this work it will be important for future studies in the cilia community to consider direct ubiquitin binding by IFT complexes.

Conceptually, the study highlights that protein transport complexes can exhibit additional intrinsic structural features for potential auto-regulatory processes. Moreover, the study adds to the functional diversity of small U-box and ubiquitin-binding domains, which will be of interest to a broader cell biology and structural biology audience.

Additional comments:

The authors investigate the consequences of the U-box deletion on ciliary TGF-beta signaling. While a cilium-dependent effect of TGF-beta signaling on the phosphorylation of SMAD2 has been demonstrated, the precise function of cilia in AKT signaling has not been fully established in the field. Therefore, the relevance of this finding is somewhat unclear. It may help to discuss relevant literature on the topic, such as Shim et al., PNAS, 2020.

We appreciate the reviewer's comment highlighting that the role of primary cilia in AKT signaling is not as well established as for SMAD2/3. However, we note that a direct functional link between AKT signaling and ciliogenesis has been demonstrated, showing that AKT regulates ciliogenesis initiation through a Rab11-effector switch mechanism (Walia et al., 2019; PMID: 31204173, co-authored by the corresponding author of this study). Furthermore, Shim et al. (PMID: 33753495) demonstrated a cilia-dependent reciprocal activation of AKT1 and SMAD2/3. In the revised manuscript (p. 19, ref. 97), we have expanded the discussion to cite these studies and provide a clearer literature context for the cilia-AKT connection, while acknowledging that the precise mechanism by which the IFT172 U-box domain influences AKT activation requires further investigation.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Points for the discussion:

(1) The discussion should mention that IFT-A subunits IFT121, IFT122 and IFT144 share a similar domain organization to IFT172 (TPRs terminating in Zn-finger-like domains). Do the authors consider these as potential ubiquitin-binding proteins with E3 ligase activity? The possibility that these Zn-finger-like regions share a common origin, and function to stabilize the proteins or mediate IFT subunit interactions without a role in ubiquitin biology should be considered.

We appreciate this important point. We agree that the shared domain architecture across IFT121, IFT122, IFT144, and IFT172 raises the question of whether these C-terminal domains primarily serve structural rather than ubiquitin-related roles. We have added a discussion paragraph (p. 16) acknowledging that a structural/stabilizing function is the more parsimonious explanation, while noting that whether IFT172's U-box-like domain has additionally acquired ubiquitin-related activity remains an open question.

(2) From their modeling data, do the authors have an explanation for why a substitution as conservative as D1605E would cause disease?

The D1605E substitution maps to the IFT172-IFT-A interaction interface (Fig. 1F). While this is a conservative change, D1605 is located at a tightly packed protein-protein interface where even the addition of a single methylene group (the difference between aspartate and glutamate) could introduce steric clashes with residues of IFT140 or IFT144, or alter the precise geometry of hydrogen bonds or salt bridges critical for the interaction. Unfortunately, this level of detail is beyond the resolution of AlphaFold models. However, the fact that this residue is positioned directly at the binding interface provides a plausible structural rationale for its pathogenicity.

(3) The authors speculate that the L1615P mutation in the Chlamydomonas fla11 strain causes a faulty switch to retrograde IFT and this provides a molecular basis for the retrograde IFT phenotype. However, because the mutation is also within the IFT144 binding site, why is anterograde IFT also not affected?

The fla11 L1615P mutation resides in helix αA, which participates in both IFT144 (anterograde) and IFT140 (retrograde) interactions. The predominantly retrograde phenotype can be rationalized by the fundamentally different structural roles of the IFT172 C-terminus in anterograde versus retrograde trains. In anterograde trains, the IFT172 C-terminus acts as a flexible tether in stoichiometric excess (2:1 IFT-B:IFT-A ratio), providing an avidity effect that likely compensates for reduced binding affinity caused by L1615P (Lacey et al., 2023). Additional lateral interactions between IFT-B subunits further stabilize the anterograde polymer independently of the IFT172-IFT144 link. In contrast, the retrograde train requires the IFT172 C-terminus to adopt a rigid, resolved conformation that is integral to the IFT-A dimeric interface, with no redundant lateral interactions to compensate (Lacey et al., 2024). The helix-breaking L1615P mutation would specifically disrupt this precise structural requirement, explaining the selective retrograde IFT defect in fla11. We have added this discussion to the revised manuscript (p. 16).

Minor:

(1) On page 5, the authors describe the fla11 phenotypes including accumulation of IFT particles at the tip and accumulation of ubiquitinated proteins in the cilium. Could the authors please expand on how this suggests that IFT172 could be involved in ciliary ubiquitination events and discuss an alternative scenario of impaired assembly of functional retrograde IFT in this strain leading to accumulation of ubiquitinated proteins?

In the revised manuscript (p. 16), we have expanded the discussion of the fla11 phenotype to address this point. We now discuss how the distinct structural roles of the IFT172 C-terminus in anterograde versus retrograde trains explain the selective retrograde IFT defect in fla11, and explicitly note that the accumulation of ubiquitinated proteins in fla11 cilia may reflect impaired retrograde IFT-mediated clearance rather than a direct role of IFT172 in ciliary ubiquitination.

(2) The authors should also expand on the literature of known UBX-IFT interactions in their manuscript (e.g. Raman et al. PMID 26389662).

We have expanded the discussion of UBX-IFT interactions in the revised manuscript (p. 7) by citing the work of Raman et al. (PMID 26389662), who identified a direct interaction between the UBX-domain protein UBXN10 and IFT-B via CLUAP1/IFT38 for VCP-mediated regulation of IFT complex integrity. This provides important context for our identification of a UBX-domain protein as an IFT172 interactor.

(3) On page 11, I1688 is incorrectly referred to as I688.

Fixed.

Reviewer #2 (Recommendations for the authors):

(1) The finding that the interaction with IFT140/144 is mutually exclusive is very interesting. Could you speculate on or do you have any data regarding the effects to the overall IFT-complex conformation and downstream biological effects depending on which partner is bound?

I am not a structural biologist so this may be an irrelevant/impossible-to-answer question: I was also wondering as Ref 46 has shown that the dynein-2 motor complex binds to the edge of IFT-B2 (for assembled trains): Could the IFT172 C-terminus be involved here or somehow influence this interaction? In your mass spec data from Cr cilia using CrIFT172_968-C you don`t mention pulling down dynein-2 components so there doesn`t seem to be a direct interaction, but could the IFT-B2 conformation depend on if IFT172 has bound IFT-140 or IFT144 and hence this interaction influence the dynein-2 binding?

We thank the reviewer for this insightful question. Based on recent cryo-ET structures of anterograde and retrograde IFT trains (Lacey et al., 2023; 2024), the switch from IFT144 to IFT140 binding fundamentally changes IFT172's structural role. In anterograde trains, the IFT172 C-terminus acts as a flexible tether tolerating the 2:1 IFT-B:IFT-A stoichiometry and permitting long polymer formation. In retrograde trains, it adopts a rigid conformation integral to the IFT-A dimeric interface, driving the formation of discrete retrograde units with distinct architecture.

Regarding Dynein-2: while IFT172 does not directly bind Dynein-2 (consistent with our MS data), the reviewer's intuition is correct that IFT172's binding partner influences Dynein-2 association. In anterograde trains, autoinhibited Dynein-2 binds a composite surface formed between adjacent IFT-B2 repeats. When IFT172 switches to IFT140 at the ciliary tip, the resulting train depolymerization destroys this composite binding site, releasing Dynein-2 from its cargo mode to function as an active retrograde motor. The IFT172 binding switch may thus indirectly acts as a structural checkpoint for Dynein-2 activation.

(2) The data provided regarding TGFbeta signalling effects in cells with heterozygous U-box-like domain deletions is interesting. While secondary effects of impaired ciliogenesis due to homozygous deletion of the U-box-like domain can cause difficulties to analysing cell signalling effects, it would still be interesting to check the effects of bi-allelic human IFT172 disease variants in this region as well (the human disease phenotype is recessive and human mutations are likely hypomorphic variants still allowing for ciliogenesis).

Also, while there may be secondary effects, it would still be interesting to check homozygous U-box deleted cells as an aggravated effect would further support the data from the het cells.

We agree that testing bi-allelic human disease variants would strengthen the physiological relevance of our findings. While generating knock-in RPE1 lines was beyond the scope of this revision, we have obtained preliminary data from patient-derived fibroblasts carrying bi-allelic IFT172 missense variants in the U-box region (NPH2161). TGF-β1 stimulation time courses in these fibroblasts show altered p-SMAD2 kinetics compared to control fibroblasts, consistent with the phenotype observed in our heterozygous U-box deleted RPE1 cells (see Author response image 3).

Author response image 3.

While these results are preliminary and require further replication, they support the involvement of the IFT172 U-box domain in TGF-β signaling regulation in a disease-relevant context. Regarding homozygous U-box deleted cells, the severe reduction in IFT172 protein levels and ciliogenesis defects (Fig. 5B,D) make it difficult to separate U-box-specific effects from secondary consequences of impaired cilia formation, as the reviewer notes. We consider this an important direction for future studies using targeted point mutations rather than domain deletions.

(3) Figure 5 E-G: Overall, the effects upon TGFB1 addition are rather small compared to previously published data eg Clement et al Cell reports 2013 where one of the authors is the senior. Are RPE cells less responsive or do you have another theory? Did you check TGFB receptor levels to ensure the differences are not due to different levels of receptor expression? I feel it could be interesting to also check ciliary phopsho-SMAD localisation by IF. In Clement et al, loss of IFT88 results in reduced phospho-SMAD2 levels, do you have any theory why these opposite effects compared to the IFT172 loss of function could occur?

We thank the reviewer for this insightful comment. The Tg737orpk fibroblasts used in Clement et al. (2013), which harbor a hypomorphic mutation in IFT88, exhibit severely stunted cilia. This defect broadly disrupts cilium-dependent signaling pathways, including R-SMAD activation, and is therefore expected to produce more pronounced signaling phenotypes. In contrast, our study utilizes RPE-1 cells with structurally intact cilia, enabling us to investigate more specific alterations in ciliary signaling associated with IFT172 function rather than the global effects of cilia loss. Consequently, the more modest effects observed in our system are consistent with the less severe structural and functional perturbation. Both fibroblasts and RPE-1 cells are known to express TGF-β receptors and to respond robustly to TGF-β stimulation, making it unlikely that differences in receptor abundance alone account for the observed discrepancies. We also note that increasing evidence supports a role for the primary cilium in fine-tuning TGF-β signaling output by coordinating both canonical (R-SMAD-mediated) and non-canonical (e.g., AKT/ERK-mediated) pathways. Our data raise the possibility that loss of the IFT172 U-box domain, or reduced IFT172 levels, may differentially affect this balance, rather than simply attenuating signaling uniformly, as seen with more severe ciliary defects such as IFT88 disruption in Tg737orpk cells. We agree that the current dataset does not fully resolve the underlying mechanism. We therefore consider it an important direction for future work to examine, in greater detail, the localization and phosphorylation status of key canonical and non-canonical signaling components in context of the primary cilium by IF analyses.

(4) In the summary conclusion at the end of the discussions, the authors propose that IFT72 could directly influence the fate of ubiquitinated TGFB receptors. Do you have any data supporting the theory that TGFB ubiquitination is influenced by IFT172 ?

We acknowledge that our current data are insufficient to establish a direct link between IFT172-dependent ubiquitination events and TGF-β receptor regulation. Accordingly, we have revised the Discussion (page 19) to remove our previous hypothesis proposing a role for IFT172 in modulating TGF-β receptor ubiquitination.

While our experiments demonstrate that the U-box region is required for both IFT172 stability and proper TGF-β signaling, we agree that establishing a direct mechanistic connection between ubiquitin-related activity of IFT172 and signaling outcomes would require additional approaches such as targeted point mutations that selectively disrupt ubiquitin-binding or conjugation functions.

Furthermore, we note that our current data do not allow us to distinguish whether the observed signaling phenotypes arise specifically from the loss of ubiquitin-related functions of the U-box domain or from reduced levels of functional IFT172 protein in the heterozygous U-box–deleted cells.

(5) Wording:

Abstract

"IFT72..is associated with several disease variants causing ciliopathies". I would change this to "..and several disease-causing IFT172 variants have been identified in ciliopathy patients".

Corrected.

Introduction

"Another cohort of patients with milder ciliopathy resembling BBS also presented with ...". I would reword this to "Another cohort of patients with phenotypically slightly different ciliopathy features resembling BBS also presented with ...". It`s not necessarily less severe (they may die of cardiovascular complications in their early thirties for example due to metabolic syndrome, they are intellectually impaired, become blind...), but rather different.

Changed according to the reviewer’s recommendations.

Reviewer #3 (Recommendations for the authors):

(1) Recommended modifications:

(a) The RPE lines generated should be described better, i.e. sequencing information should be provided, or some kind of evidence that the lines are what they are supposed to be.

As also noted above, we acknowledge that the characterization presented for the RPE cell lines was insufficient in the initial version of the manuscript. In the revised version, we have addressed this limitation by including detailed sequencing analyses to validate the modifications introduced. Specifically, we provide sequencing data confirming both the integration of the GFP tag and the successful deletion of the U-box domain in all four engineered RPE cell lines. These data verify the integrity of the edited loci and exclude the presence of unintended insertions or deletions at the targeted regions. The corresponding results are presented in Figures S6 and S7 of the revised manuscript, thereby strengthening the validation of the cellular models used in this study.

(b) It would be more convincing if more than one clone of the RPE lines were presented, as this could rule out possible clonal effects.

We acknowledge that only a single clone was characterized for each of the four genotypes (IFT172-FL homozygous, IFT172-FL heterozygous, IFT172∆U-box homozygous, IFT172∆U-box heterozygous), and we agree that independent clones would provide stronger protection against clonal artifacts. Generating and validating additional clones was not feasible within the scope of this revision. However, several features of our data mitigate this concern. First, the phenotypes scale with allele dosage: the homozygous ∆U-box line shows the strongest reduction in IFT172 protein level, ciliation, and cilium length, while the heterozygous line shows intermediate defects (Fig. 5B, D and Fig. S8). A clonal off-target effect would not be expected to produce this dose-dependent pattern across two independently isolated lines. Second, the reduced steady-state IFT172 level in the ∆U-box lines (Fig. S8) is consistent with our in vitro observation that the U-box/TPR interface is required for protein stability, providing an independent biochemical rationale for the cellular phenotype. Third, Sanger sequencing of all four lines confirmed precise in-frame integration with no indels at the targeted locus (Figs. S6, S7). We have added a sentence to the Discussion (p. 20) acknowledging that confirmation in additional independent clones remains an important goal for follow-up work.

(c) Figure 5C: distribution of the GFP-tagged IFT172∆U-box protein could be quantified to support the statement.

In the revised version of the manuscript, we have included additional quantification of GFP fluorescence across all four cell lines to support our conclusions regarding IFT172 ciliary localization. The corresponding data for each cell line are presented in Figure S5C–F.

(d) The final sentences include quite bold statements about a general function of IFT172 in signal regulation. Yet, the evidence is the weakest part of the work. It is only shown in i) one cell line, ii) in one cell clone that is not extensively characterized, and iii) for one signaling pathway that is not the best-studied cilia signaling pathway. Therefore, I recommend a more moderate statement.

Abstract last sentence has now been toned down and reads: Our findings suggest that IFT172, beyond its structural role in bridging IFT-A and IFT-B complexes within IFT trains, harbors a conserved U-box-like domain with potential involvement in ciliary ubiquitination processes and signaling, providing new insights into the molecular mechanisms underlying IFT172-related ciliopathies.

(e) The order of the figures is not followed in the main text, which is distracting.

The order of figures is now consecutive in the revised manuscript.

(2) Questions and comments to consider:

(a) It is unclear why tetra-ubiquitin chains have been used.

We thank the reviewer for this question. Recent evidence suggests that ubiquitin chains, rather than monomeric ubiquitin, act as sorting and signaling cues at the primary cilium (Shinde et al., 2020). To probe the ubiquitin-binding activity of IFT172, we therefore used a tetrameric ubiquitin chain as a model substrate, which better reflects the multivalent nature and binding avidity expected for physiological polyubiquitin signals than a ubiquitin monomer. Specifically, we used a recombinantly expressed linear (Met1-linked) tetra-ubiquitin chain, generated as a genetically encoded fusion. Linear ubiquitin chains are well-established non-degradative signaling chains recognized by a dedicated class of ubiquitin-binding domains, making them a suitable probe for detecting ubiquitin-binding activity outside the canonical proteasomal pathway. In addition, monomeric ubiquitin (~8 kDa) is poorly retained during membrane transfer in Western blotting, which further precluded its reliable use as a probe in our pull-down assays. Together, these considerations motivated the use of tetrameric ubiquitin as a biologically and technically appropriate substrate for assessing IFT172's ubiquitin-binding activity.

(b) Figure 4D: described in the text as "pulldown tetraubiquitin at comparable levels", which is not obvious from the figure presented, it appears reduced by at least 30%.

We thank the reviewer for this observation. As described on page 10 of the manuscript and evident from Figure 4D, the purified GST–HsIFT172C3 construct underwent substantial proteolytic cleavage during purification. This degradation limited our ability to include amounts of intact GST–HsIFT172C3 comparable to those of the full-length GST–HsIFT172C2 construct in the pull-down assays. Importantly, when accounting for the reduced proportion of full-length GST–HsIFT172C3 present in the assay, the observed differences in tetra-ubiquitin pull-down efficiency between the two constructs are expected to be comparable. This is supported by the Coomassie staining shown in Figure 4D, which reflects the relative abundance of the intact protein species used in the experiment.

(c) With the proposed model, why would the fla11 mutant only affect retrograde IFT?

We have revised our manuscript in page 16 of the discussion section providing a plausible explanation of why only retrograde IFT is affected in the fla11 mutant.

(3) Minor copy-editing:

(a) Page 3, first paragraph: led := leads.

(b) Kinesin-2 and Dynein-2 should be hyphenated.

(c) Page 4: wwp1 should be WWP1.

(d) Bonafide should be italicized: bona fide.

(e) Some abbreviations appear uncommon and therefore somewhat distracting: TGFB instead of TGF-beta, Cr in instances where specifically referred to the organism.

(f) Unprecise lab jargon: "very C-terminal".

(g) Lab jargon: "purified a C-terminal construct".

(h) Lab jargon: "pull-downs".

(i) Page 8: "DALI" only abbreviated.

(j) Page 9: "Appearance ... were observed" should be "was".

(k) Page 11: "I688" should be "I1688".

(l) Page 12: "PDs" unclear.

These minor points have been corrected.

We have revised the text and figures to ensure using the widely accepted nomenclature, using TGF-β to refer to the signaling pathway and TGF-β1 specifically when referring to the ligand.

We further revised the text to reflect the use “Chlamydomonas reinhardtii” in instances when referring to the organism and “Cr” when referring to the protein.

We have removed the informal phrases "very C-terminal" and "purified a C-terminal construct" from the revised manuscript. We have retained the term "pull-down," as this is well-established and widely used terminology in the biochemistry literature to describe the affinity-based co-isolation assays used here. PD has been replaced with pull-down.

The grammatical error on page 9 ("Appearance... “were observed") has been corrected to "was observed”.

Reviewer #1 (Public review):

Summary:

The authors Hall et al. establish a purification method for snake venom metalloproteinases (SVMPs). By generating a generic approach to purify this divergent class of recombinant proteins, they enhance the field's accessibility to larger quantity SVMPs with confirmed activity and, for some, characterized kinetics. In some cases, the recombinant protein displayed comparable substrate specificity and substrate recognition compared to the native enzyme, providing convincing evidence of the authors' successful recombinant expression strategy. Beyond describing their route towards protein purification, they further provide evidence for self-activation upon Zn2+ incubation. They further provide initial insights on how to design high throughput screening (HTS) methods for drug discovery and outline future perspectives for the in-depth characterization of these enzyme classes to enable the development of novel biomedical applications.

Strengths:

The study is well presented and structured in a compelling way and the universal applicability of the approach is nicely presented.<br /> The purification strategy results in highly pure protein products, well characterized by size exclusion chromatography, SDS page as well as confirmed by mass spectrometry analysis. Further, a significant portion of the manuscript focuses on enzyme activity, thereby validating function. Particularly convincing is the comparability between recombinant vs. native enzymes; this is successfully exemplified by insulin B digestion. By testing the fluorogenic substrate, the authors provide evidence that their production method of recombinant protein can open up possibilities in HTS. Since their purification method can be applied to three structurally variable SVMP classes, this demonstrates the robust nature of the approach.

Weakness

The product obtained from the purification protocol appears to be a heterogenous mixture of self-activated and intact protein species. The protocol would benefit from improved control over the self-activation process. The authors explain well why they cannot deplete Zn2+ in cell culture or increase the pH to prevent autoactivation during the current purification steps. However, this leads me to the suggestion, if the His tag could be exchanged to a different tag that is less pH sensitive and not dependent on divalent ions (Strep-Tactin XT?) to allow for removal of divalent ions and low pH during purification steps. Another suggestion would be if they could replace the endogenous protease cleavage site in their expression construct design to a TEV protease recognition site, for example, to have more control over activation of the recombinant proteins.

The graphic to explain the universal applicability of the approach, Figure S1, has some mistakes, like duplication of text, an arrow without a meaning and should be revised.

Overall, the authors successfully purified active SVMP proteins of all three structurally diverse classes in high quality and provided convincing evidence throughout the manuscript to support their claims. The described method will be of use for a broader community working with self-activating and cytotoxic proteases.

Comment on the revised version:

I find that the clarity and overall structure of the manuscript have improved. However, the weakness I previously highlighted has neither been addressed experimentally nor convincingly explained. Therefore, the assessment stayed unchanged from my side.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors Hall et al. establish a purification method for snake venom metalloproteinases (SVMPs). By generating a generic approach to purify this divergent class of recombinant proteins, they enhance the field's accessibility to larger quantities of SVMPs with confirmed activity and, for some, characterized kinetics. In some cases, the recombinant protein displayed comparable substrate specificity and substrate recognition compared to the native enzyme, providing convincing evidence of the authors' successful recombinant expression strategy. Beyond describing their route towards protein purification, they further provide evidence for self-activation upon Zn2+ incubation. They further provide insights on how to design high-throughput screening (HTS) methods for drug discovery and outline future perspectives for the in-depth characterization of these enzyme classes to enable the development of novel biomedical applications.

Strengths:

The study is well-presented and structured in a compelling way. The purification strategy results in highly pure protein products, well characterized by size exclusion chromatography, SDS page as well as confirmed by mass spectrometry analysis. Further, a significant portion of the manuscript focuses on enzyme activity, thereby validating function. Particularly convincing is the comparability between recombinant vs. native enzymes; this is successfully exemplified by insulin B digestion. By testing the fluorogenic substrate, the authors provide evidence that their production method of recombinant protein can open up possibilities in HTS. Since their purification method can be applied to three structurally variable SVMP classes, this demonstrates the robust nature of the approach.

We thank the reviewer for their positive assessment of our work.

Weaknesses:

The universal applicability of the approach could be emphasized more clearly. The potential for this generic protocol for recombinant SVMP zymogen production to be adapted to other SVMPs is somewhat obscured by the detailed optimization steps. A general schematic overview would strengthen the manuscript, presented as a final model, to illustrate how this strategy can be extended to other targets with similar features. Such a schematic might, for example, outline the propeptide fusion design, including its tags, relevant optimizations during expression, lysis, purification (e.g., strategies for metal ion removal and maintenance of protease inactivity), as well as the controllable auto-activation.

In the revised version of the manuscript, we moved the detailed description of the optimisation of SVMP expression, including mature SVMP expression, Marimastat addition, active site mutations and fusion of propeptides, into the supplement as supplementary text. We hope this improves the clarity and flow. As suggested, we now include a new figure outlining the SVMP production strategy and optimisation steps in the revised manuscript (new Figure S1).

The product obtained from the purification protocol appears to be a heterogeneous mixture of selfactivated and intact protein species. The protocol would benefit from improved control over the selfactivation process. The Methods section does not indicate whether residual metal ions were attempted to be removed during the purification, which could influence premature activation.

We agree that improved control of self-activation would be desirable. However, there is an issue: Previous studies reported that (1) SVMP zymogens are processed within secretory cells of the venom gland (Portes-Junior et al., 2014), and (2) mature SVMPs accumulate in secretory vesicles during venom production (Carneiro et al., 2002). Accordingly, preventing the auto-processing of SVMP zymogens is difficult to achieve because this would require Zn²⁺ depletion within the insect cells during production which would result in cytotoxicity. We have included this information in the updated Discussion section of the revised manuscript.

Additionally, it has not been discussed whether the shift to pH 8 in the purification process is necessary from the initial steps onwards, given that a lower pH would be expected to maintain enzyme latency.

The shift to pH 8 is required for the affinity purification of the SVMP zymogens from the medium, involving the poly-histidine-tag and immobilized metal affinity chromatography (IMAC). At lower pH, the histidines would become protonated, preventing binding of the His-tag to the column. Thus, with the His-tag the shift to pH 7.5 or pH 8 is necessary.

The characterization of PIII activity using the fluorogenic peptide effectively links the project to its broader implications for drug design. However, the absence of comparable solutions for PI and PII classes limits the overall scope and impact of the finding.

We agree that such assays would be extremely useful. However, the development of fluorescence based high-throughput assays to test for PI and PII SVMP activity is beyond the scope of this study. Here, our overarching objective is to report a broadly applicable production method for PI, PII and PIII SVMPs.

Overall, the authors successfully purified active SVMP proteins of all three structurally diverse classes in high quality and provided convincing evidence throughout the manuscript to support their claims. The described method will be of use for a broader community working with self-activating and cytotoxic proteases.

Thank you.

Reviewer #2 (Public review):

Summary:

The aim of the study by Hall et al. was to establish a generic method for the production of Snake Venom Metalloproteases (SVMPs). These have been difficult to purify in the mg quantities required for mechanistic, biochemical, and structural studies.

Strengths:

The authors have successfully applied the MultiBac system and describe with a high level of detail the downstream purification methods applied to purify the SVMP PI, PII, and PIII. The paper carefully presents the non-successful approaches taken (such as expression of mature proteins, the use of protease inhibitors, prodomain segments, and co-expression of disulfide-isomerases) before establishing the construct and expression conditions required. The authors finally convincingly describe various activity assays to demonstrate the activity of the purified enzymes in a variety of established SVMP assays.

We thank the reviewer for their positive assessment of our work.

Weaknesses:

The manuscript suffers from a lack of bottoming out and stringent scientific procedures in the methodology and the characterization of the generated enzymes.

As an example, a further characterization of the generated protein fragments in Figure 3 by intact mass spectroscopy would have aided in accurate mass determination rather than relying on SEC elution volumes against a standard. Protein shape and charge can affect migration in SEC.

We agree that intact MS would be useful to determine the mass of the produced SVMPs. In this manuscript, we performed SEC as a purification step, removing aggregates. Furthermore, SEC allowed determining if the SVMPs form monomers or dimers. MS characterisation of intact SVMPs (and their PTMs) is not trivial and beyond the scope of this manuscript (see below).

Also, the analysis of N-linked glycosylation demonstrates some reactivity of PIII to PNGase F, but fails to conclude whether one or more sites are occupied, or whether other types of glycosylation is present. Again, intact mass experiments would have resolved such issues.

We concur that glycosylation of SVMPs is an important question. However, analysing the glycosylation of the SVMPs is beyond the scope of this manuscript; it is actually a project on its own: Intact MS can indeed provide information on glycosylation but is not very precise. Unambiguous assignment of the number and occupancy of glycosylation sites is more challenging, especially for large, glycosylated proteins such as our PIII SVMP zymogen. In practice, confident mapping of glycosylation sites would require peptide-level mass spectrometry following enzymatic digestion (Trypsin and Multi-Enzymatic Limited Digestion, ideally). Sample preparation, method optimization, MS acquisition, and data analysis together would require a significant investment. Moreover, we do not have access to the native PIII SVMP from Echis carinatus sochureki venom - this is the main point of our manuscript: we describe a protocol to produce SVMPs which could not be purified from venom. Therefore, a comparison of the glycosylation of the recombinant SVMP and the native SVMP cannot be performed unfortunately (see below).

The activity assays in Figure 4 are not performed consistently with kinetic assays and degradation assays performed for some, but not all, enzymes, and there is no Echis ocellatus comparison in Figure 4h.

This is correct. The suggested control experiment is not possible for the PII SVMP and PIII SVMP because we cannot purify the native PII and PIII SVMPs from Echis venom. We have highlighted this information in the revised manuscript in the insulin B degradation section.

Overall, whilst not affecting the main conclusion, this leaves the reader with an impression of preliminary data being presented. For consistency, application of the same assays to all enzymes (high-grade purified) would have provided the reader with a fuller picture.

In the revised manuscript, we included new data showing the requested characterisations of all three SVMPs.

We have included the respective assays in Figure 5 and Supplementary Figure S11. In the original manuscript, we had omitted these assays as the data show no enzymatic activity in the respective assays. Specifically, we show that (1) PII does not cause insulin B degradation (Fig. S11b), (2) that the PI and PII SVMPs do not degrade the fluorogenic peptide which is prototypic for PIII SVMPs and MMPs (Fig. S11a), (3) PI and PIII do not cause platelet aggregation because they lack the entire disintegrin domain (PI) or the RGD motif (PIII) (Fig. 5a), and (4) that the PI and PII SVMPs, like the PIII SVMP, are not pro-coagulant and do not cause blood clotting (Fig. 5d,5e and Fig. S11c). We also included this new information in the main text of our revised manuscript.

Overall, the data presented demonstrates a very credible path for the production of active SVMP for further downstream characterization. The generality of the approach to all SVMP from different snakes remains to be demonstrated by the community, but if generally applicable, the method will enable numerous studies with the aim of either utilizing SVMPS as therapeutic agents or to enable the generation of specific anti-venom reagents, such as antibodies or small molecule inhibitors.

Thank you.

Reviewer #3 (Public review):

Summary:

The presented study describes the long journey towards the expression of members' SVMP toxins from snake venom, which are toxins of major importance in a snakebite scenario. As in the past, their functional analysis relied on challenging isolation; the toxins' heterologous expression offers a potential solution to some major obstacles hindering a better understanding of toxin pathophysiology. Through a series of laborious and elegantly crafted experiments, including the reporting of various failed attempts, the authors establish the expression of all three SVMP subtypes and prove their activity in bioassays. The expression is carried out as naturally occurring zymogens that autocleave upon exposure to zinc, which is a novel modus operandi for yielding fusion proteins and sheds also some new light on the potential mechanism that snakes use to activate enzymatic toxins from zymogenic preforms.

Strengths:

The manuscript draws from an extensive portfolio of well-reasoned and hypothesis-driven experiments that lead to a stepwise solution. The wetlands data generated is outstanding, although not all experiments along this rocky road to victory were successful. A major strength of the paper is that, translationally speaking, it opens up novel routes for biodiscovery since a first reliable platform for expression of an understudied, yet potent toxin class is established. The discovered strategy to pursue expression as zymogens could see broad application in venom biotechnology, where several toxin types are pending successful expression. The work further provides better insights into how snake toxins are processed.

We thank the reviewer for their positive assessment of our work.

Weaknesses:

The manuscript contains several chapters reporting failed experiments, which makes it difficult to follow in places.

Based on a similar comment of Reviewer 1, we now moved the ‘failed’ experiments reporting on SVMP expression optimisation to the supplement as new supplementary text. We hope that the revisions have improved the clarity and overall readability of our manuscript.

The reporting of experimental details, especially sample sizes and replicates, could be optimised.

The number of replicates has now been added to the figure legends in the revised manuscript. Detailed experimental information is found in the revised Methods part.

At the time of writing, it remains unclear whether the glycosilations detected at a pIII SVMP could have an impact on the bioactivities measured, which is a major aspect, and future follow-ups should clarify this.

A detailed analysis of glycosylation of the PIII SVMP is beyond the scope of our manuscript (see above, response to Reviewer 2). Our manuscript describes a generic protocol to produce active SVMPs. Importantly, we cannot purify the native PIII SVMP from Echis carinatus sochureki venom. Therefore, it is not possible to compare our PIII SVMP with the native PIII SVMP.

We agree that this is an important question, and we will aim in the future to perform such a comparison of a different insect cell-produced PIII with a native PIII SVMP that can be readily purified from venom.

Finally, the work, albeit of critical importance, would benefit from a more down-to-earth evaluation of its findings, as still various persistent obstacles that need to be overcome.

We consider cytotoxicity to be the principal bottleneck in SVMP production. In this study, we present a strategy to overcome this bottleneck.

Major comments to the manuscript:

(1) Lines 148-149: "indicating that expressing inactivated SVMPs could be a viable, although inefficient, approach". I think this text serves a good purpose to express some thoughts on the nature of how the current draft is set up. It is quite established that various proteases cause extreme viability losses to their expression host (whether due to toxicity, but surely also because of metabolic burden), which is why their expression as inactive fusion proteins is the default strategy in all cases I have thus far seen. I believe that, especially in venom studies, this is of importance given the increased toxicity often targeting cellular integrity, and especially here, because Echis are known to feed on arthropods at younger life history stages, making it very likely that some venom components are especially active against insects and other invertebrates. With that in mind, I would argue that exploring their production in inactive form is the obvious strategy one would come up with and not really the conclusion of a series of (well-conducted and scientifically sound!) experiments. For me, the insight of inactive expression is largely confirmatory of what is established, unless I miss something in the authors' rationale. If yes, it would be important to clarify that in the online version.

We agree that producing zymogens represents a straightforward strategy and now, in hindsight, would have wished we had tested this first thing, it would have saved us and apparently many others significant effort. However, realising this, and implementing this approach took us considerable time and insight as we described in this manuscript. The alternative strategies we describe in the manuscript, in particular the use of inhibitors and active-site mutation, have been successfully applied for recombinant production of diverse enzymes before, including enzymes that are toxic to host cells.

We have revised the manuscript as requested and moved the optimisation of SVMP expression to the Supplement. We hope this improved the clarity, overall readability of the text and thus addressed the reviewer’s comment.

(2) Line 173: Here, Alphafold 3 was used, whereas in previous sections (e.g., line 153, line 210), it was Alphafold 2. I suggest using one release across the manuscript.

Thank you for bringing this to our attention. In the revised version of the manuscript, we clarified that all models were generated using AlphaFold 3.

(3) Line 252-254: I fully agree, the PIII SVMP is glycosylated. Glycosylation is an important mediator of snake venom activity, and several works have described their importance in the field. This raises the question, which glycosylations have been introduced here in the SVMP, and to verify that these are glycosylations that belong to those found in snakes. This is important as insects facilitate thousands of N- and O- O-glycosylations to modulate the activity of their proteome, of which many are specific to insects. If some of these were integrated into the SVMP, this could have an impact on downstream produced bioassays and also antigenicity (the surface would be somewhat different from natural toxins, causing different selection).

We agree that glycosylation is important and warrants a follow-up in the future.

However, most publications we found reported that de-glycosylation has a negative effect on stability and solubility of SVMPs, which is expected to have a knock-on effect on toxin activity (e.g. AndradeSilva et al., 2025; DOI: 10.1021/acs.jproteome.5c00249). It will be difficult to separate the two effects from each other. We found only a few examples where SVMP glycosylation (sialylation and Nglycosylation) modulated proteolytic and haemorrhagic functions, including interaction with substrates such as e.g. fibrinogen (Schluga et al., 2024; https://doi.org/10.3390/toxins16110486; Chen et al., 2008; 10.1111/j.1742-4658.2008.06540.x; Nikai et al., 2000; DOI: 10.1006/abbi.2000.1795. PMID: 10871038). In our manuscript, we show that our PIII SVMP is very cytotoxic and highly active in casein, fibrinogen and ESO10 degradation assays, with a K_M and k_cat/K_M comparing favourably with other SVMPs and MMPs. We are not aware of a specific substrate for this particular PIII SVMP that depends on a distinct glycosylation pattern. Recombinant production of such SVMPs with specific glycosylation pattern requirement would be a challenge in all commonly used expression systems (yeast, plant, insect cells and mammalian cells). In fact, insect cell expression systems could be advantageous in this respect because the Sf21 and High Five (Hi5) lepidopteran cell lines we utilised are well-characterized for their ability to perform posttranslational modifications on complex secreted proteins:

(1) N-Glycan conservation: Both Sf21 and Hi5 cells typically produce N-glycans that are trimmed to a core 'paucimannose' structure (Man3GlcNAc2), often with an alpha1,6-fucosylation. While snakes can produce more complex, sialylated N-glycans, glycomic studies of native venoms (e.g., Bothrops venom) have demonstrated that high-mannose and paucimannose structures are also prevalent in native SVMPs. Therefore, the recombinant glycoforms produced in our system are not 'unnatural' in the snake venom context but rather represent a subset of the native glycan microheterogeneity.

(2) Occupancy vs structure: The critical function of glycosylation in PIII SVMPs is thought to be often structural, facilitating correct folding and protecting the large metalloprotease and disintegrin-like domains from proteolytic degradation. Because Sf21 and Hi5 cells recognize the same Nglycosylation sequon (Asn-X-Ser/Thr) as reptilian cells, the site-occupancy remains consistent with the native protein, preserving the overall topography of the toxin.

(3) Activity and authentic self-processing: We acknowledge that insect-specific alpha1,3-fucosylation can occur in Hi5 cells and is potentially antigenic. As the recombinant SVMPs will be used for binder selections and for testing in silico designed binders, useful binders will be selected based on neutralising activity against venom toxins. Here, our assays focused on auto-activation and proteolytic activity, which is primarily driven by the catalytic Zn²⁺-site and the protein backbone.

As stated above, analysis of glycosylation pattern of the PIII SVMP is a project on its own and beyond the scope of this manuscript.

We have incorporated some of the above information into the discussion section of the revised manuscript to clarify that insect cell glycosylation does not recapitulate the full diversity of SVMP glycosylation observed in native venoms.

(4) General comment for the bioassays: It would be good to specify the replicates again and report the data, including standard deviations.

We included this information in the figure legends.

Discussion:

I think the data generated in the study is very valuable and will be instrumental for pushing the frontiers in SVMP research, but still I would like to see a bit of modesty in their discussion. As I have pointed out above, it is unclear which effect the glycosilations may have (i.e., are the glycosilations found reminiscent of natural ones?), despite their being functionally important. Also, yes, isolation of SVMPs is challenging, but the reality is that their expression is equally challenging, as evidenced by the heaps of presented negative data (with which I have no problems, I think reporting such is actually important). So far, the "generic" protocol has been used to express one member per structural class of Echis SVMP, but no evidence is provided that it would work equally well on other members from taxonomically more distant snakes (e.g., the pIII known from Naja oxiana). It is very likely, but at the time of writing, purely speculative.

We have expressed additional PIII SVMPs from Echis and Daboia species and will report their production and characterisation in due course.

Lastly, the reality is also that the expression in insect cells can only be carried out by highly specialized labs (even in the expression world, as most laboratories work with bacterial or fungal hosts), whereas the isolation can be attempted in most venom labs. That said, production in insect cells also has economic repercussions as it will be very challenging to generate yields that are economically viable versus other systems, which is pivotal because the authors talk about bioprospecting and the toxins used in snakebite agent research.

We thank the reviewer for this perspective on the practicalities of protein expression. However, we respectfully disagree with the characterization of insect cell expression as an inaccessible or economically non-viable platform for toxin research. We offer the following points:

(1) Prevalence and accessibility: Contrary to the suggestion that insect cell expression is restricted to highly specialized labs, the Baculovirus Expression Vector System (BEVS) has become a cornerstone of modern biologics production, structural biology and biochemistry. For instance, our MultiBac system (which is but one of several systems currently widely in use) is utilised by over 1,000 laboratories and institutions, academic and pharma/biotech, worldwide. The maturation of commercially available kits, automated platforms, and standardized protocols has moved this technology into the mainstream, making it a standard tool for any lab requiring high-quality eukaryotic proteins.

(2) Biological necessity: Bacterial (E. coli) and fungal (P. pastoris) systems are widely accessible, however, they appear to be fundamentally incapable of producing functional SVMPs. SVMPs require complex disulfide-bond formation, intricate folding, and N-glycosylation for stability and solubility. Bacterial systems have been widely tried by us and others but typically result in very low expression or misfolded inclusion bodies. Of note, originally, we had invested significant effort to adapt P. pastoris to the production of eukaryotic proteins we are interested in, without success, before moving on to the MultiBac system. The SVMPs that we analysed here are highly cytotoxic, rendering the baculovirus/insect cell system in a way a logical choice given that the cells are no longer 'living' after infection with the baculovirus (but more akin membrane-enveloped bioreactors). Thus, one can make the argument that insect cells represent the most accessible middle ground that provides folding apparatus and necessary post-translational modifications (PTMs) required for biological relevance, and it is possible to produce mg amounts of SVMP proteins per litre cell culture as reported here in our manuscript.

(3) Economic viability and bioprospecting: Regarding the economic argument, we contend that viability in bioprospecting is defined by functional yield rather than simple volume. Producing large quantities of non-functional or misfolded protein in a cheaper system is economically inefficient. Furthermore, for snakebite research, the ability to produce specific, pure isoforms recombinantly without the contamination of other toxic venom components found in native isolations is essential for high-throughput screening and drug design.

(4) Scalability: Historically, insect cell production was seen as expensive, but current bioreactor technology and reduction in consumables and media costs allow for significant scaling. Many therapeutic reagents (vaccines, viral vectors, protein biologics) are produced routinely in baculovirus/insect cells. For the purposes of bioprospecting and lead identification, the yields provided by our Hi5/Sf21 system are sufficient for rigorous downstream bioassays and structural characterization.

Again, I believe the paper is highly important and excellently crafted, but I think especially the discussion should see some refinement to address the drawbacks and to evaluate the paper's findings with more modesty.

Thank you. We included the discussion about glycosylation patterns.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) It is not entirely clear to me if the final constructs are indeed "fusion-proteins" (line 172, 974), in the sense of chimeric proteins. From the current description, it appears that the prodomain is encoded in the same gene rather than fused as a separate domain. Thus, referring to these constructs as fusion proteins may overstate the degree of protein engineering involved in the study.

This is correct. In the revised manuscript, ‘fusion protein’ is only used in the context of the propeptide SVMP fusion construct to avoid confusion.

(2) Figure 2J: It is difficult to assess how much protein is secreted relative to the intracellular amounts. The blot is surely misleading, as the effective protein dilution differs substantially between intracellularly vs. extracellularly. Providing an estimate of the relative dilution of extracellular protein would help clarify the extent of secretion.

We estimate that the SNP and SN fractions are at least 10-times more concentrated than the media fraction. The blot is analytical and not quantitative.

(3) The manuscript appears to use both alphafold 2 and alphafold 3 for structural predictions. Clarification on the choice of the version and its impact on results would improve consistency.

In the revised version of the manuscript, we clarify that all structural models were generated using AlphaFold 3.

(4) Figure S3b and others: a clear description of the antibodies used in the Western blots would be appreciated (including in the methods).

We included this information in the figure legends and a paragraph in the methods section for Western blots in the revised manuscript.

(5) MTT cytotoxicity testing would be more convincing if done in a concentration-dependent manner.

We repeated this assay using different concentrations of SVMPs and show the results as a new Figure 5f in the revised manuscript.

(6) Figure S3c: It could be interesting to show the sequence coverage to get an impression of what part of the protein is there.

We have included this information as Supplementary Figure S4d in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

Overall, the study is presented in a step-by-step manner, and its conclusions are valid.

(1) As suggested in the public review, further characterization of the purified material would be good, for example, by intact mass-spectroscopy to characterize the enzymes in further detail.

Preliminary MALDI-MS analysis (performed in Loic Quinton’s laboratory) of our PIII SVMP revealed a broad and heterogeneous mass distribution, consistent with heterogeneity caused by the presence of multiple glycoforms (which is not unlike the microheterogeneity in native snake venom). However, owing to the inherent limitations of MALDI-MS for the analysis of glycoproteins, our data do not allow determination of the number of occupied N-glycosylation sites or the identification of additional types of glycosylation.

Moreover, the relatively large molecular mass of these proteins (zymogen 70.2 kDa protein only, mature PIII 50.6 kDa protein only) makes analysis by electrospray ionisation mass spectrometry technically challenging.

An MS-based deep analysis of the glycosylation patterns would therefore be a project on its own, and beyond the scope of the present manuscript.

(2) The studies involving PII appear challenging due to low yields and stability of the enzyme and the mentioned self-degradation. Some studies, such as the casein-degradation, would benefit from working with a well-characterized batch of enzymes to ensure, it is not auto-degrading during the experiment.

We believe that the finding that the PII SVMP degrades itself after incubation with Zn²⁺ is an important observation. It is novel to the best of our knowledge. Moreover, the key message of our manuscript is that we can produce and characterise novel SVMPs that cannot be readily purified from venom (and thus are not well characterised).

Besides, there are very few intact PII SVMPs in venom (e.g. Suntravat et al. BMC Molecular Biol 2016); the vast majority cleaves itself into a PI and a disintegrin.

(3) Figure 4h. Degradation of insulin is only shown for recombinant PIII, not the native enzyme, and therefore doesn't convey any information with respect to how well they compare.

We do not have available any native PII and PIII SVMPs for a comparison with the recombinant SVMPs (in our manuscript we show expression of new, uncharacterised SVMPs). We have included the PIII SVMP in the original manuscript to show that the enzyme is active and has a different specificity compared to PI SVMP. In the revised manuscript, we also included the PII SVMP insulin B degradation assay in Supplementary Figure S11b.

(4) Figure 5a. Inconsistent use of enzymes - data for PII is presented (both as mature protein and Zymogen) and compared to PIII, but not PI, as both zymogen and mature protein. The current data presentation is confusing and gives the idea of the manuscript assembled with figures produced during the exploratory phase of the study, and not from subsequent experiments systematically conducted for the purposes of clarity and completeness.

In the revised manuscript, we included the missing enzymatic characterisations in Figure 5 (panel a and e) and Supplementary Figure S11a-c. These data were initially not included because the respective enzymes are inactive in these assays.

(5) The manuscript would benefit from editing to make it more concise. For an early-career reader, it is of interest and utility to follow the thought and experimental processes that led to the successful solution, but there is a risk of losing the reader's interest along the way by going through expression experiments that did not "work" in the typical sense of the word. To this reviewer, there is no added value in a full paragraph around co-expression with disulfide isomerase, as it did not improve the protein yield. A single sentence, "co-expression with PDI did not improve yields," with a reference to a supplemental figure would convey that message.

We have moved the optimisation of SVMP expression to the Supplementary Information, which we hope has improved the clarity and flow of the main text.

We note that the hypothesis that co-expression of protein disulfide isomerases (PDIs) enhances yields of functional SVMPs, given the high expression of PDIs in snake venom gland cells, is well established in the field. While we consider PDIs (and other chaperones) likely to play an important role in SVMP expression, we were unable to demonstrate this effect using the baculovirus-insect cell expression system and hypothesize that efficient insect and/or baculoviral PDIs are already present.

(6) Similarly with N-linked glycosylation, the section needs a headline (line 241) and firming up of a sentence like "and possibly not all of the glycosylation..." which is vague and appears to state that it was not really of interest to pursue this further. My view is that either an experiment is done properly with a stated aim and purpose, interpreted, and then, based on whether the results are of interest to the main story or not, they are included. If N-linked glycosylation is to be included in the manuscript, it should be with a purpose (e.g., N-linked glycosylation affects enzyme activity). As it stands, the message is "there is some N-linked glycosylation" without further explanation, and this generates information without justifying the inclusion hereof.

Please see our reply above regarding an in-depth characterisation of insect cell glycosylation of the recombinant PIII SVMP without access to the native enzyme for comparison. In our revised manuscript, we confirm that the PIII SVMP is glycosylated and that this at least partly accounts for the apparent discrepancy in molecular weight observed in SEC and SDS PAGE. We have modified the text to clarify the purpose of the PNGase deglycosylation experiment.

(7) The manuscript, in its current form, appears to have been copied from a Thesis with very detailed step-by-step logic and description. While this is useful in a scholarly context, a scientific manuscript should be presented more compactly, assuming the readers know basic biochemistry.

We trust that this Reviewer finds the revised version of our manuscript more compact and concise. 

Reviewer #3 (Recommendations for the authors):

(1) Material and Methods plus Figures:

Please report the number of replicates per experiment and how data is presented (means/ medians/ standard deviation/ others), and add error bars to the plots where needed.

In the revised manuscript we have included the number of repeats in the figure legends.

(2) Abstract

Line 4: I would not say that SVMPs are the most potent viper toxins. This place is probably taken by some of the highly neurotoxic PLA2, such as Crotoxin. Nevertheless, SVMPs are surely some of the most important toxins responsible for pathophysiological effects stemming from viper envenoming, but I would suggest rephrasing for accuracy.

In the revised manuscript, we have modified this sentence.

(3) Introduction

Lines 27-31: I would like to see a reference supporting the existence of all SVMP types across vipers.

We have included references supporting the existence of PI, PII and PIII SVMPs in viper venom. We also rewrote the sentence to state that “representatives of all three sub-classes are present in different viper venoms.” This clarifies that we do not say that all classes are present in all venoms.

Lines 59-60: I am not sure if this should be considered such an important impediment. Essentially, many vipers yield double- to triple-digit mg amounts of crude venom per specimen from only a single milking.

We have rewritten this text in the revised manuscript.

Currently, it is not possible to purify any given SVMP of interest from venom; in particular for E. ocellatus SVMP isoform mixtures are typically purified rather than individual enzymes (see also introduction section of our manuscript line 57ff). Also, many SVMPs are not present in sufficient amounts in the venom. Here, we provide an approach to recombinantly produce any SVMP of interest, independent of its abundance in the venom.

(4) Results

Line 102: The army-fallworms name is Spodoptera, not Spotoptera. Please correct the typo.

Done. Apologies for our oversight.

Line 311: Please provide the data at least as a supplement.

In the revised manuscript, we have included this experiment in Supplementary Figure S6c.

Line 432- 433: It would be useful to clarify whether the protein should have a pro-coagulant activity (or not).

We have changed this sentence as follows in the revised manuscript: This shows that our recombinantly produced SVMPs have no pro-coagulant activity, which was unknown before.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) The pathogenic mechanism of the E182STOP variant is unclear. The mutant protein does not appear to affect WT protein localization, arguing against a dominant-negative effect. Yet, overexpression of HSD17B7-E182* alone causes toxicity in zebrafish and mislocalizes cholesterol in HEI-OC1 cells, suggesting a gain-of-function or toxic effect. In addition, the variant mRNA is expressed at a low level, consistent with nonsense-mediated decay. This apparent complexity and inconsistency need clearer explanation.

We appreciate the reviewer’s careful evaluation of this mechanistic complexity. Based on our combined molecular, cellular, and in vivo data, we propose that the pathogenic effect of the HSD17B7-E182* variant reflects a composite mechanism, rather than a classical dominant-negative effect.

At the transcript level, the E182* variant introduces a premature termination codon and shows markedly reduced mRNA abundance, consistent with partial degradation by nonsense-mediated mRNA decay. This reduction is expected to decrease overall HSD17B7 dosage, contributing a loss-of-function component. Unlike HSD17B7, the truncated HSD17B7^E182* mislocalizes cholesterol in HEI-OC1 cells, and overexpression alone reduces hair cell MET function and startle response in zebrafish embryos. We therefore propose that the truncated protein disturbing local cholesterol homeostasis, thereby exerts a toxic or ectopic gain-of-function.

We have revised the manuscript to clarify the dual-mechanism model.

(2) The link to human deafness is based on a single heterozygous patient with no syndromic features. Given that nearly all known cholesterol metabolism disorders are syndromic, this raises concerns about causality or specificity. The term "novel deafness gene" is premature without additional cases or segregation data.

We thank the reviewer for this important point. We fully agree that, based on a single heterozygous case without segregation data, it is premature to designate HSD17B7 as a novel deafness gene. Therefore, we have revised the manuscript to use the description of "candidate deafness genes".

(3) The localization of HSD17B7 should be clarified better: In HEI-OC1 cells, HSD17B7 localizes to the ER, as expected. In mouse hair cells, the staining pattern is cytosolic and almost perfectly overlaps with the hair cell marker used, Myo7a. This needs to be discussed. Without KO tissue, HSD17B7 antibody specificity remains uncertain.

We thank the reviewer for the constructive comments regarding HSD17B7 localization and antibody specificity.

Regarding subcellular localization, the original Figure 1K was intended to demonstrate the expression of HSD17B7 in mouse hair cells. To address this concern, we performed additional immunostaining on dissected organ of Corti sections at P1, P4, and P7 using higher magnification. Using parvalbumin as a hair cell marker, HSD17B7 displayed a partially punctate intracellular pattern in hair cells (revised Figure 1K). This pattern is consistent with localization to membrane-associated compartments, including the endoplasmic reticulum, and agrees with the ER-associated localization observed in HEI-OC1 cells and zebrafish hair cells. In mature hair cells, ER-associated signals may appear cytosolic and overlap with general hair cell markers such as Myo7a.

Regarding antibody specificity, although HSD17B7 knockout tissue was not available, we performed complementary validation experiments in HEI-OC1 cells. Cells were transfected with pCMV-Flag, pCMV-Flag-hHSD17B7WT, or pCMV-hHSD17B7WT-EGFP constructs and stained with anti-Flag, anti-EGFP, and anti-HSD17B7 antibodies. The HSD17B7 antibody signal showed strong co-localization with both FLAG- and EGFP-tagged HSD17B7 (revised Figure S1A and B), supporting its specificity.

Reviewer #2 (Public review):

(1) The statement that HSD17B7 is "highly" expressed in sensory hair cells in mice and zebrafish seems incorrect for zebrafish:

(a) The data do not support the notion that HSB17B7 is "highly expressed" in zebrafish. Compared to other genes (TMC1, TMIE, and others), the HSB17B7 level of expression in neuromast hair cells is low (Figure 1F), and by extension (Figure 1C), also in all hair cells. This interpretation is in line with the weak detection of an mRNA signal by ISH (Figure 1G I"). On this note, the staining reported in I" does not seem to label the cytoplasm of neuromast hair cells. An antisense probe control, along with a positive control (such as TMC1 or another), is necessary to interpret the ISH signal in the neuromast.

We thank the reviewer for this detailed evaluation and agree that the description of HSD17B7 expression in zebrafish hair cells requires clarification.

To address this, we performed a quantitative comparison of average expression levels within neuromast hair cells using log-normalized single-cell RNA-seq data. This analysis shows that hsd17b7 is expressed at a level comparable to several known MET-associated genes (e.g., tmc1 and lhfpl5a) (revised Figure 1D). Regarding the pseudotime heatmap (Figure 1F), we now state that this analysis illustrates temporal expression dynamics within neuromast hair cell development.

In addition, we have clarified the interpretation of the whole-mount in situ hybridization data by emphasizing that the signal indicates spatial enrichment rather than high transcript abundance.

We have updated the figure panels, legends, and corresponding text in the Results section to reflect these changes.

(b) However, this is correct for mouse cochlear hair cells, based on single-cell RNA-seq published databases and immunostaining performed in the study. However, the specificity of the anti-HSD17B7 antibody used in the study (in immunostaining and western blot) is not demonstrated. Additionally, it stains some supporting cells or nerve terminals. Was that expression expected?

To assess antibody specificity, we performed validation experiments using distinct epitopes. In HEI-OC1 cells transfected with pCMV-Flag-HSD17B7, or pCMV-HSD17B7-EGFP constructs, immunostaining with anti-HSD17B7 showed strong co-localization with both FLAG- and EGFP-tag (revised Figure S1B). In addition, western blot analyses using the same constructs confirmed the specific detection of HSD17B7 protein (revised Figure S1B). These validation data have now been included as supplementary figures in the revised manuscript and provide independent supporting evidence for the specificity of the anti-HSD17B7 antibody.

(2) A previous report showed that HSD17B7 is expressed in mouse vestibular hair cells by single-cell RNAseq and immunostaining in mice, but it is not cited: Spatiotemporal dynamics of inner ear sensory and non-sensory cells revealed by single-cell transcriptomics. Jan TA, Eltawil Y, Ling AH, Chen L, Ellwanger DC, Heller S, Cheng AG. Cell Rep. 2021 Jul 13;36(2):109358. doi: 10.1016/j.celrep.2021.109358.

We have now cited this reference in the revised manuscript.

(3) Overexpressed HSD17B7-EGFP C-terminal fusion in zebrafish hair cells shows a punctiform signal in the soma but apparently does not stain the hair bundles. One limitation is the consequence of the C-terminal EGFP fusion to HSD17B7 on its function, which is not discussed.

We thank the reviewer for raising this important technical point. The apparent absence of an HSD17B7-EGFP signal in hair bundles is primarily due to the imaging strategy and the selection of representative images. In zebrafish hair cells, the EGFP signal within hair bundles is extremely strong. To better visualize the intracellular distribution of HSD17B7 within the hair cell soma, we selected representative confocal optical sections that were focused on the cell body rather than on the apical hair bundle plane. As a result, the hair bundle signal is not visible in the images shown.

Importantly, we agree that C-terminal EGFP fusion may potentially influence protein localization or function. We have therefore revised the Discussion to discuss this limitation and to clarify that our central conclusions regarding HSD17B7 function are primarily supported by loss-of-function analyses, rescue experiments using untagged mRNA, and cholesterol perturbation phenotypes, rather than relying solely on EGFP-tagged overexpression constructs.

(4) A mutant Zebrafish CRISPR was generated, leading to a truncation after the first 96 aa out of the 340 aa total. It is unclear why the gene editing was not done closer to the ATG. This allele may conserve some function, which is not discussed.

Targeting regions close to the ATG is indeed a commonly used strategy for CRISPR-mediated gene disruption. In this study, sgRNA selection was guided by online CRISPR design tools (CRISPRscan), prioritizing predicted cutting efficiency and specificity. This strategy resulted in a frameshift mutation introducing a premature stop codon after amino acid 96 of the 340-aa Hsd17b7 protein.

Importantly, this truncation removes most of the conserved catalytic core required for 17β-hydroxysteroid dehydrogenase activity, including key motifs involved in NAD(P)-binding and substrate recognition. Therefore, although the mutation does not occur immediately adjacent to the ATG, the resulting allele is predicted to lack enzymatic function. We have clarified this rationale and discussed the functional consequences of the truncation in the revised manuscript.

(5) The hsd17b7 mutant allele has a slightly reduced number of genetically labeled hair cells (quantified as a 16% reduction, estimated at 1-2 HC of the 9 HC present per neuromast). On a note, it is unclear what criteria were used to select HC in the picture. Some Brn3C:mGFP positive cells are apparently not included in the quantifications (Figure 2F, Figure 5A).

Upon re-evaluation, we recognized that the original figure annotations were not sufficiently clear and may have led to confusion regarding hair cell selection. In the original images, the absence of dashed outlines around some Brn3c:mGFP⁺ cells may have been misinterpreted as their exclusion from analysis. To address this issue, we have revised Figures 2F and 5A by updating the annotations to ensure that all Brn3c:mGFP⁺ hair cells within each neuromast are clearly visible and unambiguously included (revised Figures 2F and 6A). Corresponding figure legends have also been revised to clarify the criteria used for hair cell identification and quantification.

(6) The authors used FM4-64 staining to evaluate the hair cell mechanotransduction activity indirectly. They found a 40% reduction in labeling intensity in the HCs of the lateral line neuromast. Because the reduction of hair cell number (16%) is inferior to the reduction of FM4-64 staining, the authors argue that it indicates that the defect is primarily affecting the mechanotransduction function rather than the number of HCs. This argument is insufficient. Indeed, a scenario could be that some HC cells died and have been eliminated, while others are also engaged in this path and no longer perform the MET function. The numbers would then match. If single-cell staining can be resolved, one could determine the FM4-64 intensity per cell. It would also be informative to evaluate the potential occurrence of cell death in this mutant. On another note, the current quantification of the FM4-64 fluorescence intensity and its normalization are not described in the methods. More importantly, an independent and more direct experimental assay is needed to confirm this point. For example, using a GCaMP6-T2A-RFP allele for Ca2+ imaging and signal normalization. 

We have revised the FM4-64 quantification strategy. Instead of measuring fluorescence intensity at the neuromast level, FM4-64 uptake was re-quantified at the single hair cell level. Hair cells within each neuromast were identified based on mGFP labeling, and the mean FM4-64 fluorescence intensity was measured for each individual hair cell. The average FM4-64 intensity per hair cell was then calculated for each neuromast and used for group comparisons (revised Figures 2F, 6B, and 8B, Figure S5B). The updated quantification method, normalization procedure, and analysis pipeline have now been described in the revised Methods section.

As supportive evidence, we further analyzed single-cell RNA-seq data from control and hsd17b7 mutant hair cells (revised Figure 3). This analysis revealed dysregulation of multiple genes involved in the MET machinery, including reduced expression of tip-link–associated components and altered expression of other MET-related genes. While these transcriptional changes do not constitute a direct functional assay, they are consistent with perturbation of MET-associated pathways and complement the FM4-64 findings.

(7) The authors used an acoustic startle response to elicit a behavioral response from the larvae and evaluate the "auditory response". They found a significative decrease in the response (movement trajectory, swimming velocity, distance) in the hsd17b7 mutant. The authors conclude that this gene is crucial for the "auditory function in zebrafish".

This is an overstatement:

(a) First, this test is adequate as a screening tool to identify animals that have lost completely the behavioral response to this acoustic and vibrational stimulation, which also involves a motor response. However, additional tests are required to confirm an auditory origin of the defect, such as Auditory Evoked Potential recordings, or for the vestibular function, the Vestibulo-Ocular Reflex. 

We thank the reviewer for highlighting the limitations in interpreting the acoustic startle assay. We have revised the manuscript to avoid overstatement and now describe the observed phenotype as a reduction in the behavioral response to acoustic and vibrational stimulation, rather than concluding a specific impairment of auditory function.

(b) Secondly, the behavioral defects observed in the mutant compared to the control are significantly different, but the differences are slight, contained within the Standard Deviation (20% for velocity, 25% for distance). To this point, the Figure 2 B and C plots are misleading because their y-axis do not start at 0.

We have corrected Figures 2B and 2C so that the y-axes start at zero, thereby providing a more transparent visualization of the behavioral differences. The figure legends have also been revised to clarify the presentation of the data.

(8) Overexpression of HSD17B7 in cell line HEI-OC1 apparently "significantly increases" the intensity of cholesterol-related signal using a genetically encoded fluorescent sensor (D4H-mCherry). However, the description of this quantification (per cell or per surface area) and the normalization of the fluorescent signal are not provided. 

The quantification of the D4H-mCherry signal in HEI-OC1 cells was performed at the single-cell level. Specifically, individual cells were segmented based on morphology, and the mean fluorescence intensity of D4H-mCherry per cell was measured. To account for variability in cell size and imaging conditions, fluorescence intensity was normalized to the background signal measured from cell-free regions in the same field of view. We have now clarified the quantification strategy and normalization procedure in the revised Methods and Results sections.

(9) When this experiment is conducted in vivo in zebrafish, a reduction in the "DH4 relative intensity" is detected (same issue with the absence of a detailed method description). However, as the difference is smaller than the standard deviation, this raises questions about the biological relevance of this result.

We have now clarified the quantification strategy and normalization procedure in the revised Methods and Results sections.

(10) The authors identified a deaf child as a carrier of a nonsense mutation in HSB17B7, which is predicted to terminate the HSB17B7 protein before the transmembrane domain. However, as no genetic linkage is possible, the causality is not demonstrated.

We thank the reviewer for raising this important point. Unfortunately, we were unable to obtain the parents' genetic testing data to perform formal genetic and linkage analysis. To address this limitation, we have revised the manuscript to avoid causal overstatement and now describe the HSD17B7 E182* variant as a candidate pathogenic variant associated with hearing loss. Importantly, our functional analyses in zebrafish and cell-based systems demonstrate that the E182* truncation abolishes key biological activities of HSD17B7, including subcellular localization, cholesterol regulation, mechanotransduction-related activity, and behavioral responses. These convergent functional data provide biological support for the potential pathogenic relevance of this variant.

(11) Previous results obtained from mouse HSD17B7-KO (citation below) are not described in sufficient detail. This is critical because, in this paper, the mouse loss-of-function of HSD17B7 is embryonically lethal, whereas no apparent phenotype was reported in heterozygotes, which are viable and fertile. Therefore, it seems unlikely that heterozygous mice exhibit hearing loss or vestibular defects; however, it would be essential to verify this to support the notion that the truncated allele found in one patient is causal.

Hydroxysteroid (17beta) dehydrogenase 7 activity is essential for fetal de novo cholesterol synthesis and for neuroectodermal survival and cardiovascular differentiation in early mouse embryos.

Jokela H, Rantakari P, Lamminen T, Strauss L, Ola R, Mutka AL, Gylling H, Miettinen T,

Pakarinen P, Sainio K, Poutanen M. Endocrinology. 2010 Apr;151(4):1884-92. doi: 10.1210/en.2009-0928. Epub 2010 Feb 25.

We thank the reviewer for raising this important point. We acknowledge that previous work has shown that complete loss of Hsd17b7 in mice is embryonically lethal, whereas heterozygous animals are viable and fertile (Jokela et al., 2010). Notably, this study primarily focused on embryonic development, cholesterol metabolism, and cardiovascular and neuroectodermal survival, and auditory or vestibular functions were not specifically examined. Therefore, subtle or sensory organ–specific phenotypes in heterozygous mice cannot be excluded.

The human variant identified in this study (E182*) is a nonsense mutation predicted to truncate the HSD17B7 protein prior to the transmembrane and cytoplasmic domains. We therefore present it as a candidate loss-of-function variant, providing supportive human genetic evidence that is consistent with our functional analyses in zebrafish hair cells, rather than as definitive proof of causality. We have revised the manuscript to clarify these points and to acknowledge this limitation.

(12) The authors used this truncated protein in their startle response and FM4-64 assays. First, they show that contrary to the WT version, this truncated form cannot rescue their phenotypes when overexpressed. Secondly, they tested whether this truncated protein could recapitulate the startle reflex and FM4-64 phenotypes of the mutant allele. At the homozygous level (not mentioned by the way), it can apparently do so to a lesser degree than the previous mutant. Again, the differences are within the Standard Deviation of the averages. The authors conclude that this mutation found in humans has a "negative effect" on hearing, which is again not supported by the data. 

We thank the reviewer for this important comment. We agree that the overexpression strategy employed in this study does not fully replicate the endogenous heterozygous state observed in patients, and that the magnitude of the observed effects varies across samples. Accordingly, our experiments were not intended to demonstrate a definitive causal role of the HSD17B7 ^E182* variant in hearing loss.

Instead, the overexpression assays were designed to assess whether the truncated HSD17B7 protein displays abnormal cellular properties and whether its presence can interfere with processes relevant to hair cell function. Under these conditions, HSD17B7^E182* exhibited aberrant subcellular localization, altered intracellular cholesterol distribution, and was associated with reduced FM4-64 uptake and changes in startle-associated behaviors, whereas the wild-type protein did not.

We revised the manuscript to moderate our conclusions. Rather than claim that the E182* mutation has a definitive “negative effect on auditory function,” we now describe it as a functionally compromised allele that disrupts cholesterol distribution and MET-related activity under overexpression conditions, providing mechanistic support consistent with our zebrafish loss-of-function data and the identification of this variant in a patient with hearing loss. In addition, the "negative effect" statement was based on the result that overexpression of the E182* mutation in wild-type embryos caused the compromised MET function and startle response defect.

(13) The authors looked at the distribution of the HSB17B7 in a cell line. The WT version goes to the ER, while the truncated one forms aggregates. An interesting experiment consisted of co-expressing both constructs (Figure S6) to see whether the truncated version would mislocalize the WT version, which could be a mechanism for a dominant phenotype. However, this is not the case.

We thank the reviewer for raising this important point regarding a potential dominant-negative mechanism. Consistent with the reviewer’s interpretation, we found that HSD17B7^WT predominantly localizes to the endoplasmic reticulum, whereas the truncated HSD17B7^E182* protein forms intracellular aggregates. Importantly, we further observed that the E182* mutation markedly reduces the stability of both HSD17B7 mRNA and protein, resulting in substantially decreased abundance of the truncated protein (Figure S6B–E). As a consequence, the cellular levels of HSD17B7^E182* are abnormally low.

Based on these findings, we consider it unlikely that the E182* variant exerts its effect through interference with the wild-type protein. Our results suggest that the heterozygous c.544G>T (p.E182*) variant contributes to auditory dysfunction through potential pathogenic mechanisms: 1, haploinsufficiency caused by reduced HSD17B7 expression, 2, functional impairment due to altered protein subcellular localization and cholesterol distribution.

We have revised the Results and Discussion sections. Our conclusions now emphasize that the functional impact of this variant is attributable to decreased effective HSD17B7 dosage, consistent with the observed defects in cholesterol synthesis, MET-related activity, and auditory-associated phenotypes in our model.

(14) Through mass spectrometry of HSB17B7 proteins in the cell line, they identified a protein involved in ER retention, RER1. By biochemistry and in a cell line, they show that truncated HSB17B7 prevents the interaction with RER1, which would explain the subcellular localization.

Consistent with the reviewer’s interpretation, wild-type HSD17B7 interacts with RER1, a protein known to participate in ER retention, whereas this interaction is lost in the truncated HSD17B7 variant. We propose that RER1 is an interacting partner of HSD17B7, providing a mechanistic explanation for the protein's subcellular localization.

(15) Information and specificity validation of the HSB17B7 antibody are not presented. It seems that it is the same used on mice by IF and on zebrafish by Western. If so, the antibody could be used on zebrafish by IF to localize the endogenous protein (not overexpression as done here). Secondly, the specificity of the antibody should be verified on the mutant allele. That would bring confidence that the staining on the mouse is likely specific.

We thank the reviewer for raising this important point regarding antibody specificity and validation. Information on the HSD17B7 antibody and its validation has been provided in our response to comment 1, where we described the use of antibodies recognizing different epitopes and the experimental strategies employed to assess specificity (revised Figure S1A and B).

Although the same antibody was used for Western blot analysis in zebrafish samples, its performance in immunofluorescence staining of zebrafish tissues was suboptimal, with relatively high background. For this reason, we did not rely on this antibody for endogenous Hsd17b7 localization in zebrafish by immunofluorescence and instead employed tagged constructs for subcellular localization analyses. This approach provides more reliable and interpretable localization information under the current experimental conditions.

Recommendations for the authors:

Reviewing Editor Comments:

Suggested revisions to help improve the study and the eLife Assessment:

(1) FM4-64 uptake: Isolate the effect of hair cell loss and MET reduction.

(2) Clarify the mechanistic model: Is the mutant protein pathogenic due to toxicity, lack of expression or function, or both? Come up with a clearer causal chain of events.

(3) Mouse immunostaining: Validate the HSD17B7 antibody, and since mouse RNAseq data (gEAR database) suggest that HSD17B7 expression increases dramatically between P0-P5, show this developmental progression by immunostaining of the mouse organ of Corti at P0, P3, and P5.

(4) The HSD17B7-E182* expression disrupts cholesterol (D4H staining) in OC1 cells. This should also be demonstrated in the mutant zebrafish.

(5) Structural modeling of E182* is uninformative; half the protein is absent. This kind of analysis is better suited for missense variants. Suggest removing this analysis.

We thank the Reviewing Editor for these constructive suggestions. The major points raised here substantially overlap with the concerns raised in the public reviews. In response, we have:

(1) revised FM4-64 quantification and interpretation to better distinguish hair cell loss from MET impairment;

(2) Clarify the mechanistic mode. Mechanistically, the mutation decreases mRNA abundance and significantly reduces protein levels. Moreover, expression of the p.E182* mutation disrupted the interaction between HSD17B7 and the ER retention receptor RER1, leading to aberrant subcellular localization and altered cholesterol distribution, thereby exacerbating HC dysfunction.

(3) provided additional validation of the HSD17B7 antibody using antibodies targeting distinct epitopes, and extended mouse organ of Corti immunostaining to postnatal stages P1, P4, and P7 to demonstrate the developmental upregulation of HSD17B7 expression;

(4) added in vivo zebrafish experiments demonstrating that expression of HSD17B7^E182* disrupts cholesterol distribution in hair cells, consistent with the effects observed in HEI-OC1 cells using D4H staining;

(5) removed the structural modeling of the E182* variant.

Recommendations for the authors:

The recommendations from Reviewer #1 and Reviewer #2 were carefully considered and addressed. Most of these points overlap with the public reviews and the Reviewing Editor's comments and have been addressed through a revised mechanistic interpretation, additional clarifications in the Methods, more moderate claims regarding auditory function and human genetics, and the removal or revision of potentially misleading analyses. In addition, a number of minor issues were corrected, including missing or incorrect references, repetitive or unclear statements in the Introduction, insufficient methodological details, imprecise terminology, and typographical or formatting errors. Collectively, these revisions improve the clarity, rigor, and transparency of the study without altering its central conclusions.

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Reviewer #1 (Public review):

Summary:

This study examines the role of the long non-coding RNA Dreg1 in regulating Gata3 expression and ILC2 development. Using Dreg1 deficient mice, the authors show a selective loss of ILC2s but not T or NK cells, suggesting a lineage-specific requirement for Dreg1. By integrating public chromatin and TF-binding datasets, they propose a Tcf1-Dreg1-Gata3 regulatory axis. The topic is relevant for understanding epigenetic regulation of ILC differentiation.

Strengths:

(1) Clear in vivo evidence for a lineage-specific role of Dreg1.

(2) Comprehensive integration of genomic datasets.

(3) Cross-species comparison linking mouse and human regulatory regions.

Weaknesses:

(1) Mechanistic conclusions remain correlative, relying on public data.

(2) Lack of direct chromatin or transcriptional validation of Tcf1-mediated regulation.

(3) Human enhancer function is not experimentally confirmed.

(4) Insufficient methodological detail and limited mechanistic discussion.

Comments on revisions:

The authors have provided clear evidence that Dreg1 is necessary for ILC2 development, but their refusal to perform any mechanistic experiment remains a significant weakness. While their appeal to the 3Rs and the use of public datasets is noted, re-analyzing external data from heterogeneous sources cannot substitute for direct, internal validation of the Tcf1-Dreg1-Gata3 axis in their specific knockout model. This is particularly problematic because ILC2 progenitors, though rare, can be isolated from bone marrow, especially since assays like CUT&Tag and others are specifically designed for low cell numbers. By relying on public T-cell CRISPR screens to justify human ILC2 functions, the authors are substituting cross-cell-type correlation for definitive functional proof. Consequently, the manuscript currently describes a discovery of necessity without providing a verified molecular mechanism, which should be more explicitly reflected in the title and conclusions.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study examines the role of the long non-coding RNA Dreg1 in regulating Gata3 expression and ILC2 development. Using Dreg1-deficient mice, the authors show a selective loss of ILC2s but not T or NK cells, suggesting a lineage-specific requirement for Dreg1. By integrating public chromatin and TF-binding datasets, they propose a Tcf1-Dreg1-Gata3 regulatory axis. The topic is relevant for understanding epigenetic regulation of ILC differentiation.

Strengths:

(1) Clear in vivo evidence for a lineage-specific role of Dreg1.

(2) Comprehensive integration of genomic datasets.

(3) Cross-species comparison linking mouse and human regulatory regions.

Weaknesses:

(1) Mechanistic conclusions remain correlative, relying on public data.

We agree that the mechanistic conclusions are of our study are indeed correlative and we mention this in the discussion. The primary work of the study is the discovery of Dreg1's necessity for ILC2 development via the new knockout mouse model. Re-analysing good quality publicly available data on rare cell populations is an appropriate approach and in line with DORA guidelines for ethical research.

(2) Lack of direct chromatin or transcriptional validation of Tcf1-mediated regulation.

The most appropriate way to examine direct Tcf1 target genes in primary cells is to examine the association of Tcf1 binding with the changes that occur in Tcf1-bound genes after Tcf7 knockout. By analysing publicly available data on ILC progenitors we indeed did this. We revealed that Tcf1 bound to Dreg1 and that Dreg1 was not expressed when Tcf1 was knocked out in ILC progenitors. In addition we examined H3K27ac at the Dreg1 locus in the same ILC progenitors to demonstrate that Tcf1 appears to be important for decorating the Dreg1 gene with this histone modification. We believe that this analysis is sufficient to conclude that Tcf1 is required for the expression of Dreg1 in ILC progenitors.

(3) Human enhancer function is not experimentally confirmed.

We agree that the potential human enhancer of GATA3 we identified has not been confirmed in human ILC. However, a previous study showed clear evidence that this region has GATA3 enhancer activity in human T cells. Therefore, while not specific to ILC2s the region where the DREG1 homologues lie does indeed harbour enhancer activity.

(4) Insufficient methodological detail and limited mechanistic discussion.

We have now made the changes suggested by the reviewer to both the methods/figure legends and also the discussion.

Reviewer #1 (Recommendations for the authors):

The authors generated Dreg1-deficient mice and demonstrated that loss of this locus selectively reduces ILC2s but not T or NK cells, indicating a lineage-specific requirement for Dreg1 in ILC development. By analyzing publicly available chromatin accessibility and transcription factor-binding datasets, they link Dreg1 expression to Tcf1-dependent chromatin activation and extend their findings to human data by identifying a syntenic GATA3 enhancer that produces homologous Dreg lncRNAs in ILC2s. While the study addresses an interesting question, most of the mechanistic interpretations rely heavily on publicly available datasets rather than the authors' own functional evidence. To establish causality and reinforce the overall conclusions, I provide below some comments and suggestions for additional experiments and clarifications that would considerably strengthen the manuscript.

(1) In Figure 3, the authors use public datasets to argue that Tcf1 regulates Dreg1 expression by modulating chromatin accessibility and H3K27ac at its locus. However, since these data are derived from heterogeneous external sources, the conclusions remain associative. To better support causality, the authors should generate matched datasets from their own sorted progenitor populations and perform CUT&Tag for Tcf1 and H3K27ac in wild-type and Tcf7 knockout progenitors to directly test whether Tcf1 binding establishes an active chromatin state at Dreg1. Also, complementing this with nascent RNA or pre-mRNA quantification would link chromatin activation to transcriptional output. These experiments are technically feasible in progenitors and would substantially strengthen the claim that Tcf1 directly drives Dreg1 activation during ILC development.

We believe that utilising publicly available data sufficiently answers this question while also adhering to ethical considerations. The ILC populations used to produce the publicly available data were akin to those we examined in our analyses, and the data was of sufficient quality. Moreover, they enable us to access data from Tcf1-deficient mice. Redoing large-scale chromatin profiling on rare cell types would require hundreds of mice to achieve sufficient cell numbers. Repeating this solely for “originality” contradicts the 3Rs principles (replacement, reduction, refinement) if high quality public data already exists and we feel will require years of redundant work. In addition, we believe the fact that the data derive from heterogenous external sources, yet align well, only strengthen our conclusions. We have now added mention to our use of publicly available data in the discussion.

(2) In Figure 4, the authors provide correlative evidence from public datasets suggesting that the human region syntenic to the murine Dreg1 locus acts as a distal enhancer of GATA3 and gives rise to two ILC2-specific lncRNAs. To substantiate this claim, the authors should perform CUT&Tag for H3K27ac in human ILC2s to confirm enhancer activation and use 3C or HiChIP to demonstrate physical interaction with the GATA3 promoter. These experiments should be doable by fusing pooled ILC2 samples and would provide more direct evidence that this region actively regulates GATA3 expression.

Assessing the activity of a distal enhancer region on its target gene in primary human cells is extremely difficult, due to a number of technical and biological complications such as enhancer redundancy. This is why we chose to reanalyse an extensive enhancer deletion screen performed in human T cells by Chen et al., AJHG 2023. This analysis clearly showed deletion of the region we identified as harbouring Dreg1 homologues affected GATA3 expression, thus confirming its enhancer activity. While we agree with the reviewer that specific profiling of human ILC populations for H3K27ac and 3D genome architecture would provide further correlative evidence this will be a time-consuming and costly endevour with human material and ultimately the definitive proof in ILCs would require specific deletion of this region in ILC2s. We have mentioned this caveat in the discussion.

(3) Several figure legends lack essential methodological details. Figure 1 should specify how NK and ILC populations were gated, including intermediate steps and markers used. The same applies to Supplementary Figure 1, and particularly to Supplementary Figure 2, where gating strategies for progenitors are shown but not explained. Figure 2 should also indicate that these analyses were performed in bone marrow. Clearer legends are crucial for interpreting and reproducing the data.

We have made the suggested changes.

(4) It is also unclear throughout the manuscript whether the authors performed any ATACseq experiments themselves or relied entirely on public datasets. This information should be stated explicitly in the main text and figure legends, not only in the Methods section. Similarly, the source of the ChIPseq or CUT&Run datasets should be clearly indicated alongside the relevant figures.

We apologise for not making this clearer and have now clearly articulated if the data was public in the text.

(5) As the authors themselves suggest, performing experiments that selectively suppress Dreg1 transcription using antisense oligonucleotides or CRISPR interference at the Dreg1 promoter would provide more valuable mechanistic insights. Conducting these experiments in their own system would allow them to determine whether Dreg1 functions through its RNA product or as a DNA enhancer element, thereby strengthening the causal link between Dreg1 activity and Gata3 regulation.

We agree with the reviewer, however, this, in our opinion is beyond the scope of this manuscript. The strength of this manuscript lies in the findings from the novel Dreg1 knockout mouse strain. Future studies will focus on understanding how Dreg1 influences Gata3 expression.

(6) The discussion would benefit from a clearer and more integrated explanation of how Dreg1 fits into the transcriptional network that controls ILC2 differentiation. The authors could elaborate on whether Dreg1 fine-tunes Gata3 expression or functions as part of a regulatory loop with Tcf1, and better explain how this mechanism might be conserved in humans. In addition, the authors should explicitly acknowledge the limitations of relying on publicly available datasets and emphasize the need for direct experimental validation to support their mechanistic interpretation.

We have now made these suggested inclusions.

Reviewer #2 (Public review):

The authors investigate the role of the long non-coding RNA Dreg1 for the development, differentiation, or maintenance of group 2 ILC (ILC2). Dreg1 is encoded close to the Gata3 locus, a transcription factor implicated in the differentiation of T cells and ILC, and in particular of type 2 immune cells (i.e., Th2 cells and ILC2). The center of the paper is the generation of a Dreg1-deficient mouse. While Dreg1-/- mice did not show any profound ab T or gd T cell, ILC1, ILC3, and NK cell phenotypes, ILC2 frequencies were reduced in various organs tested (small intestine, lung, visceral adipose tissue). In the bone marrow, immature ILC2 or ILC2 progenitors were reduced, whereas a common ILC progenitor was overrepresented, suggesting a differentiation block. Using ATAC-seq, the authors find that the promoter of Dreg1 is open in early lymphoid progenitors, and the acquisition of chromatin accessibility downstream correlates with increased Dreg1 expression in ILC2 progenitors. Examining publicly available Tcf1 CUT&Run data, they find that Tcf1 was specifically bound to the accessible sites of the Dreg1 locus in early innate lymphoid progenitors. Finally, the syntenic region in the human genome contains two non-coding RNA genes with an expression pattern resembling mouse Dreg1.

The topic of the manuscript is interesting. However, there are various limitations that are summarized below.

(1) The authors generated a new mouse model. The strategy should be better described, including the genetic background of the initially microinjected material. How many generations was the targeted offspring backcrossed to C57BL/6J?

The mice were backcrossed for at least 2 generations to C57BL/6. This information is now included in the methods section.

(2) The data is obtained from mice in which the Dreg1 gene is deleted in all cells. A cell-intrinsic role of Dreg1 in ILC2 has not been demonstrated. It should be shown that Dreg1 is required in ILC2 and their progenitors.

We now provide new mixed bone marrow irradiation chimera data that shows that the effect is intrinsic to Dreg1-deficient ILC2 cells (Figure 1F and Supplementary Figure 1E-G).

(3) The data on how Dreg1 contributes to the differentiation and or maintenance of ILC2 is not addressed at a very definitive level. Does Dreg1 affect Gata3 expression, mRNA stability, or turnover in ILC2? Previous work of the authors indicated that knockdown of Dreg1 does not affect Gata3 expression (PMID: 32970351).

We have indeed shown that Dreg1-deficient ILC2P have reduced levels of Gata3 (Figure 2H) however we have not determined the exact mechanisms by which Dreg1 controls ILC2 development.

(4) How Dreg1 exactly affects ILC2 differentiation remains unclear.

We agree with the reviewer, however, this article is focused on the first description of the Dreg1 knockout mice and the surprisingly specific effect on ILC2 development.

Reviewer #2 (Recommendations for the authors):

(1) Relating to point 2 of public review:

It should be shown that Dreg1 is required in ILC2 and their progenitors. Mixed bone marrow chimeras would be an adequate strategy.

We have now done this and clearly showed that the effect is intrinsic to Dreg1-deficient ILC2s.

(2) Relating to point 3 of public review:

Minimally, Gata3 expression should be analyzed in ILC2, ILC2P, and the ILC progenitors by qRT-PCR and antibody stain.

We have indeed shown reduced Gata3 levels by antibody stain in Figure 2H.

(3) Relating to point 4 of public review:

The manuscript would benefit from additional data studying ILC2 differentiation in (competitive) adoptive transfer experiments or using in vitro differentiation assays.

We have performed the mixed bone marrow chimera experiments which are testing the competitiveness of Dreg1-deficient bone barrow with control wildtype. In this case the WT ILC2s outcompeted the Dreg1-deficient ILC2s for the same niche.

Author response:

[These author responses are to reviews from another journal.]

Reviewer #1:

This manuscript investigates the behaviour of a variety of clock proteins in cultured cells when epitope tagged and transiently expressed and try to draw general implications for endogenous function of circadian clock proteins.

Clock proteins are expressed at low levels in most cells, and so the clock interacting proteins (other kinases, phosphatases, ubiquitin-conjugated enzymes, etc.) are likewise probably at low abundance. Over-expression of one or two or even three components of a multicomponent system is going to produce odd and obscure non-physiological imbalances. The authors do not extend detailed study of these imbalances to more physiologic levels so the importance of their observations to clock function is not clear, and importantly, they are not tested in more biologically relevant models.

To study the function of components within a system, the steady state must be perturbed in one way or another. This can be achieved through pharmacological treatment, mutagenesis, downregulation, or overexpression. Such interventions are inherently non-physiological, and the relevance of the resulting observations must therefore be carefully validated.

In our study, the purpose of PER2 overexpression was to investigate its subcellular dynamics in the absence and presence of CRYs, specifically CRY1. This is far less trivial than it might appear at first glance, because our data clearly show that PER2 overexpression triggers, within 24 h, the accumulation of endogenous CRY1 (Fig. 1A), due to PER2-mediated stabilization of CRY1 (Fig. 4). PER2 overexpression also induces the accumulation of endogenous PER1, CK1, and BMAL1 (Fig. 2).

This effect was not considered in previous studies, such as Yagita et al. (2002), in which PER2 subcellular localization was assessed at a single time point following transient transfection. Yagita et al. found roughly equal proportions of cells with PER2 exclusively in the nucleus, exclusively in the cytoplasm, or distributed between both compartments. Such extreme cell-to-cell variability cannot be explained solely by PER2’s shuttling dynamics, as that would imply synchronous export in one cell and synchronous import in another.

Our time-resolved analysis of DOX-induced PER2 expression strongly suggests that the variability reported by Yagita et al. reflects a heterogeneous population of unsynchronized cells at different temporal stages along a trajectory from cytoplasmic PER2 (unbound) to nuclear PER2 fully saturated with CRYs (bound), owing to stabilization of endogenous CRYs. Similarly, Öllinger et al. (2014) analyzed PER2 nuclear export in cells constitutively expressing PER2-Dendra. Under such steady-state conditions, PER2-Dendra is already in complex with endogenous CRYs. The slow export rate and lack of dependence on additional CRY1 expression therefore likely reflect export of the complex, which is intrinsically slow.

Thus, prior to our work, no data on the true shuttling dynamics of PER2 were available.

Importantly, our results show not only that CRY1 promotes nuclear accumulation of PER2 (as reported by Öllinger et al.) but also that, conversely, PER2 promotes cytosolic accumulation of CRY1, depending on their expression ratio. Since CRY1 is predominantly nuclear and PER2 predominantly cytosolic, and because a PER2 dimer can bind one or two CRY1 molecules, our data suggest that the shuttling equilibrium depends on PER2 saturation state: a PER2 dimer bound to one CRY1 remains cytosolic, whereas a dimer bound to two CRY1 is nuclear.

These observations are novel and have not been reported previously. They were only possible through time-resolved analysis of overexpressed proteins.

A number of the findings are confirmatory rather than novel - the phosphorylation-regulated nuclear-cytoplasmic shuttling of CK1 and PER proteins is long known, and it's not clearly stated what is novel here. 

We acknowledge prior work by Milne et al. (2001), who showed that kinase-dead CK1 is predominantly nuclear and that prolonged treatment with leptomycin B (16 h) enhances its nuclear localization. We cite this study at the beginning of the relevant paragraph. While we confirm these earlier observations, our work extends them in several important and novel ways:

(1) Rapid dynamics of CK1 localization – We show that pharmacological inhibition of CK1 with PF670 induces rapid (within 1 h) depletion of CK1δ from the centrosome, accompanied by nuclear accumulation and elevated CK1δ levels. These kinetics have not previously been reported. We also show that proteasome inhibition with MG132 enhance centrosomal staining, indicating that centrosomal binding sites are not saturated. Together, the data show that CK1δ equilibrates rapidly between its binding partners. 

(2) Integration of localization with protein stability – We relate the known localization patterns of WT CK1 and the kinase-dead mutant K38R to CK1 degradation dynamics and further compare them to the tau-like kinase mutant CK1δ-R1178Q. This integration of subcellular localization data with turnover mechanisms provides new mechanistic insight.

(3) Comprehensive regulatory model – In the revised manuscript, we now include a schematic summarizing how CK1δ is posttranslationally regulated via subcellular shuttling, nuclear degradation, and dynamic interactions with binding partners (Figure EV5C). To our knowledge, such a comprehensive view of CK1δ regulation, linking localization, stability, and partner association, has not been presented before.

We believe these additions clearly distinguish our findings from prior reports and highlight the novel aspects of our study.

The formation of PER and CRY and CK1 complexes likewise is well established. The finding that formation of multiprotein complexes stabilize otherwise unstable over-expressed proteins is interesting but not novel.

We fully agree that the existence of PER–CRY–CK1 complexes is well established. It is also known that PER2 stabilizes CRY1 by occupying the FBXL3 binding site and that CRY1 promotes the nuclear accumulation of PER2. We do not present these established interactions as novel findings.

Our novel contribution, as outlined above, is the discovery that the shuttling and subcellular localization of PER2 and CRY1 are mutually dependent on their expression ratio. Specifically, we show for the first time that the steady-state shuttling distribution PER2 alone is cytosolic due to its rapid nuclear export wherease CRY1 is predominantly nuclear (known). Given that CRY1 facilitates the nuclear import of PER2 (known) and that a PER2 dimer can bind either one or two CRY1 molecules, our data showing that cytoplasmic PER2-CRY1 foci contain less CRY1 than nuclear foci lead us to conclude that cytoplasmic PER2 complexes contain one CRY1 molecule, while nuclear complexes contain two.

This model provides a mechanistic explanation for the distribution of PER2 between the cytosol and nucleus and for the relatively lower cytosolic CRY1 levels. Moost importantly, we further show (for the first time) that CK1-mediated phosphorylation of PER2 displaces CRY1. This phosphorylation event would produce PER2 dimers with one or no CRY1 bound, promoting their export to the cytosol. We believe this represents a novel and potentially important mechanism for regulating circadian clock function.

The results from many of the imaging assays are not quantitated, and the figures often show single cells. It's hard to draw statistical significance from these.

The phenotypes we report here are result of multiple technical and biological replicates (n >3). Image analysis and statistical analysis was performed when required. We show additional examples in the EVs.

There are a number of phenomena seen whose physiological relevance is unclear. In figure 1, forced over-expression of CRY1 and PER2 leads to formation of nuclear foci. It is unlikely these foci form at non-overexpressed levels, and so the general interest and relevance is not high nor investigated. This reduces the impact of the finding.

It has been shown that PERs and CRYs do not form thermodynamically stable, large (detectable) foci under physiological conditions, as we have stated in the manuscript. Whether these proteins have the propensity to form smaller, more dynamic structures of physiological relevance is an interesting question that could be explored elsewhere, but it is not relevant to our study. In our work, these foci are simply convenient markers for analyzing the interaction and subcellular (co)localization of clock proteins under investigation. In the revised version, we have kept the analysis of these foci and the discussion of their potential relevance to a minimum in order to avoid confusion and unnecessary discussions.

The finding that CK1δ is keep in the dephosphorylated state by binding to PER has been established previously by Johnson and colleagues and should perhaps be mentioned (Qin JBR 2015 (doi: 10.1177/0748730415582127).

There is clearly a misunderstanding here. Qin et al.’s data show that, in a cell-free system, CK1ε phosphorylates PER2 and also autophosphorylates its C-terminal tail (autoradiograph, Fig. 1E).  

However, because PER2 phosphorylation is carried out by CK1ε that is tightly anchored to PER2, there is competition between PER2 phosphorylation and tail autophosphorylation. As a result, the kinetics of tail phosphorylation are slower (Fig. 3B and quantification in C) than those observed with free CK1ε (as seen in the presence of the p53 substrate, Fig. 3A,C). We believe that his is also happening in the cell.

Author response image 1.

Our data, in contrast, address a different point. It has been known from the Virshup lab for decades that CK1δ/ε undergo futile cycles of (auto)phosphorylation and dephosphorylation, resulting in an active, dephosphorylated kinase in cells because cellular phosphatases are more efficient than CK1 autophosphorylation. We now show that CK1δ is also efficiently dephosphorylated when bound to PER2 (Fig. 3). Nevertheless, despite dephosphorylation of PER2-bound CK1δ, PER2 itself becomes hyperphosphorylated, indicating that cellular phosphatases act differently on these two substrates. To clarify this point, we inhibited phosphatases with calyculin A (CalA). Under these conditions, both PER2 and PER2-bound CK1δ became efficiently hyperphosphorylated (new Fig. 3).

The degradation of kinase-active but not inactive CK1 is only shown here with 50-fold overexpressed protein so it's interesting, but the relevance to circadian biology is not made clear. The fact that over-expressed CK1 is degraded primarily in the nucleus is interesting, but needs further characterization - is this affected by the epitope tag? Is it true of endogenous CK1 or only over-expressed CK1? Is this not seen with e.g. other forms of CK1, e.g. lacking the C-terminus?

The observation that unassembled kinase is rapidly degraded is most clearly demonstrated by overexpression experiments. However, Fig. 3 shows that overexpression of CRY1 and PER2 leads to the accumulation of elevated levels of endogenous CK1δ (untagged), indicating that endogenous kinase is likewise degraded in the absence of a stabilizing binding partner. In addition, we present data showing that overexpression of tagged CK1δ reduces the levels of endogenous, untagged CK1δ, further supporting the conclusion that unassembled endogenous CK1δ is unstable and subject to degradation.

Further characterization of the CK1 degradation pathway is of considerable interest and could form the basis of a separate study, particularly to identify the components that mediate activity-dependent nuclear export and activity-dependent nuclear degradation. The Δ-tail kinase is expressed at very low levels, although interpretation is complicated by the possibility that this reflects pleiotropic effects.

The final figure, showing that nuclear CK1 is the form responsible for shortening rhythms, is interesting. Is this because massive increases in nuclear CK1 alter PER, or BMAL/CLOCK, or proteasome activity?  

Our data show that cells expressing either nuclear or cytosolic CK1 are viable, proliferate normally, and maintain a functional circadian clock. Therefore, overexpression of the kinase does not produce pleiotropic effects.

To assume it's due to PER phosphorylation is in disagreement with the studies of Meng et al. Neuron 2008 DOI 10.1016/j.neuron.2008.01.019.

The data are not in disagreement with Meng et al.; in fact, they align quite well. Meng et al. showed that CK1ε-tau shortens the circadian period, which we had also previously reported for CK1δ-tau-like (Marzoll et al., 2022). We now demonstrate that CK1δtau-like is enriched in the nucleus, contributing to its period-shortening phenotype. Furthermore, we show that active CK1δ (but not CK1δ-K38R) promotes cytoplasmic accumulation of PER:CRY complexes, consistent with PER2 degradation in the cytosol as described by Meng et al.

Taken together, these findings suggest that PER proteins acquire their CK1 in the nucleus, and this interaction determines the circadian period length. Following a time delay—set by the kinetics of PER2 phosphorylation—PER2:CRY complexes are exported to the cytosol along with their bound CK1, where they are subsequently degraded.

Reviewer #2:

Interactions between the circadian clock proteins PER1/2 with CK1d/e and CRY1/2 influence each of their stability, subcellular localization, and activity, as countless studies over the last two decades have shown. However, many questions still remain, especially in light of newer models of the transcription-translation feedback loop (TTFL) in which the repression phase relies on two distinct mechanisms, a phosphorylation-dependent displacement of the transcription factor by CK1-PER-CRY complexes from DNA early in repression, and a CRY1dependent sequestration of the transcription factor activation domain later in repression. In particular, questions remain about mechanisms triggering nuclear entry/export and activity of these proteins in the cytoplasm and nucleus. 

Here, the authors utilize a system of induced and/or transient overexpression of proteins with or without with fluorophores to track subcellular localization, stability, and interactions. As the authors point out throughout the manuscript, the overexpression of these clock proteins often causes them to behave differently from the endogenous proteins. It looks as though the authors have done their best to account for these changes, and they have certainly been rigorous in pointing them out, but there is concern that some of the conclusions may be influenced by this overexpression. For example, the relevance of work related to the overexpression-dependent foci is unclear. 

Same answer as to Reviewer 1: It has been shown that PERs and CRYs do not form thermodynamically stable, large (detectable) foci under physiological conditions, as we have stated in the manuscript. Whether these proteins have the propensity to form smaller, more dynamic structures of physiological relevance is an interesting question that could be explored elsewhere, but it is not relevant to our study. In our work, these foci are simply convenient markers for analyzing the interaction and subcellular (co)localization of the clock proteins under investigation. In the revised version, we have kept the analysis of these foci and the discussion of their potential relevance to a minimum in order to avoid confusion.

The findings that the stability of the kinase depend on localization, its intrinsic activity, and interaction with PER2 are interesting and important. Use of the CKBD deletion to show that CK1 stabilization depends on its anchoring interaction with PER2 is a nice touch. The authors bring up an excellent point that most of the potential phosphorylation sites on PER1 and PER2 have not been functionally characterized aside from the phosphoswitch mechanism. Their observation that CK1 eventually induces cytoplasmic localization of the CK1-PER-CRY1 complex and the release of CRY1 is intriguing. In particular, the finding that pretreatment of PER2 with CK1 in vitro blocked its ability to interact with CRY1 is very interesting. However, the absence of mechanistic data to explore this in more detail limits the impact of this conclusion. Using the system they have established here to identify the site(s) on PER2 and/or CRY1 that lead to this would help to solidify this work and increase the impact of this work. Overall, there are some interesting findings here but the inclusion of some competing viewpoints and mechanistic data would strengthen the impact of the work.

Major

(1) The characterization of the tau-like CK1 mutant R178C as less active than the wild type enzyme is not entirely correct-it is less active on the FASP region as described, but it has increased activity on S478 in the phosphodegron that is independent of inhibition from the FASP region (Gallego et al. PNAS, 2007 and Philpott et al. eLife, 2020). It is still possible that some of the period shortening effects of the mutant could arise from enhanced nuclear accumulation, but the oversimplified description of the mutant as less active should be corrected.  

In the revised version, we discuss that the enhanced nuclear localization of the Tau-like kinase may contribute, at least in part, to period shortening, similar to how forced nuclear overexpression of wild-type kinase also shortens the period. We emphasize, however, that CK1 Tau is compromised in its priming-dependent activity, whereas its priming-independent activity is context-specific and enhanced toward the β-TrCP site.

(2) One of main conclusions from the paper, that CK1 induces cytoplasmic localization of the CK1-PER2-CRY1 complex and subsequent release of CRY1 would be strengthened significantly by identifying the phosphorylation site(s) responsible for the cytoplasmic localization of the complex and the release of CRY1. The system they have developed here seems ideal to identify these sites.

We fully agree with the reviewer. We substituted the known phosphorylation sites in PER2 surrounding the CRY-binding domain, but this had no effect on the phosphorylationdependent release of CRY1. Therefore, a more systematic analysis will be required, including the possibility that phosphorylations in CRY1 itself may contribute. To this end, we are generating PER2 and CRY1 variants in which all Ser/Thr residues are replaced by Ala. Using these constructs alongside the wild-type versions, we will by PCR systematically create hybrids in which specific regions containing phosphorylation sites are exchanged.

Nevertheless, this will require considerable time and effort, and we believe this investigation exceeds the scope of the present manuscript and will address it in future work.

(3) The concept of delayed release of CRY1 presented here is an interesting one. It's unclear why the authors have also not incorporated prior findings (Ukai-Tadenuma et al. Cell, 2012, Koike et al. Science, 2012) that peak levels of CRY1 are expressed in a later phase than CRY2, PER1, and PER2. It seems like figure EV6 should reflect the observation that CRY2 is the predominant cryptochrome present during early repression (Koike et al. Science, 2012).

The reviewer is absolutely right: the expression phases of CRY1, CRY2, PER1, and PER2 are important. I have recently discussed these issues in detail in a News & Views article in The EMBO Journal, commenting on a paper by Smyllie et al. In this News & Views article, I discuss that the presently available data suggest that CRY1 is always present throughout the circadian cycle and keeps circadian transcription partially repressed even at peak phases of expression. In the revised version, I refer to these publications, including those mentioned by the reviewer. However, I would like to keep the model presented in the supplementary figure as simple as possible and specifically focused on the work presented in this manuscript, rather than presenting a comprehensive conceptual model of the circadian clock.

(4) The model presented in figure EV6 and described throughout the text shows that PER-CRY complexes interact with CK1 in the nucleus, and not in the cytoplasm prior to nuclear entry. Prior work on endogenous protein complexes has shown that CK1-PER-CRY complexes exist in the cytoplasm very early on in the repression phase (Aryal et al. Mol Cell, 2017-ref. 14 in the manuscript). Work by Sancar and colleagues (Cao et al. PNAS, 2020) also shows with endogenous proteins that CK1d has a circadian pattern of nuclear entry (or possibly retention) concomitant with PER2 that is dependent on the presence of PERs and CRYs. Together, these data seem to be inconsistent with your model. 

We think the data are not inconsistent. The recent Smyllie et al. paper in EMBO Journal shows that PER2 is present in both the cytosol and the nucleus at all times when it is expressed, but cytosolic PER2 is not saturated with CRY, which is more nuclear. Our data demonstrate that PER2 shuttles between the cytosol and the nucleus depending on its occupancy with CRYs (see schematic Fig. 1). Occupancy, in turn, depends on expression levels and binding affinities, including those of CRY2 and PER1. Consequently, PER2 complexes could shuttle continuously throughout the circadian cycle—either because they are not saturated with CRYs due to the balance between expression levels, freely available CRY, and binding affinity, or later in the cycle because CRYs are displaced by phosphorylation. If PER2 acquires casein kinase in the nucleus early in the cycle, it will shuttle out to the cytosol together with the bound CK1. We believe this does occur, but early in the circadian cycle the saturation of PER2 with casein kinase is likely to be very low due to the limited availability of CK1 in the nucleus. I am aware that not everyone will share this interpretation point by point, but discussing it in greater length and detail exceeds the scope of the present manuscript.

Reviewer #3:

This manuscript by Serrano and co-workers is a tight body of work that provides much needed insights into the regulation of clock proteins by CK1D, and into the regulation of CK1D itself. While the whole paper relies on artificial overexpression of chimeric/tagged proteins that may have significant differences in the function, the stability and subcellular distribution of the endogenous proteins they are suppose to model, this limitation was been clearly stated by the authors, and nevertheless their study still provides important insights. 

While the authors have specified which Ck1d isoform (Ck1d1) they are overexpressing in their model cell lines, they may have thought to consider that the overexpression of one Ck1 homologue may affect the endogenous expression of the other homologues and their isoforms, e.g. ck1d1 overexpression may cause an increase in Ck1d2 or Ck1e, which would in turn affect the conclusions. 

We show in revised Fig. 3 that overexpression of CK1δ1 reduces the expression of endogenous CK1δ1/2. This is consistent with our prediction that overexpressed and endogenous CK1 (including CK1ε) compete for the same stabilizing binding partners, leading to rapid degradation of unassembled kinases.

Moreover, the antibody they used for endogenous Ck1d (which is ab85320, also mentioned as AF12G4 but that is the clone number, not the catalogue number) is discontinued and its specificity against Ck1d1, Ck1d2 or even the highly identical Ck1e, has not been clearly demonstrated. We know from Fig 3 that it can detect Ck1d1 but it would be great if the authors would provide additional evidence for the specificity of this antibody, for example by overexpressing Ck1d1/Ck1d2/Ck1e to see really which "endogenous" Ck1 we are seeing.

Are the three bands for example seen in Fig 4A corresponding to the different isoforms? This simple experiment would reinforce the conclusions. 

We show in the revised figure that the antibody recognizes CK1δ1 and CK1δ2, but not CK1ε. In U2OS cells, the antibody detects a single band (Figure); we do not know whether this represents predominantly one splice isoform or both, which are not resolved. However, this distinction is not relevant for our interpretation, because overexpression of tagged CK1δ1 reduces the expression of whichever endogenous kinase is present.

There are no minor comments, as the figures, the figure legends and main text are all of good quality and ready for publication.

Reviewers’ Responses to Point-by-Point Response to Peer Review 

Referee #1:

I appreciated the additional efforts by the authors to improve the manuscript. Unfortunately, the underlying approach of forced over-expression remains artifact-prone, and has been largely supplanted by readily available knockin and targeted mutagenesis methods. Over-expression may give clues, but I think more rigorous mechanistic validation is needed to make this compelling. I cannot support publication of this manuscript.

Referee #2:

In their response to reviewers, the authors make the valid point that the steady state of a system is usually perturbed to study it. In this study, they have used overexpression of the clock proteins PER2, CRY1 and CK1 to study their effects on subcellular dynamics and stability. In justifying this choice, they refer to several papers that similarly overexpressed at least one of these components, stating that their time-resolved approach brings novel insights. However, there is a missed opportunity here to translate any lessons learned from overexpression studies to a system where the proteins are expressed at physiological levels and stoichiometry.

The authors reply to reviewer 1 stating that they conclude PER proteins acquire CK1 in the nucleus, but this does not account for other studies showing an apparent PER-CK1 complex in the cytoplasm during the early phases of repression and/or a pattern of PER-dependent nuclear entry of CK1 (Lee et al. 2001, Cell; Aryal et al. 2017 Mol Cell; Cao et al. 2021 PNAS). Given that all 3 of these studies were done with native expression levels, it seems incumbent upon the authors to demonstrate that their conclusions from the overexpression study are physiologically relevant by translating them in some way to a more native system. This also addresses a point made by reviewer 2, major concern 4 that was not satisfactorily addressed by the authors. Perhaps they could validate their hypothesis of PER shuttling and interactions with CK1 or CRY1 that alter this in a native system similar to Aryal or Cao et al. with the use of nuclear export inhibitors?

The response to reviewer 2, major concern 1 is thoughtful and much appreciated. However, simplifying the effects of the tau mutation on CK1 as having a decreased rate on priming-dependent phosphorylation but not priming-independent is not quite true-the tau mutation also decreases the rate of priming-independent phosphorylation of S662 (in humans) (Philpott et al. 2020, eLife).

Other papers appearing in this journal seem to all include at least one major new mechanistic insight. Although the authors do a diligent job in characterizing the overexpressed proteins in this system, some of their conclusions are at odds with prior studies of the system in more native conditions, so the potential impact of this work is unclear. To verify these conclusions or test new ones (ie, that CK1 disrupts PER-CRY1 interactions), they should use their insights to generate mutations or make perturbations in a native system and demonstrate that they still hold.

Referee #3:

The authors have adequately addressed the reviewers' comments, and it is my opinion that the manuscript is ready for publication. It is true, as previously mentioned by other reviewers, that the evidence presented rely on overexpression, which for the other reviewers seem to preclude publication. However, I find this to be a too strict opinion.

If the authors had indeed provided evidence using crispr-cas9-mediated genetic manipulation and tagging/mutating endogenous genes for all their experiments, thereby providing more physiological evidence of how clock proteins interact, they would probably have submitted their manuscript to an alternative journal with a higher impact.

As it stands, it is my opinion that, considering the evidence and limitations of the study, this manuscript is a good match for the journal.

Author Rebuttal:

Apologies for the delayed reply regarding our manuscript. In the meantime, we have added several new experiments which address the comments of the reviewers and more. These are now included as Figures 1C, EV3, 4D, 6E, 6F, EV6D, and EV7.

Figure 1C reinforces our observations from Figure 1B showing that induction of stably-integrated PER2 also results in accumulation of endogenous CRY1 at a timescale that is compatible with the gradual localization of overexpressed PER2 into the nucleus.

Figure EV3 addresses several technical comments from Reviewers #3 and #1, respectively: Figure EV3A shows that our CK1δ antibody recognizes CK1δ1 and CK1δ2, but not CK1ε. Figures EV 3B and C clearly show how overexpression of our transgenic CK1δ results in decreased endogenous CK1δ which further demonstrates the rapid turnover of active kinase.

Figure 4D addresses the comment from Reviewer #2. We clearly show that CK1δ is not kept in a dephosphorylated state by binding to PER. In addition to our direct comment to this point, Figure 4D shows that CK1δ regardless if it is expressed alone or in complex with PER2 is phosphorylated to a similar extent when the cells are treated with the phosphatase inhibitor CalA. As indicated in our direct response, we are rather more interested in the observation that cellular phosphatases act differently on PER2 compared to CK1δ despite being in the same PER:CK1δ complex (as shown by the clear stabilization of overexpressed CK1δ by co-expression of PER2).

Figures 6E, 6F, and EV6D demonstrate that our observations from overexpression systems are also observed in a more physiological context, addressing comments from Reviewers #1 and #2. Figure 6E shows that dephosphorylation of PER2 leads to its relocalization from the cytosol to the nucleus, while Figure 6F analyzes the subcellular localization of PER2 in the context of a functional circadian clock in U2OS cells. The latter demonstrates that PER2 is predominantly nuclear early in the circadian cycle, but redistributes to the cytosol at later time points. We included these experiments in response to the reviewer’s request for a more physiological context. Since we are not a mouse lab, this cell-based system represents the most physiological model we can provide. Figure 6F show the dynamics of endogenous PER2 from DEX-synchronized cells. At early timepoints, PER2 is predominantly nuclear likely due to the incorporation of CRY1 forming the PER:CRY complex. At later timepoints PER2 is redistributed between the cytoplasm and nucleus due to PER2 phosphorylation. Importantly, these results are consistent with and recontextualize the results from Liu et al. (Xie et al., PNAS, 2023) showing the hypophosphorylated PER2 at early timepoints post-DEX is predominantly nuclear and hyperphosphoryated PER2, that appear later post-DEX is predominantly cytoplasmic.

Finally, Figure EV7 provides a model how the subcellular distribution of CK1δ affects its assembly into the PER:CRY complex emphasizing how nuclear kinase enacts its role in the circadian clock.

Response to Reviewers:

We were disappointed by the categorical rejection of overexpression experiments. Without a specific discussion of why they would be inappropriate or not sufficient in the context of the work presented here, the blanket assertion that overexpression inevitably produces artifacts functions more as a rhetorical device than as a substantiated scientific argument. The fact that the term ‘physiological’ generally carries a positive connotation, whereas ‘overexpression’ is often perceived negatively, does not in itself justify the categorical rejection of experiments.

While we appreciate that some reviewers may personally prefer alternative strategies, we believe that the suitability of any approach must be evaluated in light of the specific biological questions being addressed. I cannot see a single specific point in the reviewers’ responses indicating that any of our experiments yielded artificial results. It is true that targeted knock-in and mutagenesis methods are available, however, these approaches are simply not suited to the questions raised in this manuscript. We also fully agree that, whenever possible, insights from overexpression studies should be validated in systems with a functional clock where proteins are expressed at physiological levels, which we did using U2OS cells, and noting the compatibility of our results with those in the literature using endogenously-tagged constructs. We have cited several recent studies that have investigated the subcellular distribution and circadian dynamics of endogenous or endogenously-tagged clock proteins in mice (Cao et al, 2021; Smyllie et al, 2022, 2016, 2025) and U2OS cells (Öllinger et al, 2014; Gabriel et al, 2021; Xie et al, 2023). While we cannot substantially expand on these previous observations, we confirm them in the revised version by demonstrating the nuclear-to-cytoplasmic relocalization of PER2 in U2OS cells over the course of a circadian cycle. In addition, we show that this process is, in principle, reversible: when CK1 is inhibited with PF670, overexpressed hyperphosphorylated cytosolic PER2 becomes dephosphorylated and accumulates in the nucleus.

Overall, we consider our approach not only complementary but also essential, as it enables us to address two key questions that would otherwise be difficult or even impossible to resolve:

(1) Mutual impact of PER2 and CRY1 on subcellular dynamics and the role of PER2 phosphorylation

Evidence from mouse liver (Cao et al, 2021), mouse SCN (Smyllie et al, 2022, 2025), and U2OS cells (Xie et al, 2023) indicates that a substantial fraction of PER2 remains cytoplasmic throughout its expression cycle, even in the presence of CRY1, which promotes PER’s nuclear import. The mechanisms underlying this cytoplasmic retention remain unclear, and no circadian function has yet been attributed to the cytosolic PER2 pool. Our study addresses how PER2 abundance, phosphorylation state, and stoichiometry relative to CRY1 govern their interaction and subcellular dynamics. This is physiologically relevant because PER1/2 and CRY1/2 proteins oscillate in expression and degradation out of phase, such that their concentrations, stoichiometry, and phosphorylation state vary systematically over the circadian cycle. Transient transfection and inducible overexpression combined with time-lapse microscopy are essential here, as they uniquely allow modulation of protein ratios and CK1δ levels and to resolve their dynamics.

Previous work established that CRY1 is nuclear and promotes PER2 nuclear accumulation (Smyllie et al, 2022). Our data extend this by showing that subcellular distribution is determined by the CRY1:PER2 ratio. While CRY1 alone is nuclear we show that PER2 alone is cytoplasmic due to rapid nuclear export. Mixed conditions reveal ratio-dependent shifts: at low CRY1-to-PER2 ratios, CRY1 relocalizes to the cytoplasm, whereas at high ratios, PER2 is retained in the nucleus. We explain this behavior by PER2 dimerization: dimers bound to two CRY1 molecules remain nuclear, while dimers bound to a single CRY1 localize to the cytosol. Such species can be expected to form in a physiological context depending on binding affinities and rhythmic expression levels and ratios across circadian time. Importantly, we show that CK1δ-mediated phosphorylation destabilizes PER2 and CRY1 interactions. From this, we infer that PER2 dimers with only a single bound CRY1 transiently form and accumulate in the cytosol, consistent with the lower CRY1-to-PER2 ratio we observe in the cytosol and that has also been reported in the SCN (Smyllie et al, 2025). With continued phosphorylation, PER2 dimers lose CRY1 altogether, while the released CRY1 accumulates in the nucleus. We suggest that this mechanism supports and extends the late repressive phase of the circadian cycle. Recent data show that hypophosphorylated PER2 is predominantly nuclear, whereas hyperphosphorylated PER2 is largely cytoplasmic in mouse liver (Cao et al, 2021; Xie et al, 2023), linking our data to a physiological context.

Taken together, these findings suggest a mechanism whereby stoichiometry, subunit composition, and CK1δ phosphorylation determine PER:CRY complex composition and localization. Crucially, these complexes and their dynamic relocalization could only be observed using inducible overexpression; knock-in strategies at endogenous levels would not be able to capture such states.

(2) Posttranslational regulation and subcellular homeostasis of CK1δ and impact on the clock

Previous work has shown that nuclear export of CK1δ depends on its kinase activity (Milne et al, 2001). Here, we further demonstrate that unassembled CK1δ is subject to degradation, with nuclear turnover accelerated by its catalytic activity. Thus, when evaluating the impact of CK1δ mutants on the circadian clock, one must consider not only kinase activity but also protein stability and subcellular distribution. We find that CK1δ availability for PER2 differs between cytosol and nucleus. In particular, nuclear CK1δ is limiting, and its abundance directly determines circadian period length. This is significant because subcellular CK1δ availability and posttranslational regulation have not previously been examined or incorporated into circadian clock models, as the kinase has been assumed to be non-limiting given its constant expression throughout the circadian cycle. Complex formation between CK1δ and PER is a well-established determinant of circadian timing, with CK1δ overexpression known to shorten period length. Our data explain why: the binding equilibrium between CK1δ and PER must be finely tuned. Previous studies suggested that PER associates with CK1δ in the cytosol and enters the nucleus as a PER:CRY:CK1δ complex (Lee et al, 2001; Aryal et al, 2017). Our data suggest that nuclear PER is not saturated with CK1δ. This is because levels of free, active CK1δ in the nucleus are low, owing to its rapid export or degradation by the nuclear proteasome, which limits its availability for PER binding.

Our overexpression studies support this mechanism. NES-tagged CK1δ overexpression does not alter circadian period length, because it fails to increase nuclear CK1δ levels: Each PER molecule can coimport only one kinase, a process already occurring in wild-type cells, and the few co-imported molecules rapidly equilibrate with the nuclear pool, where they are subject to export or degradation. In contrast, NLS-tagged CK1δ overexpression directly increases nuclear kinase abundance by antagonizing export, thereby enhancing PER binding and shortening circadian period. This multilayered regulation of CK1δ stability and localization and its consequences for PER2 availability would not have been revealed without targeted overexpression. Our findings therefore fill a key knowledge gap and remain fully consistent with previous studies (Lee et al, 2001; Aryal et al, 2017; Cao et al, 2021).

Conclusion: In sum, our findings are novel and physiologically relevant, aligning with data from mouse liver and SCN. While studies at strictly endogenous protein levels are important and necessary, perturbation of steady state is a standard strategy to uncover and observe novel mechanisms. Endogenous-level experiments would demand technically unrealistic systems (for example, even the simplest case, analyzing the subcellular dynamics of PER2 alone, would require cells lacking PER1, CRY1/2, and CK1δ/ε). Moreover, adjustment of PER2-to-CRY1 ratios cannot be achieved with stably integrated genes and of course not at physiological expression levels. Thus, inducible overexpression is not merely practical but currently the most feasible approach to dissect these dynamics. We complement our findings with data from U2OS cells with a functional clock, showing that the availability of nuclear CK1δ directly determines circadian period length. Although specific aspects of our extended model require further experimental validation, no published evidence contradicts it to date. Mechanistic discussions of the circadian clock have so far focused primarily on PER protein degradation. Our model broadens this perspective by incorporating CK1δ homeostasis, PER:CRY complex composition, subcellular localization, and their regulation by phosphorylation. In doing so, it provides a detailed framework to be critically tested and refined in future studies.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

This manuscript investigates how dentate gyrus (DG) granule cell subregions, specifically suprapyramidal (SB) and infrapyramidal (IB) blades, are differentially recruited during a high cognitive demand pattern separation task. The authors combine TRAP2 activity labeling, touchscreen-based TUNL behavior, and chemogenetic inhibition of adult-born dentate granule cells (abDGCs) or mature granule cells (mGCs) to dissect circuit contributions.

This manuscript presents an interesting and well-designed investigation into DG activity patterns under varying cognitive demands and the role of abDGCs in shaping mGC activity. The integration of TRAP2-based activity labeling, chemogenetic manipulation, and behavioral assays provides valuable insight into DG subregional organization and functional recruitment. However, several methodological and quantitative issues limit the interpretability of the findings. Addressing the concerns below will greatly strengthen the rigor and clarity of the study.

Major points:

(1) Quantification methods for TRAP+ cells are not applied consistently across panels in Figure 1, making interpretation difficult. Specifically, Figure 1F reports TRAP+ mGCs as density, whereas Figure 1G reports TRAP+ abDGCs as a percentage, hindering direct comparison. Additionally, Figure 1H presents reactivation analysis only for mGCs; a parallel analysis for abDGCs is needed for comparison across cell types.

In Figure 1G and 1H we report TRAP+ abDGCs as a percentage rather than density because we are analyzing colocalization of the two markers, which are very sparse in this population. Given the very low number of double-labeled abDGCs, calculating density would not be practical. In the revised manuscript we have clarified the rationale for using these measures. As noted in the current text, we did not observe abDGCs co-expressing TRAP and c-Fos; we have made this point more explicit to guide interpretation of these data.

(2) The anatomical distribution of TRAP+ cells is different between low- and high-cognitive demand conditions (Figure 2). Are these sections from dorsal or ventral DG? Is this specific to dorsal DG, as itis preferentially involved in cognitive function? What happens in ventral DG?

The sections shown in Figure 2 were obtained from the dorsal dentate gyrus (see Methods, “Histology and imaging”: stereotaxic coordinates −1.20 to −2.30 mm relative to bregma, Paxinos atlas). From a feasibility standpoint, it is not possible to analyze the entire longitudinal extent of the hippocampus with these low-throughput histological approaches. We therefore focused on the dorsal DG, for which there is a strong functional rationale. A large body of work indicates that the dorsal hippocampus, and specifically the dorsal DG, is preferentially involved in spatial memory and in the fine contextual discrimination that underlies pattern separation. The dorsal hippocampus is critical for encoding and distinguishing similar spatial representations, a core component of the high-cognitive demand task used here. In contrast, the ventral DG is more strongly associated with emotional regulation and affective memory processing and is less implicated in high-resolution spatial encoding. For these reasons, the present study was designed to assess TRAP+ cell distributions specifically in the dorsal DG.

(3) The activity manipulation using chemogenetic inhibition of abDGCs in AsclCreER; hM4 mice was performed; however, because tamoxifen chow was administered for 4 or 7 weeks, the labeled abDGC population was not properly birth-dated. Instead, it consisted of a heterogeneous cohort of cells ranging from 0 to 5-7 weeks old. Thus, caution should be taken when interpreting these results, and the limitations of this approach should be acknowledged.

We agree that prolonged tamoxifen administration results in labeling a heterogeneous population of abDGCs spanning approximately 0 to 5–7 weeks of age, rather than a precisely birth-dated cohort. This is a limitation of this approach and we have included discussion of this in more detail in the revised manuscript.

(4) There is a major issue related to the quantification of the DREADD experiments in Figure 4, Figure 5, Figure 6, and Figure 7. The hM4 mouse line used in this study should be quantified using HA, rather than mCitrine, to reliably identify cells derived from the Ascl lineage. mCitrine expression in this mouse line is not specific to adult-born neurons (off-targets), and its expression does not accurately reflect hM4 expression.

We agree that mCitrine is not a marker that allows localization of hM4Di as it is well known that the mCitrine can be independently expressed in a Cre independent manner in this mouse. As suggested, we have removed the figure that showed the mCitrine and have performed immunohistochemical localization of the DREADD with an antibody against the HA tag. This is now shown in Figure 5.

(5) Key markers needed to assess the maturation state of abDGCs are missing from the quantification. Incorporating DCX and NeuN into the analysis would provide essential information about the developmental stage of these cells.

The goal of this study was to examine activity patterns of adult-born versus mature granule cells, rather than to assess maturation state. The adult-born neurons analyzed were 25–39 days old, an age at which point most cells have progressed beyond the DCX⁺ stage and are expected to express NeuN based on prior work. We therefore do not think that including DCX or NeuN quantification would provide additional information relevant to the aims or interpretation of this study.

Minor points:

(1) The labeling (Distance from the hilus) in Figure 2B is misleading. Is that the same location as the subgranular zone (SGZ)? If so, it's better to use the term SGZ to avoid confusion.

We have updated Figure 2B, the Methods, and the main text to more explicitly localize this which it the boundary between the subgranular zone (SGZ) and the hilus.

(2) Cell number information is missing from Figures 2B and 2C; please include this data.

We have now added the cell number information to the figure legends. In Figures 2B and 2C, each point corresponds to a single cell, with an equal number of mice per group. The total number of TRAP⁺ cells per mouse is shown in Figure 1F, which reports TRAP⁺ cell densities by group.

(3) Sample DG images should clearly delineate the borders between the dentate gyrus and the hilus. In several images, this boundary is difficult to discern.

We made the DG-hilus boundaries clearer in the sample images to improve visualization and interpretation.

(4) In Figure 6, it is not clear how tamoxifen was administered to selectively inhibit the more mature 6-7-week-old abDGC population, nor how this paradigm differs from the chow-based approach. Please clarify the tamoxifen administration protocol and the rationale for its specificity.

We apologize for the confusion here. The protocol used in Figure 6 is the same tamoxifen chow–based approach as in Figure 5, differing only in the duration of tamoxifen exposure. Mice in Figure 5 received tamoxifen chow for 7 weeks, whereas mice in Figure 6 received it for 4 weeks, restricting labeling to a younger and narrower cohort of adult-born DGCs. Thus, the population targeted in Figure 6 is younger than that in Figure 5 and does not correspond to mature 6–7-week-old neurons. By contrast, the experiment in Figure 4 targets a more mature population, consisting predominantly of ~5-week-old adult-born neurons as well as mature granule cells, which are Dock10-positive and express Cre endogenously, allowing selective manipulation of this later-stage population.

We have corrected the paragraph accordingly and clarified the age range of the labeled populations in the revised manuscript.

Comments on revisions:

I appreciate the authors' careful and thorough revisions. They have addressed all of my previous concerns satisfactorily, and the manuscript is now significantly strengthened. I have no further concerns.

Reviewer #2 (Public review):

In this study, the authors investigate how increasing cognitive demand shapes activity patterns in the dorsal dentate gyrus (DG). Using a touchscreen-based TUNL task combined with TRAP/c-Fos tagging, birth-dating of adult-born granule cells (abDGCs), and chemogenetic inhibition, they show that higher task demand increases mature granule cell (mGC) recruitment and enhances suprapyramidal (SB) versus infrapyramidal (IB) blade bias. Functionally, mGC inhibition reduces overall activity and impairs performance without disrupting blade bias, whereas inhibition of {less than or equal to}7-week-old abDGCs increases mGC activity, abolishes blade bias, and impairs discrimination under high-demand conditions. These findings suggest that effective pattern separation depends not only on overall DG activity levels but also on the spatial organization of recruited ensembles.

The integration of touchscreen TUNL with temporally controlled activity tagging and birth-dated cohorts is technically strong. Quantification of SB-IB bias and radial/apical distributions adds anatomical precision beyond bulk activity measures. The comparison between mGC and abDGC inhibition is conceptually compelling and supports dissociable functional roles. Overall, the data convincingly demonstrate that increasing cognitive demand amplifies blade-biased DG recruitment and that mGCs and abDGCs differentially contribute to both behavioral performance and network organization.

However, how abDGCs are integrated into the mGC network under high cognitive demand remains unresolved. Additional experiments are needed to clarify how abDGCs shape spatial recruitment patterns and whether they directly inhibit or indirectly regulate mGC activity to maintain high performance.

Furthermore, the authors frame "high cognitive demand" as a multidimensional construct encompassing broad behavioral challenge. It would strengthen the work to delineate how local abDGC-mGC circuit interactions regulate specific task components in real time. This will require higher temporal resolution approaches, as TRAP and c-Fos labeling integrate activity over prolonged windows and primarily reflect sustained engagement rather than moment-to-moment computations.

The central conclusion that dentate function depends on coordinated spatial recruitment rather than total activity magnitude is supported by the data, although mechanistic interpretations should be tempered given methodological limitations.

Overall, this work advances models of adult neurogenesis by emphasizing a critical-period modulatory role of abDGCs in organizing DG network activity during high-demand discrimination. The combined behavioral and circuit-level framework is likely to be influential in the field.

Reviewer #3 (Public review):

This study examines the role of dentate gyrus neuronal populations, reflecting neurogenesis and anatomical location (suprapyramidal vs infrapyramidal blade), in a mnemonic discrimination task that taxes the pattern separation functions of the dentate. The authors measure dentate gyrus activity resulting from cognitive training and test whether adult neurogenesis is required for both the anatomical patterns of activity and performance in the cognitive task. The authors find that more cognitively challenging variants of the task evoked more dentate activity, but also distinct patterns of activity (more activity in the suprapyramidal blade, less in the infdrapyramidal blade). Using chemogenetic approaches they silence mature vs immature dentate gyrus neurons and find that only mature neurons (either the general population or specifically mature adult-born neurons), and not immature adult-born neurons, are required for the difficult version of the task. Inhibition of mature adult-born neurons furthermore increased overall activity in the dentate and reduced the biased pattern of activity across the blades, consistent with evidence that adult-born neurons broadly regulate dentate gyrus activity.

Comments on revisions:

I appreciate the efforts the authors have taken to revise this manuscript. I have only minor concerns with this revised version of the manuscript:

Methods state that significance is defined as P<0.05 but some results are interpreted as significant when P=0.05. Either the alpha value needs to change or the interpretation needs to change.

We have corrected the statement in the Methods section to define statistical significance as P ≤ 0.05, which aligns with how significance was interpreted throughout the manuscript.

I believe the statistical results for group and blade effects for the ANOVAs, in Figs 2,3 & 4, appear to be switched (blade should be significant, not group).

We thank the reviewer for pointing out this mistake. We have corrected the reported statistical results for the group and blade effects in the manuscript accordingly.

I appreciate that sometimes there is not a perfect overlap between immunohistochemical signals, but I continue to believe that the spatially-non-overlapping TRAP and EDU signals in Fig 3 is caused by these 2 markers being in different cells. A Z-stack or orthogonal projection could verify/disprove this concern.

We agree that limited overlap in single optical sections can raise the possibility that TRAP and EdU signals originate from different cells. However, based on our imaging conditions and inspection across focal planes, the signals are consistent with being present within the same cells, with partial spatial separation likely reflecting subcellular localization and/or sectioning effects.

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

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Reply to the reviewers

Response to the Reviewers

We thank three anonymous Reviewers for their careful examination of our manuscript. Below, we provide a point-by-point response.

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

1. EVIDENCE, REPRODUCIBILITY AND CLARITY Summary

Hubbert and colleagues describe ExTaSy, a CRISPR-Cas9-based platform for the endogenous tagging of proteins in Drosophila melanogaster. The system combines several established molecular tools into a single-vector framework: homology-directed repair (HDR) for the insertion of a 3XHA tag at the endogenous locus, piggyBac transposase-mediated near-scarless removal of a transgenic selection marker, and φC31 integrase-mediated recombination-mediated cassette exchange (RMCE) for subsequent tag swapping. The authors demonstrate the system across a set of 65 genomic loci and provide a bioinformatic pipeline to automate guide RNA and homology arm design.

Major Comments

1. Validation of knock-in lines is inadequate and does not reflect current standards in the field. The authors state that correct insertions were confirmed using "two PCRs per inserted fragment done with primers binding to the 5' and 3' ends of the inserted DNA and corresponding gene-specific validation primers." This strategy is well known to produce false positives, as it cannot distinguish correctly targeted single-copy integrants from concatemeric insertions at the target locus (e.g. Skryabin et al., 2020). The current standard for validating CRISPR-mediated knock-ins requires PCR amplification using primers that anneal outside the homology arms and span the entire inserted cassette. These reactions must be performed under conditions that minimise the formation of PCR chimeras, specifically low cycle numbers and use of a high-processivity polymerase. The authors should either provide data from such experiments for their characterised lines, or clearly acknowledge this limitation and qualify their efficiency estimates accordingly (see related point 2 below).

__Response: __We originally opted for using primers that span a fragment from the inserted DNA into the genomic locus for ease of amplification, which is currently standard in the field (e.g., Kanca et al. 2022). We usually run these PCRs in a heterozygous background (before homozygous stocks are established or because tagged lines remain balanced), and the unmodified locus preferentially amplifies in a whole-fragment PCR. However, we have recently started running whole-fragment PCRs and plan to repeat them for all loci and will report the results in a revised version of the manuscript. We are also revising the manuscript to reflect the necessity (or at least preference) to perform insert-spanning PCRs.

Reported efficiency metrics do not adequately distinguish correctly targeted integrants from marker-positive flies.

A related concern is that many of the efficiency parameters reported in the manuscript appear to be based solely on the detection of the marker cassette. The 63.1% overall success rate, for example, seemingly reflects the recovery of DsRed-positive flies rather than of sequence validated, single-copy, on-target integrants. These are fundamentally different quantities, with only the latter being of practical value for the users of the described technique. The authors should either provide data that properly accounts for correct integration, or more carefully define what each reported metric represents and explicitly acknowledge the limitations of using marker presence as a proxy for successful knock-in.

__Response: __The reviewer is correct that the numbers we report are DsRed-positive flies. However, most have been confirmed with end-of-fragment/locus spanning PCRs, so are on-target (although not necessarily single-copy; see comment #1). While we cannot categorically exclude off-target insertions, we have not observed any cases where the DsRed segregates independently of the targeted chromosome, which at least makes off-target insertions on other chromosomes highly unlikely. We will clarify in the text that the 63.1 % success rate relates to DsRed marker expression and insertion site-spanning PCR and acknowledge the limitations as suggested by the reviewer.

The characterisation of tag exchange requires expansion or more careful framing of its scope.

The possibility of exchanging tags through fly crosses rather than repeated microinjections is, in the view of this reviewer, the most practically useful feature of ExTaSy and the aspect most likely to drive community adoption. It is therefore important that this feature is characterised with sufficient rigour to allow prospective users to assess its reliability. In the current manuscript, tag exchange has been demonstrated at only five loci using a single replacement tag (sfGFP). The dataset includes one outright failure (the Met C-terminus) and one instance of an unexpected 9 bp insertion at the recombination site, leaving the success rates and failure modes across a broader range of loci and tags uncharacterised. The authors should either expand the tag exchange experiments to cover a more representative set of conditions, or frame the current data explicitly as a proof of concept and limit their conclusions about the practical utility of tag exchange accordingly. In either case, the value of this work to the community would be substantially increased if a collection of donor lines carrying the most commonly used tags for different applications, as the authors themselves enumerate in the Discussion, were generated and deposited at a public stock centre such as the VDRC concurrent with publication. On this note, it is also worth flagging that at present the plasmids described in this study have not yet been deposited at Addgene or the European Plasmid Repository, and that fly lines are available only on request. For a methods paper aimed at community adoption, deposition of reagents in publicly accessible repositories at the time of publication is the expected standard.

__Response: __We are in the process of increasing the number of fly stocks for which tags have been exchanged and will be able to provide a more rigorous characterization with an updated version of the manuscript. We are also working on additional swap lines (for example T2A-GAL4). Regarding submission of the materials to relevant databases, we are in the process of depositing the plasmids on Addgene. We plan to deposit the swap lines and other toolkit stocks (new hs-Flp, vas-int lines as well as pBac transposase lines) at the VDRC or BDSC. To make the tagged fly lines viable for distribution via the VDRC, we are working to increase their numbers, and we plan to publish them separately as a resource, where we also plan to characterize the expression of more transcription factors and their isoforms in greater detail.

The Introduction should better reflect the current state of the field, including explicit comparison with MiMIC and CRIMIC.

The introduction would benefit from a clearer distinction between transgene-based approaches that introduce additional gene copies and true CRISPR-mediated knock-ins at the endogenous locus. As it stands, the discussion of prior methods does not sufficiently acknowledge that CRISPR-based knock-in is already the standard approach in Drosophila, and that the individual techniques employed in ExTaSy are well established. Notably, the MiMIC and CRIMIC systems (Nagarkar-Jaiswal et al., 2015; Li-Kroeger et al., 2018), which also support RMCE-based tag exchange at endogenous loci and for which large collections of lines are already publicly available, are not adequately discussed. These are arguably the closest comparators to ExTaSy, and the authors should explicitly address how their approach differs from and offers advantages over this existing framework, particularly given that MiMIC/CRIMIC insertions can also tag internal sites and thus avoid some of the terminus-specific complications described here.

__Response: __We will expand the introduction and the discussion to give more reference to other resources for endogenously and exogenously tagged genes in Drosophila and compare ExTaSy in greater detail with other methods, highlighting advantages and disadvantages of each and making clear that RMCE-based tag exchange and marker removal are not novel inventions.

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Minor Comment

The labelling of sgRNA target sites in Figure 1 is inaccurate and should be corrected.

In Figure 1, the sgRNA target sites are annotated with triangles labelled "PAM synth." The presence of a PAM is necessary but not sufficient to define a target site; the label should therefore be changed to "target site" or an equivalent term. Additionally, the Methods section incorrectly expands PAM as "primary adjacent motif"; the correct expansion is "protospacer adjacent motif."

__Response: __The labelling in Figure 1 will be changed and the PAM abbreviation corrected.

Could the fly crossing scheme in Figure S3 be simplified?

In the scheme in Fig. S3 the second step seems to be intended to introduce the hs-Flp and vase-Int transgenes. Would it not be possible to already incorporate the Integrase into the swap fly line when it is made and the hs-Flp into the ExTaSy line, thereby saving one generation?

__Response: __This would in principle be possible; however, we prefer to keep the lines “clean” in case a tag exchange is not desired, and so this would require an initial crossing step. We therefore prefer the crossing scheme as it is.

Figure 1F has no call out in the main text.

__Response: __This will be corrected.

Line 155: What was the reason for the low survival rate? Is this likely to be indicative of a problem during marker removal, or a stochastic event as not all fly crosses are always productive (bad food, early death of flies, etc.)?

__Response: __This was a stochastic event. The fly line we used for expression of piggyBac transposase (BDSC_8285) is generally not growing well, and we could only use one eighth of all offspring to ensure correct segregation. We will make this clear in the text.

Line 160: What is the N number of "all cases"?

__Response: __This will be changed to “We performed Sanger sequencing for one established line for each of the 17 loci and confirmed clean excision of the piggyBac sites in all cases.”

Scale bars are missing in Fig. 3g,h.

__Response: __These will be included.

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Line 219: The labeling of the panels got mixed up. Panel F does not show an immunostaining.

__Response: __The labeling will be corrected.

Line 226 and Fig. 3h: It is unclear what area is shown in the inlay. The overview image highlights three POIs, but none seem to fit the inlay.

__Response: __The images were indeed misleading as the inlay did not show a magnification of the same focal plane. We will show the inlay together with the overview of the corresponding focal plane as part of Supplementary Figure 5 and will amend the text accordingly.

Line 233: Why was the transgenic marker not removed? The authors want to highlight the easy and advantage of marker removal, so leaving in the marker is an odd choice.

__Response: __In this case, we observed that flies become homozygous even with the marker, so we assumed that a marker removal would not be necessary. We are currently performing additional experiments to remove the marker and repeat the staining, which we will submit with a revised version of the manuscript.

Line 250: Why was only one isoform of hth tagged? Without a rational this seems to be an odd choice, in particular since the authors seem to suggest in the introduction (Line 38) that a disadvantage of previous technologies is the tagging of only selected isoforms.

__Response: __While expanding the introduction (see comment #4), we will also rephrase it to highlight that current CRISPR-based methods (MiMIC and CRIMIC) are designed to tag all isoforms simultaneously or select isoforms, whereas overexpression constructs are limited to one isoform. In contrast, ExTaSy allows tagging of all isoforms that share a terminus. We will emphasize advantages and disadvantages in the discussion. In the case of hth, three different C-termini are annotated, and we are currently performing experiments to also tag the other termini and co-stain them with Ubx. We will submit the results in a revised version of the manuscript.

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Reviewer #1 (Significance (Required)):

SIGNIFICANCE

ExTaSy assembles a set of well-established tools, namely CRISPR-mediated HDR, piggyBac-based marker excision, and φC31-mediated RMCE, into a unified, single-vector framework for endogenous protein tagging in Drosophila. The individual components have all been described and are in routine use in the field; the conceptual advance is therefore limited. Nevertheless, the integration of these features into a streamlined platform with accompanying automated design software represents a practical contribution that is likely to be of genuine utility to the Drosophila community, particularly for laboratories without specialist transgenesis infrastructure.

The possibility of tag exchange by fly crossing is the most distinctive feature of the system. However, as discussed above, this is currently demonstrated at only five loci with a single replacement tag, which limits the conclusions that can be drawn about its generality. More broadly, ExTaSy employs well-proven strategies throughout, which is a source of reliability but also means that the study does not incorporate more recent developments in the field. For example, approaches based on single-strand annealing, such as the recently described Seed/Harvest system (Aguilar et al., 2024), can achieve entirely scarless marker removal and thus circumvent the TTAA scar left by piggyBac excision, a limitation the authors themselves acknowledge may reduce expression at modified N-terminal loci. Similarly, the current system is restricted to N- and C-terminal tagging. Given that the goal of endogenous tagging is to minimally perturb protein function, and given the now widespread availability of high-quality protein structure predictions for the Drosophila proteome, a modern tagging platform might be expected to use structural modelling to identify optimal insertion sites irrespective of their location. These are not oversights that diminish the practical value of the current work, but highlight that this study does not always operate at the cutting edge of method development in this area. A brief discussion of these more recent developments in the context of ExTaSy's design choices would usefully situate the work within the broader landscape and help readers understand both what the system offers today and where improvements are likely to come from.

__Responses: __

• As stated above, we are currently performing experiments to further validate the tag exchange.
• Regarding the SEED/Harvest system, we have considered this; however, this would leave both flanking attP/attB sites at the genomic locus rather than only the site between the tag and the CDS. Both sites would have to be incorporated into the CDS or they would leave an even bigger scar. Additionally, since SEED/Harvest relies on micro-homology between two tag halves, it would require removal of the transgenesis marker before tagged lines become usable. Our system is advantageous in that C-terminally tagged lines can usually be used immediately. However, we will refer to the paper by Aguilar et al. and discuss how a similar system could be incorporated into ExTaSy.
• Regarding structure-function predictions, these could be incorporated into the bioinformatic pipeline. It would then be possible to modify ExTaSy to introduce tags internally together with a SEED/Harvest-like modification. We will include this in the discussion.

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

Summary

Hubbert et al. describes ExTaSy (Exchangeable Tagging System), a method for endogenous protein tagging in fruitflies. The technique attempts to address some limitations of current tagging strategies, such as non-physiological expression from transgenes, disruption of the target gene, and limited usefulness of a single tag type. The basic approach is not novel, rather it effectively incorporates ideas from several previously published methods:

• Crispr-based release of the HDR donor from the backbone in vivo (Kanca et al., 2019 and 2021).
• PBac scarless tagging (flycrisprdesign)
• In vivo RMCE to swap out tags (Nagarkar-Jaiswal et al., 2015) Although not novel, the authors show the completeness and effectiveness of the approach. They were able to tag genes across multiple chromosomes, with knock-in rates comparable to other approaches, and demonstrate tag swapping through RMCE. Overall, this work introduces a versatile and modular platform that combines several previous innovations into a single effective package.

Major comments

1.The manuscript would benefit from a more upfront discussion of how ExTaSy relates to existing methods. As currently written, the implies a higher degree of novelty than is warranted, since ExTaSy combine several previously established approaches, including, as already noted. While this is valuable, the authors should more clearly acknowledge in the abstract and introduction that the primary advance is the unification and streamlining of these existing technologies into a single platform, rather than the introduction of fundamentally new components.

__Response: __While we did cite most of the publications mentioned by the reviewer, we will make clearer that our system combines several previously established Drosophila systems and is not per se a novel invention. We will expand the introduction and discussion to reflect this and cite additional publications.

• *

2.Comparison to prior systems. The manuscript should include a direct comparison to existing tagging pipelines. For example: What practical steps are eliminated relative to prior approaches? Does ExTaSy reduce the number of injections or constructs required? How does the workflow differ in terms of time, cost, or technical expertise? This is vaguely addressed in the discussion, but more specific and clear comparisons would improve things for the reader who is trying to decide which method to use. For example, how does this strategy directly compare with the protein trap alleles described in Kanca et al., 2022? This could be done as a supplemental table.

__Response: __A similar concern has been raised by reviewer #1 (comment #4). We will expand the introduction and the discussion to compare ExTaSy in more detail with other methods, highlighting advantages and disadvantages of each.

3.Only 4 successful RMCE swaps are presented. This is too few to make a confident conclusion about the efficiency. The authors should do at least 4 more and include negative data.

__Response: __A similar point has been made by reviewer #1 (comment #3). We are in the process of expanding the number of fly stocks for which tags have been exchanged and will be able to provide a more rigorous characterization with an updated version of the manuscript.

4.Some discussion of the potential limitations of the linker from the residual att sites is needed.

__Response: __We will include this in the discussion.

Minor comments

1.It would be helpful to include a workflow overview figure summarizing the full pipeline.

__Response: __We will include such a figure in the supplement.

2.Line 124: Most genes we tagged at the C-terminus were homozygous viable, indicating limited detrimental effects. Need to include the numbers? What is "most genes."

__Response: __We will include these numbers in the text.

3.Briefly explain how the tested genes were selected (e.g., random, representative, biased toward certain classes), as this could affect interpretation of generalizability. If most of the genes are essential for viability, this makes the viability of tagged lines more impressive.

__Response: __This is an excellent suggestion, and we thank the reviewer for pointing this out. We have mainly tagged genes that are relevant for work in our labs and for collaborators, focusing almost entirely on transcription factor-encoding genes that are largely essential for normal development. We will include a brief discussion of this.

Reviewer #2 (Significance (Required)):

Significance

1.General assessment: This study presents ExTaSy, a practical and well-executed platform for endogenous protein tagging in Drosophila. Its main strength is the integration of multiple existing technologies into a streamlined workflow that enables tagging, marker removal, and tag swapping. The system is clearly functional and broadly applicable. However, the conceptual novelty is limited, and the manuscript should more explicitly frame the work as an engineering advance. Tagging and RMCE efficiencies are moderate.

2.Advance: ExTaSy represents a technical advance that combines CRISPR HDR tagging, piggyBac scarless editing, and RMCE into a single platform. The biggest improvement is the ability to tag once and flexibly swap tags via crosses, reducing the need for repeated genome engineering. This extends existing methods by improving experimental flexibility.

3.Audience: This work will primarily interest a specialized audience in Drosophila genetics, CRISPR technologies, and functional genomics, with broader relevance to researchers developing tagging systems in other model organisms.

4.Field of expertise: CRISPR screening, Drosophila genetics, functional genomics. No limitations on my ability to evaluate.

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

This methods paper is targeting the long-standing ambition of how to most efficiently tag proteins at the endogenous gene locus in Drosophila. Since the invention of CRISPR-Cas9 many genes have been successfully modified in Drosophila, but the community is still lacking a large collection of tagged proteins under endogenous control made with the same method.

This manuscript is using a small tag, 3xHA, which supposedly is easier to integrate, and the design allows to then swap the tag with larger fluorescent tags, solely by fly crossing. Then, the dsRed or white markers, allowing identification, can be removed with a biggybac recombinase leaving only a small scar. However, attP/B/R scars do remain. Design and cloning appear straightforward. Overall, this is an interesting strategy.

However, the manuscript falls short in really describing the resource, apart from the cloning design. A more rigorous analysis of a number of lines should be presented to better judge if the strategy practically works. It is quite disappointing to see that only 2 or 3 genes/proteins were analysed here in a bit more detail. This does not sound like a very straightforward resource that aims to go large scale.

Major comments:

1. The important novelty here is not only the design that allows high-throughput cloning but more importantly that the tagged lines are actually correct and functional. To present this better, I suggest to rearrange Figure 1 to show the flow: 65 constructs cloned, 41 "successfully" inserted. Of how many the dsRed marker was removed, of how many expression or function was tested? Hence the reader knows about the current state of the resource. These numbers would be informative to have in the abstract, too.

__Response: __We will include these numbers in the abstract. Reviewer 2 asked for an overview figure of the workflow, which we will include as a supplementary figure, where we can also include numbers as suggested by this reviewer.

The 41 tagged gene insertions need at least some basic characterisation to verify that they are at the correct place or make a functional protein. Which genes were chosen? I do not see 41 genes tagged in the table provided. I supposed the N-terminal tags should initially be loss of function. Are the N-term lines lethal when inserted in an essential gene? Again, this could be shown in an overview, instead by a non-quantitative statement in the text.

__Response: __We have verified the insertion site of the lines with genotyping PCR. We will include a table to show in more detail which genes were tagged at which terminus, and which protein isoforms are captured by the respective tag.

• *

How many of the 41 tagged proteins are functional? The authors only provide information on Ubx-3xHA (functional) and Mef2-3xHA (non-functional), which I find weak.

__Response: __We will include this information in the table mentioned in the above comment.

Stainings are only shown for 2 proteins, Ubx-GFP and Exd-3xHA. How about the others?

__Response: __We are currently in the process of using ExTaSy to establish a library of tagged fly lines, which we intend to characterize in more detail and publish separately. For the current manuscript, we prefer to focus on the methodology of the tagging system itself.

I am not sure about how to calculate the transgenesis rates, but strictly speaking to ones that did not result in an insertion should also be counted for the statistics, I guess.

__Response: __There is indeed no commonly agreed upon way to calculate these rates, and it is done differently in different publications. We felt that metrics that discriminate between the overall success rate (i.e., all those injections that lead to transgenics) and the success rate within successful injections would be most useful. We will try to make clear in the text where we refer to all attempts and where we exclusively refer to the successful ones.

Minor comments:

1. The introduction states that ExTaSy would tag all isoforms of genes. However, I find this an overstatement, as for complex genes tagging at the one place cannot always label all isoforms, see the Hth line generated here (Iso E).

__Response: __This was indeed badly phrased and we will correct the wording also in response to reviewer #1 comment #14 to reflect that overexpression constructs are limited to a specific isoform, whereas ExTaSy enables simultaneous tagging of all isoforms that share a terminus.

Why does it matter on which chromosome the target gene is? This can be moved to supplement. I would rather like to know what the genes are.

__Response: __We presume that the reviewer refers to Figure 1, where we show the success rates for individual chromosomes. We felt that the lower success rate for injections targeting gene on chr3 (which is, as we describe, due to lower survival of the injection line) warranted this separation by chromosome. As stated above, we will include a list of tagged genes as a table.

**Referees cross-commenting**

I agree with the 2 other reviewer's points. In particular that the knock-in lines need better verifications. This was also my major point.

__Response: __As also stated for reviewer #1 comment #1, we have now begun to run whole-fragment PCRs for all loci to investigate this further and will report the results in a revised version of the manuscript.

Reviewer #3 (Significance (Required)):

The methodology presented here is per se not really new. The 3xP3-dsRed eye marker is standard, its removal by biggbac transposase has been done before and RMCE to change the tagging cassettes with attP/B is done since many years. The latter has the disadvantage to not be seamless, as one attR site remains, which is translated, the other attR site remains in the 5'- or 3'-UTR, which can have an effect. U6-driven sgRNA expression is also standard.

__Response: __We will make clearer that our system combines several previously established Drosophila systems and is not per se a novel invention. We will expand the introduction and discussion to reflect this and cite additional publications.

The design includes the sgRNA and the HDR template cassette in a single vector, which is smart and makes cloning straight forward. Again, the paper would be stronger if the list of all cloned clones would be listed (are 65 all that were clones or all that were injected?

__Response: __We will include this as a table.

As the authors do not rigorously test the function of the tagged genes, it is hard to judge how valuable the pipeline is. This can be easily solved by providing more data that support the easy, high-throughput exchange tagging pipeline that produces tagged Drosophila lines that are useful to the community.

__Response: __As stated above, we plan to publish a more detailed analysis of tagged lines as a separate resource paper. We will state in the manuscript which lines were homozygous viable before and after marker removal, which gives at least an indication of whether the tagged protein is functional.

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Referee #3

Evidence, reproducibility and clarity

This methods paper is targeting the long-standing ambition of how to most efficiently tag proteins at the endogenous gene locus in Drosophila. Since the invention of CRISPR-Cas9 many genes have been successfully modified in Drosophila, but the community is still lacking a large collection of tagged proteins under endogenous control made with the same method. This manuscript is using a small tag, 3xHA, which supposedly is easier to integrate, and the design allows to then swap the tag with larger fluorescent tags, solely by fly crossing. Then, the dsRed or white markers, allowing identification, can be removed with a biggybac recombinase leaving only a small scar. However, attP/B/R scars do remain. Design and cloning appear straightforward. Overall, this is an interesting strategy. However, the manuscript falls short in really describing the resource, apart from the cloning design. A more rigorous analysis of a number of lines should be presented to better judge if the strategy practically works. It is quite disappointing to see that only 2 or 3 genes/proteins were analysed here in a bit more detail. This does not sound like a very straightforward resource that aims to go large scale.

Major comments:

1. The important novelty here is not only the design that allows high-throughput cloning but more importantly that the tagged lines are actually correct and functional. To present this better, I suggest to rearrange Figure 1 to show the flow: 65 constructs cloned, 41 "successfully" inserted. Of how many the dsRed marker was removed, of how many expression or function was tested? Hence the reader knows about the current state of the resource. These numbers would be informative to have in the abstract, too.
2. The 41 tagged gene insertions need at least some basic characterisation to verify that they are at the correct place or make a functional protein. Which genes were chosen? I do not see 41 genes tagged in the table provided. I supposed the N-terminal tags should initially be loss of function. Are the N-term lines lethal when inserted in an essential gene? Again, this could be shown in an overview, instead by a non-quantitative statement in the text.
3. How many of the 41 tagged proteins are functional? The authors only provide information on Ubx-3xHA (functional) and Mef2-3xHA (non-functional), which I find weak.
4. Stainings are only shown for 2 proteins, Ubx-GFP and Exd-3xHA. How about the others?
5. I am not sure about how to calculate the transgenesis rates, but strictly speaking to ones that did not result in an insertion should also be counted for the statistics, I guess.

Minor comments:

1. The introduction states that ExTaSy would tag all isoforms of genes. However, I find this an overstatement, as for complex genes tagging at the one place cannot always label all isoforms, see the Hth line generated here (Iso E).
2. Why does it matter on which chromosome the target gene is? This can be moved to supplement. I would rather like to know what the genes are.

Referees cross-commenting

I agree with the 2 other reviewer's points. In particular that the knock-in lines need better verifications. This was also my major point.

Significance

The methodology presented here is per se not really new. The 3xP3-dsRed eye marker is standard, its removal by biggbac transposase has been done before and RMCE to change the tagging cassettes with attP/B is done since many years. The latter has the disadvantage to not be seamless, as one attR site remains, which is translated, the other attR site remains in the 5'- or 3'-UTR, which can have an effect. U6-driven sgRNA expression is also standard. The design includes the sgRNA and the HDR template cassette in a single vector, which is smart and makes cloning straight forward. Again, the paper would be stronger if the list of all cloned clones would be listed (are 65 all that were clones or all that were injected?

As the authors do not rigorously test the function of the tagged genes, it is hard to judge how valuable the pipeline is. This can be easily solved by providing more data that support the easy, high-throughput exchange tagging pipeline that produces tagged Drosophila lines that are useful to the community.

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Referee #2

Evidence, reproducibility and clarity

Summary

Hubbert et al. describes ExTaSy (Exchangeable Tagging System), a method for endogenous protein tagging in fruitflies. The technique attempts to address some limitations of current tagging strategies, such as non-physiological expression from transgenes, disruption of the target gene, and limited usefulness of a single tag type. The basic approach is not novel, rather it effectively incorporates ideas from several previously published methods:

• Crispr-based release of the HDR donor from the backbone in vivo (Kanca et al., 2019 and 2021).
• PBac scarless tagging (flycrisprdesign)
• In vivo RMCE to swap out tags (Nagarkar-Jaiswal et al., 2015) Although not novel, the authors show the completeness and effectiveness of the approach. They were able to tag genes across multiple chromosomes, with knock-in rates comparable to other approaches, and demonstrate tag swapping through RMCE. Overall, this work introduces a versatile and modular platform that combines several previous innovations into a single effective package.

Major comments

1.The manuscript would benefit from a more upfront discussion of how ExTaSy relates to existing methods. As currently written, the implies a higher degree of novelty than is warranted, since ExTaSy combine several previously established approaches, including, as already noted. While this is valuable, the authors should more clearly acknowledge in the abstract and introduction that the primary advance is the unification and streamlining of these existing technologies into a single platform, rather than the introduction of fundamentally new components. 2.Comparison to prior systems. The manuscript should include a direct comparison to existing tagging pipelines. For example: What practical steps are eliminated relative to prior approaches? Does ExTaSy reduce the number of injections or constructs required? How does the workflow differ in terms of time, cost, or technical expertise? This is vaguely addressed in the discussion, but more specific and clear comparisons would improve things for the reader who is trying to decide which method to use. For example, how does this strategy directly compare with the protein trap alleles described in Kanca et al., 2022? This could be done as a supplemental table. 3.Only 4 successful RMCE swaps are presented. This is too few to make a confident conclusion about the efficiency. The authors should do at least 4 more and include negative data. 4.Some discussion of the potential limitations of the linker from the residual att sites is needed.

Minor comments

1.It would be helpful to include a workflow overview figure summarizing the full pipeline. 2.Line 124: Most genes we tagged at the C-terminus were homozygous viable, indicating limited detrimental effects. Need to include the numbers? What is "most genes." 3.Briefly explain how the tested genes were selected (e.g., random, representative, biased toward certain classes), as this could affect interpretation of generalizability. If most of the genes are essential for viability, this makes the viability of tagged lines more impressive.

Significance

1.General assessment: This study presents ExTaSy, a practical and well-executed platform for endogenous protein tagging in Drosophila. Its main strength is the integration of multiple existing technologies into a streamlined workflow that enables tagging, marker removal, and tag swapping. The system is clearly functional and broadly applicable. However, the conceptual novelty is limited, and the manuscript should more explicitly frame the work as an engineering advance. Tagging and RMCE efficiencies are moderate. 2.Advance: ExTaSy represents a technical advance that combines CRISPR HDR tagging, piggyBac scarless editing, and RMCE into a single platform. The biggest improvement is the ability to tag once and flexibly swap tags via crosses, reducing the need for repeated genome engineering. This extends existing methods by improving experimental flexibility. 3.Audience: This work will primarily interest a specialized audience in Drosophila genetics, CRISPR technologies, and functional genomics, with broader relevance to researchers developing tagging systems in other model organisms. 4.Field of expertise: CRISPR screening, Drosophila genetics, functional genomics. No limitations on my ability to evaluate.

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Referee #1

Evidence, reproducibility and clarity

Summary

Hubbert and colleagues describe ExTaSy, a CRISPR-Cas9-based platform for the endogenous tagging of proteins in Drosophila melanogaster. The system combines several established molecular tools into a single-vector framework: homology-directed repair (HDR) for the insertion of a 3XHA tag at the endogenous locus, piggyBac transposase-mediated near-scarless removal of a transgenic selection marker, and φC31 integrase-mediated recombination-mediated cassette exchange (RMCE) for subsequent tag swapping. The authors demonstrate the system across a set of 65 genomic loci and provide a bioinformatic pipeline to automate guide RNA and homology arm design.

Major Comments

1. Validation of knock-in lines is inadequate and does not reflect current standards in the field.

The authors state that correct insertions were confirmed using "two PCRs per inserted fragment done with primers binding to the 5' and 3' ends of the inserted DNA and corresponding gene-specific validation primers." This strategy is well known to produce false positives, as it cannot distinguish correctly targeted single-copy integrants from concatemeric insertions at the target locus (e.g. Skryabin et al., 2020). The current standard for validating CRISPR-mediated knock-ins requires PCR amplification using primers that anneal outside the homology arms and span the entire inserted cassette. These reactions must be performed under conditions that minimise the formation of PCR chimeras, specifically low cycle numbers and use of a high-processivity polymerase. The authors should either provide data from such experiments for their characterised lines, or clearly acknowledge this limitation and qualify their efficiency estimates accordingly (see related point 2 below). 2. Reported efficiency metrics do not adequately distinguish correctly targeted integrants from marker-positive flies.

A related concern is that many of the efficiency parameters reported in the manuscript appear to be based solely on the detection of the marker cassette. The 63.1% overall success rate, for example, seemingly reflects the recovery of DsRed-positive flies rather than of sequence validated, single-copy, on-target integrants. These are fundamentally different quantities, with only the latter being of practical value for the users of the described technique. The authors should either provide data that properly accounts for correct integration, or more carefully define what each reported metric represents and explicitly acknowledge the limitations of using marker presence as a proxy for successful knock-in. 3. The characterisation of tag exchange requires expansion or more careful framing of its scope.

The possibility of exchanging tags through fly crosses rather than repeated microinjections is, in the view of this reviewer, the most practically useful feature of ExTaSy and the aspect most likely to drive community adoption. It is therefore important that this feature is characterised with sufficient rigour to allow prospective users to assess its reliability. In the current manuscript, tag exchange has been demonstrated at only five loci using a single replacement tag (sfGFP). The dataset includes one outright failure (the Met C-terminus) and one instance of an unexpected 9 bp insertion at the recombination site, leaving the success rates and failure modes across a broader range of loci and tags uncharacterised. The authors should either expand the tag exchange experiments to cover a more representative set of conditions, or frame the current data explicitly as a proof of concept and limit their conclusions about the practical utility of tag exchange accordingly. In either case, the value of this work to the community would be substantially increased if a collection of donor lines carrying the most commonly used tags for different applications, as the authors themselves enumerate in the Discussion, were generated and deposited at a public stock centre such as the VDRC concurrent with publication. On this note, it is also worth flagging that at present the plasmids described in this study have not yet been deposited at Addgene or the European Plasmid Repository, and that fly lines are available only on request. For a methods paper aimed at community adoption, deposition of reagents in publicly accessible repositories at the time of publication is the expected standard. 4. The Introduction should better reflect the current state of the field, including explicit comparison with MiMIC and CRIMIC.

The introduction would benefit from a clearer distinction between transgene-based approaches that introduce additional gene copies and true CRISPR-mediated knock-ins at the endogenous locus. As it stands, the discussion of prior methods does not sufficiently acknowledge that CRISPR-based knock-in is already the standard approach in Drosophila, and that the individual techniques employed in ExTaSy are well established. Notably, the MiMIC and CRIMIC systems (Nagarkar-Jaiswal et al., 2015; Li-Kroeger et al., 2018), which also support RMCE-based tag exchange at endogenous loci and for which large collections of lines are already publicly available, are not adequately discussed. These are arguably the closest comparators to ExTaSy, and the authors should explicitly address how their approach differs from and offers advantages over this existing framework, particularly given that MiMIC/CRIMIC insertions can also tag internal sites and thus avoid some of the terminus-specific complications described here.

Minor Comment

1. The labelling of sgRNA target sites in Figure 1 is inaccurate and should be corrected.

In Figure 1, the sgRNA target sites are annotated with triangles labelled "PAM synth." The presence of a PAM is necessary but not sufficient to define a target site; the label should therefore be changed to "target site" or an equivalent term. Additionally, the Methods section incorrectly expands PAM as "primary adjacent motif"; the correct expansion is "protospacer adjacent motif." 6. Could the fly crossing scheme in Figure S3 be simplified?

In the scheme in Fig. S3 the second step seems to be intended to introduce the hs-Flp and vase-Int transgenes. Would it not be possible to already incorporate the Integrase into the swap fly line when it is made and the hs-Flp into the ExTaSy line, thereby saving one generation? 7. Figure 1F has no call out in the main text. 8. Line 155: What was the reason for the low survival rate? Is this likely to be indicative of a problem during marker removal, or a stochastic event as not all fly crosses are always productive (bad food, early death of flies, etc.)? 9. Line 160: What is the N number of "all cases"? 10. Scale bars are missing in Fig. 3g,h. 11. Line 219: The labeling of the panels got mixed up. Panel F does not show an immunostaining. 12. Line 226 and Fig. 3h: It is unclear what area is shown in the inlay. The overview image highlights three POIs, but none seem to fit the inlay. 13. Line 233: Why was the transgenic marker not removed? The authors want to highlight the easy and advantage of marker removal, so leaving in the marker is an odd choice. 14. Line 250: Why was only one isoform of hth tagged? Without a rational this seems to be an odd choice, in particular since the authors seem to suggest in the introduction (Line 38) that a disadvantage of previous technologies is the tagging of only selected isoforms.

Significance

ExTaSy assembles a set of well-established tools, namely CRISPR-mediated HDR, piggyBac-based marker excision, and φC31-mediated RMCE, into a unified, single-vector framework for endogenous protein tagging in Drosophila. The individual components have all been described and are in routine use in the field; the conceptual advance is therefore limited. Nevertheless, the integration of these features into a streamlined platform with accompanying automated design software represents a practical contribution that is likely to be of genuine utility to the Drosophila community, particularly for laboratories without specialist transgenesis infrastructure.

The possibility of tag exchange by fly crossing is the most distinctive feature of the system. However, as discussed above, this is currently demonstrated at only five loci with a single replacement tag, which limits the conclusions that can be drawn about its generality. More broadly, ExTaSy employs well-proven strategies throughout, which is a source of reliability but also means that the study does not incorporate more recent developments in the field. For example, approaches based on single-strand annealing, such as the recently described Seed/Harvest system (Aguilar et al., 2024), can achieve entirely scarless marker removal and thus circumvent the TTAA scar left by piggyBac excision, a limitation the authors themselves acknowledge may reduce expression at modified N-terminal loci. Similarly, the current system is restricted to N- and C-terminal tagging. Given that the goal of endogenous tagging is to minimally perturb protein function, and given the now widespread availability of high-quality protein structure predictions for the Drosophila proteome, a modern tagging platform might be expected to use structural modelling to identify optimal insertion sites irrespective of their location. These are not oversights that diminish the practical value of the current work, but highlight that this study does not always operate at the cutting edge of method development in this area. A brief discussion of these more recent developments in the context of ExTaSy's design choices would usefully situate the work within the broader landscape and help readers understand both what the system offers today and where improvements are likely to come from.

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Reply to the reviewers

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

This paper describes the localisation of DNA repair proteins, which carry out their DNA repair function in the nucleus, to the cytoplasmic Golgi apparatus. Using the Human Protein Atlas to identify candidates, the authors use antibody localisation to show that a significant number of DNA repair proteins also localise at the Golgi. It appears that proteins involved in common DNA repair pathways localise to common regions of the Golgi. The Golgi-nucleus distribution of the DNA repairs proteins changes upon DNA damage, indicating a dynamic relationship. The authors focus on the DNA repair protein RAD51C and show that its loss from the Golgi and translocation to the nucleus upon DNA damage is mediated by the ATM kinase. Anchoring at the Golgi is shown to be mediated by the golgin giantin. A functional role for giantin in DNA repair is shown in knockdown studies, supporting a mechanism whereby Golgi anchoring of RAD51C, and possibly other DNA repair proteins, by giantin, is required to maintain proper control of DNA repair. The data are clear and support the authors' conclusions. The data are carefully quantified throughout. I found the text easy to read.

• Major points:*

• 1.) To validate the Golgi localisation, KD using siRNA was used. It was deemed that a signal reduction of 25% was enough to indicate specific antibody labelling. This seems like a low number, and not very stringent. For some of the hits, expressing tagged versions of the proteins would greatly strengthen the Golgi assignment. This may not be possible for all, but for RAD51C would seem an important experiment. *

Response: We thank the reviewer for raising the important issue of antibody validation stringency. We agree that for a single-candidate study, a larger reduction after knockdown would generally be preferable. In our case, the 25% cutoff was used only in the primary high-content screening step as part of an intentionally inclusive two-stage workflow, for the following reasons:

First, because this dataset is generated in a screening format across hundreds of targets, knockdown-efficiency, protein turnover, and the relative size of the Golgi associated pool are unknown and highly variable between genes. For many proteins the Golgi pool represents a small fraction of total cellular signal, and a modest change in total abundance can translate into a smaller absolute change in the Golgi ROI after segmentation, background subtraction, and imaging noise. We therefore selected a permissive cutoff to reduce false negatives and ensure we did not systematically miss candidates with slower turnover, partial knockdown, or small Golgi pools. This strategy is consistent with large scale subcellular mapping efforts, including the Human Protein Atlas, where genetic depletion by siRNA is used as a key validation pillar for immunofluorescence localization and is combined with additional validation strategies when deeper confidence is required (Stadler et al, 2012). Furthermore, it is important to note that this validation was performed in a high-content screening format in which fixation, permeabilisation, antibody concentration, and blocking conditions were kept uniform across all candidates rather than optimised for each individual antibody. In standard single-target immunofluorescence experiments, these parameters would be titrated to maximise signal-to-noise for the specific antibody and antigen in question. Under non-optimised screening conditions, the absolute magnitude of signal change upon knockdown is inherently attenuated compared to what would be expected from a purpose-optimised assay. We therefore consider a 25% reduction threshold under these uniform, non-optimised screening conditions to be a meaningful and appropriately calibrated criterion.

Second, we wish to clarify that the primary intent of our screen was not to validate the Golgi-nuclear localisation of any single protein in isolation, but rather to identify whether entire functional pathways are represented at the two organelles. This is precisely why the bioinformatic network analysis was performed as an integral part of the workflow, and not as an afterthought. The finding that the validated hit list is significantly enriched for coherent functional clusters, most notably a network spanning multiple core DNA repair pathways (HR, MMR, BER, MMEJ) serves as an in silico validation of the dataset as a whole. The emergence of pathway-level organisation, with proteins from the same repair pathways co-associating, localising to the same Golgi sub-compartments, and redistributing in the same direction upon genotoxic stimuli, provides biological coherence that goes beyond what individual antibody validation can offer, and substantially reduces the likelihood that the Golgi signal represents a collection of unrelated false positives.

Third, our mechanistic conclusions do not rely on the 25% screening threshold. For RAD51C, we used multiple orthogonal validation approaches, including independent antibodies recognizing distinct RAD51C epitopes and genetic depletion, supported by biochemical evidence.

In response to this comment, we have provided the full screening validation dataset as source data (Supplementary____Table S1), including intensity changes for the candidates, so that readers can inspect the distributions and apply their own thresholds. We have also clarified in the Results section the rationale behind our screening strategy (lines 128-139) and the role of the bioinformatic network analysis as an integral validation step (lines 141-156).

Turning to the specific suggestion of tagged RAD51C, we fully agree that tagged proteins can provide valuable orthogonal validation. We attempted endogenous tagging using CRISPR-mediated homologous recombination but were unable to obtain viable colonies following editing, consistent with the essential role of RAD51C in homologous recombination. We also attempted ectopic expression of tagged RAD51C but were unable to obtain constructs that preserved physiological expression levels, maintained robust cell viability or produced interpretable localization. This difficulty is not unique to our laboratory: colleagues working on RAD51 paralog complexes have reported that tagging or overexpression of RAD51C perturbs both its localisation and its ability to form functional paralog complexes (Greenhough et al, 2023; Rawal et al, 2023; Somyajit et al, 2015; Berti et al, 2020) all use purified complexes or untagged proteins for functional assays. We discussed these challenges extensively with experts in the DNA damage repair field at several international meetings (EMBO Sounio, Keystone Symposia, German DNA Repair Society). For these reasons, we relied on orthogonal approaches that do not require tagging (genetic depletion plus independent antibodies, and biochemical fractionation) to support the Golgi localization claim. We agree with the reviewer that this represents a limitation of this study, and we addressed these concerns in the discussion of our revised manuscript (lines 630-641).

*2.) The total signal should be quantified for each DNA repair protein upon genotoxic stress, in addition to the Golgi to nucleus ratio. For many of the proteins it looks like the total signal goes down, which could influence interpretation. *

Response: __We thank the reviewer for this important point. We wish to clarify that our imaging pipeline uses marker-based segmentation throughout, the Golgi compartment is segmented using GM130 and the nucleus using Hoechst, as unsegmented whole-cell masks without organelle markers yield unreliable intensity measurements in this experimental setup. True total cellular signal is therefore not directly accessible in this dataset. In the revised manuscript we provide the absolute fluorescence intensities for both the Golgi and nuclear compartments separately. In addition, we now include total (Golgi + nuclear) intensity measurements for each protein (__Supplementary Figures 3D, 4D, __and 5E__) as the most reliable proxy for overall protein distribution. These data are presented alongside the redistribution ratio to enable comprehensive interpretation.

As the reviewer correctly notes, a subset of proteins shows a reduction in total signal after treatment, particularly with doxorubicin. This is consistent with known effects of doxorubicin-induced DNA damage on cellular proteostasis, including widespread ubiquitination and suppression of protein translation (Halim et al, 2018). Several DDR regulators are subject to ubiquitin-dependent turnover following genotoxic stress, such as CHK1 (Zhang et al, 2005). More broadly, ubiquitin and proteasome mediated regulation is an integral component of the DNA damage response and can affect the abundance and detectability of DDR factors (Brinkmann et al, 2015). Changes in abundance are therefore an expected biological feature of the response. For this reason, we used the Golgi-to-nucleus ratio as the primary redistribution readout, as it captures relative compartmental partitioning independently of changes in total protein levels.

*3.) The study would benefit from live imaging of the Golgi to nucleus translocation of RAD51C. This would give a better indication of dynamics. *

__Response: __We agree that live imaging would directly visualize the dynamics of RAD51C redistribution between the Golgi and the nucleus. This was indeed one of our initial goals following the identification of the Golgi-associated RAD51C pool. However, as described above in our response to Major Comment 1, live imaging requires a fluorescently tagged RAD51C construct, and all tagging strategies we attempted, both endogenous CRISPR-mediated tagging and ectopic expression, failed to yield cell lines with robust signal while preserving physiological behaviour. This appears to be a broader challenge for highly conserved and functionally constrained DNA repair proteins, and is not unique to our laboratory.

Given these constraints, we focused on tag-independent approaches: multiple independent RAD51C antibodies combined with genetic depletion controls, quantitative fixed-cell time courses, and biochemical fractionation. These orthogonal datasets together support compartment-specific changes over time in a manner consistent with redistribution. We have clarified this limitation explicitly in the manuscript and avoided any wording that could be interpreted as implying direct single-molecule tracking in live cells. We present this as an important avenue for future work, contingent on the development of viable RAD51C-expressing cell lines (lines 630-641).

*4.) The double depletion experiments suggest a functional relationship between giantin and RAD51C. But they do not formally show it. Experiments to more directly address the functional role of the interaction between these two proteins would strengthen the study. *

Response: We agree with the reviewer that double depletion alone cannot formally prove that the physical Giantin-RAD51C interaction is the sole determinant of the observed DDR phenotypes. However, we would like to highlight the breadth of evidence we have assembled in support of this functional relationship:

• Physical interaction between endogenous Giantin and RAD51C demonstrated by colocalisation (Figure 4F-G) and co-immunoprecipitation (Figure 4H-I).
• Damage-induced dissociation of the Giantin-RAD51C complex that is prevented by ATM inhibition or Importazole treatment, directly linking the interaction to the DDR signalling axis (Figure 3K-P)
• Premature nuclear accumulation of RAD51C upon Giantin depletion, producing aberrant nuclear foci lacking canonical HR markers and impaired ATM signalling (Figure 4B-E & J-M)
• DR-GFP reporter assay confirming that Giantin depletion reduces HR efficiency to approximately 60% of control, consistent with the reduction previously reported in the genome-wide HR screen (Adamson et al. 2012) and validating the functional significance of Giantin in HR (Figure 5L).
• Partial rescue of ATM phosphorylation, genomic instability and proliferation phenotypes by RAD51C co-depletion, arguing for RAD51C as a functionally relevant conduit of the Giantin-dependent phenotype (Figures 5M-5P). These observations are further supported by the established literature on RAD51C function, its roles in CHK2 phosphorylation, replication fork stabilisation, and RAD51 filament formation (Badie et al, 2009; Somyajit et al, 2015; Prakash et al, 2022) providing a mechanistically coherent framework in which mislocalisation of RAD51C, whether directly or indirectly through Giantin, leads to dysregulation of DDR signalling and repair capacity, as we directly demonstrate with the HR efficiency assay.

Nonetheless, we fully agree that the most direct proof of the functional relevance of the physical Giantin-RAD51C interaction would come from separation-of-function experiments, ideally using an interaction-deficient Giantin mutant or an RAD51C variant unable to bind Giantin. We wish to be transparent that both approaches face substantial technical barriers in this system. RAD51C tagging consistently compromised cell viability and protein function, precluding the generation of interaction-deficient variants at physiological expression levels. Engineering an interaction-deficient Giantin mutant presents an independent challenge: Giantin is one of the largest Golgi matrix proteins (~376 kDa), composed almost entirely of extended coiled-coil domains that are resistant to structural prediction, and identifying a discrete RAD51C interaction interface without disrupting broader scaffolding function would require a dedicated structural and biochemical programme. We have framed these explicitly as the most important future priorities in the Discussion (lines 555-564), rather than over-interpreting the current data.

*5.) The Kaplan-Meier plots in Fig S9 seems to be quite selective in that only breast cancer is shown. Does giantin reduction correlate with poor prognosis in other cancers? *

__Response: __We thank the reviewer for this suggestion. We initially focused on breast cancer because RAD51C is a clinically established hereditary breast and ovarian cancer susceptibility gene (Meindl et al, 2010; Ghannoum et al, 2023), providing direct clinical context for a study centred on RAD51C dynamics and genome stability. We agree however that restricting the survival analysis to a single cancer type can appear selective.

To address this directly, we expanded the in-silico survival analysis of Giantin (GOLGB1) using GEPIA2 (Tang et al, 2019) across all available TCGA cohorts (overall survival, median cutoff, FDR correction). In the pooled pan-cancer analysis, higher GOLGB1 expression is significantly associated with improved overall survival (HR(high) = 0.75, p = 6.6 × 10⁻¹⁵). When stratified by tumour type, the majority of individual associations do not reach statistical significance. The two most robust statistically significant associations are kidney renal clear cell carcinoma (KIRC; HR(high) = 0.57, p = 3.4 × 10⁻⁴), where high GOLGB1 expression is associated with improved survival, and lower-grade glioma (LGG; HR(high) = 1.5, p = 0.036), where the association is in the opposite direction. A significant association is also observed in thymoma (THYM; HR(high) = 7.3, p = 0.031), though this should be interpreted with caution given the small cohort size (n = 59). Notably, the breast cancer association observed in the KM Plotter analysis (HR = 0.71, p = 1.8 × 10⁻¹¹; n = 4,929) does not reach significance in the TCGA BRCA cohort (HR = 1.1, p = 0.68; n = 1,070), most likely reflecting the substantially smaller sample size of the TCGA cohort, which is approximately 4.6-fold smaller and therefore underpowered to detect a modest effect. These context-dependent associations are consistent with the tumour-type-specific roles of Golgi scaffolding proteins and are discussed accordingly in the revised manuscript.

In the revised manuscript we have retained the original breast cancer Kaplan-Meier plots and supplemented them with a pan-cancer survival map across all TCGA cohorts (lines 611-625; Figure S9G) and a summary table (Supplementary Table 3) reporting hazard ratios, sample sizes, and p-values for each tumour type, allowing readers to assess the clinical relevance of GOLGB1 expression.

*Minor points: There are a few grammatical errors here and there. The figures do not appear in the correct order in the text, which makes the early parts of the paper a bit difficult to follow. Some of the figures don't seem to clearly match the text. For example, it is mentioned that RAD51C labelling was done with 3 different antibodies. I could not find this data. *

Response: __We thank the reviewer for these helpful observations. In the revised manuscript we have (i) carefully proofread the text and corrected grammatical errors throughout; (ii) revised the Results section to ensure that figures and supplementary figures are cited in sequential order and that each panel is explicitly introduced before being discussed, improving readability in the early sections. and (iii) corrected figure callouts to ensure they match the text. In particular, the statement that RAD51C labeling was performed with three different antibodies has been linked to the corresponding figure panels in the Results section. Antibody identifiers, sources, and dilutions are clearly reported in the Methods and in the table in __Supplementary Table S1.

__ Reviewer #1 (Significance (Required)):__

*This paper is novel and should be of significant interest to the field. It has important implications for how we think about the Golgi apparatus, and for how DNA repair pathways may be controlled. The pattern is clearly complex, with many DNA repair proteins localising to the Golgi, and some showing opposite dynamics. However, by focussing on RAD51C and giantin, the paper nicely demonstrates a novel mechanism for controlling DNA repair by these proteins. *

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

Background - Eukaryotic cells rely on tightly regulated DNA repair pathways to preserve genome stability under the constant threat of both endogenous and exogenous genotoxic stress. While the nucleus, and to a lesser extent the mitochondria, is the primary site where DNA damage is detected and repaired, accumulating evidence indicates that extranuclear organelles, particularly the Golgi apparatus, play a surprisingly important role in modulating stress signaling, proteostasis, and the trafficking/activation of key DNA repair factors.

• Emerging evidence has shown that genotoxic stress can result in a major remodeling of the Golgi apparatus; however, the crosstalk between the Golgi and the nucleus, and its contribution to the DNA damage response, remains poorly defined. The present study offers timely insight by examining the spatiotemporal behavior of DNA repair proteins that shuttle between the Golgi and the nucleus, and how this trafficking contributes to the maintenance of genomic stability.*

Main findings - The authors employed the Human Protein Atlas (HPA) project to shortlist proteins that might link Golgi-nuclear function and validated each candidate using an siRNA-mediated antibody-validation pipeline, thereby identifying 163 proteins that localize to both the Golgi and the nucleus. Bioinformatic analysis of these candidates revealed a significant enrichment for DNA damage response (DDR) regulators, including multiple factors from core DNA repair pathways, suggesting that a portion of the DDR machinery may reside in the Golgi at steady state. Interestingly, the authors observed that dual-localizing DDR proteins undergo lesion-specific redistribution between the Golgi and the nucleus in response to specific types of DNA injuries. For instance, BER and MMEJ proteins shifted from nucleus to Golgi in response to doxorubicin, whereas MMR and HR proteins redistributed from Golgi to nucleus. This trend was reversed with H2O2 or KBrO3 treatments.

• To gain further insight into the link between the DDR and Golgi-nuclear communication, the authors focused on the HR factor RAD51C, which also plays a key role during the replicative stress response. The authors noticed that RAD51 is significantly associated with the Golgi, in addition to its known nuclear pool. Interestingly, they demonstrated that doxorubicin triggers the ATM-dependent release of this Golgi-tethered RAD51C pool and its Importin-β-mediated import into the nucleus, where it forms repair-associated foci. They further identified Giantin as the Golgi scaffold that anchors RAD51C at steady state in this subcellular compartment and showed that its depletion leads to premature nuclear accumulation of RAD51C, formation of aberrant RAD51C foci lacking canonical HR markers, reduced ATM activation, elevated genomic instability, and increased cell proliferation. *

Together, this study revealed an underappreciated and functionally meaningful spatiotemporal level of regulation within the DDR, suggesting that the Golgi, rather than functioning solely as a trafficking organelle, acts as a platform that anchors, releases, and temporally controls the availability of key DNA repair factors in response to genotoxic stress. In particular, the authors demonstrated that the timely and regulated release of RAD51C from the Golgi is essential for maintaining genome stability and is dependent on canonical DDR signaling pathways, including ATM activation and Importin-β-mediated nuclear import.

• Overall Critique - This manuscript offers a novel and compelling perspective on the regulation of the DDR by positioning the Golgi as an active participant in the spatiotemporal control of DNA repair factors. By integrating multiple experimental layers, including a systematic localization screening, a sub-Golgi mapping, several dynamic redistribution assays, and functional perturbation read-outs, the authors built a strong and coherent case for a biologically meaningful Golgi-nucleus communication axis during the DDR. Therefore, the study is timely and highly relevant for the DNA repair field, with broader implications for our understanding of how subcellular organelles coordinate genome maintenance and cellular homeostasis.

While the manuscript is clearly written and the figures are coherent and supportive of the main findings of the study, several issues should be addressed to ensure full interpretability and reproducibility.

Major Comments*

*1. Limited use of agents causing genotoxic stress - The authors report intriguing lesion-specific shifts in Golgi-nuclear redistribution, yet much of the mechanistic work relies heavily on doxorubicin, a pleiotropic drug that induces diverse forms of DNA damage beyond DSBs. Expanding the core analysis of the study to include a broader panel of mechanistically defined genotoxins (e.g., etoposide, camptothecin, neocarzinostatin, or ionizing radiation) would substantially strengthen the conclusion that the trafficking patterns reflect damage-type specificity rather than drug-specific off-target effects. Such broader analysis would also clarify whether Golgi-nucleus communication responds differentially to replication-associated breaks, Topo II-dependent lesions, oxidative stress, or crosslinks. *

__Response: __We thank the reviewer for this important point. We would first note that while doxorubicin is indeed pleiotropic, its primary and best-established mechanism of action is the poisoning of Topoisomerase II, leading to DNA double-strand breaks, a mechanism it shares with etoposide (van der Zanden et al, 2021; Thorn et al, 2011). The additional effects of doxorubicin, including reactive oxygen species generation and chromatin remodelling, are well-documented but secondary to this DSB-inducing activity, as we note in the revised manuscript. Nonetheless the goal of this study was not to comprehensively map lesion-specific trafficking for every DDR protein, but rather to establish the existence of a dynamic Golgi-nucleus redistribution axis and then focus mechanistically on the validated targets, in this case RAD51C. The lesion-dependent redistribution patterns are therefore presented as an initial, hypothesis-generating observation emerging from our screening and characterisation framework. A systematic, lesion-by-lesion dissection of redistribution kinetics across the broader DDR network would represent a substantial additional study and is beyond the scope of the present work.

Importantly, our key mechanistic observations for RAD51C are not restricted to doxorubicin. We tested a panel of genotoxic agents covering mechanistically distinct lesion classes: camptothecin (CPT; Topoisomerase I-associated replication breaks), etoposide (ETO; Topoisomerase II-dependent DSBs), and mitomycin C (MMC; interstrand crosslinks) (Figures S8A-S8I). Across all DSB-inducing agents, RAD51C consistently redistributed from the Golgi to the nucleus, demonstrating that this response is not a doxorubicin-specific off-target effect. Notably, RAD51C did not redistribute in response to oxidative lesions induced by hydrogen peroxide or potassium bromate, consistent with its established role in homologous recombination and DSB repair rather than oxidative damage pathways, as discussed in the manuscript. This lesion-type selectivity provides additional evidence that the Golgi-nuclear redistribution we observe is a biologically specific response rather than a non-selective stress effect.

*2. Functional implications of RAD51C redistribution for HR efficiency - Although the study convincingly demonstrates a release of RAD51C from the Golgi and its subsequent nuclear foci formation, it remains unclear how this redistribution influences HR efficiency. Incorporating a functional HR assay (e.g., DR-GFP reporter, RAD51 filament assembly, or fork protection assays) would help determine whether Golgi-anchored RAD51C release is directly required for HR or instead primarily modulates upstream DDR signaling. *

Response: __We thank the reviewer for this important suggestion. We have performed DR-GFP reporter assays to directly assess HR efficiency following Giantin and RAD51C depletion. Depletion of Giantin reduced HR efficiency to approximately 60% of control levels, and RAD51C depletion to approximately 40%, consistent with the HR reduction previously reported in the genome-wide HR screen (Adamson et al, 2012). Co-depletion of Giantin and RAD51C reduced HR to levels comparable to RAD51C depletion alone, suggesting that the effect of Giantin on HR is mediated primarily through RAD51C, consistent with RAD51C being the key effector of the Giantin-dependent spatial regulatory mechanism we describe. These data are included in the revised manuscript (__lines 455-465; Figure 5L).

*In addition, the manuscript does not fully reconcile how Golgi-tethering of RAD51C fits with its well-established nuclear roles during replication stress, where timely availability of RAD51C is essential for fork stabilization and restart. *

Response: __We agree that the nuclear function of RAD51C during replication stress is well established and important to reconcile with our findings. Our imaging data consistently show a detectable nuclear RAD51C population at steady state across all cell lines examined, and we do not propose that RAD51C is exclusively Golgi-localised. We suggest that the two pools serve distinct functional purposes: the constitutive nuclear pool supports ongoing replication fork stabilisation and restart, processes that require RAD51C availability independently of acute DNA damage, while the Golgi-tethered fraction represents a damage-responsive reserve that is released acutely upon DSB induction in an ATM-dependent manner. We wish to be transparent that this two-pool model is speculative at present, formally distinguishing the contributions of each pool would require direct labelling of the Golgi-anchored fraction, which was not technically feasible in this system as discussed above. Nonetheless, this model is consistent with established principles of signal-responsive protein sequestration in cell biology, and is directly supported by our Giantin depletion data: premature release of the Golgi pool leads to aberrant nuclear RAD51C foci lacking canonical HR markers and impaired ATM signalling, demonstrating that unscheduled nuclear accumulation is actively detrimental rather than simply redundant. We have added a paragraph to the revised Discussion explicitly framing the two-pool distinction as a working model and identifying direct pool-identity tracking as an important future direction (__lines 566-587).

*3. Specificity of Giantin-related phenotypes - The phenotypes observed upon Giantin depletion (e.g., increased micronuclei, comet tail moments, impaired ATM signaling, and elevated proliferation) could partially reflect a global dysfunction of the Golgi rather than RAD51C-specific tethering defects. Although co-depletion of RAD51C provides partial rescue, additional controls examining Golgi integrity, trafficking competence, or rescue with siRNA-resistant Giantin would help confirm specificity and distinguish direct from indirect effects. *

__Response: __We thank the reviewer for raising this important concern, which was a central consideration throughout our investigation. We address it through three complementary lines of evidence.

First, regarding Golgi structural integrity and trafficking competence: as previously reported, Giantin depletion has not been associated with strong Golgi fragmentation or major morphological alterations (Koreishi et al, 2013; Bergen et al, 2017; Stevenson et al, 2021), and we observed no significant Golgi fragmentation upon Giantin knockdown in our system. Consistent with the literature, Giantin has been implicated in specific cargo trafficking, most notably collagen secretion, rather than general secretory pathway function (Stevenson et al, 2021). To directly confirm that general Golgi trafficking competence was preserved in our experimental system, we performed the VSV-G-YFP trafficking assay (Presley et al, 1997), a well-established functional readout of general secretory trafficking. Giantin depletion did not result in a significant change in trafficking efficiency compared to control siRNA (Rebuttal Figure 1), consistent with the literature and arguing against a general collapse of Golgi function as the basis for the phenotypes observed.

Rebuttal ____Figure 1. VSV-G-YFP trafficking assay.

(A) Representative images of cells treated with control siRNA or giantin siRNA. Nuclei are stained with Hoechst. Total VSV-G-YFP (YFP-tsO45G) signal is shown together with antibody staining against VSV-G in non-permeabilized cells to assess cell surface levels. Scale bars, 10 μm.

(B) Quantification of VSV-G trafficking from two independent biological replicates.

Second, the phenotypes are RAD51C-dependent and not a generic Golgi dysfunction: the genomic instability and DDR signalling defects we observe upon Giantin depletion are not phenocopied by GMAP210 depletion, another Golgin family member, indicating that the phenotypes are not a generic consequence of Golgin loss. Critically, we now directly demonstrate using the DR-GFP reporter assay that Giantin depletion reduces HR efficiency to approximately 60% of control, and that co-depletion of RAD51C produces no further reduction beyond RAD51C depletion alone, consistent with RAD51C epistasis over Giantin for HR capacity (Figure 5L). This functional epistasis, together with the physical interaction between Giantin and RAD51C by co-immunoprecipitation, their co-localisation within the same Golgi sub-compartment, and the partial rescue of ATM phosphorylation, micronuclei formation and proliferation phenotypes upon RAD51C co-depletion, provides a coherent mechanistic chain linking Giantin specifically to RAD51C-dependent DDR outcomes. While we cannot formally exclude indirect contributions from other Giantin-associated factors, none of our observations are consistent with the phenotype arising from non-specific Golgi perturbation.

Third, Giantin may play a broader role in connecting DDR signalling to cytoplasmic and Golgi-resident processes, beyond RAD51C tethering alone: we consider this a feature of the biology rather than a confound. Golgins are well established as multi-cargo scaffolding platforms, and Giantin in particular occupies a strategic position where several processes converge: the tethering of DDR factors, the regulation of damage-induced signalling cascades, and the directional trafficking of repair factors between compartments. This would explain why Giantin depletion produces a phenotype that extends beyond what RAD51C co-depletion alone can fully rescue, and is consistent with the pathway-level coherence we observe across our screen. Understanding the full complement of Giantin-associated DDR interactions represents one of the most compelling directions emerging from this work.

In response to this comment, we have expanded the Discussion (lines 545-565) to explicitly propose that Giantin functions as a broader organisational node coordinating multiple DDR factors, while our data specifically and consistently implicate RAD51C as a primary conduit.

*4. Positioning of ATM in the Golgi-nuclear signaling - While ATM inhibition prevents RAD51C release, its spatial and mechanistic basis of this regulation remains obscure. It is not clear whether ATM acts locally at the Golgi, through cytoplasmic pools, or indirectly via nuclear feedback signaling. Clarifying or discussing this point in more depth would improve the mechanistic coherence of the proposed model. *

__Response: __We thank the reviewer for raising this important mechanistic question. The spatial basis of ATM action at the Golgi is indeed an emerging and exciting area of cell biology. A growing body of evidence demonstrates that ATM associates with the Golgi membrane through binding to phosphatidylinositol-4-phosphate (PI4P), and that this Golgi-resident pool modulates the magnitude and kinetics of the nuclear DDR (Ovejero et al, 2023). Importantly, the most recent work in this area demonstrates that Golgi-associated ATM is not merely a passive reservoir but is enzymatically active and capable of phosphorylating Golgi-resident substrates (Soulet et al, 2026), providing a compelling mechanistic basis for how damage-induced ATM signalling could reach the Golgi to license RAD51C release.

To directly examine whether ATM localises to the Golgi in our system and whether its activation state changes upon DNA damage, we performed a biochemical Golgi enrichment assay using the Minute{trade mark, serif} Golgi Apparatus EnrichmentKit (Cat #: GO-037) to examine ATM distribution across cis- and trans-Golgi fractions. Fraction purity was validated using GM130 (cis-Golgi), TGN46 (trans-Golgi), and HSP60 (membrane fraction) (Rebuttal Figure 2A). This analysis revealed that ATM is detectable in the total membrane fraction and enriched in the cis-Golgi fraction under basal conditions (Rebuttal Figure 2A). Under normal physiological conditions, activated ATM (pATM) was absent from Golgi-enriched fractions (Rebuttal Figure 2B), but was detectable in the cis-Golgi fraction following doxorubicin-induced genotoxic stress (Rebuttal Figure 2C). While these observations are preliminary and require further validation, they are consistent with the emerging literature and raise the intriguing possibility that ATM is recruited to and activated at the Golgi in a damage-dependent manner, where it could act locally to license RAD51C release.

Rebuttal Figure 2. Biochemical Golgi fractionation confirms ATM enrichment in cis-Golgi compartments.

*Western blot of HeLa-K fractions enriched for cis- and trans-Golgi membranes, probing for (A) ATM under basal conditions, and (B and C) pATM under basal conditions and (B) pATM (C) after treatment with DOX (40 μM) (markers: GM130 for cis-Golgi, TGN46 for trans-Golgi, HSP60 for membrane fraction (MEM). *

We consider the precise spatial and mechanistic dissection of ATM signalling at the Golgi and its relationship to nuclear feedback, one of the most exciting directions to emerge from this work, and one that we hope our study has helped to open. We have expanded the Discussion (lines 525-543) accordingly to place our findings in the context of the emerging Golgi-ATM literature and to frame this as an important unresolved question for future investigation.

*5. RAD51C is examined in silo, without consideration for the BCDX2 complex - RAD51C is exclusively analyzed in isolation, despite its well-established function as part of the BCDX2 paralog complex (RAD51B-RAD51C-RAD51D-XRCC2). Because RAD51C does not normally operate as a standalone factor, it is unclear why only RAD51C, among all paralogs, would be subjected to Golgi tethering, ATM-dependent release, and Importin-β-driven nuclear import. This raises important mechanistic questions: Are other BCDX2 members also Golgi-associated? Do they undergo similar trafficking dynamics? Does Golgi tethering selectively regulate RAD51C, or does the complex translocate together? Addressing these points would greatly strengthen the biological plausibility and mechanistic coherence of the proposed model. *

Response: We thank the reviewer for raising this important point. We fully agree that RAD51C functions as a core component of the BCDX2 (RAD51B-RAD51C-RAD51D-XRCC2) and CX3 (RAD51C-XRCC3) paralog complexes, and that its canonical roles in HR and replication fork protection occur within these assemblies. Our decision to focus on RAD51C was driven by the screening data: of the DDR proteins identified, RAD51C displayed the most robust Golgi-associated pool, the clearest damage-induced redistribution dynamics, and a tractable anchoring interaction with Giantin that could be interrogated biochemically.

We would also note that extending this analysis to other RAD51 paralogs is not straightforward with current tools. The available commercial antibodies against RAD51B, RAD51D and XRCC2 perform poorly in immunofluorescence applications, and most localisation studies for these proteins have relied on overexpression of tagged constructs, a strategy that, as discussed above, risks perturbing both localisation and complex assembly. The lack of reliable antibodies for endogenous paralog detection at the resolution required for Golgi localisation analysis represents a genuine technical barrier that we encountered directly during this study.

Whether Golgi association and ATM-dependent release involve RAD51C alone or extend to other BCDX2 or CX3 members is therefore a genuinely open and important question. We note that our co-immunoprecipitation data were performed on total cell lysate and cannot distinguish whether the Golgi-associated RAD51C is complexed with other paralogs or represents a monomeric subpopulation. Golgins are well established as multi-cargo scaffolding platforms, and it is entirely plausible that Giantin organises a broader paralog module rather than tethering RAD51C as an isolated subunit. A systematic analysis of RAD51 paralogs for Golgi localisation and lesion-dependent trafficking enabled by improved reagents such as proximity labelling or endogenous tagging approaches compatible with essential proteins would determine whether the BCDX2 complex translocates as a unit or whether individual subunits are differentially regulated, with potentially distinct consequences for HR fidelity. We have revised the manuscript accordingly and identify this as an explicit priority for future work in the revised Discussion (lines 583-602).

Minor Comments

1. Pathway-specific sub-Golgi localization patterns - The finding that DDR proteins map to distinct cis/trans Golgi subdomains is an interesting and potentially important observation. However, the dataset is limited to 15 proteins, making the proposed pathway-level trends (e.g., HR factors enriched in cis-Golgi; BER/MMEJ factors enriched in trans-Golgi) preliminary. Strengthening this conclusion by increasing the number of DDR proteins analyzed would help determine whether sub-Golgi compartmentalization contributes meaningfully to DNA repair pathway regulation.

Response: We thank the reviewer for this constructive suggestion. We agree that extending sub-Golgi mapping to a larger number of DDR proteins would be valuable, and we present the current dataset explicitly as a first, hypothesis-generating map rather than a definitive pathway atlas.

We would like to highlight, however, that the value of this observation lies not simply in the number of proteins mapped, but in the biological coherence of the patterns that emerge. The finding that proteins from the same repair pathway tend to occupy the same Golgi sub-compartment: BER and MMEJ factors enriching in the trans-Golgi, HR factors in the medial/cis-Golgi, and that this sub-compartmental positioning correlates with the direction of their redistribution upon genotoxic stress, is a pattern that would be unlikely to arise by chance across 15 independently validated proteins. This internal consistency argues that the sub-Golgi organisation reflects genuine pathway-level biology rather than noise, even if the dataset is not yet exhaustive. Together with the bioinformatic network analysis, which independently supports pathway-level clustering across the broader validated hit list, these observations reinforce each other as complementary layers of evidence.

2. Is the Golgi-released RAD51C indeed the pool that enters the nucleus? The major assumption of the study is that the RAD51C population released from the Golgi upon DNA damage is the same pool that subsequently accumulates in the nucleus to form repair foci. While the imaging and fractionation data are consistent with this model, the study does not directly track or distinguish Golgi-derived RAD51C from cytoplasmic or pre-existing nuclear pools. Without a method to specifically label, pulse-chase, or track the Golgi-anchored fraction, it remains formally possible that nuclear RAD51C originates from other subcellular reservoirs.

__Response: __We thank the reviewer for highlighting this important mechanistic point, which we agree cannot be fully resolved with the current dataset. Several independent lines of evidence are nonetheless consistent with a model in which the Golgi-associated pool contributes directly to damage-induced nuclear accumulation.

• Our time-resolved imaging demonstrates a reciprocal decrease at the Golgi and a concurrent increase in the nucleus following genotoxic stress, consistent with redistribution rather than independent compartment-specific changes (Figures 3E-3I).
• Biochemical fractionation provides an orthogonal readout of the same reciprocal shift under identical conditions (Figures 3J and S6D).
• ATM inhibition simultaneously prevents Golgi loss and blunts nuclear accumulation, while Importin-β perturbation blocks nuclear entry, together supporting an active and regulated translocation route (Figures 3K-3P).
• Giantin depletion, which releases the Golgi-tethered RAD51C pool prematurely, leads to aberrant nuclear RAD51C foci lacking canonical HR markers and impaired ATM signalling, strongly supporting that the Golgi-tethered fraction has functional consequences in the nucleus consistent with it being the relevant pool (Figures 4B-4E and 4J-4M).
• In the revised manuscript we have included cytoplasmic RAD51C signal quantification across the doxorubicin time course (Figure 3H). The cytoplasmic signal shows only a moderate and gradual reduction that is kinetically distinct from the sharp Golgi decrease and does not precede the nuclear increase. This pattern is inconsistent with a large pre-existing cytoplasmic reservoir driving the nuclear accumulation; if the cytoplasmic pool were the primary source, one would expect a rapid and prominent cytoplasmic decrease coinciding with or preceding nuclear accumulation, which we do not observe. Instead, the data are more consistent with rapid transit of Golgi-released RAD51C through the cytoplasm rather than stable cytoplasmic accumulation prior to nuclear entry. We acknowledge that definitive pool-identity tracking would require spatially restricted labelling approaches such as Giantin-proximal TurboID or photoactivatable tagging strategies, which are precluded by the technical constraints on RAD51C tagging described above. We have revised the manuscript to avoid overstatement on this point and identify these approaches as important future directions (lines 297-305 & lines 715-719).

Reviewer #2 (Significance (Required)):

General assessment - This study presents a novel and conceptually compelling view of the DNA damage response (DDR) by positioning the Golgi apparatus as an active regulator of the spatiotemporal availability of DNA repair factors. The strongest aspects of the work include its integration of a systematic immune-localization screening, a sub-Golgi compartment mapping, dynamic redistribution assays, and functional perturbations to build a coherent model of Golgi-nucleus communication during genotoxic stress. The mechanistic focus on RAD51C provides a clear case study linking organelle-level regulation to genome stability.

• Advance - To my knowledge, this is the first comprehensive demonstration that the Golgi can serve as a spatiotemporal coordination node for DDR proteins, including those involved in HR. The identification of a substantial pool of RAD51C, and reportedly other DDR factors, anchored within specific Golgi subdomains represents a significant conceptual advance. The demonstration that Golgi-tethered RAD51C is released in an ATM-dependent manner and subsequently participates in nuclear foci formation suggests a previously unrecognized organelle-level regulatory checkpoint in genome maintenance. This work therefore extends current models of the DDR by revealing a layer of intracellular coordination that bridges classical nuclear pathways with cytoplasmic organelle function.*

• Audience - This study will be of strong interest to a specialized audience in the fields of DNA repair, genome stability, and cell biology, particularly those studying the spatial organization of repair pathways and intracellular stress signaling. It will also appeal to researchers investigating organelle biology, intracellular trafficking, and the broader coordination of cytoplasmic and nuclear responses to stress. Beyond these communities, the work may be relevant to cancer, as it suggests new mechanisms by which organelle perturbations or Golgi-associated scaffolding proteins could influence therapeutic responses or genomic instability.

Reviewer expertise - Field of expertise: DNA repair, genome stability, organelle biology, cancer cell biology.*

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

*This study investigates the communication between the Golgi complex and the nucleus of the cell, which remains a largely unexplored field. The authors used publicly available siRNA and antibody data from the Human Protein Atlas as a basis for finding overlap between the proteomes of the two cellular compartments. In validating the data from the HPA, the study finds a novel cluster of DNA repair proteins present in the Golgi, which they validate and resolve to sub-compartmental localization. To do so they use immunofluorescence (IF) localization on ¬cis- and trans-Golgi cisternae marked by GM130 and TGN46, respectively. The authors find that many of the fully validated proteins present in both the nucleus and Golgi redistribute between the Golgi and the nucleus dependent on the protein and the type of DNA lesion. They focused on RAD51C, a recombination factor. They show that RAD51C resides in both the ¬cis- and trans- subsections prior to damage and responds to DNA damage in an ATM-dependent manner via release of a Golgi-based pool bound to Giantin, which is then imported into the nucleus via Importin-β. Knockdown experiments showed that Giantin regulates RAD51C spatially and temporally. The work reveals a dynamic interchange of proteins between the Golgi and nucleus that controls cell functions beyond the classic secretory, membrane trafficking, and PTM roles of the Golgi. The authors build on prior work on Golgi impacts on DDR, offering an alternative cellular compartment for storage of DDR factors prior to damage. Overall, the data is timely and relevant, as it finds new roles for the Golgi in DNA damage response (DDR) regulation. The data is largely convincing and well controlled. The IF data is presented in black and white single channels and merged in color, which allows good comparison of the different protein stains. The scope of the initial screen of HPA antibodies and Golgi/Nuclear dual proteomes is impressive, and the overlap of DDR proteins is characterized for fifteen different proteins at a sub-compartmental level. The focus on RAD51C as a member of the HR pathway was a strong choice, and the study presents interesting information on its regulation by Golgi complex members, as well as a feedback look with pATM. The possibility of the Golgi storing specific DDR factors in specific compartments is well-supported and intriguing. There are a few major and minor points that should strengthen the paper and improve clarity prior to publication. *

Major Comments:

*1. Much of the strength of the IF data is lost in the choice of scale for presentation of the data. In almost all cases, enlarged sections should be shown of the areas currently indicated by arrow, in all channels. This is done well in Figure 3A, where an area of the Golgi is enlarged and the overlap of RAD51C in the GM130-marked Golgi is clearly visible in the merged channel, even when printed out. I would highly recommend including the white box and enlarged in all images and channels, while keeping the representative fields as is (e.g. if the image is 40mm, draw a 7mm box around representative cells/Golgi, and enlarge to 15mm in the bottom left). This change should be made to F1E, F2F, F3E, F3J, and F3M, as well as having enlarged figures in the corners in all supplementary data IF figures. Where possible, a fully enlarged image of the bounding box could also be included. Some of the IF data would be strengthened by using the nuclei stain to draw a masking outline to include in the black and white channels, to clearly delaminate what is Golgi-localized and what is nuclear. *

Response: We thank the reviewer for this helpful suggestion and fully agree that enlarged insets substantially improve the visibility of Golgi-localised signal, particularly when figures are printed. We share the reviewer's view that alternative display formats with larger insets would be preferable, and we have implemented enlarged boxed regions wherever space constraints permitted.

Specifically, we have added boxed regions with enlarged insets to Figure 1E, all panels of Figure 3. For Figure 2, the number of conditions and proteins displayed simultaneously within the constraints of standard journal figure dimensions made it impractical to include enlarged insets for all panels without reducing the overall field size to the point of losing contextual information. We have nonetheless improved the visibility of the Golgi signal in Figure 2 as much as possible within these constraints, and note that the final figure layout will be further optimised in line with the journal's specific formatting guidelines. In addition, all figures have been provided as high-resolution image files to allow electronic magnification, enabling readers to inspect the Golgi-localised signal in detail beyond what is visible in the printed version.

Regarding the use of nuclear outline masks in single-channel images, we tested this approach but found that given the number of structures present within each field, including Golgi stacks, nuclear foci, and cytoplasmic signal, overlaying nuclear outlines on individual channels added visual complexity that made the images harder rather than easier to interpret. As an alternative, we have included a full-colour merged panel, when possible, which we consider a cleaner way to delineate nuclear versus Golgi-localised signal and allows the reader to directly compare compartment-specific distributions across channels.

• 1. *There is a lack of consistency in the representative images shown by IF. For example, Figure 1 gives the impression of very little RAD51C in the nucleus but this is rightly shown to not be the case in Supp. Fig 2A. The same is true of the various images of LIG1. The authors should use representative data that better reflects the distribution of the proteins being studied and maintain consistency across images. If there is a lot of variation in staining patterns, the authors should show images and percentages corresponding to the variations especially for the key gene studied, RAD51C.

Response: We agree and have replaced the representative IF panels for RAD51C and LIG1 with images that better reflect the quantified distributions across biological replicates. The revised panels were selected to match the quantified compartment intensities shown in the accompanying graphs rather than representing outlier cells. We would also note that the apparent discrepancy between Figure 1E and Supplementary Figure S2A partly reflects a difference in imaging conditions: Supplementary Figure S2A __and __Figure 2F were acquired directly from the high-content screening pipeline under uniform, non-optimised antibody and fixation conditions at widefield resolution, whereas Figure 1E shows representative single optical section confocal images acquired after candidate identification with antibody conditions optimised for each individual protein. The improved signal-to-noise in the optimised confocal images more faithfully captures the dual Golgi and nuclear localisation of RAD51C, and the apparent difference between the two image sets is therefore expected rather than inconsistent. We have updated the figure legends to clarify the imaging modality and conditions for each panel. Furthermore, the quantified distribution of RAD51C across Golgi, nuclear and cytoplasmic compartments across multiple cell lines is shown in Figure 3B and 3D, providing a population-level representation of the dual localisation that complements the representative images shown in Figure 1E.

• 1. *The initial screening by siRNA-mediated knockdown pipeline that validated and confirmed dual Golgi and nuclear localization of 163 of the 329 dual-localization HPA proteins does not have any data included. This seems like a very large amount of data to gloss over and not include even as supplementary data. This should be included as source data, and discussion of the in-text information should be strengthened. The data included with the networking of these validated proteins is strong, but the process of elimination and validation has not been shown. In addition, the antibody information included in the supplementary data does not include dilution factors or blocking factors is not included, which would be beneficial to future studies to include.

Response: We agree and have addressed this in full. We note that the HPA antibody validation data, including immunofluorescence images and siRNA knockdown results, are publicly available for inspection on the Human Protein Atlas website (www.proteinatlas.org) for the majority of candidates, providing an independent layer of verification. In the revised submission, we additionally provide the complete siRNA-mediated validation dataset generated in our laboratory as source data (Table S1; lines 1025-1041), including for each candidate the HPA antibody identifier, gene symbol, Ensembl ID, antibody staining pattern, siRNA identifier, cell number per replicate, and normalised Golgi and nuclear signal ratios for both experimental replicates. This allows readers to inspect the validation metrics directly and apply alternative thresholds if desired. We have also expanded the antibody information to include diluent conditions (4% FBS in 0.1% Triton-X100 for all HPA antibodies used at 2 μg/ml in the screening pipeline), enabling reproducibility and reuse of the dataset by the community.

• 1. *The authors should expand upon the paragraph lines 155-162 to include more discussion on Figure S2A and S2B. The expanse of this data is some of the strongest in the paper, and it should be further discussed in-text. Also, the rationale behind the choice in the specific proteins that are included in these analysis / figures is not always clear in -text, and more attention should be spent on the narrowing down of the analysis to the final proteins. This is also especially important as many of the DDR proteins chosen are not the most common DDR proteins. Also note in text that the Golgi marker GM130 (presumably) was used for the screening, which means that some proteins which are only localizing to the TGN46 trans Golgi might have been lost in the validation step (or, explain why this is not the case).

Response: __We expanded the Results text (__lines 141-163) to discuss Figures S2A and S2B in more depth and clarified the rationale for selecting the final set of DDR proteins taken forward, including considerations of pathway representation, bioinformatic annotations, literature-described roles in DNA repair. We would also note that the identity of the DDR proteins identified in this screen was determined by the HPA dataset and the unbiased validation pipeline rather than by prior assumptions about which repair factors would be present at the Golgi. The presence of less commonly studied DDR factors is therefore a direct reflection of the screen output, and we consider this one of the strengths of the approach.

We would also like to address the reviewer's concern about potential GM130-based bias directly: at the widefield or confocal resolution used in the high-content screening pipeline, the Golgi apparatus appears as a single perinuclear structure and cis- and trans-Golgi subdomains cannot be resolved. GM130 was therefore used purely as a segmentation marker to define the Golgi compartment as a whole rather than to selectively label the cis-Golgi cisternae. The resulting Golgi mask captures signals from the entire Golgi ribbon, including trans-Golgi regions, meaning that proteins with exclusively trans-Golgi localisation would not have been systematically excluded at the screening stage. Sub-compartmental resolution of cis versus trans localisation was only possible in subsequent analyses using nocodazole-dispersed mini-stacks imaged by confocal microscopy with co-staining for both GM130 and TGN46.

*5. The relationship between Giantin loss, increased cell proliferation, and elevated endogenous DNA damage as it relates to RAD51C remains insufficiently resolved and requires further clarification. Several of the proliferation assays used are not optimal for addressing changes in cell growth. For example, Figure 5O appears to quantify cell numbers by counting fields from IF images, which is an unconventional approach. This should be done by growth curves, luminescent viability or colony formation assays. In addition, this point will be greatly strengthened by performing rescue experiments for Giantin directly (instead of co-depletion as a means of rescue) and/or using a mutant of RAD51C that does not bind to Giantin. If these additional experiments are beyond the current scope, the conclusions should be softened in the discussion. *

Response: We thank the reviewer for raising these important points, which we address in turn:

Giantin-RAD51C relationship and mechanistic interpretation. __We acknowledge that establishing the full causal chain between Giantin loss, RAD51C mislocalisation, elevated endogenous DNA damage and increased cell proliferation is challenging within the scope of a single study, and we discuss this openly in the Discussion (__lines 555-564). Our evidence collectively includes: physical interaction between endogenous Giantin and RAD51C by co-immunoprecipitation (Figures 4H and 4I), premature nuclear accumulation of RAD51C upon Giantin depletion (Figures 4B-4E and 4J-4M), new additional experiment showing direct reduction of HR efficiency in the DR-GFP assay (Figure 5L), impaired ATM signalling (Figures 5J and 5M), elevated genomic instability (Figures 5A-5E), and epistatic rescue by RAD51C co-depletion (Figures 5M-5P). These observations are further contextualised by the established literature on RAD51C function: RAD51C is known to regulate CHK2 phosphorylation and cell cycle checkpoint signalling (Badie et al, 2009), stabilise replication forks (Somyajit et al, 2015), and promote RAD51 filament formation required for DSB repair (Prakash et al, 2015). Dysregulation of these functions through Giantin-dependent mislocalisation provides a mechanistically coherent explanation for the elevated genomic instability and altered proliferation we observe, and is entirely consistent with our model. Together, the experimental evidence and the published biology of RAD51C support a model in which Giantin spatially regulates RAD51C to maintain proper DDR signalling and HR capacity.

We agree that separation-of-function tools would further strengthen this model and identify these as important future priorities. We wish to note however that both approaches face substantial technical barriers in this system. As described in our response to Reviewer 1 Major Comment 1, RAD51C tagging, whether by CRISPR-mediated endogenous editing or ectopic expression, consistently compromised cell viability and protein function, precluding the generation of interaction-deficient variants at physiological expression levels. Engineering an interaction-deficient Giantin mutant presents an independent and considerable challenge: Giantin is one of the largest Golgi matrix proteins (~376 kDa), composed almost entirely of extended coiled-coil domains that are intrinsically difficult to model structurally, and identifying a discrete interaction interface with RAD51C without disrupting the broader scaffolding function of the protein would require a dedicated structural and biochemical programme. We therefore consider these important but substantial future directions rather than straightforward experimental additions to the current study.

Proliferation assays. Colony formation assays provide a rigorous readout of long-term proliferative capacity, and these data are presented for single knockdown conditions in Figures 5F-5I. The cell number quantification in Figure 5P was specifically included to assess the double knockdown of Giantin and RAD51C simultaneously, a condition not covered by the colony formation assay. We respectfully note that automated fluorescence microscopy-based nuclear counting is a well-established approach for measuring cell proliferation in siRNA screening contexts. Nuclear counting from high-content imaging has been used as a direct readout of cell growth and proliferation in RNAi screens (Boutros et al, 2004; Martin et al, 2014; Garvey et al, 2016; Mikheeva et al, 2024), and has been shown to produce results comparable to or superior to conventional viability assays including MTT and flow cytometry-based methods (Mikheeva et al, 2024). We have nonetheless clarified in the revised figure legend that Figure 5P reports relative cell number quantified by automated nuclear counting from high-content imaging fields as a secondary concordant measure alongside the colony formation data, rather than a standalone proliferation assay.

*6. It is unclear from the discussion and from presented data whether proteins are directly transported between the Golgi and the nucleus, or whether they go into the cytoplasm for a transient period, presumably when they could interact with Importin β. There is also some data where cytoplasm signal could be quantified to address this (Figure 3E-I). *

Response: We thank the reviewer for this mechanistic point. In the revised manuscript we have included cytoplasmic RAD51C signal quantification alongside Golgi and nuclear measurements for the doxorubicin time course (lines 297-305; Figure 3H). The cytoplasmic signal shows a moderate and gradual reduction distinct in both magnitude and kinetics from the sharp Golgi decrease, consistent with a transient cytoplasmic intermediate rather than a stable pool. Regarding the identity of the translocating pool, two observations directly support a Golgi origin. First, Importazole treatment prevents RAD51C release from the Golgi following genotoxic stress and simultaneously reduces nuclear RAD51C foci formation, demonstrating that Importin-β-mediated import is required both for Golgi clearance and for productive nuclear accumulation. Second, Giantin depletion which prematurely releases the Golgi-tethered pool, leads to aberrant nuclear RAD51C foci, directly linking the Golgi-anchored fraction to nuclear accumulation. Together these data support a model in which Golgi-resident RAD51C transits through the cytoplasm for Importin-β-mediated nuclear import. We acknowledge that without direct labelling of the Golgi-anchored fraction, the precise contribution of each subcellular pool to the nuclear accumulation cannot be fully resolved with the current dataset. We discuss the development of appropriate tagging strategies as an important future direction to dissect the dynamics of this process in further detail.

*7. Statistical analysis on experiments with more than two samples need to be performed with ANOVA and a follow up post-hoc test, not with two-tailed unpaired Student's t-test, which only compares the control and each individual sample. This type of analysis inflates the Type 1 error rates (false positives) in your datasets. For example, the two-tailed unpaired Student's t-test is appropriate in Figure 2F-H, but not in Figure 3 when the samples are timepoints. In this case, a One-way ANOVA with Tukey's post-hoc test (if you want to show all coparisons), or Bonferroni/Sidak if you only need to compare several samples). *

Response: We agree with the reviewer and thank them for highlighting this important statistical issue. We have revised the statistical analysis for all experiments involving more than two groups to avoid inflation of Type I error rates caused by multiple pairwise Student's t tests. Specifically, for Figures 3F-I, 4C-E, and Figure 5, the data were reanalysed using one way ANOVA followed by the appropriate multiple comparisons post hoc test. The Methods section and corresponding figure legends have been updated to clearly state the statistical tests used for each dataset.

Minor Comments: General 1. Throughout the text, the reference to many figures and supplementary figures in the same sentence, with little discussion of the data therein makes it hard to follow. In-text referencing is particularly confusing in the section "Dual-localising DDR proteins dynamically redistribute between the Golgi and nucleus in response to specific types of DNA injuries," where the reader is switching between multiple figures and supplementary figures.

__Response: __We thank the reviewer for this helpful comment. In the revised manuscript, we have improved the readability of the text and revised the figure references to make them clearer. We hope these revisions make the manuscript easier to follow and allow readers to better inspect the figures.

1. In figures that display technical replicates as individual data points, consider distinguishing each replicate by using different marker shapes (e.g., repeat 1 = upright triangle; repeat 2 = inverted triangle; repeat 3 = diamond). This would provide additional clarity regarding the consistency and repeatability of each technical repeat.

__Response: __We thank the reviewer for this suggestion. We have updated the data presentation to distinguish biological replicates using different marker shapes in datasets where replicate tracking is of particular relevance to the interpretation. For datasets where individual replicate values are already clearly separable, we have maintained the existing presentation to avoid unnecessary visual complexity.

1. Make sure all western blot data includes the marker size (F3C and F5L has none, F4H/I have size of proteins not size of markers).

__Response: __We added missing marker sizes to our western blot data in the revised manuscript.

1. Be consistent with use of capitalization in figure legends and graph/figure labels.

__Response: __We made sure that the capitalisation is consistent in figure legends, graph and figure legends in the revised manuscript.

Figure 2

In Figure 2A, please include in the figure itself that GM130 is the cis Golgi, and TGN46 is the trans Golgi (Figures should not be dependent on the text for full understanding).

__Response: __We revised Figure 2A and 2C to label GM130 as cis-Golgi and TGN46 as trans-Golgi within the figure, making it self-explanatory.

1. Why are LRIG2 and LRRIQ3 not included in the 2E cis vs trans Golgi data, when all other proteins from F1D are included? Include, or comment on in-text.

__Response: __Both LRIG2 and LRRIQ3 are included in 2E in both the original and revised manuscript.

1. Be sure to include scale bar data in each figure legend (F2A-E is currently missing it), and include updated scales included in the enlarged data.

__Response: __Scale bar data is now included in each figure legend in the revised manuscript.

1. In Figure 2F, make sure that the merged green channel is presented at the same intensity as it is in the single black and white channel, as the green looks very overexposed in several of the merged (CCAR1 DMSO merged is the most noticeable).

__Response: __We agree and thank you for pointing this out. We have now revised the images and corrected the issue by updating all image panels in the figure.

1. In Figure 2G, include the grey label in the figure legend.

__Response: __We thank the reviewer for this comment. The grey label has now been included in the figure legend in the revised manuscript.

1. In Figure 2G-H, the method of data presentation in the graphs coupled with the statistical analysis is confusing and should be expanded upon in the legend.

__Response: __We agree that the amount of data presented may appear overwhelming. In the revised figure, we have adjusted the placement of the statistical annotations to improve clarity. Also, we improved the figure legend, to make the figure easier to read and interpret.

Figure 3

Figure E/F/G: Is there cytoplasmic quantification as well? Your rationale is that the Golgi RAD51C goes into the nucleus, but via the cytoplasm (due to Importin β import); do you see the cytoplasmic levels increase? Or is it too dilute to notice a difference? At least, this omission needs to be mentioned in-text.

Figure H/I also include the quantification of the cytoplasmic fraction. It is mentioned in-text on line 272, but not quantified. This comes up as a big question: Do the proteins go directly between the Golgi and nucleus, or do they go through the cytoplasm?

__Response: __We thank the reviewer for both of these related points. As described in our response to Major Comment 6 above, we have added cytoplasmic RAD51C signal quantification to the doxorubicin time course in the revised manuscript (Figure 3H) and discuss the implications for the proposed translocation route.

Figure 3A, 3E, and if the data is present for 3J and 3M, could all benefit from using the nuclei staining as a mask to draw an outline around the nucleus in the other channels, and then show a merge in full color instead of a nuclei-only channel. Also note from the major comments, that this data especially is so small to see without enlarged images.

__Response: __We thank the reviewer for this suggestion. Regarding nuclear outline masks, we tested this approach but found that the number of structures present in each field, including Golgi stacks, nuclear foci and cytoplasmic signal, made overlaid outlines visually confusing rather than clarifying. We have instead included a full-colour merged panel in Figure 3E, which we consider a cleaner way to distinguish nuclear from Golgi-localised signal while preserving the spatial context of the data.

Regarding image size, we have added enlarged insets to Figures 3E, 3J and 3M in the revised manuscript. We have chosen to display multiple cells per panel rather than a single enlarged cell in order to capture the heterogeneity of the cell population, which we consider important for an accurate representation of the data. All figures have been provided as high-resolution image files to allow electronic magnification, enabling detailed inspection of the signal beyond what is visible in the printed version. We acknowledge that the constraints of standard journal figure dimensions limit how large individual panels can be, and the final layout will be optimised in line with the journal's formatting guidelines.

*In-text discussion of the results from Figure 3 has an in-depth discussion of the NLS and NES in RAD51C, but this is not followed up on with site-directed mutagenesis or any data; perhaps move this to the discussion instead of results section. *

__Response: __We have removed the discussion of the NLS and NES from the Results section.

Figure 4

Comments from earlier figures hold, with size of enlarged events and using the nuclei as an outline in the single channels. E.g. Figure 4F arrows appear to point to nothing at the chosen scale. The zoom in 4G is insufficient, as the chosen feature is so small it is not even visible in full fields.

__Response: __We thank the reviewer for this comment. The arrows in Figure 4F indicate individual nocodazole-dispersed Golgi mini-stacks, which are displayed at higher magnification in Figure 4G. The full field in Figure 4F is intentionally shown to illustrate the degree of Golgi dispersion achieved by nocodazole treatment, a context that may be unfamiliar to readers outside the Golgi field, before zooming into a single representative mini-stack in Figure 4G for the cisternal localisation analysis.

• Figure 4H and 4I need to show the size of the markers *

__Response: __The size of the markers are now included in the revised manuscript.

*The representative image in 4L for siGiantin pATM has no pATM foci, while the quantification in 4M has a reduction from ~50% to ~25%, so this image is not representative of this data, or the data quantification is not as strong as the actual data. *

__Response: __We thank the reviewer for this observation. We wish to clarify that the quantification in Figure 4M reports the mean percentage of RAD51C foci co-localising with pATM across the entire cell population from three independent biological replicates. A reduction from ~50% to ~25% therefore reflects a population-level shift in co-localisation frequency, not that every individual cell shows exactly 25% co-localisation. Given the inherent cell-to-cell variability in foci number and co-localisation, individual cells will span a range of values around this mean, and the representative image shown in Figure 4L reflects one such cell.

Figure 5

*Figure 5A has overexposure of the nuclei stain in order to visualize micronuclei. Readjust the levels, and enlarge the images for better visualization. (is this DAPI-stained? Please label). *

__Response: __The display levels of the nuclear stain in Figure 5A are intentionally set to allow visualisation of micronuclei, which are significantly dimmer than the main nucleus and would not be detectable at display settings optimised for the primary nuclear signal. This is standard practice in micronuclei quantification studies and is necessary to accurately identify and score these structures. The nuclear stain is Hoechst 33342, and this has been explicitly labelled in the revised figure legend.

*Figure 5A-C: Figure 5A does not show siRAD51, but it is included in the DMSO only graph. Please either show RAD51 data in 5A and 5C, or do not include in 5B. If the DMSO and ETO experiments were performed separately and that accounts for this discrepancy, then show separately. *

__Response: __We thank the reviewer for this observation. The siRAD51C condition is included in Figure 5B as an internal positive control, consistent with its well-established role in genome stability. RAD51C depletion combined with etoposide treatment resulted in severe cellular toxicity and insufficient cell numbers for reliable quantification, and this condition was therefore excluded from Figure 5C. This has been clarified in the revised figure legend.

*Figure 5M the white label is difficult to see in the green box. *

__Response: __We have updated the label colour in Figure 5M to improve visibility against the green background in the revised manuscript.

* Supplementary Figures*

Consider reordering/ subdividing supplementary figures for ease of reference during reading.

Response: We thank the reviewer for this suggestion. The current supplementary figure structure was intentionally designed to minimise the total number of supplementary figures and maintain a logical correspondence with the main figures, avoiding a situation where readers need to navigate an extensive supplementary section, a concern the reviewer raised regarding figure presentation. We believe the current organisation achieves a reasonable balance between completeness and accessibility.

SF1 and SF2A: Include enlarged boxes or full images so that data is visible.

__Response: __As described in our response to Major Comment 1, all figures have been provided as high-resolution image files to allow electronic magnification. Space constraints within standard journal figure dimensions preclude the addition of enlarged insets to all supplementary panels without substantially reducing the contextual field of view.

*SF3A, SF4A, and SF5A: Include enlarged images, include nuclei marker if possible (otherwise, the nuclear intensity is not proven nuclear). *

Response: We appreciate the suggestion, but adding enlarged insets and nuclei markers to all panels in Figures S3A, S4A and S5A would disproportionately increase the length and complexity of the supplementary section, making it harder rather than easier to navigate. The nuclear intensity measurements are derived from automated segmentation of the Hoechst channel using CellProfiler, which reliably defines nuclear boundaries independently of the antibody channel, and are therefore not dependent on visual confirmation of nuclear localisation in each representative image.

*SF3B-C, SF4B-C, and SF5 B-D: Change the data presentation in the same method as changed for F2G-H. *

Response: We have updated the figure legends for Figures S3B-C, S4B-C and S5B-D to improve readability.

SF3D: List proteins in the same order as in B and C.

Response: The proteins in Figure S3D are listed in the same order as in Figures S3B and S3C.

SF6D: Label M N and C more clearly. Include size labels.

Response: We have added clearer labels for the membrane (M), nuclear (N) and cytoplasmic (C) fractions and included molecular weight size markers in the revised Figure S6D.

*SF7A-B: Include enlarged. *

Response: We respectfully note that the purpose of Figures S7A-B is to display the overall cellular response to inhibitor treatments across the cell population, rather than to highlight specific subcellular structures. Enlarged insets would reduce the number of cells visible per panel and would not add scientific value in this context. The Golgi and nuclear signals are clearly visible at the chosen magnification.

*SF8: Include arrows as in previous experiments, include enlarge. *

Response: Arrows have been added to Figure S8 to indicate Golgi and nuclear RAD51C signal, consistent with the annotation style used in the main figures. The images already show two representative cells per condition to maximise the visible detail at the chosen scale.

*SF9G: G is labelled, but not included. *

Response: Figure S9G has been added in the revised manuscript, showing the pan-cancer overall survival map for GOLGB1 expression across all TCGA cohorts generated using GEPIA2. The figure legend has been updated accordingly.

*Reviewer #3 (Significance (Required)): *

* The work finds new roles for the Golgi in regulation of DNA damage responses and the screen could be an important dataset (but results need to be made available) for the DNA repair community. The scope of the initial screen of HPA antibodies and Golgi/Nuclear dual proteomes is impressive, and the overlap of DDR proteins is characterized for fifteen different proteins at a sub-compartmental level. The work provides important insights into RAD51C regulation, however, there are key mechanistic insights and control experiments missing from the studies involving RAD51C and Giantin, dampening its impact. The idea of an alternative cellular compartment for storage of DDR factors prior to damage is interesting, and suggests the spatial regulation of specific lesion responses are stored in specific sub-compartments of the Golgi, which could contribute to repair regulation.*

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Author response:

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

Reviewer #1 (Public review):

Summary:

This work demonstrates that MORC2 undergoes phase separation (PS) in cells to form nuclear condensates, and the authors demonstrate convincingly the interactions responsible for this phase separation. Specifically, the authors make good use of crystallography and NMR to identify multiple protein: protein interactions and use EMSA to confirm protein: DNA interactions. These interactions work together to promote in vitro and in cell phase separation and boost ATPase activity by the catalytic domain of MORC2.

However, the authors have very weak evidence supporting their potentially valuable claim that MORC2 PS is important for the appropriate gene regulatory role of MORC2 in cells. Exploring causal links between PS and function is an important need in the phase separation field, particularly as regards the role of condensates in gene regulation, and is a non-trivial matter. Any study with convincing data on this matter will be very important. For this reason, it is crucial to properly explore the alternative possibility that soluble complexes, existing in the same conditions as phase-separated condensates, are the functional species. It is also critical to keep in mind that, while a specific protein domain may be essential for PS, this does not mean its only important function pertains to PS.

In this study, the authors do not sufficiently explore the role that soluble MORC2 complexes may play alongside MORC2 condensates. Neither do they include enough data to solidly show that domain deletion leads to phenotypes via a loss of phase separation per se, rather than the loss of phase separation being a microscopically visible result, not cause, of an underlying shift in protein function. For these reasons, the authors' conclusions regarding the functional role of MORC2 condensates are based on incomplete data. This also dampens the utility of this work as a whole, since the very nice work detailing the mechanism of MORC2 PS is not paired with strong data showing the importance of this observation.

We thank the reviewer for this thoughtful and constructive critique. We agree that establishing a causal link between phase separation (PS) and biological function—particularly in transcriptional regulation—is a central and non-trivial challenge in the condensate field. We also appreciate the reviewer’s emphasis on two critical alternative interpretations: (i) that soluble MORC2 complexes, rather than condensates, may represent the primary functional species, and (ii) that loss of phase separation upon domain deletion could reflect a downstream consequence of altered protein function rather than its cause.

To address these concerns, we have performed a series of new experiments specifically designed to decouple condensate formation, and condensate dynamics, thereby allowing us to more rigorously interrogate the functional relevance of MORC2 condensates.

First, to overcome the limitation of domain deletions which may affect MORC2 function beyond phase separation we introduced a micropeptide-based kill switch (KS) to the C terminus of MORC2. This strategy has recently emerged as a powerful approach to selectively reduce condensate dynamics without disrupting protein expression, folding, or domain architecture [1]. Importantly, unlike CC3 or IDRa deletions, MORC2+KS robustly form nuclear condensates but exhibits markedly reduced internal dynamics, as demonstrated by FRAP analyses showing minimal fluorescence recovery after photo bleaching (Fig. 6a-c). This strategy therefore allows us to perturb condensate material properties independently of MORC2 domain integrity.

Second, we systematically compared the transcriptional consequences of rescuing MORC2-knockout HeLa cells with MORC2FL, condensation-deficient mutants (ΔCC3 and ΔIDRa), and the dynamics-defective MORC2+KS (Fig. 6d). Despite being expressed at substantially higher levels than MORC2FL (Fig. 6e), all three mutants showed a striking and consistent failure to restore MORC2-dependent transcriptional regulation (Fig. 6f-h). This effect was particularly pronounced for transcriptionally repressed genes, including two sets of high-confidence MORC2 targets reported in prior studies (Fig. 6i and Fig.S10). These findings demonstrate that neither increased protein abundance nor the mere presence of condensate-like structures alone is sufficient to restore MORC2 function.

Third, our data instead support a model in which both soluble MORC2 complexes and dynamic MORC2 condensates are required for full transcriptional regulation activity. While soluble MORC2 is likely involved in target recognition and complex assembly, our results indicate that proper condensate formation—and critically, condensate dynamics—are essential for effective transcriptional repression and activation. The inability of the MORC2+KS mutant to rescue transcriptional defects, despite intact condensate formation, points away from a model in which MORC2 condensates represent only microscopically visible byproducts of MORC2 activity.

We believe these new data strengthen the manuscript by pairing the detailed mechanistic dissection of MORC2 phase separation with direct functional evidence, enhancing the conceptual impact and biological significance of the study.

Strengths:

Static light scattering and crystallography are nicely used to demonstrate the dimerization of MORC2FL and to discover the structure of the CC3 domain dimer, presumably responsible for the dimerization of MORC2FL (Figure 1).

Extensive use of deletion mutants in multiple cell lines is used to identify regions of MORC2 that are important for forming condensates in the nucleus: the IBD, IDR, and CC3 domains are found to be essential for condensate formation, while the CW domain plays an unknown role in condensate morphology (Figure 3). The authors use NMR to further identify that the IBD domain seems to interact with the first third of the centrally located IDR, termed IDRa, but not with the latter two-thirds of the IDR domain (Figure 4). This leads them to propose that phase separation is the product of IDB:IDRa interaction, CC3 dimerization, and an unknown but important role for the CW domain.

Based on the observation that removal of the NLS resulted in diffuse cytoplasmic localization, they hypothesized that DNA may play an important role in MORC2 PS. EMSA was used to demonstrate interaction between DNA and several MORC2 domains: CC1, CC2, IDR, and TCD-CC3-IBD. Further in vitro microscopy with purified MORC2 showed that DNA addition significantly reduces MORC2 saturation concentration (Figure 5).

These assays convincingly demonstrate that MORC2 phase separates in cells, and identify the protein domains and interactions responsible for this phenomenon, with the notable caveat that the role of the CW domain here is left unexplored.

We appreciate the reviewer for their positive and detailed assessment of the strengths of our study. Our understanding of the CW domain’s function remains preliminary. Although we observed that the CW domain can influence condensate size, the IDR, IBD, and CC3 domains constitute the core structural elements driving phase separation. Consequently, the CW domain was not a primary focus of the current study. Nonetheless, investigating its functional contributions represents an interesting avenue for future work.

Weaknesses:

Although the authors demonstrated phase separation of MORC2FL, their evidence that this plays a functional role in the cell is incomplete.

Firstly, looking at differentially upregulated genes under MORC2FL overexpression, the authors acknowledge that only 10% are shared with differentially regulated genes identified in other MORC2FL overexpression studies (Figure 6c, d). No explanation is given for why this overlap is so low, making it difficult to trust conclusions from this data set.

We thank the reviewer for raising this important concern. In response, we have improved the quality and robustness of our RNA-seq analysis by repeating the experiments with optimized sample handling and increased sequencing depth. Using this updated dataset, we identified a considerably higher overlap between MORC2-regulated genes in our study and those reported previously.

Specifically, we observed 84 overlapping genes with the study by Nikole L. Fendler et al. [2], corresponding to approximately 32% of the MORC2-regulated genes reported in that work (Fig. 6i). In addition, we identified 102 overlapping genes with the dataset reported by Iva A. Tchasovnikarova et al. [3], representing approximately 22% of the genes identified in that study (Fig. S10b).

We note that complete concordance with previous reports is not expected, given substantial differences in experimental design. For example, Fendler et al. employed a doxycycline-inducible MORC2 expression system [2], whereas our study relies on transient overexpression in MORC2-knockout HeLa cells. In contrast, Tchasovnikarova et al. compared transcriptomes between MORC2 knockout and wild-type cells [3], rather than MORC2 rescue conditions. Moreover, RNA-seq results are inherently influenced by cell line batch variability, sequencing depth, and analysis pipelines, all of which differ across studies.

Taken together, we consider an overlap in the range of ~20–30% to be reasonable and biologically meaningful in the context of these experimental differences, and we believe that the revised RNA-seq data provide a more reliable foundation for our conclusions regarding MORC2-dependent transcriptional regulation.

Secondly, of the 21 genes shared in this study and in earlier studies, the authors note that the differential regulation is less pronounced when a phase-separation-deficient MORC2 mutant is overexpressed, rather than MORC2FL (Figure 6e). This is taken as evidence that phase separation is important for the proper function of MORC2. However, no consideration is made for the alternative possibility that the mutant, lacking the CC3 dimerization domain, may result in non-functional complexes involving MORC2, eliminating the need for a PS-centric conclusion. To take the overexpression data as solid evidence for a functional role of MORC2 PS, the authors would need to test the alternative, soluble complex hypothesis. Furthermore, there seems to be low replicate consistency for the MORC2 mutant condition (Figure S6a), with replicate 3 being markedly upregulated when compared to replicates 1 and 2.

We thank the reviewer for raising these important concerns. In the revised manuscript, we have substantially strengthened both the experimental evidence and the data presentation to directly address the alternative “soluble complex” interpretation as well as the issue of replicate consistency. Specifically, we now provide data that clarify the functional impact of phase-separation-deficient MORC2 mutants and explicitly show replicate-level RNA-seq analyses. The Fig. 6 and Fig. S10support these improvements and enhance both the robustness and transparency of our transcriptional analyses. Collectively, these revisions directly address the reviewer’s concerns regarding the functional interpretation of MORC2 phase separation.

Thirdly, the authors close by examining the in-cell PS capabilities and ATPase activity of several disease-associated mutants of MORC2 (Figure 7). However, the relevance of these mutants to the past 6 figures is unclear. None of these mutations is in regions identified as important for PS. Two of the mutations result in a higher percentage of the cell population being condensate-positive, but this is not seemingly connected to ATPase activity, as only one of these two mutants has increased ATPase activity. Figure 7 does not add any support to the main hypotheses in the paper, and nowhere in the paper do the authors investigate the protein regions where the mutations in Figure 7 are found.

We thank the reviewer for raising this point regarding Fig. 7. At the current stage, the results for disease-associated mutations are primarily descriptive. While we observed that certain mutations clustered at the N-terminus can affect MORC2 condensate formation, ATPase activity, and DNA binding, we did not identify a mechanistic explanation for these correlations. Notably, the T424R mutation, previously reported to significantly enhance ATPase activity [4], also increased both intracellular condensate formation and in vitro DNA binding in our experiments. In contrast, other mutations did not show such consistent effects. Previous studies have established that MORC2’s ATP-binding and DNA-binding activities are independent [4]. Our results further suggest that MORC2’s phase separation behavior is independent of both ATP and DNA binding affinity, although existing evidence hints at potential cross-regulatory interactions among these three functions.

We would also like to emphasize an additional observation that may help contextualize the relevance of N-terminal mutations. Although deletion of the MORC2 N-terminus does not prevent the remaining C-terminal region from forming nuclear condensates, these C-terminal condensates exhibit a marked loss of fluorescence recovery in FRAP assays (Fig. S11). This finding suggests that while the N-terminus is not strictly required for condensate assembly, it plays an important role in regulating condensate fluidity. Accordingly, disease-associated mutations distributed across the N-terminal region may influence MORC2 function by modulating condensate material properties rather than condensate formation per se. Based on this hypothesis, we evaluated the fluidity of condensates formed by the E236G and T424R mutants. FRAP measurements indicated substantially reduced fluorescence recovery in E236G, whereas T424R exerted minimal effects (Fig. 7e, f).

Overall, our interpretation of the results in Fig. 7 is still at a preliminary stage. Nevertheless, the role of the MORC2 N-terminus in modulating condensate fluidity, together with the observed impairment caused by the E236G mutation, appears to be robust, although the underlying mechanism remains to be elucidated. We have incorporated additional discussion on this point and consider it an important direction for future study.

Reviewer #1 (Recommendations for the authors):

(1) Why does MORC2 overexpression lead to changes in gene regulation that are so different from past MORC2 overexpression studies? This is unsettling to me.

(2) Likewise, why is replicate 3 for the MORC2ΔCC3 variant so different from replicates 1 and 2? Perhaps repeating this experiment would be helpful, both for showing better repeatability and perhaps as regards pulling out a stronger phenotype.

We have repeated the experiments and obtained improved data quality.

(3) A better explanation of the relevance of Figure 7 to the story of the rest of the paper, especially the phase-separation of MORC2, would be important to improving this paper.

We thank the reviewer for this suggestion. We have performed additional experiments and expanded the discussion.

(4) Are expression levels of mutant proteins in Figure 7 uniform between mutants? If not, is it possible that expression levels might account for the difference in condensate-positive cells between mutants?

We cannot fully exclude the possibility that differences in expression levels may contribute to the observed differences among mutants. In our experiments, equal amounts of plasmid DNA were used for transfection across all conditions. Although we did not directly quantify post-transfection protein expression levels by immunoblotting or similar approaches, even if certain mutations were to affect protein expression, it would be technically challenging to further optimize the strategy to fully normalize expression levels across mutants.

Importantly, we note that MORC2 does not form condensates in all transfected cells, even when EGFP fluorescence indicates robust expression levels that are comparable to, or even exceed, those observed in condensate-positive cells. This observation suggests that high expression alone is not sufficient to drive MORC2 phase separation in cells. Therefore, we do not favor the interpretation that the E236K and T424R mutations enhance MORC2 condensation simply by increasing MORC2 protein expression levels.

Minor:

(1) I would suggest considering using the term "dynamic" rather than "liquid-like", as FRAP is technically a measurement of the dynamicity of a protein within a volume, rather than a measurement of the actual fluidity of that volume.

We thank the reviewer for this helpful suggestion. We agree that FRAP measurements primarily report protein mobility and condensate dynamics rather than the physical fluidity of the condensates. We have therefore revised the manuscript to replace “liquid-like” with “dynamic” where conclusions are based on FRAP analyses.

(2) A further investigation of the role of the CW domain would be very interesting, since it clearly has a major role in condensate morphology. Perhaps CW confers important heterotypic interactions which contribute to compositional control of the MORC2 condensates, and thus function and morphology? However, due to the complexity of this specific question and the potentially marginal improvement offered by this paper, I do not think this is a critical addition.

We thank the reviewer for this insightful suggestion. We have noted this possibility in the Discussion as an important avenue for future investigation.

(3) Why is TCD not tested alone by EMSA for affinity to DNA in Figure 5?

Our inference regarding the DNA-binding capacity of the TCD domain was based on comparative EMSA analyses. Specifically, we found that the TCD–CC3–IBD fragment was able to bind DNA, whereas the CC3–IBD fragment alone showed no detectable DNA binding. From this comparison, we inferred that the TCD domain is responsible for the observed DNA-binding activity.

Because the TCD domain does not affect MORC2 condensate formation, it was not a central focus of the present study, which primarily aims to elucidate the mechanisms underlying MORC2 phase separation and its functional relevance. For this reason, we did not further test TCD alone by EMSA in Figure 5.

Reviewer #2 (Public review):

Summary:

The study by Zhang et al. focuses on how phase separation of a chromatin-associated protein MORC2, could regulate gene expression. Their study shows that MORC2 forms dynamic nuclear condensates in cells. In vitro, MORC2 phase separation is driven by dimerization and multivalent interactions involving the C-terminal domain. A key finding is that the intrinsically disordered region (IDR) of MORC2 exhibits strong DNA binding. They report that DNA binding enhances MORC2's phase separation and its ATPase activity, offering new insights into how MORC2 contributes to chromatin organization and gene regulation. The authors try to correlate MORC2's condensate-forming ability with its gene silencing function, but this warrants additional controls and validation. Moreover, they investigate the effect of disease-linked mutations in the N-terminal domain of MORC2 on its ability to form cellular condensates, ATPase activity, and DNA-binding, though the findings appear inconclusive in the manuscript's current form.

Thank you for your thorough and constructive review of our manuscript. In response to the concerns raised regarding the functional relevance of MORC2 condensate formation, we have redesigned and expanded the experiments presented in Fig. 6 and Fig. S6 to directly link MORC2’s condensate-forming capacity with its transcriptional regulatory function. These new experiments provide additional controls and validation, strengthening the causal relationship between MORC2 condensate dynamics and gene regulation.

At the current stage, the results for disease-associated mutations are descriptive. While we observed that certain mutations clustered at the N-terminus can affect MORC2 condensate formation, ATPase activity, and DNA binding, we did not identify a mechanistic explanation for these correlations. Notably, the T424R mutation, previously reported to significantly enhance ATPase activity [4], also increased both intracellular condensate formation and in vitro DNA binding in our experiments. In contrast, other mutations did not show such consistent effects. Previous studies have established that MORC2’s ATP-binding and DNA-binding activities are independent [4]. Our results further suggest that MORC2’s phase separation behavior is also independent of both ATP and DNA binding, although existing evidence hints at potential cross-regulatory interactions among these three functions.

Strengths:

The authors determined a 3.1 Å resolution crystal structure of the dimeric coiled-coil 3 (CC3) domain of MORC2, revealing a hydrophobic interface that stabilizes dimer formation. They present extensive evidence that MORC2 undergoes liquid-liquid phase separation (LLPS) across multiple contexts, including in vitro, in cellulo, and in vivo. Through systematic cellular screening, they identified the C-terminal domain of MORC2 as a key driver of condensate formation. Biophysical and biochemical analyses further show that the IDR within the C-terminal domain interacts with the C-terminal end region (IBD) and also exhibits strong DNA-binding capacity, both of which promote MORC2 phase separation. Together, this study emphasizes that interactions mediated by multiple domains-CC3, IDR, and IBD- drives MORC2 phase separation. Finally, the authors quantified the effect of removing the CC3 on the upregulation and downregulation of target gene expression.

We thank the reviewer for their appreciation of the key findings presented in this manuscript.

Weaknesses:

Though the findings appear compelling in isolation, the study lacks discussion on how its findings compare with previous studies. Particularly in the context of MORC2-DNA binding, there are previous studies extensively exploring MORC2-DNA binding (Tan, W., Park, J., Venugopal, H. et al. Nat Commun 2025), and its effect on ATPase activity (ref 22). The contradictory results in ref 22 about the impact of DNA-binding on ATPase activity, and ATPase activity on transcriptional repression, warrant proper discussion. The authors performed extensive in-cellulo screening for the investigation of domain contribution in MORC2 condensate formation, but the study does not consider/discuss the possibility of some indirect contributions from the complex cellular environment. Alternatively, the domain-specific contributions could be quantified in vitro by comparing phase diagrams for their variants. While the basis of this study is to investigate the mechanism of MORC2 condensate-mediated gene silencing, the findings in Figure 6 appear incomplete because the CC3 deletion not only affects phase separation of MORC2 but also dimerization. Furthermore, their investigation on disease-linked MORC2 mutations appears very preliminary and inconclusive because there are no obvious trends from the data. Overall, the discussion appears weak as it is missing references to previous studies and, most importantly, how their findings compare to others'.

We thank the reviewer for their careful assessment of MORC2’s DNA-binding properties and its relationship with ATPase and transcriptional activities. We would like to offer the following clarifications to address these concerns, which will also be incorporated into the Discussion section of the revised manuscript.

First, recent work by Tan et al. [5] similarly identified multiple DNA-binding sites in MORC2, consistent with our findings, though there are discrepancies in the precise binding regions. In particular, they reported that isolated CC1 and CC2 domains do not bind 60 bp dsDNA, which contrasts with our observations. We attribute this difference to the types of DNA used in the assays. In our study, we employed 601 DNA, a defined nucleosome-positioning sequence, which differs substantially from randomly designed short dsDNA. For instance, prior work by Christopher H. Douse et al. [54] also confirmed that MORC2’s CC1 domain can bind 601 DNA.

Second, in the study by Fendler et al. [2], DNA binding was reported to reduce MORC2’s ATPase activity—an observation that appears inconsistent with the results presented in our Fig. 5j. A critical distinction between the two studies lies in the experimental systems used: Fendler et al. [2] employed MORC2 constructs and 35 bp double-stranded DNA (dsDNA), whereas our experiments utilized full-length MORC2 and 601 bp DNA (a sequence with high nucleosome assembly potential). These differences including the absence of potentially regulatory C-terminal regions in the truncated construct and the varying length/structural properties of the DNA substrates introduce variables that substantially complicate direct comparative analysis of ATPase activity outcomes.

Separately, Douse et al. [4] demonstrated that the efficiency of HUSH complex-dependent epigenetic silencing decreases as MORC2’s ATP hydrolysis rate increases, implying an inverse relationship between ATPase activity and silencing function. Notably, our current work has not established a direct mechanistic link between MORC2 phase separation and its ATPase activity. Thus, we refrain from inferring that the effect of MORC2 phase separation on transcriptional repression is mediated through modulation of its ATPase function this remains an important question to address in future studies.

Finally, we have redesigned and expanded the experiments presented in Fig. 6 and Fig. S6 to directly link MORC2’s condensate-forming capacity with its transcriptional regulatory function.

Reviewer #2 (Recommendations for the authors):

Major concerns:

(1) Unaddressed discrepancies with the previous study:

(a) Inadequate discussion of Reference 22 and apparent contradictions. Notably, Reference 22 provides evidence for reduced ATPase activity upon DNA binding, in contrast to the current study's observations. Moreover, Reference 22 demonstrates that ATP hydrolysis (ATPase activity) is inversely associated with MORC2-mediated gene silencing, whereas this study concludes that 'the silencing function of MORC2 requires its ATPase activity'. These apparent contradictions warrant a more thorough discussion to reconcile the differences, including potential mechanistic explanations and experimental context that could account for the discrepancies. Additionally, the authors should discuss potential reasons why Ref. 22 may not have observed phase separation during MORC2 biophysical analysis. For instance, in Ref. 22, SEC-MALS was performed at 2 mg/mL (~16 µM) MORC2 FL in the presence of 150 mM NaCl, conditions that could influence phase behavior based on the current manuscript's results. Addressing whether differences in protein construct, buffer composition, or experimental design might account for this discrepancy would strengthen the discussion.

We thank the reviewer for pointing out the apparent discrepancies between our results and those reported in Ref. 22. We agree that these differences warrant explicit discussion, and we have revised the Discussion accordingly to clarify the experimental and conceptual distinctions between the two studies.

First, regarding the effect of DNA binding on ATPase activity, Ref. 22 examined MORC2 ATPase activity under conditions where MORC2 does not undergo detectable phase separation, whereas our ATPase assays were performed under conditions in which MORC2 readily forms condensates in the presence of DNA. We therefore propose that the observed increase in ATPase activity in our study may reflect a distinct biochemical regime in which phase separation and/or high local protein concentration modulates enzymatic activity. Importantly, our data do not exclude the possibility that DNA binding per se can inhibit ATPase activity under non-condensing conditions, as reported in Ref. 22.

Second, with respect to transcriptional repression, Ref. 22 reported an inverse correlation between ATP hydrolysis and MORC2-mediated silencing, whereas our study finds that ATPase activity is required for efficient repression. We suggest that these observations are not necessarily contradictory but may reflect different regulatory layers of MORC2 function. Specifically, ATP binding and hydrolysis may be required for MORC2 structural remodeling and chromatin engagement, while excessive or dysregulated ATP hydrolysis could impair stable silencing complexes, as suggested previously [4]. We now explicitly discuss this possibility in the revised manuscript.

Finally, we appreciate the reviewer’s suggestion regarding the absence of phase separation in Ref. 22. Indeed, SEC-MALS experiments in Ref. 22 were conducted at ~16 µM MORC2 in the presence of 150 mM NaCl (the purification condition is 500 mM NaCl, 10% glycerol), conditions that based on our phase diagrams—are close to or above the saturation concentration but also strongly influenced by ionic strength. This combination of factors explains why the UV peak from SEC-MALS is not indicative of a homogeneous sample [3].

(b) The DNA binding capacity of individual MORC2 domains was tested in Fig. 5. IDR appears to be the strongest DNA binder among others. Is this the effect of IDR being isolated from the rest of the protein? A recent paper (Tan, W., Park, J., Venugopal, H. et al. Nat Commun 2025) also investigated DNA binding capacity of different regions of MORC2 using hydrogen-deuterium exchange experiments and EMSA. Interestingly, it can be seen in Figure S9 that the DNA binding capacity of different regions changes when compared together to when in isolation (MORC2 1-603 vs 1-265; 1-495; 496-603). In line with the above, MORC2 IDR's interaction with DNA warrants additional investigation, taking the system as a whole to avoid misinterpretation arising from non-specific interactions.

We appreciate the reviewer’s insightful comments regarding domain-specific DNA binding and the potential caveats of studying isolated regions. In Figure 5, our EMSA analyses show that the isolated IDR exhibits the strongest DNA-binding signal among the tested fragments. We agree that this observation may, at least in part, reflect the removal of structural or regulatory constraints imposed by the full-length protein.

Consistent with the reviewer’s point, Tan et al. [5] demonstrated that DNA-binding behavior of MORC2 regions differs when analyzed in isolation versus in the context of larger constructs. We have now incorporated this comparison into the Discussion and explicitly note that DNA binding by the IDR should be interpreted as a contextual and potentially cooperative property rather than an autonomous function.

Importantly, our conclusions do not rely on the IDR acting as an independent DNA-binding module in vivo. Rather, we propose that the IDR contributes to DNA engagement and phase behavior within the architectural framework of full-length MORC2. We now emphasize this limitation and highlight the need for future studies that probe DNA binding in the context of intact MORC2 or minimally perturbed constructs.

(2) MORC2 DNA binding impacting phase separation and ATPase activity:

While it is clear that MORC2: DNA interaction facilitates MORC2 phase separation, the impact on ATPase activity is not conclusive. First, they observe an opposite trend (compared to ref. 22) for DNA binding on MORC2's ATPase activity. Secondly, it is not clear if the increase in ATPase activity is mediated by DNA binding or phase separation. The ATPase activity was measured at 1 µM MORC2 protein concentration in the presence of DNA, where MORC2 appears to phase separate. To draw more definitive conclusions, additional controls are necessary. Specifically, a phase separation-deficient mutant (from this study) and a DNA-binding-deficient mutant (see ref. 22) should be included to disentangle the contributions of DNA binding and phase separation to ATPase activity. The choice of ATP-binding-deficient mutant N39A as a negative control seems inconclusive in this regard. Additionally, why is there an increase in ATP hydrolysis rate for the ATP-binding-deficient mutant in the presence of DNA, resulting in ATP hydrolysis rates similar to WT MORC2? This raises further questions about the underlying mechanism.

We agree with the reviewer that disentangling the contributions of DNA binding and phase separation to ATPase activity is challenging and that our current data do not fully resolve this issue. As noted, ATPase assays were performed at protein concentrations (1 µM) where MORC2 undergoes DNA-induced phase separation, making it difficult to distinguish whether enhanced ATP hydrolysis arises directly from DNA binding or indirectly from condensate formation.

We acknowledge that inclusion of additional mutants such as phase separation deficient or DNA-binding deficient variants would provide a more definitive mechanistic separation of these effects. However, generating and validating such mutants in a manner that preserves overall protein integrity is beyond the scope of the current study. Accordingly, we have revised the text to present our findings more cautiously and to frame the observed ATPase enhancement as a correlation rather than a causal mechanism.

Regarding the ATP-binding–deficient N39A mutant, we agree that its behavior in the presence of DNA raises interesting mechanistic questions. We now explicitly note this unexpected observation and discuss possible explanations, including partial ATP binding, altered oligomeric states, or indirect effects mediated by condensate formation.

(3) Dissecting the domain-specific contribution in MORC2 phase separation:

(a) While in cellulo data indicate that the presence of IDR, NLS, CC3, and IBD is all essential for MORC2 condensate formation, it is not clear if this is the effect of the complex cellular environment or whether it is intrinsic for MORC2 phase separation ability. In lines 256-259, the authors suggest IDRa interaction with IBD may serve as a nucleation mechanism for LLPS. In other places, it has been mentioned that CC3 dimerization acts as a scaffold for condensate formation. It is not clear if all of these are essential for MORC2 phase separation, or one of them is essential while the other domain(s) facilitates the phase separation. Though Figure 3 provides a qualitative overview of the contribution of different regions in MORC2 phase separation in cellulo-influenced by the complex cellular environment and substrate interactions, the absolute domain contribution in phase separation would be better studied in vitro by quantitatively comparing phase diagrams (for example, c-sat vs temperature) of different domain deletion constructs.

We thank the reviewer for highlighting the distinction between intrinsic phase separation propensity and cellular context dependent effects. Our in cellular screening was designed to identify regions required for condensate formation under physiological conditions, where chromatin, binding partners, and macromolecular crowding are present. We agree that this approach does not directly quantify the intrinsic phase separation contribution of individual domains.

While CC3 dimerization, IDR–IBD interactions, and nuclear localization all contribute to condensate formation, our data do not imply that these elements are mechanistically equivalent. Rather, we propose that CC3 provides a structural scaffold, while IDR-mediated interactions lower the energetic barrier for condensation. We have revised the manuscript to clarify this hierarchical model and to avoid implying that all domains contribute equally or independently.

We agree that quantitative in vitro phase diagrams would provide valuable insight into intrinsic domain contributions. Whereas the MORC2ΔCC3-IBD (1–900) and CC3-IBD (900-1032) fragment fails to induce phase separation, the IDR mix CC3–IBD fragment drives robust phase separation; additionally, phase separation is entirely abrogated in the absence of domain–domain interactions. These observations collectively verify that phase separation is contingent on specific domain combinations and their interactions.

(b) Similarly, for line 228-231: 'Notably, condensates formed exclusively in the nucleus and not in the cytoplasm of transfected HeLa cells, suggesting that chromatin-associated nuclear factors, such as DNA, may contribute to the nucleation or stabilization of MORC2 condensates.' This is an important observation made by the authors. Since MORC2 readily phase separates in vitro under physiological conditions, it is important to discuss why MORC2 does not make condensates in the cytoplasm (in the case of MORC2deltaNLS). In this regard, how does the concentration of overexpressed EGFP-MORC2 constructs compare with in vitro tested droplets of MORC2?

We thank the reviewer for highlighting this important conceptual point. Although MORC2 readily undergoes phase separation in vitro under physiological buffer conditions, the absence of condensate formation in the cytoplasm of cells expressing MORC2ΔNLS underscores the importance of the nuclear environment in promoting MORC2 assembly.

The cytoplasm differs fundamentally from the nucleus not only in overall molecular composition but also in the availability of high-valency scaffolds such as chromatin. We propose that chromatin-associated components, particularly DNA, provide a platform that locally concentrates MORC2 and increases its effective valency, thereby facilitating nucleation or stabilization of condensates in the nucleus. In contrast, the cytoplasm lacks such scaffolds, even when MORC2 is expressed at appreciable levels. In cultured cells, MORC2 is seldom observed in the cytoplasm. While specific experimental contexts may facilitate its cytoplasmic localization, such observations are rarely reported [6]. In transfection-based systems, MORC2 predominantly displays droplet-like behavior in the nucleus. Notably, in endogenous EGFP–MORC2 chimeric mice, we detected punctate MORC2 structures in the neuronal cytoplasm of the brain and spinal cord. The functional significance and biophysical state of cytoplasmic MORC2 remain largely unexplored.

With respect to protein concentration, while EGFP-MORC2 is robustly expressed in cells, direct comparison between cellular expression levels and the protein concentrations used in vitro is inherently challenging. Importantly, in vitro phase separation is driven by bulk protein concentration under defined conditions, whereas in cells, effective local concentration and interaction valency are strongly shaped by spatial confinement and chromatin association. We have revised the manuscript text to emphasize this distinction and to avoid interpreting nuclear specificity as a purely concentration-dependent phenomenon.

(c) Lines 227-228: '... CW domain restricts condensate overgrowth or fusion', this inference is based on CTDdeltaCW puncta being larger in size (Figure 3a). However, in Figure 4h MORC2deltaIDRb and MORC2deltaIDRc also result in larger puncta. Making a final conclusion that the CW domain restricts condensate overgrowth or fusion warrants additional investigation.

We thank the reviewer for pointing out the limitation of our original conclusion. We agree that the enlarged puncta in both CTDΔCW (Figure 3a) indicate that condensate size regulation involves the CW domain was insufficiently rigorous.

Re-analysis of existing data identifies clear phenotypic disparities between the mutants: MORC2ΔIDRb/ΔIDRc mutants show two distinct phenotypes (reduced puncta number with enlarged size, or unchanged puncta number with uniform enlargement), and their total puncta area per cell is comparable to the WT. By contrast, CTDΔCW mutants display markedly larger puncta relative to the WT. Based on this distinction, we have revised our conclusion to a more cautious formulation: "These observations suggest that the CW domain may participate in regulating initial nucleation size and the exact molecular mechanisms require further investigation."

(4) MORC2 condensate-mediated gene silencing:

This is one of the key investigations of this study where the authors evaluate the ability of MORC2 condensates to regulate gene silencing (transcriptional repression). The major concern here is that the authors are drawing their conclusion based on a CC3 domain deletion mutant of MORC2 and comparing it with wild-type MORC2. Notably, the CC3 domain is responsible for MORC2 dimerization, and as the authors quote, 'The dimeric assembly of CC3 is essential for maintaining the structural integrity of the protein', the absence of CC3 would have a direct impact on its function (such as ATPase activity). With these considerations, it is not clear whether the effect of CC3 domain deletion on gene regulation is an effect of no phase separation or a consequence of loss of function. This necessitates additional validation by including other controls, such as IBD domain deletion mutant, IDRa domain deletion mutant, where the phase separation is impeded without affecting dimerization.

We appreciate the reviewer’s concern regarding the interpretation of CC3 deletion experiments. We agree that CC3 deletion affects both dimerization and phase separation, complicating attribution of gene regulatory effects solely to condensate formation. Our intention was not to claim that loss of repression arises exclusively from impaired phase separation, but rather to demonstrate that disrupting condensate-dynamic capacity correlates with impaired silencing.

To directly address these concerns, we have performed a series of new experiments specifically designed to decouple condensate formation, condensate dynamics, and protein abundance, thereby allowing us to more rigorously interrogate the functional relevance of MORC2 condensates.

First, to overcome the limitation of domain deletions which may affect MORC2 function beyond phase separation we introduced a micropeptide-based kill switch (KS) to the C terminus of MORC2. This strategy has recently emerged as a powerful approach to selectively reduce condensate dynamics without disrupting protein expression, folding, or domain architecture [1]. Importantly, unlike CC3 or IDRa deletions, MORC2+KS robustly form nuclear condensates but exhibits markedly reduced internal dynamics, as demonstrated by FRAP analyses showing minimal fluorescence recovery after photo bleaching (Fig. 6a-c). This strategy therefore allows us to perturb condensate material properties independently of MORC2 domain integrity.

Second, we systematically compared the transcriptional consequences of rescuing MORC2-knockout HeLa cells with MORC2FL, condensation-deficient mutants (ΔCC3 and ΔIDRa), and the dynamics-defective MORC2+KS (Fig. 6d). Despite being expressed at substantially higher levels than MORC2FL (Fig. 6e), all three mutants showed a striking and consistent failure to restore MORC2-dependent transcriptional regulation (Fig. 6f-h). This effect was particularly pronounced for transcriptionally repressed genes, including two sets of high-confidence MORC2 targets reported in prior studies (Fig. 6i and Fig. S10). These findings demonstrate that neither increased protein abundance nor the mere presence of condensate-like structures alone is sufficient to restore MORC2 function.

Third, our data instead support a model in which both soluble MORC2 complexes and dynamic MORC2 condensates are required for full transcriptional activity. While soluble MORC2 is likely involved in target recognition and complex assembly, our results indicate that proper condensate formation and critically, condensate dynamics are essential for effective transcriptional repression and activation. The inability of the MORC2+KS mutant to rescue transcriptional defects, despite intact condensate formation, points away from a model in which MORC2 condensates represent only microscopically visible byproducts of MORC2 activity.

We believe these new data strengthen the manuscript by pairing the detailed mechanistic dissection of MORC2 phase separation with direct functional evidence, enhancing the conceptual impact and biological significance of the study.

(5) Uncertain impact of pathogenic MORC2 mutations:

Line 356-365: While the statements such as "disease-associated mutations primarily affect enzymatic and phase behaviors rather than DNA affinity" and "these findings provide mechanistic insight into how specific mutations may contribute to distinct pathological outcomes" are conceptually compelling, the data presented in Figure 7b-d do not appear to fully support these conclusions. For many of the mutants, the differences from WT across key parameters-condensation, ATPase activity, and DNA binding-are either modest or statistically insignificant. As such, drawing a unified mechanistic conclusion from these datasets may overstate what the data actually support.

We agree that the effects of disease-associated MORC2 mutations described in Fig. 7 are modest and, in some cases, statistically insignificant. Our intention was to document observable trends rather than to propose a unified mechanistic framework. We have revised the manuscript to temper these conclusions and to emphasize the descriptive nature of these data.

(6) Important conceptual clarifications:

(a) Intrinsically disordered regions (IDRs) are not synonymous with phase separation. As the authors show, it is a combination of IDR-mediated interactions and CC3 dimerization that contributes towards the phase separation of MORC2. While IDRs can act as scaffolds for multivalent weak interactions that may promote biomolecular condensate formation, many IDRs serve other roles-such as mediating transient interactions, signaling, or regulatory functions-without undergoing phase separation. Researchers should avoid generalizing the assumption that the mere presence of IDRs in a protein implies its ability for phase separation. In this regard, authors should consider restructuring some of their generalized statements: Line 87-88: 'Recent studies suggest that intrinsically disordered regions (IDRs) can drive liquid-liquid phase separation (LLPS)' and Line 159-161: 'we noticed a long unstructured region at its C-terminus (Fig. S1b), a characteristic often associated with proteins capable of phase separation'.

We agree that IDRs are not synonymous with phase separation and have revised the Introduction to avoid generalized statements. The revised text now emphasizes that IDRs can contribute to phase separation in a context-dependent manner and act in concert with structured oligomerization domains such as CC3-IBD.

(b) Liquid-liquid phase separation: I would suggest switching the phrase to just phase separation. The rationale is that the in vitro studies of MORC2 (FRAP, droplet imaging) do not show liquid-like behavior, but perhaps liquid-solid. The FRAP studies suggest liquid-like behavior for some of the constructs. Given the differences in viscoelastic properties across the in vitro and in cellulo studies, it is better to generalize to "phase separation". Movies for droplet fusion and FRAP, wherever applicable, would be much appreciated. As the nature of in vitro MORC2 droplets appears different than in cells, movie representations of the above would enable readers to better assess the viscoelastic nature of the droplets (whether liquid, gel, etc).

We appreciate the reviewer’s insight regarding the viscoelastic properties of MORC2. Our experimental data indeed show a disparity in dynamics between the two environments: while in vitro MORC2-FL condensates exhibit relatively low internal mobility, the in cellulo MORC2-FL puncta display high dynamics, characterized by rapid internal recovery in FRAP assays and droplet fusion events (Fig. S2f).

This contrast suggests that the intracellular microenvironment plays a critical role in regulating the material state of MORC2 condensates. Consequently, we have focused on providing in vivo fusion data, as we believe in vitro characterizations (such as fusion or FRAP under various artificial conditions) may not faithfully represent the physiological behavior of MORC2. We have revised the manuscript to use the more general term “phase separation” or “condensation” and have added a discussion on these limitations to avoid overinterpreting the material properties observed in vitro.

(7) Methods:

(a) Figure 6 S2b: If phase separation occurs at, say, 1.8 µM protein concentration, this indicates that the protein has reached its saturation concentration (c-sat). Beyond c-sat, any additional protein should partition into the dense phase, while the concentration of the dilute phase remains constant. However, in this figure, the dilute phase concentration appears to increase with increasing total protein concentration, which is inconsistent with expected phase separation behavior. As the methods section does not have any sub-section for the sedimentation assay, it becomes difficult to understand how this experiment was performed, whether there is any technical discrepancy in the way soluble and pellet fractions were handled and processed for loading onto the gels. This is also the case with Figure 3d.

We thank the reviewer for carefully examining the sedimentation assay and for raising this important conceptual point. We agree that, for an ideal two-phase system at thermodynamic equilibrium, the concentration of the dilute phase is expected to remain constant once the saturation concentration (c-sat) is reached.

In our study, the sedimentation assay was used as an operational readout to assess concentration-dependent partitioning rather than to quantitatively define equilibrium phase boundaries. The assay involves centrifugation-based separation of supernatant and pellet fractions followed by SDS–PAGE analysis, and therefore does not necessarily report the equilibrium concentrations of coexisting dilute and dense phases. In particular, this approach can be influenced by incomplete physical separation of phases, kinetic trapping, and redistribution of material during handling, especially in systems where condensate maturation or internal reorganization occurs on longer timescales.

Consequently, the apparent increase in the supernatant fraction with increasing total protein concentration likely stems from kinetic limitations and inherent technical constraints of the sedimentation assay, rather than a genuine deviation from classical phase separation behavior. These caveats are now explicitly clarified in the Methods section, with similar limitations of centrifugation-based assays for defining equilibrium phase behavior of biomolecular condensates reported previously.

(b) Figure 4: The NMR comparisons appear to be primarily qualitative, lacking quantitative analyses such as chemical shift perturbation (CSP) and intensity ratio plots, which would offer deeper mechanistic insights. The NMR spectra detailing interactions among the IDR domains need to be quantified.

We thank the reviewer for the suggestion. We have now performed quantitative CSP analyses for the NMR data shown in Fig. 4, and the corresponding CSP plots have been added to the revised manuscript (Fig. S7).

As expected for interactions mediated by intrinsically disordered regions involved in phase separation, the observed CSPs are generally small. Notably, the CSP profile of IDRa closely matches that observed for the full-length IDR, whereas IDRb and IDRc show minimal perturbations. These results indicate that the interaction is primarily mediated by IDRa, with little contribution from the remaining regions.

Peak intensity analyses were also examined but did not reveal additional residue-specific trends. Together, the quantitative CSP data support our conclusion that the interaction is weak, dynamic, and region-specific, consistent with an IDR-driven, phase-separation-related mechanism. We add this statement in method: CSPs were calculated in Hz at 600 MHz using the following equation:

Minor comments:

(1) Line 59-60: The Authors mention the HUSH-complex and then the MORC protein family, but do not discuss the relation between the two.

We thank the reviewer for this comment. We have revised the Introduction to explicitly state that MORC2 may serve as a component of the HUSH complex and to clarify the functional relationship between MORC family proteins and HUSH-mediated transcriptional repression.

(2) Line 74: 'Despite their structural similarities...', similarities between what all?

We agree that this statement was ambiguous. We have revised the text to explicitly specify that the comparison refers to structural similarities among MORC family members.

(3) Line 75: 'MORC-mediated repression remains...', this is the first time the word 'repression' is mentioned in the text and directly as an outstanding question.

We have revised the Introduction to introduce the concept of transcriptional repression earlier and to provide appropriate context before posing it as an outstanding question.

(4) The third paragraph does address issues in comments 1 and 3 to some extent, but the introduction needs some restructuring to provide a proper flow of information.

We agree that the Introduction required restructuring. We have revised this section to improve logical flow, better integrate prior studies, and more clearly articulate the motivation and scope of the present work.

(5) Line 83-85: How does the presence of IDRs suggest potential regulatory mechanisms?

We have revised this sentence to clarify that IDRs may contribute to regulatory mechanisms by enabling multivalent and dynamic interactions, rather than implying that IDRs inherently confer regulatory function or phase separation capability.

(6) Line 106-107: 'To determine whether MORC2 has N- and C-terminal dimerization interfaces similar to those...', reference 14 has already established that CC3 (denoted as CC4 in ref 14) is responsible for dimerization. Consider acknowledging their work in this regard?

We thank the reviewer for this reminder. We have now explicitly acknowledged Ref. 14, which previously established the role of CC3 (denoted CC4 in that study) in MORC2 dimerization.

(7) Lines 117-122: Are the authors comparing morphology from negative stain EM with AlphaFold predicted structure (Figure S1a and S1b)? If so, providing a zoomed-in inset from Figure S1a would be helpful.

Yes, the comparison was intended to relate the negative-stain EM morphology to the AlphaFold-predicted architecture. We have added a zoomed-in inset in Fig. S1a to facilitate clearer comparison.

(8) Line 152-153: '...even under varying physiological conditions', what are these varying conditions? Are the authors trying to point towards any of their specific results?

We have revised this phrase to explicitly refer to variations in salt concentration and protein concentration tested in our in vitro assays.

(9) Line 154-155: 'The dimeric assembly of CC3 is essential for maintaining the structural integrity of the protein', if it has been established, then please provide a reference.

We thank the reviewer for this suggestion. For MORC family proteins, C-terminal coiled-coil–mediated dimerization is necessary for correct homodimer formation and functional stability (Xie et al., 2019, Cell Commun Signal. 17:160, Ref 14 in the revised manuscript).

(10) Line 159-161: 'we noticed a long unstructured region at its C-terminus (Figure S1b), a characteristic often associated with proteins capable of phase separation25.', again authors are generalizing a statement which is, in most cases, context-dependent. For example, ref 25 mentions that unstructured regions or IDRs serve as a scaffold for multivalent interactions.

We agree with the reviewer and have revised this sentence to avoid generalization. The revised text now emphasizes that IDRs may facilitate multivalent interactions in a context-dependent manner, rather than being intrinsically indicative of phase separation. Additionally, we have explicitly cited the mechanistic insight from Reference 25 that IDRs serve as scaffolds for multivalent interactions, to strengthen the logical link between the structural feature and its potential functional relevance.

(11) Methods section for NMR (Line 665-667) mentions that nucleotides were added to a final concentration of 10 mM. There is no figure or section for MORC2 NMR with added nucleotides/DNA.

We thank the reviewer for pointing this out. The nucleotide (ATP) addition was part of preliminary NMR trials and is not directly associated with the figures presented. We have deleted this in the Methods section to avoid confusion.

(12) Line 285-294: Authors compare the effect of DNA binding on the phase separation of both MORC2FL and MORC2 CTDdeltaCW and conclude that DNA-induced condensation is primarily mediated through interactions with the IDR-NLS region. This appears not to be backed by proper control experiments. The authors do not show whether DNA binding mediates any phase separation for the isolated NTD or not? Similarly, what is the effect of DNA binding on MORC2 deltaIDR?

We thank the reviewer for this insightful comment and agree that additional controls are essential for rigorously dissecting the contribution of DNA binding to MORC2 phase separation. Our interpretation that DNA-enhanced condensation is primarily mediated through the IDR–NLS region was based on comparative analyses of MORC2FL and MORC2 CTDΔCW, together with EMSA results demonstrating that DNA binding activity is conferred by the IDR–NLS–containing region. We acknowledge, however, that DNA binding alone is not sufficient to infer phase separation behavior.

To address this point, we have performed additional analyses using the isolated NTD’ (residues 1–536) and MORC2 ΔIDR–NLS mutants (Fig. S6). The isolated NTD’ exhibited detectable DNA binding [4] but did not undergo DNA-induced condensation under conditions while MORC2FL or MORC2 CTDΔCW (residues 537-1032) readily formed condensates, indicating that DNA binding by itself is insufficient to drive phase separation. In parallel, MORC2 ΔIDR–NLS mutants showed severely compromised solubility and stability in vitro, which limited their quantitative characterization in phase separation assays. Nevertheless, under the conditions tested, these mutants did not display DNA-enhanced condensation comparable to MORC2FL.

Taken together, these observations support a model in which the IDR–NLS region plays a critical role in coupling DNA binding to condensation, while additional domains are required to sustain robust phase separation. We have revised the manuscript text to clarify the experimental scope and to avoid overinterpreting the contribution of DNA binding in the absence of fully reconstituted control systems.

(13) How did the authors assign the backbone amide NMR chemical shifts for MORC2?

Backbone assignments of MORC2 IBD (1004-1032) were obtained using SOFAST versions of standard triple-resonance experiments, including HNCACB and CBCACONH, recorded at 298 K. Residual assignment ambiguities were resolved using [15] N-edited HMQC-NOESY-HMQC spectra.

(14) Line 256: 'The partial compaction of IDRa...', what does the author mean here with 'partial compaction'? How did they measure compaction here?

Regarding the term “partial compaction” mentioned previously, we apologize for the typographical error this phrase was erroneously used in place of “key component”.

(15) Line 312-315: Why is there even a MORC2 readout for MORC2 KO cells with only EGFP? Also, the authors suggest that IDR deletion may impair mRNA stability or transcription; however, the expression levels of MORC2 deltaIDR and MORC2 deltaCC3 do not appear drastically different in Figure 3a.

We thank the reviewer for raising these points. The apparent MORC2 signal in MORC2 knockout cells transfected with EGFP alone is due to the presence of residual MORC2 mRNA. Although CRISPR–Cas9–mediated knockout introduces a frameshift that prevents MORC2 protein expression, the mRNA can still be detected by RNA-seq. This is because nonsense-mediated decay (NMD), which targets transcripts with premature stop codons for degradation, is not always 100% efficient. Therefore, some MORC2 transcripts remain and produce detectable RNA-seq reads, even though no functional protein is expressed.

Regarding the apparent discrepancy in expression levels, Fig. 3a displays only EGFP-positive cells, within which the fluorescence intensity of MORC2ΔIDR and MORC2ΔCC3 appears comparable to that of WT MORC2. However, the overall fraction of EGFP-positive cells is markedly reduced for these mutants compared to WT. Thus, while expression levels among successfully transfected cells are similar, fewer cells express detectable levels of the ΔIDR or ΔCC3 constructs across the total population. We therefore interpret this reduction in EGFP-positive cell fraction as reflecting impaired expression efficiency of these mutants, potentially arising from altered transcriptional output, mRNA stability, or protein stability. We have revised the manuscript text to clarify this distinction and to avoid overinterpreting the underlying mechanism in the absence of direct measurements.

Author response image 1.

EGFP, EGFP–MORC2 (FL), EGFP–MORC2 (ΔCC3), and EGFP–MORC2 (ΔIDR) were re-expressed in MORC2-knockout HeLa cells. Confocal imaging revealed that full-length MORC2 formed condensates in the nucleus, whereas mutants lacking either the CC3 or IDR domain failed to exhibit such behavior. Notably, under identical experimental conditions, we observed a marked reduction in the transfection efficiency of the EGFP-MORC2 (ΔIDR) construct. In contrast to the other variants, EGFP signals for ΔIDR were detectable in only a small fraction of the total cell population, despite consistent DNA loading and protocol synchronization. This observation suggests that the IDR might be required not only for biomolecular condensation but also for maintaining the steady-state levels of the MORC2 mRNA/protein or overall cellular fitness.

(16) Line 330: 'MORC2 deltaCC3 failed to repress any of the 18 downregulated targets...'. This does not appear to be entirely true as repression of some targets (LBH, TGFB2, GADD45A) are closer to MORC2 FL than the EGFP control.

We thank the reviewer for pointing out this inconsistency and for highlighting the need for precise wording. We have updated the dataset and revised the text to describe the results more accurately. We now describe that the mutants impair MORC2FL-mediated transcriptional regulation, consistent with the overall trend observed across these target genes.

(17) Line 347-350: Based on the percent of cells with condensates, the authors conclude that CMT2Z-linked E236G and SMA-linked T424R mutants promote MORC2 phase separation. Again, the effect of these mutations on MORC2 condensation in cells may be direct or indirect. This can be investigated by comparing the in vitro effect of these mutations on MORC2 phase separation.

We thank the reviewer for raising this important point and fully agree that the effects of disease-associated MORC2 mutations on condensate formation in cells may arise from either direct alteration in intrinsic phase separation propensity or indirect influences mediated by the cellular environment.

In our study, disease-associated MORC2 mutants were assessed for condensate formation in HEK293F cells. Attempts were made to characterize these mutants in vitro; however, the E236G mutant exhibited markedly reduced solubility and stability upon purification, which precluded reliable in vitro phase separation analysis. We therefore evaluated the impact of E236G in cells and found that this mutation significantly impaired the dynamics of nuclear MORC2 condensates. For the T424R mutant, we note that its intracellular condensates displayed FRAP recovery kinetics comparable to those of WT MORC2, suggesting broadly similar dynamic properties of the assemblies formed in cells, but not necessarily implying a direct enhancement of intrinsic phase separation.

In light of these considerations, we have revised the text in Lines 347–350 to avoid attributing a direct causal role of these mutations in promoting MORC2 phase separation. Instead, we now describe the observed increase in the fraction of cells containing condensates as a descriptive cellular correlation. We further emphasize that systematic in vitro characterization of disease-associated MORC2 mutants will be required to distinguish direct from indirect effects and represents an important direction for future investigation.

(18) The discussion section lacks referencing to individual figures in the results section as well as previous literature.

We agree with the reviewer that the Discussion would benefit from clearer integration with both the Results figures and prior literature. In the revised manuscript, we have substantially restructured the Discussion to explicitly reference key figures when interpreting experimental findings and to more clearly distinguish conclusions drawn from specific datasets. In addition, we have expanded citations to previous studies where relevant, particularly in the context of MORC2 DNA binding, ATPase regulation, chromatin association, and disease-linked mutations. These revisions aim to better situate our findings within the existing literature and to guide readers more clearly between experimental observations and their interpretation.

Reviewer #3 (Public review):

Summary:

The manuscript by Zhang et al. demonstrates that MORC2 undergoes liquid-liquid phase separation (LLPS) to form nuclear condensates critical for transcriptional repression. Using a combination of in vitro LLPS assays, cellular studies, NMR spectroscopy, and crystallography, the authors show that a dimeric scaffold formed by CC3 drives phase separation, while multivalent interactions between an intrinsically disordered region (IDR) and a newly defined IDR-binding domain (IBD) further promote condensate formation. Notably, LLPS enhances MORC2 ATPase activity in a DNA-dependent manner and contributes to transcriptional regulation, establishing a functional link between phase separation, DNA binding, and transcriptional control. Overall, the manuscript is well-organized and logically structured, offering mechanistic insights into MORC2 function, and most conclusions are supported by the presented data. Nevertheless, some of the claims are not sufficiently supported by the current data and would benefit from additional evidence to strengthen the conclusions.

Thank you for your insightful review and constructive suggestions, which have been invaluable in refining our manuscript.

The following suggestions may help strengthen the manuscript:

Major comments:

(1) The central model proposes that multivalent interactions between the IDR and IBD promote MORC2 LLPS. However, the characterization of these interactions is currently limited. It is recommended that the authors perform more systematic analyses to investigate the contribution of these interactions to LLPS, for example, by in vitro assays assessing how the IDR or IBD individually influence MORC2 phase separation.

We appreciate the reviewer’s insightful comment regarding the characterization of IDR–IBD interactions. In this study, we combined NMR spectroscopy, domain deletion analysis (in vivo), and in vitro phase separation assays to demonstrate that interactions between the IDR and IBD contribute to MORC2 condensate formation. To systematically assess the individual contributions of the IDR and IBD to MORC2 phase separation, we performed in vitro reconstitution assays using purified domain constructs (Fig. S6). Neither the isolated IDR nor the IBD alone exhibited phase separation under buffer conditions approximating the physiological environment, indicating that each domain is individually insufficient to drive condensation. Upon the addition of 10% PEG8000, phase separation was selectively observed for the IDR but not for the IBD, suggesting that the IDR possesses an intrinsic propensity for phase separation that can be enhanced by crowding molecular. Importantly, when the IDR and IBD were mixed, phase separation was robustly induced, supporting a model in which cooperative inter-domain interactions between the IDR and IBD promote MORC2 condensation. In the absence of PEG, no phase separation was observed for the IDR–IBD mixture. These observations imply that IDR–IBD interactions cannot drive phase separation on their own, but require cooperation with CC3-mediated dimerization to achieve this process, which is the central point we wish to emphasize.

(2) The authors mention that DNA binding can promote MORC2 LLPS. It is recommended that they generate a phase diagram to systematically assess how DNA influences phase separation.

We agree that constructing a full phase diagram would provide a more systematic evaluation of the effect of DNA on MORC2 phase separation. In the current study, we assessed DNA-dependent condensation across multiple protein and DNA concentrations, which consistently showed that DNA enhances MORC2 phase separation. At low protein concentration (0.5 µM), phase separation requires sufficient DNA, whereas increasing either DNA or protein concentration promotes liquid droplet formation. At high DNA and protein concentrations, amorphous structures dominate, indicating a transition away from dynamic assemblies. We have clarified this point in the Results and Discussion sections and now note that a comprehensive phase diagram analysis represents an important direction for future work.

(3) The authors use the N39A mutant as a negative control to study the effect of DNA binding on ATP hydrolysis. Given that N39A is defective in DNA binding, it could also be employed to directly test whether DNA binding influences MORC2 phase separation.

We thank you for your constructive suggestions. The purified wild-type MORC2(1–603) exhibited weak but detectable ATPase activity, whereas the N39A mutant was completely inactive [5]. Based on this characteristic, the N39A mutant was used as a negative control for the ATP-binding-deficient mutant in this study [3]. However, no evidence has been provided to demonstrate that the N39A mutant is defective in DNA binding. Importantly, both our results and previous studies [5-6] indicate that MORC2 engages DNA via multiple domains, suggesting that a single-point mutation is unlikely to significantly compromise its overall DNA-binding capacity.

(4) Many of the cellular and in vitro LLPS experiments employ EGFP fusions. The authors should evaluate whether the EGFP tag influences MORC2 phase separation behavior.

We appreciate the reviewer’s concern regarding the potential influence of the EGFP tag. The use of EGFP fusions in our study was primarily to maintain consistency with the in-cell experiments. Importantly, we confirmed that EGFP alone does not undergo phase separation in cells, and this observation is consistent with previous studies [7]. Additionally, in vitro phase separation of MORC2 was independently validated using Cy3–labeled CTD (Fig. S5), which recapitulated the condensate formation seen with EGFP-fused protein. Together, these results indicate that the EGFP tag does not significantly influence MORC2 phase separation, supporting the validity of our conclusions.

Reviewer #3 (Recommendations for the authors):

(1) The authors claim to have obtained nucleic acid-free protein, but no data are provided to support this assertion. It is recommended that they include appropriate validation to confirm the absence of nucleic acids.

We thank the reviewer for highlighting this point. To validate that the purified MORC2 protein is indeed free of nucleic acid contamination, we have additional experimental evidence (e.g., A260/280 measurements, agarose gel analysis, or EMSA in Fig. 5), which has been added to the Methods section and Table S2.

Note: Agarose gel analysis for MORC2 constructs to confirm the absence of nucleic acids. The pET32 vector as the positive control, the protein preparation for analysis is 0.05 mg. E means E. coli and H means HEK293F.

(2) The FRAP recovery curves are not normalized to 0, making comparison difficult. The authors should normalize the post-bleach intensity to 0 and re-plot the curves to allow a more standard interpretation of mobile fractions.

We agree with the reviewer and have now normalized the FRAP recovery curves by setting the post-bleach intensity to 0. The revised plots are presented in the Figures (2f, j, l; 6c, 7f), allowing for more direct comparison of mobile fractions across different conditions.

(3) The HSQC spectra for IBD appear inconsistent: the peak positions in Fig. 4C do not align with those shown in panels D-F. The authors should verify the spectral assignments and ensure consistency across figures.

We thank the reviewer for pointing this out. The apparent inconsistency arose from the fact that different spectral regions were displayed in Fig. 4c versus Fig. 4d-f for visualization purposes, which may have given the impression of mismatched peak positions. The spectral assignments themselves are consistent across all panels.

To avoid confusion, we have now adjusted the spectral window shown in Fig. 4c to match that used in Fig. 4d-f. The revised figure ensures consistent presentation of the same spectral region across all panels.

Reference:

(1) Zhang, Y., Stöppelkamp, I., Fernandez-Pernas, P. et al. Probing condensate microenvironments with a micropeptide killswitch. Nature 643, 1107–1116 (2025).

(2) Fendler NL, Ly J, Welp L, et al. Identification and characterization of a human MORC2 DNA binding region that is required for gene silencing. Nucleic Acids Res.53(4):gkae1273 (2025).

(3) Tchasovnikarova, I., Timms, R., Douse, C. et al. Hyperactivation of HUSH complex function by Charcot–Marie–Tooth disease mutation in MORC2. Nat Genet 49, 1035–1044 (2017).

(4) Douse, C. H. et al. Neuropathic MORC2 mutations perturb GHKL ATPase dimerization dynamics and epigenetic silencing by multiple structural mechanisms. Nat Commun 9, 651 (2018).

(5) Tan, W., Park, J., Venugopal, H. et al. MORC2 is a phosphorylation-dependent DNA compaction machine. Nat Commun 16, 5606 (2025).

(6) Sánchez-Solana B, Li DQ, Kumar R. Cytosolic functions of MORC2 in lipogenesis and adipogenesis. Biochim Biophys Acta. 1843(2):316-326 (2014).

(7) Li, C.H., Coffey, E.L., Dall’Agnese, A. et al. MeCP2 links heterochromatin condensates and neurodevelopmental disease. Nature 586, 440–444 (2020).

💻/thinkpad/🧊/me/📓/2026/04/28

personal.web.archiv-hypothes.is~faceted.search-gyuri-open+interoperable

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giag039), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 2:

General Comments This manuscript introduces a tool named HVRLocator, designed to address the issue of missing or non-standard metadata in 16S rRNA sequencing data found in public databases such as the SRA. The tool identifies amplicon regions by aligning sequences to a reference genome and attempts to detect the presence of primers using a machine learning model. This is a subject with significant practical value, particularly for conducting large-scale meta-analyses. However, there are still many issues regarding methodological rigor, the depth of validation, and comparisons with existing tools that require further clarification by the authors. Major Comments 1. Concerns regarding the singularity of the reference sequence The authors mention aligning sequences to a single Escherichia coli (J01859.1) reference genome to determine start and end positions. Is a single E. coli reference sufficient to cover Archaea or bacterial phyla that are distantly related to Proteobacteria, which may be present in environmental samples (e.g., soil, ocean)? For taxa with significant length variations or insertions/deletions (Indels), could forced alignment to the E. coli reference lead to misjudgment of start/end positions? Have the authors evaluated the impact on accuracy if a more universal reference database (such as representative sequences from SILVA or Greengenes) were used? 2. Rationality of the primer detection model (Random Forest based on Quality Scores) The authors developed a Random Forest model to predict primer presence by analyzing the quality score distribution of the first 1,000 reads. Primer detection is typically based on the sequence itself rather than quality scores. Can the authors explain why quality scores were chosen as features? Sequencing quality scores are influenced by technical factors such as sequencer status, reagent batches, and run cycles, which have no direct biological correlation with the presence of primers. Is there a risk that this model is "overfitting" specific sequencing platforms or datasets? Since the reads are already downloaded, why not directly use degenerate primer sequence matching (e.g., using Cutadapt or SeqKit logic) to determine primer presence? This seems to be a more direct and accurate method. 3. Verification of accuracy claims In the validation section, the authors claim to achieve 100% accuracy on certain datasets. In bioinformatics tool development, a claim of 100% accuracy is often a red flag. Have the authors manually checked those samples marked as "correct" by the model that might suffer from edge effects or borderline cases? 4. Dataset imbalance in the Random Forest model For the Random Forest model, the authors used 882 samples with primers and 8,940 samples without primers for training. Such an extremely imbalanced dataset, even with stratified sampling, may cause the model to be biased towards the majority class. 5. Comparison with existing tools The manuscript mentions that no tool has been designed for this specific purpose, but this may overlook some existing general-purpose tools or scripts. Many pipelines (such as certain plugins in QIIME 2, USEARCH, etc.) possess functionalities to identify primers or evaluate amplicon regions. The authors should discuss how their tool compares to these existing workflows. Minor Comments 1. Confusion regarding processing speed metrics The abstract mentions a processing speed of "0.147 samples per minute", but later the text mentions "6.5 samples per minute" and "one sample every 0.147 minutes". There is confusion regarding units and values in these three descriptions (is it samples per minute or minutes per sample?). Please unify and correct these data to ensure consistency. 2. Usage of fastq-dump The use of fastq-dump is mentioned. The SRA Toolkit's fastq-dump is relatively slow and has largely been superseded by fasterq-dump for efficiency. Why did the authors not use the more efficient fasterq-dump? 3. Definition of "Standardized metadata" The term "standardized metadata" is used frequently. Please explicitly define what constitutes "standard" metadata in the context of this tool within the text. 4. Robustness and error handling The results section mentions that some samples failed due to "NCBI portal-related issues". Does this imply the tool lacks breakpoint resumption or retry mechanisms? Given that network fluctuations are common during large-scale downloads, how is the tool's robustness demonstrated? 5. Output confidence intervals The output file contains "TRUE/FALSE" and a probability score. For samples where the probability score is at a critical threshold (e.g., around 0.5), does the tool provide an "uncertain" tag, or does it force a classification? It is suggested to add an indicator for ambiguous ranges.

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giag040), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 2:

General Comments This manuscript introduces a tool named HVRLocator, designed to address the issue of missing or non-standard metadata in 16S rRNA sequencing data found in public databases such as the SRA. The tool identifies amplicon regions by aligning sequences to a reference genome and attempts to detect the presence of primers using a machine learning model. This is a subject with significant practical value, particularly for conducting large-scale meta-analyses. However, there are still many issues regarding methodological rigor, the depth of validation, and comparisons with existing tools that require further clarification by the authors. Major Comments 1. Concerns regarding the singularity of the reference sequence The authors mention aligning sequences to a single Escherichia coli (J01859.1) reference genome to determine start and end positions. Is a single E. coli reference sufficient to cover Archaea or bacterial phyla that are distantly related to Proteobacteria, which may be present in environmental samples (e.g., soil, ocean)? For taxa with significant length variations or insertions/deletions (Indels), could forced alignment to the E. coli reference lead to misjudgment of start/end positions? Have the authors evaluated the impact on accuracy if a more universal reference database (such as representative sequences from SILVA or Greengenes) were used? 2. Rationality of the primer detection model (Random Forest based on Quality Scores) The authors developed a Random Forest model to predict primer presence by analyzing the quality score distribution of the first 1,000 reads. Primer detection is typically based on the sequence itself rather than quality scores. Can the authors explain why quality scores were chosen as features? Sequencing quality scores are influenced by technical factors such as sequencer status, reagent batches, and run cycles, which have no direct biological correlation with the presence of primers. Is there a risk that this model is "overfitting" specific sequencing platforms or datasets? Since the reads are already downloaded, why not directly use degenerate primer sequence matching (e.g., using Cutadapt or SeqKit logic) to determine primer presence? This seems to be a more direct and accurate method. 3. Verification of accuracy claims In the validation section, the authors claim to achieve 100% accuracy on certain datasets. In bioinformatics tool development, a claim of 100% accuracy is often a red flag. Have the authors manually checked those samples marked as "correct" by the model that might suffer from edge effects or borderline cases? 4. Dataset imbalance in the Random Forest model For the Random Forest model, the authors used 882 samples with primers and 8,940 samples without primers for training. Such an extremely imbalanced dataset, even with stratified sampling, may cause the model to be biased towards the majority class. 5. Comparison with existing tools The manuscript mentions that no tool has been designed for this specific purpose, but this may overlook some existing general-purpose tools or scripts. Many pipelines (such as certain plugins in QIIME 2, USEARCH, etc.) possess functionalities to identify primers or evaluate amplicon regions. The authors should discuss how their tool compares to these existing workflows. Minor Comments 1. Confusion regarding processing speed metrics The abstract mentions a processing speed of "0.147 samples per minute", but later the text mentions "6.5 samples per minute" and "one sample every 0.147 minutes". There is confusion regarding units and values in these three descriptions (is it samples per minute or minutes per sample?). Please unify and correct these data to ensure consistency. 2. Usage of fastq-dump The use of fastq-dump is mentioned. The SRA Toolkit's fastq-dump is relatively slow and has largely been superseded by fasterq-dump for efficiency. Why did the authors not use the more efficient fasterq-dump? 3. Definition of "Standardized metadata" The term "standardized metadata" is used frequently. Please explicitly define what constitutes "standard" metadata in the context of this tool within the text. 4. Robustness and error handling The results section mentions that some samples failed due to "NCBI portal-related issues". Does this imply the tool lacks breakpoint resumption or retry mechanisms? Given that network fluctuations are common during large-scale downloads, how is the tool's robustness demonstrated? 5. Output confidence intervals The output file contains "TRUE/FALSE" and a probability score. For samples where the probability score is at a critical threshold (e.g., around 0.5), does the tool provide an "uncertain" tag, or does it force a classification? It is suggested to add an indicator for ambiguous ranges.

DOI: 10.1111/bph.70443

Resource: RRID:AB_3720449

Curator: @scibot

SciCrunch record: RRID:AB_3720449

What is this?

On 2026-04-09 21:38:21, user Alizée Malnoë wrote:

The manuscript by Fridman et al. explores the unexpected finding that Aeromonas jandaei antagonistically employs a Type VI secretion system (T6SS) in a liquid environment. While researching the effector protein Awe1, which forms part of the T6SS apparatus, the authors observed T6SS-dependent intoxication of susceptible bacteria. Using a novel fluorescence-based screening method (named LiQuoR for liquid quantification of rivalry), the authors further determine that this intoxication is contact-dependent, and that contact between kin and non-kin Aeromonas bacteria in liquid is mediated by specific adhesins. Fridman et al. also identify additional marine bacteria capable of inflicting T6SS-mediated intoxication in liquid media, suggesting a mechanism for specific and contact-dependent bacterial competition and positing that such competition in liquid media may be more common in marine bacteria than previously documented. These findings have exciting implications for bacterial antagonism, potentially shifting the paradigm of how we view bacterial interactions in marine environments. We found this study to be well-written, containing high-quality data. Overall, the data presented in this manuscript are done well and support the claims made by the authors. We outline some major and minor adjustments aimed at aiding the clarity of reporting and presentation, strengthening the findings, as well as providing additional context for a broader audience.

Major Comments<br /> - We are interested in the broader implications of the LiQuoR assay, particularly pertaining to this workflow’s application to different bacteria. The observation that the amount of prey luminescence in WT on solid media grew/increased after 4 h seemed counterintuitive to us (Figure 1E). It seems as if this result could make the workflow less sensitive for experiments done solely on solid media, further explanation of this finding would clarify on the workflows applicability to other solid surface experiments. Is this related to surface area? While this does not change the findings that inhibition is occurring in both liquid and in solid, it would enhance the clarity of these results to provide speculation on why this was seen.<br /> - We are curious about your perspective on the observation that kin-kin aggregation facilitated by CaCl2 supplementation does not increase kin intoxication but does increase non-kin intoxication (Figure 2A). Please speculate on this result in the discussion. Is the concentration used physiological? <br /> - While the images shown in Figure 2B make it clear that aggregates are forming in liquid media, we have a suggestion to improve the strength of these results and account for the images not shown. For instance, quantification of the % of prey cells displaying Sytox staining would more strongly demonstrate the presence of permeabilized E. coli in multiple aggregates. This quantification could substitute Figure 2C (which can be moved into the supplemental): it was not totally clear to us why an orthogonal view was included here. If this is significant for the findings, it would increase clarity to include an explanation for an audience less familiar with this system.<br /> -Lines 192-214: From a genomics perspective, we think further explaining how potential adhesins were identified would be helpful to increase the clarity and reproducibility of the experimental design. Please explain how you narrowed down these adhesins and located them in the genome, and why adhesins were targeted for this analysis over other proteins that could facilitate a physical interaction between predator and prey species. Define the acronyms and provide rationale for naming. <br /> -Figure 6B nicely demonstrates that intoxication takes place in liquid between certain marine bacteria but not in Vpara. However, please include a control showing that V. para does intoxicate prey in solid media to strengthen these findings and confirm that this strain of V. para is capable of intoxicating prey under typical conditions.<br /> -Given the significance of the TssB deletion for the core message of this work that type VI intoxication occurs in liquid media, please consider including data that confirm the TssB deletion e.g. sanger sequencing in supplemental or as source data. A complementation assay of TssB to show that regaining TssB restores the awe1 toxicity would be valuable.<br /> - Lines 224-225/Figure 5: We are curious and excited about the implications of the balance between kin-aggregation and non-kin aggregation and how this may aid our understanding of bacterial interactions in marine environments. Based on our understanding of these results, the observation that deletion of CraAj (responsible for kin-kin aggregation) increased non-kin intoxication (mediated by LapAj) could suggest that aggregation between two kin cells, who both contain the needed immunity proteins, could dampen the intoxication of nearby non-kin cells. This result is implied by the data but not specifically speculated on or addressed. Though it may not be within the scope of this experimental design, our group was intrigued by these findings. Given your expertise in this area, consider discussing how these bacterial interactions may play out and/or include these observations as part of Figure 5.

Minor Comments<br /> -All figures: In the legends, it is stated “these experiments were repeated three times with similar results”. Please define what is meant by an experiment e.g. technical or biological replicate.<br /> -All figures: We felt that having the exact p-values indicating statistical significance is not necessary. For instance, in Figure 3B and 3D, we found it distracting that all of the values were significant by a factor of <1E-4, even when they appear different from each other. If this is simply a cutoff value, it would be helpful to keep that consistent between figures. Also, Figure 6A/B: The p-values presented, specifically the comparison between WT and T6SS – supplemented with 1 mM CaCl2 (6A) and the two left hand panels of 6B, do not appear to match the differences shown between the experimental groups. By eye, these groups do not appear different from one another but are shown to be either highly statistically significant or not statistically significant at all.<br /> - Figure 1A: To increase readability, we suggest that the colors could be more intuitive here- put WT in grey and then mix colors for double mutants. Bringing the light pink line (Δawei1 ΔtssB + pAwe1) to the front of the graph would further increase clarity.<br /> -Figure 1B/F: Making color scheme consistent between 1B and 1F would increase clarity.<br /> -LiQuoR assay: As there is often some level of variation in expression levels when working with a transformed population, confirmation that all prey strains luminesce to a similar level would provide further validation of this novel assay (similarly to what is done in FigS3B). <br /> -Figure 2A: The colored box legends showing whether CaCl2 is present or absent are inverted relative to one another, which we found to be confusing. To increase readability, please make them on the same side.<br /> -Figure 3B,C,D,E: To help guide the eye on the graphs, we suggest adding dashed lines between each new mutation group (+/- TssB).<br /> - Figure S1: Please include a loading control to verify assay input. <br /> - Table S1: Clarify the gene and strain for each mutation.<br /> - Line 112-113: It serves as an excellent control that the action of the T6SS apparatus is required for intoxication, however, since the T6SS apparatus is contained within the bacterium, would spent media contain free-floating T6SS proteins, or are these proteins only ejected from the bacterium in the presence of prey species? Please clarify. Direct evidence, such as immunoblotting, that effectors are present in the spent media from WT would make this claim more compelling.<br /> - Line 35: While this part of the introduction provides excellent background regarding the role of T6SS in interactions with eukaryotic cells, it would be helpful to also specifically mention the role of T6SS in prokaryotic communities, as much of the later work focuses on competition between bacteria.<br /> -Lines 70-71: A more thorough background on Aeromonas (lifestyle, importance, etc) is warranted.<br /> -Line 84: Please provide the exact genotype when first introducing this mutant, it would improve clarity for the reader to explicitly state that this is a double mutant.<br /> -Line 97: Clarify here that “Aj prey” in this paragraph refers to Aj which do not possess the cognate immunity protein, as the current phrasing could be interpreted to mean “prey of Aj”.<br /> -Line 138: “Desired conditions for competition” is vague. Is solid media also incubated with shaking or is it static?<br /> -Lines 156-157: The statement that all three effectors are injected into prey cells is broad and not necessarily supported within these findings. The injection of one effector could be favored, but other effectors could compensate in its absence.<br /> -Line 189: Describes Aj as stably binding to other competing bacteria. To this point, imaged aggregates have been fixed so stability of aggregates may not be known.<br /> -Line 248: Here, it is mentioned that there was a switch from using the Lux operon to using the RFP mCherry for improved cell detection. It might be helpful to clarify which fluorescent tag was used for each assay, as multiple different fluorescent tags are used.<br /> -Line 317: As the choice to test CaCl2 and the biological relevance of calcium for Aeromonas hosts is explained earlier in the manuscript, it would be interesting to include a brief explanation about the choice to include sodium chloride when assessing Vibrio intoxication rates. Presumably, sodium chloride was picked because Vibrio is commonly found in brackish water, but someone from outside the field may not be familiar with this biology. Additionally, since Aeromonas can be found in both fresh and brackish water, an interesting follow-up experiment would be to test the Aeromonas strains under different salinities.<br /> -Line 375-377: Needs citation.<br /> -Line 385: Clarify “under specific conditions not addressed within the scope of this study”.

Carter Collins and Lily Pumphrey (Indiana University Bloomington) - not prompted by a journal; this review was written within a Peer Review in Life Sciences graduate course led by Alizée Malnoë with input from group discussion including Camy Guenther, Josy Joseph and Tahreem Zaheer. We are part of the Dept. of Biology where Julia Van Kessel’s group is located, Julia is a collaborator of the corresponding author and did not influence the choice of this preprint for our class.

On 2026-04-07 08:39:09, user Guest wrote:

I must confess, on first reading I found the manuscript quite exciting, but having gone through the earlier comments, I now see rather more clearly the gulf between what the data actually show and what the authors claim.

One thing I would add to what has already been said: there is, quite remarkably, no protein localisation of KCNT1: not by GFP tag, not by antibody, in the multiciliated epidermis of Xenopus, mouse, or indeed human tissue. That is a rather glaring omission, to put it mildly. I would also agree that the proposed connection between KCNT1 and Piezo is tenuous at best.

On 2025-11-19 21:19:50, user Daniel Vásquez-Restrepo wrote:

This preprint already received a “major revision” decision. Unfortunately, the original reviewers were not available to evaluate it again, and the process stalled. Despite sending 15 additional peer-review invitations, no one agreed to take it on. Although the manuscript has now entered a new review process, I am attaching the previous reviewers’ comments.

Reviewer 1

This isn’t a finding as not only is it already available information, the use of the available IUCN maps and statuses was part of the methodology.

R/ We rephrased the sentence to clarify that it refers to the underlying data itself and not to our results.

I like the approach they’ve taken, but none of this is novel information or unexpected.

R/ Although it is well known that mountains promote diversity and endemism at a global macroevolutionary scale, this information has not been explicitly tested in Colombian squamates in conjunction with threat categories. We consider that clearly stating the result of hotspots of diversity and endemism in Colombian squamates can help local environmental policies. Therefore, while our results are consistent with theoretical expectations, this alignment does not diminish the novelty of our findings, as we provide the first quantitative analysis supporting these patterns in the local context.

This is the main novel finding of the work and I’d recommend reorganising the text to stress this.

R/ We modified several sections of the text to emphasize the finding highlighted by the reviewer, also in accordance with comments made by the other reviewer.

Unclear what this means in the context of this paper.<br /> R/ We rephrased the section for clarity.

This is just the existing EDGE list, so I’m not sure it warrants mentioning as an output here.

R/ In accordance with a comment from Reviewer 2, we acknowledge that this is a local rather than a global list, and that species rankings may differ between the two. Therefore, we believe it is an output worth highlighting. Nevertheless, we have clarified in the text the differences between the local and global scores and their implications.

This entire paragraph seems superfluous, and this work has nothing to do with the latitudinal gradient so it’s a strange thing to focus discussion on.

R/ While we briefly mention the latitudinal gradient, the main purpose of this introductory paragraph is to provide general context on biodiversity, leading into the key argument of the subsequent sections: the need to understand biodiversity and extinction risk as multidimensional phenomena. We have made minor adjustments to better integrate the role of the latitudinal gradient in promoting tropical diversity, thereby reinforcing the importance of prioritizing conservation efforts in regions of exceptionally high biodiversity.

Suggested added context as this was unclear as worded.

R/ We accepted the reviewer’s suggestion and revised the text accordingly.

I’m not sure this follows - more that, as the paragraph goes onto say, it results in a lack of understanding of the impacts and vulnerability of the species.

R/ We rephrased the idea to make it clearer.

This seems to be an inappropriate reference, as Paez et al. 2006 focused on turtles rather than squamates. Please check and reword as needed.

R/ We double-checked the reference and confirmed that it is correct, as it covers not only turtles but all Colombian reptiles (including squamates, crocodiles, and turtles).

This seems inconsistent with the earlier statement that “a local assessment is lacking” - should this rather say a recent local assessment? Though as the paper goes on to reference a 2015 ‘local assessment’, it’s unclear what this section means.

R/ We agree with the reviewer and revised the text to clarify that we refer to a recent assessment that also considers different facets of biodiversity, not just species richness (i.e., taxonomic diversity).

The figure given later is 597, and that was used as the basis for the analysis. This may be a discrepancy due to a later update, but the same Reptile Database update should be cited throughout the paper for consistency.<br /> R/ In the Introduction, we refer to the most recent estimate of 620 reptile species for Colombia, based on the latest update of the Reptile Database (2024). However, the analyses in this study were based on the 2023 version of the database, which listed 597 species at that time. Given that the analyses were conducted using the 2023 data, and a complete reanalysis would be required to incorporate the updated figures, we chose to retain the original dataset to ensure consistency and reproducibility. We have clarified this point in the text to avoid confusion.

Better to use the term ‘squamates’ rather than ‘reptiles’ if crocs and turtles are to be excluded.

R/ Done, we have consistently replaced "reptiles" with "squamates" throughout the text where appropriate.

Once again, this could benefit from clarity. The data in the Reptile Database should be reviewed with reference to available material and literature to be used as a formal checklist, but it should be ‘complete’ - it’s more likely to erroneously list species from a country than to miss ones that actually occur there.

R/ We agree with the reviewer and rephrased the sentence to make the idea clearer.

Are the authors able to explain the discrepancy between this figure and the maps (which represented 81% of the dataset)? Most IUCN assessments will have maps, but no IUCN maps will be associated with species that don’t have assessments.

R/ The figures were validated against the information provided in Table S1. As the reviewer correctly points out, there are more assessments than polygons, consistent with the supplementary material. The figure of 77% corresponds to 461 species (excluding DD and NE categories) out of 597 species in our dataset (461/597 = 0.77). Meanwhile, the figure of 81% refers to 481 species with available geographic information, including species categorized as DD (481/597 = 0.81). The discrepancy arises because DD species were included when considering geographic data but excluded from threat category analyses. We have revised the Methods and Results sections to clarify this distinction explicitly. Also, we updated the previous 77% figure to include DD species too, increasing it to 92%.

This is not a sufficient way to evaluate whether the assessments are likely to need updating - the Criteria take account of the distribution and extent of threats to each species, not simply its distribution. The ‘needs update’ tag is applied by the Red List only to assessments more than 10 years old, which is all that should be mentioned here.

R/ We understand the reviewer’s concern and acknowledge that a mismatch between EOO and threat classification is not sufficient by itself to determine if an update is needed. We have separated these ideas in the text: first, we highlight species whose assessments are formally tagged as “needs update” after 10 years; second, we discuss species whose EOO does not align with their current threat classification. We moved the second point to the 3.2 Geographic patterns section, and expanded the Discussion to better explain these observations.

See above. The authors didn’t ‘show’ this, they interpreted the Criteria incorrectly.

R/ See previous answer. We further expanded the Discussion section to better frame this point.

I would consider it suitable for the manuscript to be more fully revised as a shorter paper, as the region-scale analysis within Colombia and the phylogenetic results are of more interest than the well-trodden path of identifying the Andes as an area of greater endemism than Amazonia and the additional analyses included in the paper render its main findings somewhat opaque in places.

R/ We consider that highlighting the Andes as an area of high endemism is necessary to provide context for interpreting the patterns of phylogenetic diversity. While it may be a well-known topic, not all readers will have the same background. Although the manuscript is extensive because it covers taxonomic, geographic, and phylogenetic patterns, its current length (ca. 6,300 words, excluding references) is well within the 9,000-word limit for Original Research articles in Biodiversity and Conservation and only slightly above the typical 5,000-word range. Nevertheless, we made an effort to shorten unnecessary sections to improve focus and clarity. For example, we removed some analysis related to diversification rates and extinction risk, since as the Reviewer 2 pointed out, some metrics depending on branch lengths may be biased.<br /> <br /> Reviewer 2

L393-405: it is important to acknowledge the phylogenetic incompleteness of a national-level analysis, and how that might be affecting these results – divergence times are influenced by phylogenetic coverage and structure, removing >90% of squamate species from the phylogeny will give you divergence times between Colombian species, not true lineage age/divergence time information. This could be addressed with sensitivity analyses to explore how lineage age varies between pruned and complete trees, or with stronger discussion of the pitfalls of this approach in the methods and discussion, with clearer wording in the results.

R/ We appreciate the reviewer’s insightful comment and fully agree. We performed additional calculations to assess sensitivity, and indeed, the age of some lineages can be severely affected, while others remain largely unchanged. Following the reviewer’s recommendation, we revised the Methods and Discussion sections to place greater emphasis on the limitations of using evolutionary metrics derived from pruned trees and on the considerations needed when interpreting these results. As the reviewer also notes, these results are not necessarily incorrect, since global conservation priorities do not always align with local ones. Additionally, we introduced local and global subscripts to our metrics to explicitly distinguish between them.

407-418: Distinction is needed between EDGE scores and national EDGE scores (literally just saying ‘national EDGE scores’ would suffice). It may also be useful to identify national-specific priorities – i.e. high ranking national EDGE species that are not highly ranked in global context. There are EDGE scores available for all vertebrates at the global level here ( https://www.nature.com/articles/s41467-024-45119-z) . There are endemic Colombian squamates that are high EDGE in this study and also high EDGE at the global scale (e.g. Lepidoblepharis miyatai) but also species that are high EDGE nationally because of the phylogenetic diversity they are solely responsible for in Colombia, but the responsibility for which is shared beyond Colombia’s borders. These key cases can be instrumental in ensuring species that are globally ‘safe’ but locally important do not fall through the cracks.

R/ Please refer to the previous response. We now explicitly distinguish between national EDGE scores and global EDGE scores throughout the text and highlight cases where species are locally important but not necessarily globally prioritized.

L41 and throughout: “threatenedness” = “extinction risk” or “level of threat”.

R/ Done.

Throughout: It’s the IUCN Red List, not IUCN, particularly when referring to versions of the Red List database.

R/ Done.

L145: make it clear you’re referring to national endemics.

R/ The Resolución 0126/2024 from Colombia’s Ministry of Environment (MADS) covers not only national endemics but all species occurring within the country’s administrative boundaries.

L167: ensure it’s clear that its imputation based on taxonomy alone.

R/ Done.

L182: check references.

R/ We reviewed the references cited at this point and confirm they are correct.

L222-224 and throughout: phylogenetic diversity == Faith’s PD – the other measures are indices of phylogenetic distance/relatedness that are calculated in same units as PD, but are not phylogenetic diversity – that should be clarified.

R/ Done. We clarified that Faith’s PD refers specifically to phylogenetic diversity, while the other metrics represent measures of phylogenetic relatedness or distance.

L393: extinction risk should not be though of as a trait evolving but as the manifestation of extrinsic and intrinsic factors.

R/ Agreed. We rewrote the sentence.<br /> L393-397: unclear what the relationships discussed are, and what they infer.

R/ We have removed this section from both the Methods and Results. Given that the correlations discussed involved metrics dependent on branch length — and, as the reviewer previously pointed out, branch lengths can be affected by pruning the phylogenetic trees — we decided to eliminate this section. Overall, it did not substantially contribute to the text or to the discussion.

L428-429: This is higher than, or at least comparable to, the global % of DD/NE squamates I think, so might not be considered relatively low for squamates.

R/ We rewrote the sentence to clarify that it is comparable to or higher than the global percentage, as the reviewer correctly pointed out.

L429-432: it might be worth highlighting how taxonomists and others can contribute to rapid reassessment of species with basic information in ecological publications see: https://doi.org/10.1016/j.biocon.2018.01.022

R/ Done. We incorporated the reviewer’s suggestion.

L442-444: Unclear what is meant here? A species can be assessed as CR with a wide range if its under population decline criteria, and a small-ranged species can be assessed as not-threatened if there is no evidence of decline/ongoing degradation.

R/ This comment was also raised by Reviewer 1. We addressed it accordingly by revising the text to clarify that species can indeed have wide distributions and still qualify as Critically Endangered if facing significant threats, and vice versa. Please refer to our responses to Reviewer 1.

On 2025-08-27 07:16:38, user YY Xie wrote:

We are thrilled to announce the first release of DeepHalo, a groundbreaking deep learning-integrated workflow for high-throughput discovery of halogenated metabolites from HRMS data!<br /> A user friendly Standalone Executable (for Windows Users) is available at: https://github.com/xieyying/deephalo/releases/tag/DeepHalo_V1.0.0) and https://pan.baidu.com/s/1fzHqWDY6FNK0lzy6AnHoTw?pwd=deep

On 2025-07-23 15:35:02, user Kate Nyhan wrote:

Interesting analysis. <br /> In light of the reliance on MeSH subject indexing, I draw your attention to NLM's own data on the performance of machine indexing approaches in different categories, documented in the NLM Technical Bulletin: https://www.nlm.nih.gov/pubs/techbull/ma24/ma24_mtix.html . The check tag category (which includes the species labels on which the OPA iCite tool relies) F1 score (combining precision and recall) for MTIX (introduced in 2024) was 87% versus the original (human) indexing approach -- that is, significantly lower performance. And for a period of time before the introduction of MTIX, NLM was using a different machine indexing system, MTIA, whose F1 score for the check tag category was only 62% compared with human indexing. So, depending on when MTIA started to be used, and the proportion of records that were indexed with MTIA versus human indexers, I wonder how confident we can be that the relative proportions of different categories of MeSH terms truly reflect the prevalence of different categories of research over time. <br /> I also note, in the same source, that the performance of MTIA and MTIX at appropriately labeling Medline articles with supplementary concept terms was even worse than their performance with check tags: 39% and 71% versus human indexing. Supplementary concept terms are especially relevant to innovative, novel science (including basic science) -- terms that may in the future become MeSH terms. It's perhaps not surprising that tools trained on historical data are not great at handling novel concepts, but poor performance by machine indexing tools at applying appropriate supplementary concept records may be another factor in the apparent decline in basic science research. <br /> I'd also like to comment on the iCite Translation Module (of which the Human/Animal/MCB category assignment is part). I'm not really clear on how many PubMed records get such category labels. On the one hand, iCite includes all PubMed records. On the other hand, presumably only articles with MeSH terms can be assigned in the Triangle of Biomedicine -- that is, articles in journals that are indexed in PMC but not Medline are not included in the human/animal/MCB analysis. I assume that the proportion of PubMed records with Medline indexing has gone down, as NIH-funded authors publish more papers in journals that aren't indexed in Medline (many of which didn't exist at the start of this longitudinal analysis). Indeed, thanks to Ed Sperr's handy tool PubMed-By-Year, we can see that Medline records (ie, records with MeSH terms that can be analyzed by the human/animal/MCB categories in iCite) as a proportion of PubMed records was above 90% until (I am eyeballing the figure at https://esperr.github.io/pubmed-by-year/?q1=medline [sb]&startyear=1990) around 2011, at which point Medline coverage started declining quite precipitously. So, any analysis that relies so heavily on MeSH indexing is going to be leaving out a large number (and an increasing proportion) of recent papers.

On 2025-05-17 03:57:12, user thegradstudent wrote:

Summary<br /> This study introduces a novel computational pipeline for the de novo design of peptides that localize preferentially at the interface of biomolecular condensates. These condensates are membrane-less compartments created by protein and RNA molecules that form ‘dense’ and ‘dilute’ phases. The interface between these phases has been shown to promote the aggregation of the proteins that are part of the condensates and the formation of disease-associated fibrils of hnRPNA1. Previous literature has demonstrated preferential interfacial partitioning of a few proteins, but not of small molecules or peptides.

This technique combines coarse-grained molecular simulations, mixed-integer linear programming (MILP), and machine learning. The authors use this workflow to design peptides that localize at the interface of biological condensates, hnRNPA1, LAX-1, and DDX4, which are formed by intrinsically disordered proteins. They test these designed peptides in vitro and show that they exhibit their intended surfactant-like activities using confocal microscopy. They also identify how the charge of these peptides is a crucial element of their physicochemical features.

Overall, this study successfully shows that these short peptides preferentially distribute between the interface of the biomolecule condensate and the surrounding environment, showing surfactant-like properties. They also show that the net charge and the amino acid composition of these peptides in relation to their biomolecular condensate are crucial to determining whether they will preferentially partition at the interface.

The authors have opened the potential to study more complex condensates using this rigorous strategy. This paper is exceptionally well written and thorough. I recommend this paper for publication with minor revisions.

Major Point<br /> To experimentally validate this computational pipeline, you fluorescently label the selected peptides. This may show my lack of knowledge on this subject, but my one concern is regarding the potential effects of the fluorescent tag on the condensate system. This JBC paper from 2023 shows that fluorescently tagging a protein can promote phase separation , in this paper specifically huntingtin exon-1 with red fluorescent protein ( https://pmc.ncbi.nlm.nih.gov/articles/PMC10825056/ ). So, what is to say that the Cy5- fluorophore isn’t playing a role in creating these surfactant-like properties of the designed peptide?

Minor Points<br /> - Figure 1: Placing the label descriptors of the figure in front of the written text makes it clearer when reading, instead of having them at the end.<br /> - Figure 1C: The grey color used for the box is a little dark, making it slightly hard to read the words and it is very close to the grey coloring within the figure. Maybe switch this box into an outline or go with a lighter shade of grey.<br /> - Figure 1A and the figure in the abstract: The question marks are a little confusing to me. There may be a better way to describe what you mean without them.<br /> - Figure 5C & D: There is green text next to red text, which can be confusing to the color impaired.

On 2025-05-16 23:27:04, user Andie Souder wrote:

Summary: <br /> The major goal of this paper was to understand FAD binding to Cry4b isoform in vitro. This was done by in vitro binding assays, simulations of FAD binding to Cry4b and solvent accessibility, and mRNA transcription levels of in vivo and immunoprecipitation. The major success of this paper is establishing protocols for optimization and finding new methods to work with the Cry4b isoform. The major weaknesses stem from a lack of reliable experimental data. But this paper brings to attention the need for thorough and rigorous protocols. It also highlights how little is known about these proteins and sheds light on areas that need to be explored.

Major Issues:<br /> Perhaps I am misunderstanding the conclusion of this paper, but it seems like the results of your experiments do not support your conclusion. In the introduction, it states that genome analysis of Cry4b exon has stop codons in the intrinsic region and asks if the mRNA is translated into function protein in vivo. How do we know that the samples collected didn’t have a nonfunctioning version of mRNA being translated?

https://pubmed.ncbi.nlm.nih.gov/32978454/ This paper states that the Cry4b is expressed only at night, were the specimens harvested during the day vs night to compare Cry4 isoform expression? Could that be the reason for the discrepancy in the MS results? As stated in the paper: “...the latest avian genome analyses showed that the CRY4b-specific exon carries loss-of-function mutations (e.g., stop codons), a pattern characteristic for intronic regions [29]This poses the question whether the ErCRY4b mRNA isoform is translated into a functional protein product in vivo.” Is this a factor that impacts the results of the experiments done?

Considering that the major goal of this paper is to understand FAD binding in vitro, why weren’t those experiments thought out more carefully? It seems as if the inclusion of the vivo studies as well as the simulations were done in an attempt to reinforce the weak results of the experimental data. But the experimental data is hard to draw concrete conclusions from. In the paper, it states that the Cry4b might be misfolded, is there an experiment that verifies the fold of the protein? That is an important thing to consider, especially because these experiments are the basis of the paper. Does the solubility tag block FAD binding? What about the chaperone?

Minor Issues:<br /> Resolution quality of figure 1 does not match the other figures<br /> Please add the confidence of the alpha fold generated structure<br /> Add to the figure 1 caption that the structures were generated using alpha fold<br /> Please clarify if there are competing interests as the bioRXIV webpage states that there is not but paper states that competing interest is present

On 2024-07-21 00:09:37, user Meet Zandawala wrote:

Manuscript title: TRPγ regulates lipid metabolism through Dh44 neuroendocrine cells

Summary: This manuscript from Youngseok Lee lab examines the role of TRP gamma channel in regulating metabolic physiology. Specifically, it focuses on the regulation of lipid metabolism via DH44 neuroendocrine cells. It is a follow-up on the work from the same lab where they showcased the importance of TRP gamma in DH44 cells in regulating post-ingestive food selection (Dhakal et al 2022: https://doi.org/10.7554/eLife.56726 ). Overall, this work adds to the growing body of work on DH44 neuroendocrine cells which appear to be crucial internal metabolic sensors. We have a few major comments and suggestions on the preprint which could help clarify the mechanisms by which TRP gamma regulates lipid metabolism.

1. TRP gamma mutants exhibit higher TAG and protein levels compared to controls. Inhibition of DH44 neurons using Kir2.1 recaptiulates the phenotype of increased TAG however protein levels are unaffected. Since these manipulations are not restricted to the adult stage, it is not possible to rule out developmental defects. It would be beneficial to also include the fly weight for these manipulations to see if their size is altered by these manipulations. Also, is there any impact on developmental timing?
2. The experiments implicating the role of AMPK in DH44 neurons are quite interesting. However, the link between TRP gamma activation, AMPK and DH44 signaling is missing. How is DH44 release altered when TRP gamma is knocked down specifically in DH44 neurons?
3. The author rescue the increased TAG levels in TRP gamma mutants by driving UAS-TRP expression using DH44-GAL4. However, they also able to rescue the phenotype by expressing UAS-TRP in DH44-R2 expressing cells. As far as we are aware, DH44 and DH44-R2 represent two independent populations. This raises some questions. What is the identity of the DH44-R2 cells which normally express TRP? What is the importance of having TRP gamma in both the source (DH44 cells) and the target (DH44-R2 cells) to regulate lipid homeostasis? Wouldn’t modulation of DH44 release alone be sufficient to regulate lipid homeostasis?
4. DH44 is released as a hormone from both the PI neurons in the brain and endocrine cells in the VNC ( https://link.springer.com/article/10.1007/s00018-017-2682-y ). Neither this or the previous study on TRP gamma in DH44 neurons examined the presence or absence of TRP gamma in DH44 neurons the VNC. It is not clear if the DH44-GAL4 used in this study targets the DH44 neurons in the VNC.
5. General comment about structure: The manuscript could benefit if additional context was provided for some of the experiments. The experiments using metformin are interesting and a valuable addition. However, since the link between metformin and DH44 signaling was not explored, the rationale for conducting these experiments is not quite clear. Is the rescue of TAG levels with metformin in TRP gamma mutants DH44-dependent or is metformin directly acting on the fat body? Metformin treatment in DH44 > TRP RNAi flies can clarify this.
6. The manuscript would benefit from having a model which includes all the components in this inter-organ pathway (TRP gamma, DH44 neurons, gut etc).

Minor comment:<br /> 1. Stock numbers for fly strains have not been provided.

Signed by,<br /> Meet Zandawala <br /> Jayati Gera<br /> (Zandawala lab members)

On 2023-07-09 14:02:36, user Bianca Migliori wrote:

The repository associated with this work can be found here: https://github.com/NYSCF/NY...

On 2022-11-28 00:06:07, user Shyam Bhakta wrote:

Rather than predict the folding energy of the entire mRNA, it makes more sense to predict the folding energy of just the 5' UTR through first 10 codons, with and without the SKIK tag, as it is only this region that primarily controls the translation initiation rate by RNA structure. Even better would be to predict the translation initiation rates by inputting the mRNA sequence into the Salis Lab RBS Calculator (denovodna.com). This would better show how much the SKIK codon sequence alone can be expected to affect the protein production rates.

On 2022-10-29 08:23:12, user Karen Lange wrote:

This study investigates the autoproteolytic cleavage of polycystin1/PC1 in the C. elegans ortholog LOV-1. Walsh et al used CRISPR genome editing to tag the endogenous LOV-1 protein at both the N-terminus (mScarlet) and C-terminus (mNeonGreen).

Figure 1 clearly shows that the N and C tagged fragments have different localisation patterns. The N and C terminal tagged fragments also displayed different transport dynamics (Figure 4). When a point mutation that is predicted to prevent cleavage (C2181S) was introduced in the mScarlet::LOV-1::mNeonGreen strain the localisation of LOV-1 was severely disrupted. Interestingly the the N-termini of LOV-1 was enriched in the cilia of three ray neurons suggesting that some cleavage can still occur in this mutant. Taken together this body of work presents strong evidence that LOV-1 is processed in C. elegans.

The mScarlet::LOV-1::mNeonGreen strain will be a very useful tool for use in future studies to model conserved ciliopathy variants. I would predict that missense variants in the N or C terminal fragment do not affect the function of the other. Modelling these variants will help to elucidate disease mechanisms.

One concern I have is whether or not the double tagged LOV-1 protein is fully functional. I can see in Figure 3D/F that the mating efficiency with unc-52 and the response behaviour is not significantly different from wild-type. However, I do not see the comparison to wild-type in the dpy-17 mating efficiency assay (Figure 3E). I would have appreciated a supplemental figure when the double tagged LOV-1 allele is first introduced to immediately address whether or not it is functional.

On 2022-10-17 09:00:34, user Iratxe Puebla wrote:

Review coordinated via ASAPbio’s crowd preprint review

This review reflects comments and contributions by Ruchika Bajaj, Sree Rama Chaitanya Sridhara and Sara El Zahed. Review synthesized by Ruchika Bajaj.

This study has developed a novel one-step methodology for the incorporation of membrane proteins from cells to lipid Salipro nanoparticles for structure-function studies using surface plasmon resonance (SPR) and single-particle cryoelectron microscopy (cryo-EM), which is a profound technology in the field of membrane protein structural biology. We raise some points that may strengthen the manuscript below:

Main section, 4th paragraph “resuspended in digitoxin-containing buffer”- Does the sentence mean that membrane proteins were solubilized by detergent before reconstitution into salipro particles? Are salipro and digitoxin added at the same step? If this is the case, it is unclear how one can distinguish between the step wise solubilization and reconstitution or direct reconstitution into salipro particles. Further discussion on the mechanism of reconstitution would be helpful. In the same paragraph, the fragment “to increase membrane fluidity and render lipids” raises the question of whether the concentration of digitonin was optimized to balance the increase in membrane fluidity but not rendering the solubilization of membrane proteins.

Main section, 4th paragraph, “the formation of saponin-containing mPANX1-GFP particles was assessed by analytical size exclusion chromatography using fluorescence detector” - It is assumed that fluorescence is detected from GFP. As the construct expressed is PANX1-GFP, GFP fluorescence signal will be received from reconstituted as well as not reconstituted PANX1. Is saponin specific signal being used as a signal for measuring the reconstitution of PANX1-GFP? In the same paragraph, “PreScission protease for on-column cleavage” is mentioned. Is GFP still intact in the expressed PANX-1 or is it cleaved? A diagram of these procedures showing the various steps will be helpful for readers.

Main section, 4th paragraph “SDS-PAGE revealed the formation of pure and homogeneous Salipro-mPANX1 nanoparticles”- However, extra bands are present above the major band in Figure 1E, can some comment be provided on this point. Possible explanations for the additional bands could be post translational modifications or degradation of mPANX1.

Methodology section, “membrane protein reconstitution screening using fluorescence-detection size exclusion chromatography (FSEC)” -The amount of salipro is given in ug. A comment on the ratio of protein to salipro particles would be important to decide the concentration of salipro with respect to the mass of the cell pellet.

Figure 1G: The molecular weight of Salipro-mPANX1 particles is mentioned to be approximately 466kD. mPANX1 weighs about 48kD and heptamer will be 336kDa. A discussion on comparison of experimental and actual molecular weight would be interesting.

hPANX1 was expressed in sf9 insect cells. A description regarding trials of expression of this construct in expi293 cells would be informative.

Supplemental Figure 1B: The gel is overloaded and shows multiple bands for hPANX1, recommend selecting an alternative image for hPANX.

Paragraph 6A phrase, “challenged with bezoylbenzoyl-ATP(bzATP), spironolactone and cabenoxolone” - Please explain the meaning of ‘challenged’ here.

Supplementary Figure 2: Paragraph 6 mentions “binding constant could not be determined”. Please provide an explanation for this. Is it about the saturation phase not being approachable because of the feasibility of the binding experiment at higher concentration of cabenoxolone?

The last summary sentence in Paragraph 6 is not clear, recommend rephrasing it.

Figure 2A shows that Salipro particles have His tag. This suggests that an additional step of affinity purification with His tag could have been used to distinguish or separate reconstituted and un-reconstituted PANX1.

Supplementary figure 4: Please explain whether the datasets for samples in the presence and absence of fluorinated lipids were combined together.

Paragraph 8, “intracellular helices were not well resolved” - Please comment on a possible explanation. Does the Salipro scaffold contribute to the resolution? Please mention any future possibilities regarding improving the resolution by modifying the salipro scaffold or alternative scaffold. In the same paragraph, rmsd is mentioned at promoter level, please comment on how this value changes at heptamer level and why is it important to report the rmdd value to appreciate the direct reconstitution methodology.

Last paragraph 10, “future membrane protein research” - Please comment on the utility of this methodology on prokaryotic membrane proteins, bacterial outer or inner membrane proteins or eukaryotic membrane proteins. Some more examples of reconstitution with the same method will support the applicability of this methodology on diverse kinds of membrane proteins. A discussion section comparing this methodology to other methods would also be useful for readers.

On 2022-10-13 19:16:01, user BacillusBaRosh wrote:

Author responses to feedback posted on hypothes.is - cut and paste because could not figure out how to respond there https://hypothes.is/a/5fVcAEaSEe2k4CPVTDZz7Q

AtanasRadkov<br /> Oct 7<br /> on "Magnesium modulates Bacillus s…"<br /> (www.biorxiv.org)<br /> General comments:

This study carefully delineates the role of magnesium in cell division versus cell elongation. The results are really important specifically for rod-shaped bacteria and also an important contribution to the broader field of understanding cell shape. Specifically, I love that they are distinguishing between labile and non-labile intracellular magnesium pools, as well as extracellular magnesium! These three pools are really challenging to separate but I commend them on engaging with this topic and using it to provide alternative explanations for their observations!

A major contribution to prior findings on the effects of magnesium is the author’s ability to visualize the number of septa in the elongating cells in the absence of magnesium. This is novel information and I think the field will benefit from the microscopy data shown here.

I completely agree with the authors that we need to be more careful when using rich media such as LB. It is particularly sad that we may be missing really interesting biology because of that! It’s worth moving away from such media or at least being more careful about batch to batch variability. Batch to batch variability is not as well appreciated in microbiology as it is for growing other cell types (for example, mammalian cells and insect cells).

For me, the most exciting finding was that a large part of the cell length changes within the first 10min after adding magnesium. The authors do speculate in the discussion that this is likely happening because of biophysical or enzymatic effects, and I hope they explore this further in the future!

I love how the paper reads like a novel! Congratulations on a very well-written paper!

Kudos to the authors for providing many alternative explanations for their results. It demonstrates critical thinking and an open-mind to finding the truth.

Comment<br /> Figure 2C → please include indication of statistical significance<br /> Figure 3C → please include indication of statistical significance<br /> Figure 6A → please include indication of statistical significance<br /> Figure 8B → please include indication of statistical significance<br /> Figure S1B → please include indication of statistical significance<br /> Figure S3B → please include indication of statistical significance

Response<br /> Easy to add

Comment<br /> For your overexpression experiments, do the overexpressed proteins have a tag? It would be helpful to have Western blot data showing that the particular proteins are actually being overexpressed. I think the phenotypes that you observe are very compelling, so I don’t doubt the conclusions. Western blot data would just provide some additional confirmation that you are actually achieving overexpression of UppS, MraY, and BcrC.

Response<br /> The proteins are untagged. For the UppS and BcrC the cell shortening occurs with addition of inducer, , so strong indication expression is occurring. A western would provide information about degree of overexpression, but we don’t think is necessary to support conclusion drawn. Do you think there is an alternative possibility that needs to be excluded? We note that in another preprint (https://www.biorxiv.org/con... the authors delete the native uppS in their inducible Phy-uppS strain (Fig S4) and at 100 uM IPTG (10X less than what we used in experiment) the cells have wt growth on LB plates, so we at least know the Phy-uppS is functional and made (or they would die!). We are introducing the uppS deletion into our strain to see if we can identify a concentration of IPTG that doesn’t affect cell growth but still induces shortening.

For MraY, the result is negative, so you are spot on – it is impossible to tell if due to lack of overexpression from data shown. We only know the strain is correctly made from sequencing. We will investigate if there is an antibody or functional fusion available. The reason we were not sure was worth doing is because the MraY reaction is reversible (15131133). This means that without a phenotype, there is no simple way to know the reaction can even be pushed forward even if the overexpression is confirmed (more negative data). We actually overexpressed some other proteins that act downstream (MraY, MurJ, AmJ) and they were also negative for shortening. Probably we should remove the negative data or reword to make the caveats of the negative result clear.

Question<br /> Based on your data, there are definitely differences in gene expression when you compare cells grown in media with and without magnesium. Because the majority in cell length increase occurs in such a short time though (the first 10min), I was wondering if you think that some or most of it is not due to gene expression?

Response<br /> The shortening is even faster than 10 min (not only statistically significant, but also obvious qualitatively if we mount immediately after adding Mg2+ ). We did not include the first timepoint because original purpose was to check everything was ready with microscope – did not expect shortening so fast! We can definitely add that data in. When we saw, we tried to capture the transition on pads, but going from culture to pad seems to stress the cells too much in the small window where the cool stuff happens. Since growth rate doesn’t appear to be a big factor in those initial divisions, we might be able to grow at lower temp and shift to pads for adjustment period before adding Mg2+. Did not play with it much due to lack of resources atm, but a flowcell setup would probably be best.<br /> In short, we think rapid divisions right after transition do not require transcription or translation. It really “smells” more like a biophysical thing.

Question<br /> Do you have any hypotheses what is most likely to be affected by magnesium? Do you think if the membrane may be affected?

Response<br /> We have a lot of hypotheses – all of which are speculative. There could be an extracytoplasmic enzyme involved in envelope synthesis is sensitive to Mg2+ availability, and that at lower concentrations, it’s activity is affected. There is some old literature with membrane preps that suggests PG synthesis requires higher Mg2+ than teichoic acid synthesis. If Und-P is limiting, higher Mg2+ may shift make the pool more available to make the septum. Tingfeng initially hypothesized there might be a receptor/signal mechanism but has not been able to identify one. Und-P seems to be important, but “availability” is not just pool, but how fast (and where!) the flipping across the membrane occurs. If Und-PP needs to be dephosphorylated to Und-P before being flipped back to cytoplasmic side, anything that effects the PPi equilibrium would be predicted to affect the reaction rate, with lower Pi (in periplasm or pseudoperiplasm in case of G+) favoring the dephosphorylation. Cell wall associated Mg2+ could shift equilibrium to be more favorable for a Und-PP phosphatase more closely associated with the divisome. I could go all day… In short, we don’t know enough!

Question<br /> Why do you think less magnesium activates this program of less division and more elongation? Additionally why is abundant magnesium activating a program of increased cell division and less elongation? Do you think there is some evolutionary advantage, especially considering how important magnesium is for ATP production?

Response<br /> In the window we looked at, the elongation rate is constant (not less or more) and only the division frequency changes. Some bacteria (like Caulobacter and to lesser extent E. coli) clearly elongate and divide simultaneously, so there is some competition for substrate (like Lipid II). Septators like Bacillus seem to delineate the two processes more, but we have found conditions where even Bacillus invaginates during division, so it’s not absolute. Like eukaryotic cells, bacterial undoubtedly have mechanisms not only commit to a round of DNA replication when there is some signal that resources are sufficient. Clearly with some bugs, this is not the case with cell division. The alternative possibility is that every cell cycle there is an opportunity to divide if some threshold of *something(s)* is reached. There is a hypothesis from Mtb literature that it may be GTP, but it’s not at all clear that is sufficient. In yeast, size at cell division is affected by perturbing 1-C pool.

Question<br /> Related to this previous question, I also wonder if this magnesium-dependent phenotype would extend to other unicellular organisms, may be protists or algae? That would be a really exciting direction to explore!

Response<br /> It’s a great question – lots to do! We didn’t even look at another Gram-positive, but we plan to. It’s trickier to limit Mg2+ in Gram-negatives (see 27471053 – we tried Bsub homolog for those wondering – it’s not responsible for phenotype we see).

Question<br /> Regarding the zinc and manganese experiments, why do you think they lead to additional phenotypes compared to magnesium? Do you have any hypotheses?

Response<br /> We have hypotheses, but if my (Jen’s) twitter engagement is any indication, way too speculative for public consumption at present. Need grant to acquire preliminary data to write grant.

Question<br /> Regarding your results that Lipid I availability may be a major a problem for the cell division in the absence of magnesium, do you think that is due to effects magnesium has on the enzymes directly, or do you think magnesium affects the substrate availability/conformation by coordinating the phosphate groups? Or something else, may be membrane conformation?

Response<br /> Several proteins involved in envelope synthesis (like UppS) are Mg2+ dependent enzymes. But at least for any intracellular players, levels of Mg2+ should be more than high enough to support enzyme activity even when levels are low (0.8 – 3.0 mM is Bsub range I recall off top of head). Could have impact extracytoplasmically by lowering pool sponged into the cell wall, but intuition (for what that is worth) is that it is not the coordination of an enzyme with a metal that is impacted rather the equilibrium with other ions like Pi and H+ and that this impacts net ATP synthesis. Lots to think about and do, and no simple answers. When Tingfeng started project idea was to find mechanism – didn’t realize we were asking “how does the cell work?” Turned out to be a bit much for a dissertation project :)

-Jen Herman and Tingfeng Guo

On 2022-10-07 09:04:58, user Iratxe Puebla wrote:

Review coordinated via ASAPbio’s crowd preprint review

This review reflects comments and contributions by Ruchika Bajaj, Gary McDowell, Sree Rama Chaitanya Sridhara. Review synthesized by Iratxe Puebla.

The preprint studies the process for mitochondrial targeting of mitochondrial precursor proteins. Using a yeast model, experiments show that the cytosol transiently stores matrix-destined precursors in dedicated granules which the authors name MitoStores. The formation of MitoStores is controlled by the heat shock proteins Hsp42 and Hsp104, and suppresses the toxicity arising from non-imported accumulated mitochondrial precursor proteins.

The manuscript is clear and well-written. The reviewers raised a few comments and suggestions as outlined below:

The introduction was extremely clear and provides a good summary of the protein homeostasis dimension of the problem in question. However, there could be a clearer discussion of the processes of import, in particular with respect to the results discussing “clogging”. It is suggested to add a penultimate transitional paragraph in the introduction that facilitates this transition e.g. this could be expansion of the first paragraph in the Results section, moved into the introduction to provide more context about the cloggers, PACE, and the Rpn4-mediated proteasomal regulation.

Figure 2E and Figure S2 - Can some further explanation be provided about what data belongs to delta-rpn otr WT, or whether the associated fold change is reported - delta-rpn/WT.

Results ‘while the levels of most chaperones were unaffected or even reduced in Δrpn4 cells, the disaggregase Hsp104 and the small heat shock protein Hsp42 were considerably upregulated (Fig. 2F, G)’ - Suggest adding some further clarification as to why Hsp104 and Hsp42 are selected despite perturbations in other protein partners. Are there other proteins than proteosomes and chaperones which are significantly up- or down-regulated? STRING or cytoscape tools may help with the interactome analysis.

Figure 3

• Figure 3A - It seems Δrpn4 cells are bigger in size than control cells, suggest commenting on this point.
• Figure 3B ‘Hsp104-GFP was purified on nanotrap sepharose’ - Please clarify on which tag the purification was based.
• ‘grown at the indicated temperatures’ - Please clarify the rationale for using 30 or 40C.
• ‘SN, supernatant representing the non-bound fraction’ - Please report what is total, wash and elute etc.

Results ‘protein accumulated at similar levels as Hsp104-GFP in the yeast cytosol (Fig. S4B)’ - Please clarify whether the image reports qualitative or quantitative data, and how the levels of DHFR-GFP and Hsp104-GFP are compared based on S4B.

‘Owing to the striking acquisition of nuclear encoded mitochondrial proteins in these structures, we termed them MitoStores’ - Suggest providing some discussion about the fraction of Hsp104 that is part of the MitoStores? Does a major portion of Hsp104 in the absence of Rpn4 form MitoStore structures?

Figure S5 C ‘Quantification of the colocalization of Hsp104-GFP with Pdb1-RFP after clogger expression for 4.5 h.’ - Suggest normalizing the intensity with one another.

Results ‘Upon clogger induction, the RFP signal formed defined punctae that colocalized with Hsp104-GFP’ - The Hsp104-GFP pattern seems different between Fig 3A, 5, and S5. In some cases, clear punctae are seen and in others, a diffused pattern. Can some comment be provided on this? This might be important to score the colocalization between Hsp104-GFP and other protein partners tagged with RFP. If different conditions were used in the figures, recommend specifying this in the figure legends.

Discussion ‘We observed that MitoStores are transient in nature and dissolve…’ - Suggest adding some discussion about the half-life of MitoStores, and about what the different stressors that can trigger MitoStores may be.

On 2022-10-03 09:55:42, user Iratxe Puebla wrote:

Review coordinated via ASAPbio’s crowd preprint review

This review reflects comments and contributions by Luciana Gallo, Claudia Molina Pelayo, Sónia Gomes Pereira, Asli Sadli. Review synthesized by Iratxe Puebla.

The preprint examines the meiotic recombination co-factor MND1 and its role in the repair of double-strand breaks (DSBs) in somatic cells. The paper reports that MND1 stimulates DNA repair through homologous recombination (HR) but is not involved in the response to replication-associated DSBs. MND1 localization to DSBs occurs through direct binding to RAD51-coated ssDNA. MND1 loss potentiates the G2 DNA damage checkpoint and the toxicity of IR-induced damage, opening avenues for therapeutic intervention, particularly in HR-proficient tumors.

The reviewers raised some minor comments and suggestions on the work:

Results ‘Therefore, we conclude that MND1-HOP2 are ubiquitously expressed proteins’ - we understand that the study looked at the transcript's expression level and not protein levels, consider revising this sentence.

Figure 1F - Due to the differences in intensity for the loading control, recommend quantifying the normalized level of MND1.

‘we used live-cell imaging of RPE1 cells’ - Are these cells p53 KO? In Suppl. Figure 1K, RPE Delpta-p53 cells are used , but the HALO tag was introduced in the normal (WT) RPE cells. Could some clarification be provided for this difference, and report what's the level of MND1 and the effects of its loss in WT RPE cells?

‘Analysis of 53BP1 foci formation and resolution in asynchronously growing RPE1 cells revealed that MND1 depletion leads to slower repair and retention of DSBs after IR (Figure 2A, Suppl. Figure 2F&G)’ - While the quantification shown in Figure 2A is explicit, the foci in the raw images displayed in Suppl. Figure 2G appears to be more frequent in the siNT, especially in the last 2 time points. It may be worth making the images bigger and maybe clearer?

‘our data show that the role of MND1 in DNA repair is most prominent in G2 phase cells and restricted to repair of two-ended DSBs’ - Can some further context be provided for the last part of this claim. Is this due to the different modes of action of the different drugs used? If so, it would be nice to clarify in the text which drugs induce the two-ended DSBs.

‘These data show that MND1 is recruited to sites of DSBs’ - The data shows that there is an increase in MND1 foci, but whether these are or not the sites of DSBs is not clear. Recommend co-staining with a known DSBs marker.

Methods

• Haploid genetic screen - Please describe how cells were fixed.
• Please detail if/what software was used for the Fisher’s exact test.
• ‘Cells were fixed after 7 days of growth in 80% methanol and stained with 0.2% crystal violet’ - Please report at which temperature and for how long the steps were completed, and provide a reference for the crystal violet reagent.
• ‘Membranes were blocked in 5% BSA’ - Please report the temperature and duration for this step.
• Please describe how the propidium iodide staining was performed.

On 2022-08-28 09:00:20, user Iratxe Puebla wrote:

Review coordinated via ASAPbio’s crowd preprint review

This review reflects comments and contributions by Ruchika Bajaj and Gary McDowell. Review synthesized by Bianca Melo Trovò.

This study demonstrates the utility of an L-Methionine analog - ProSeMet - to tag and enrich proteins which have residues that are methylated in vivo, ex vivo and in vitro. Furthermore, the study demonstrates that this can be used in combination with mass spectrometry to identify these sites. Overall this is a useful, well-verified and well-described approach that will be helpful for future identification and investigation of methylation sites.

Major comments

It would be helpful if the manuscript could additionally discuss the reversibility of methylation generally, and the reversibility of the modification of protein residues by the alkyne group specifically, in the discussion, and whether that has any implications for their results. It may be that the dynamics of methylation and demethylation vary between the two; or it may be that they are the same - either way, that may affect how they suggest others use this method and interpret its results.

Perhaps related to the question of reversibility, it would be helpful if the manuscript would comment on whether these are “true” methylation sites or not; i.e. whether they consider all these methylation sites to be functional. Trying to determine this would be an interesting direction for future work, but for this study a reflection on whether these novel functional methylation sites are simply capable of being methylated, or are likely to be methylation sites that are meaningful biologically, would be helpful.

Results, ProSeMet competes with L-Met to pseudo methylate protein in the cytoplasm and nucleus: the manuscript claims that ProSeMet is not incorporated into newly synthesized proteins but rather converted to ProSeAM and used by native methyltransferases. There does appear to be some reduction in the labeling with ProSeMet on cycloheximide treatment in Figure 2D - could this suggest that it is incorporated into newly synthesized proteins as well as being converted to ProSeAM? If not, could the manuscript explain why not? This experiment clearly shows that in contrast to AHA labeling, there is still use of ProSeMet as a substrate when translation is inhibited; however, it is not clear how this demonstrates that it is not incorporated at all into newly synthesized proteins. If methyl has been incorporated in previously present proteins, perhaps this can be clarified in the text.

Results, ProSeMet competes with L-Met to pseudomethylate protein in the cytoplasm and nucleus: the conclusion that “Cell fractionation of the cytosolic and nuclear compartments followed by SDS-PAGE fluorescent analysis revealed no fluorescent labeling of the L-Met control” is correct but may be overstated as there appears to be some background in the cytosolic fraction.

Minor comments

Introduction: Recommend including a mention to ProSeMet's permeability.

Introduction, Figure 1: the last step with CuAAC and N3 labeling in the description of the Chemoenzymatic approach for metabolic MTase labeling is not clear. Please, add the description in the legend.

Results, Figure 2D: the image suggests an overloaded gel, consider using an alternative gel image.

Supplementary Material, Fig. S1: the data with L-met is only shown with T47D stacks.

Supplementary Material, Fig. S3: please add the control for the no treatment condition.

Results, Fig. 2A ‘ incubating for 30 m in L-Met free media’: Please confirm that the length of incubation was 30 minutes.

Results, Enrichment of pseudo methylated proteins used to determine breadth of methyl proteome: Please provide some description for the SMARB1-deficient G401 cell line. Why smarb1 deficient?

Results, Figure 3: Please define BP, MF, HP, NES, and label the x and y axes in panel D.

Results, ProSeMet-directed pseudo methylation is detectable in vivo: Please, clarify if the administration was oral.

Comments on reporting

Results, ProSeMet competes with L-Met to pseudo methylate protein in the cytoplasm and nucleus: Please verify the quantity reported: 5µg on SDS-PAGE gel seems low.

Results, ProSeMet-directed pseudo methylation is detectable in vivo: the manuscript reports that “mice starved prior to ProSeMet injection had increased ProSeMet labeling in the heart, whereas mice fed prior to ProSeMet administration had increased labeling in the brain and lungs”. The error bars are large, it would be helpful to show the individual real data points for the graphs in Figure 4.

Results, Figure 4C: please report the mathematical expression used to calculate the relative fluorescence.

Supplementary Material, Fig. S7: please provide more details on the antibody employed.

Suggestions for future studies

Future studies could investigate the biological functionality of the novel methylation sites - but this is a great proof of principle.

On 2022-07-13 13:46:46, user Iratxe Puebla wrote:

Review coordinated via ASAPbio’s crowd preprint review

This review reflects comments and contributions by Oana Nicoleta Antonescu, Ruchika Bajaj, Sree Rama Chaitanya and Akihito Inoue. Review synthesized by Ruchika Bajaj.

This study has characterized the function of Hero proteins in improving the recombinant expression of TAR DNA-binding protein in E. coli and restoration of enzymatic activity of firefly luciferase during heat and stress conditions. This study may be useful for future applications of Hero proteins in life sciences research. Please see below a few points offered as suggestions to help improve the study.

• In introduction, 3rd paragraph, in context with “amino acid composition and length of Hero proteins”, please elaborate on the effect of these two factors on the function and stability of hero proteins.
• The manuscript refers to “cis and trans” terms on several occassions. Please explain these terms in context with the association of Hero protein with the target proteins.

• Introduction - A paragraph describing the origin of Hero proteins and the differences between the types of Hero proteins in the introduction section would be helpful for readers to understand the background on these proteins. For example, please explain the background on naming these proteins as Hero 7, 9, 11 etc. The genes SERF2, C9orf16, C19orf53, etc are mentioned in the plasmid construction section in the Material and methods. Please provide a brief explanation for the relationship between these genes and Hero proteins.

• Please add more details in the Material and methods section, especifically in western blotting and the luciferase assay, to support the reproducibility of these experiments.

• Figure 1A. Please explain the role of each component (for example factorXa) either in the text or the legend.
• Figure 1B: Please add clarification regarding the normalization of lanes by total protein concentration.
• Fig 1C. Please provide an explanation for the higher order bands in the western blot. The western blot using anti-FLAG antibodies shows non-specific bands. Alternative tags or antibodies or detection methods may be used, for example, GFP tag and in-gel fluorescence can be used to check the expression.
• Figure 1D and 1E, the error bars are high. Suggest checking the data and providing the mathematical expressions used to calculate relative yields.
• Figure 2D and E, the error bars are high, access to the raw data behind the graphs may aid interpretation. An explanation for the choice of temperatures 33 C and 37 C would be helpful. Is there any relation between the choice of temperature and the Tm of the protein? The protein is directly being treated at high temperature, similar experiments with cell-based assays would be helpful to understand the effect of the Hero proteins on the stability of Fluc. Would it be possible to report the mathematical expressions used to calculate “Remaining Fluc activity”. Recommend indicating n if these activities are calculated per mg of the protein. Please explain if the reduction in activity is due to loss of protein or loss of luminescence activity from each molecule of the protein.
• Figure S1, access to the raw data would be helpful to understand the signal to noise ratio for activity.
• Figure 2 and 3 show similar experiments with wild type and mutants, it may be possible to combine the figures (for example, to avoid the redundancy in Figure 2C and 3A).
• Figure 3D and G, access to the raw data would be helpful to interpret the signal and noise ratio especially given the low values.
• Figure 4, Can some further discussion be provided for the reason for higher residual activity for SM and DM than wild type? Tm experiments during stress conditions (heat shock and freeze thaw cycles) may be helpful to define the stability of Fluc and Fluc mutants.
• Figure 5: Suggest including an explanation for choosing Proteinase K -among other proteases- for these experiments.
• The residual activity is different in Figure 4 and 5, which could be due to different stress conditions. Please include some discussion about possible explanations.
• In section “Hero proteins protect Fluc activity better in cis than in trans”, ‘When the molarity of recombinant GST, Hero9, and Hero11 proteins was increased by 10-fold...’ does molarity refer to the concentration of protein ?
• In the first paragraph of the discussion, “physical shield that prevents collisions of molecules leading to denaturation” and “maintaining the proper folding” is mentioned. Is it the hypothesis for the mechanism behind the stability provided by Hero proteins? Can further discussion on this be provided, along with a relevant reference.
• In the discussion section, it is mentioned that “Hero may be reminiscent of polyethylene glycol (PEG)”. Please provide further explanation for why hero proteins are correlated with PEG in this fragment.
• A discussion on why specific Hero proteins may be better for specific target proteins may be helpful.
• In the second paragraph, of the Discussion “Hero protein can behave differently depending on the client protein and condition” and “important to test multiple Hero proteins to identify one that best protects the protein of interest” are mentioned. Suggest adding further discussion of these points, for example around any alternatives or computational predictions or simulations to test individual Hero proteins for specific client proteins.

On 2021-11-03 14:33:03, user antibodies-online wrote:

ABIN101961 used for CUT&Tag/MulTI-Tag in this preprint

On 2021-11-02 09:56:52, user David Bhella wrote:

To help readers understand the path to publication, I am adding an account of the peer review process to each preprint.

This article was initially rejected without peer-review by PLOS Pathogens. We then submitted to Scientific Reports, where the paper was accepted following review:

Reviewer comments:

Reviewer #1 (Technical Comments to the Author):

In this manuscript, Ho et al. reported a 7-Å resolution cryoEM reconstruction model of MrNV VLP expressed in insect cells. MrNV could cause white tail disease in the giant freshwater prawn with high mortality rate, therefore is a serious threat to aquaculture. Together with PvNV infecting marine shrimp, MrNV may represent a new genus in the Nodaviridae family. The structure presented here shows a different arrangement of protruding spikes on the icosahedral capsid surface, compared to other nodaviruses, supporting this classification. The most significant difference is that the protrusions are dimeric, instead of trimeric as in other nodaviruses.

This manuscript is well written. The methodology from VLP expression, purification, to imaging and 3D reconstruction is standard and clearly explained. The conclusions are logical based on the results. Some discussions could be better elaborated:

1.The authors devoted a lot of space (especially figures) to the homology modeling which did not provide much information besides that the P domain of MrNV capsid protein is different from the input homologous models. It would be more helpful to instead show figures of the models fitted in the MrNV map, to directly show the discrepancies and suggest possible location of the MrNV P domain.

2.Given the current information, there is not sufficient evidence to say whether the fuzzy density beneath 5-fold symmetry axis is RNA. The authors could discuss the possibility of it being protein, such as the N-terminal region of capsid, which is usually disordered in other nodaviral structures.

3.Literature (ref. 14 &15) has shown two different assembly states of MrNV VLP expressed in E. coli and sf9 cells respectively. Could the structural information reported here help to explain the differences?

4.Structural characterization of MrNV is in need due to the threat from white tail disease. Now with the 7-Å resolution available, the authors could discuss more about followup studies and/or downstream applications leading to potential intervention against white tail disease.

Some minor points:

1.Has the final map been deposited to the EMDataBank?

2.With the current figures, the comparison between AB and CC dimers is a little hard to follow. It would help to label the A, B, C subunits. It is fine to label the dimers with colored arrows, but it would be more clear if the coloring is consistent between Figures 2 and 3. Please also consider including the measurements of angles and lengths in the figures, and labeling the supporting legs of CC dimer with an arrow or asterisk.

Reviewer #2 (Technical Comments to the Author):

The authors present work showing a cryo-EM 3D reconstruction of MrNV virus-like particles with the finding that “pronounced dimeric blade-shaped spikes" protruding above the surface of the particle are arranged differently than canonical structures of Alphanodaviruses. Thus the authors believe the new structure supports the prior assertion that MrNV belongs to a new genus of Nodaviridae designated Gammanadovirus.

The authors use a generally accepted approach during the reconstruction process although the use of a crystal structure as an initial model rather than using an initial model generated from their experimental 2D class averages could possibly confound the interpretation. Whenever a known structure is used it can lead to potential model bias. It is this reviewer’s assumption that the authors used FHV for the initial model since FHV doesn’t have significant spikes on the surface. The authors also used a low-pass filter of 60 angstroms to the FHV initial model to partially mitigate model bias. In both of these cases this is typically an ok approach if significant homology exists. However the authors force icosahedral symmetry during reconstruction and they themselves highlight the fact that MrNV and FHV share only 20% homology. The manuscript could therefore be greatly strengthened by a reference-free 3D reconstruction where the initial model is created from the experimental 2D class averages rather than the FHV crystal structure. If the final reconstruction for the reference-free approach remains similar/identical to the current reconstruction, then the authors will have demonstrated conclusively that the interpretation is sound. Therefore it is suggested that the authors incorporate the results of a reference-free reconstruction into the manuscript (a supplemental figure will be fine). As this requires a rerun of only the 3D refinement image processing step and not new data acquisition, this should not be considered a major modification and if this is successfully implemented then this reviewer recommends publication.

A few other minor comments to be addressed:

According to Reference #9 (NaveenKumar et al. 2013) the capsid protein of MrNV and PvNV only share 44.6% homology but that drops to 22% for the last 115 amino acids at the C-terminus which is the region the author attribute to forming the protruding spikes. Thus, it seems possible that the structure of PvNV may be different. It is this reviewer’s suggestion that the authors refrain from extending their interpretation towards PvNV and simply focus on MrNV throughout the manuscript.

Please define “VLPs” as “virus-like particles” in the abstract rather than just using the acronym.

There appears to be a 6xHis-tag on the capsid protein but it is not used for purification scheme. A sentence should be added to describe why it is included and whether the additional amino acids are anticipated to be present within the dimeric spikes or otherwise impact the interpretation.

During the post-processing steps, a b-factor of -890 square angstroms was applied. Was this calculated automatically using Relion or was it manually chosen?

Figure 1, it would be helpful to see a sampling of the refined 2D class averages in addition to the central slice of the reconstruction.

On line 120, suggest deleting “sharply resolved” to leave sentence as “Inspection of figure 1(b) reveals a capsid shell measuring between 2 and…” since “sharply resolved” is a qualitative term that others may feel is only appropriate for truly atomic resolution structures.

Finally, the homology modelling is an interesting addition to the paper. However, since no conclusive results can really be drawn from the models at this time, it seems more appropriate for figure 4 to move to a supplemental figure.

On 2021-10-27 13:53:05, user antibodies-online wrote:

Proteins used for validating In Silico Driven Prediction of MAPK14 Off-Targets (among others): NMNAT1, FABP4, MEN1

On 2021-10-26 23:22:30, user Xin Chen wrote:

We appreciate that the authors tested our previous results using new reagents and methods. However, we have to point out that there is a big misunderstanding of our published work. First of all, asymmetric histones do NOT imply the existence of “immortal histones” as the authors hypothesized and used to make predictions in their experimental design. In fact, distinguishing old versus new canonical histone must be in the context of cell cycle progression: Old refers to the pre-existing histones before S phase and new refers to newly incorporated ones during S phase. These two populations can be distinguished by the tag-switch or photoconversion methods only after the switched or converted cell goes through one complete S phase and enters the subsequent M phase. Moreover, the new histones with switched or converted labels will mature over time during cell cycle and gain old histone features, and thus there are no “immortal” histones. However, we are not seeing any labels in this work that indicate active cell cycle progression, which is very concerning given these tissues are ex vivo for more than 40 hours.<br /> Second, it would be highly appreciated if the authors include germline versus somatic cell markers in their figures. As of now, it is impossible to tell whether the weak H3 signals in Figure 1C and 1E come from germ cells or somatic gonadal cells. The bright spot in Figure 3E was interpreted as hub cells, which are quiescent somatic cells. If this is the case, it would be very strange that such a quick old to new H3 turn-over occurs in these cells, as indicated in Figure 3E legend.<br /> Finally, we have to point out that our previous results were entirely misinterpreted in the “Alternative Hypothesis 2” in Figure 2, because we are not assigning random stem cells (GSC) and progenitor cells (SG) together as pairs — all GSC-GB pairs we analyzed are still connected by the spectrosome structure (Tran et al., 2012; Xie et al., 2015; Wooten et al., 2019), indicating that they are daughter cells derived from one GSC division. Furthermore, our previous conclusions were not solely based on the post-mitotic GSC-GB pairs, but also on stem cells undergoing asymmetric cell divisions, based on fixed and live cell imaging.<br /> In summary, this work is based on both misunderstanding and misinterpretation of our work, leading to an incorrect hypothesis. Additionally, there is no single dividing stem cell or a pair of daughter cells derived from stem cell division shown in this work that can lead to the conclusion of “Symmetric Inheritance of Histones H3 in Drosophila Male Germline Stem Cell Divisions”. We hope these comments clarify several critical points for both the authors and the readers of this preprint. Thank you for your attention!<br /> Xin Chen<br /> Johns Hopkins University

On 2021-08-19 14:35:18, user Meng Wang wrote:

We have recently reported that the Tn5-based epigenomic profiling methods, especially Stacc-seq and CoBATCH, are prone to open chromatin bias (https://www.biorxiv.org/content/10.1101/2021.07.09.451758v1). Rather than directly address this bias issue, the authors of Stacc-seq argued in this preprint that FC-I normalization (normalizing by input/IgG control) was better than FC-C (normalizing by background) for Stacc-seq etc. data analysis. Based on this, they claimed that our results had “a major analysis issue”. However, the truth is that we had already used both FC-I and FC-C normalization methods and both showed clear open chromatin bias for Stacc-seq and CoBATCH. The fact that our analyses demonstrating that CUT&Tag (5% FPR) showed much lower FPR than Stacc-seq (30% FPR) or CoBATCH (50% FPR) indicated that the high FPRs were not due to “artificially enhanced the relative enrichment of potential open chromatin bias”, but an intrinsic problem of Stacc-seq and CoBATCH. In our opinion, the preprint has several problems, which are detailed below.

1. The preprint ignored the fact that we had already used both FC-I and FC-C normalization methods. The authors assumed that we only used FC-C for Stacc-seq etc. (Fig. 1A in Liu et al.). However, in fact we used both FC-C and FC-I in our analyses. In Fig. 1c, d and Fig. S2 of our manuscript (Wang et al.), methods labeled with “with IgG” were results from FC-I normalization, and methods without such label were results from FC-C normalization. Importantly, results from both normalizing methods showed clear open chromatin bias for Stacc-seq and CoBATCH (Fig. 1c,d and Fig. S2 in Wang et al.).

2. The results of global H3K27me3 enrichment at the Polycomb targets in this preprint (Fig. 1C) was contradictory to their claim that using FC-C would cause “complete loss or dramatic reduction of enrichment at true targets for datasets generated by Tn5-based methods”. Fig. 1C of this preprint showed a clear H3K27me3 enrichment around the TSS of Polycomb targets compared to adjacent regions when using FC-C. The difference between results from FC-I and FC-C is caused by the y-scale. The fold change is a relative measurement, so the y-scale of different normalization methods is not directly comparable. If they set the y-scale of FC-C to 0~2, the enrichment pattern would be highly similar to that using FC-I.

3. The genome browser snapshots of several loci in a large scale (low resolution) could not demonstrate that the results from FC-I and FC-C normalization are globally different. This preprint provided several example loci (Fig. 1B and Fig. 2 in Liu et al.) to show that using FC-C would cause “complete loss or dramatic reduction of enrichment at true targets for datasets generated by Tn5-based methods”. However, showing browser view of very large regions are misleading as the resolution is too low. For genome browser display, the look of the signal track patterns depends on y-scale, x-scale and windowing and smoothing function. When viewing a very large region, the signals are sampled and aggregated by genome browser and are not the raw signals. Thus, the patterns may not reflect the real situation. Indeed, when zoomed-in to check these regions, we found the peak patterns from FC-I and FC-C normalization are highly similar. In addition, examples from several loci could not reflect the global pattern. The global enrichment shown in Fig. 1C of this preprint did not support their conclusion, as discussed in point 2.

In summary, our original analysis has already included the normalization method suggested by the authors of this preprint. Results from both normalization methods supported that Stacc-seq and CoBATCH had high open chromatin bias. In fact, the results from this preprint also support our conclusions. In Fig. 2 of this preprint, regardless whether FC-I, FC-C or RPKM were used, the discrete peaks from Stacc-seq etc. were more similar to ATAC-seq peaks, but were totally different from ChIP-seq peaks.

Meng Wang and Yi Zhang<br /> Howard Hughes Medical Institute, Boston Children’s Hospital, Boston, Massachusetts 02115, USA

On 2021-05-04 15:06:24, user AAAAAAAAAA wrote:

I noticed that you did the high salt tagmentation (300mM NaCl) for PBMC mixing experiments, which I think is the "right" way to avoid the open chromatin bias but for other experiments, you did the tagmentation in 10X ATAC buffer (10mM NaCl). Is there a particular reason for this? I thought the low salt would have serious ATAC signals, which is demonstrated in the original CUT&Tag paper.....

On 2021-01-18 08:53:01, user The_Zman wrote:

There's an error in the liganddock.xml protocol file, there's a missing closing tag for <scorefxns>

On 2020-12-04 18:31:34, user Jordan Berg wrote:

Metaboverse v0.3.1b is live!

https://github.com/Metabove...

• Improved direct-CHEBI mapping stability
• Other minor bugs fixed

See https://metaboverse.readthe... for a full list of updates.

And thank you to all who have helped track down bugs and suggested new features! More to come!

On 2020-09-21 17:20:33, user Jordan Berg wrote:

Metaboverse v0.3.0b is live!<br /> https://github.com/Metabove...

• Improved flexibility in metabolite, protein, and gene synonym mapping
• Other minor bugs fixed

See https://metaboverse.readthe... for a full description of updates.

On 2020-08-26 16:46:04, user Jordan Berg wrote:

Metaboverse v0.2.0b is live!<br /> https://github.com/Metabove...

• Improved metabolite synonym mapping
• New time-course and multi-condition features added during motif exploration

See https://metaboverse.readthe... for a full description of updates.

On 2020-07-29 18:00:44, user Jordan Berg wrote:

Metaboverse v0.1.4b released:<br /> - Fixes minor/non-critical dependency issues<br /> - Adds error log output file for error messages that do not fit in alert pop-up box for easy troubleshooting

https://github.com/Metabove...

On 2020-07-01 19:10:35, user Jordan Berg wrote:

Metaboverse v0.1.3b released:<br /> - Allows for spaces in file names and folders<br /> - Allows to be run in Windows in non-admin mode

https://github.com/Metabove...

Let us know if you have any feedback! https://forms.gle/4z51DMnag...

On 2020-11-16 23:18:09, user Fraser Lab wrote:

This manuscript details the efforts of a team of structural biology computational experts to cross-validate the proliferating SARS-CoV-2 structures emerging during the COVID-19 pandemic. Over the past five months, as soon as each new SARS-CoV-2 structure is made publicly available, the authors have subjected it to a barrage of validation metrics as well as residue-by-residue manual inspection. When they were able to get a hold of the raw data, they analyzed that as well for several of the most commonly occurring pathologies. Re-refined structures were sent back to the structures' original authors for reupload to the PDB via the recently available versioning option that preserves the PDB code (although it would be nice to quantify how many authors were contacted and what the “re-versioning” rate is after contact). In this manner, the structural biology community has simultaneously benefitted from an increased number of experimentalists' single-minded focus on the coronavirus (even where these efforts fall partly outside their areas of expertise) and these experts' careful curation of the resulting structures.

The manuscript represents an incredible effort. As the authors call attention to in a few places, the errors in data processing and modeling are not only inevitable (especially under the circumstances) but tolerable, as long as they can be identified and corrected in a timely manner — the goal is not to gatekeep so that only experts are permitted to do this work, but to tag-team as effectively and efficiently as possible. Furthermore, there is the separate issue of pathologies resulting from decisions during data collection that cannot be corrected after the fact. It is critical that fixable and unfixable issues are extremely clearly distinguished from each other. We suggest the authors rewrite some of these narratives with the deliberate aim of identifying the origins of pathologies that can be mitigated or corrected in full, again differentiating between these, and taking care that the wording is as charitable as possible toward the researchers responsible.

There are a few cases of oversimplified concepts that we believe can be succinctly expressed more accurately. For example, where the authors describe data as being "incomplete due to radiation damage," they could instead take the time to explain the difference between incompleteness resulting from a poorly chosen collection strategy, incompleteness in higher resolution bins, and radiation-induced damage that renders some reflections (and some real-space features) self-consistent but inaccurate. The "lower quality" of datasets suffering from these pathologies could be separated into uniformly low resolution datasets, which are more easily recognizable, and seemingly high-resolution datasets with serious systematic errors.

The authors could also be more clear with a couple choices of wording around concepts of correctness. They write, "While the deposited structures are often improved by PDB-REDO, they need to be checked and should not be viewed as 'more correct' purely on [the] basis of a lower R value." In this and several other instances, we challenge the authors to replace any terms assigning value (improved, correct, error, bad, misidentified) with descriptions of what metrics they are examining and what they mean for the model and data. This publication is an opportunity to instill readers with a stronger sense of how to use the existing validation tools, and what to do when they turn up serious issues. It would be highly useful to go into some explanation of what constitutes model bias and how this is detected in crystallographic and EM data, what metrics we traditionally use to detect it, what happens when we refine against those metrics (!), and how the tradeoff between agreement with priors (geometry, clashscore) and agreement with data (real space CC, FSC) should vary with map quality. If the authors are willing to go as deep as explaining how the available validation metrics were devised, the average reader might learn quite a bit!

A separate but closely related issue is the identification of real features that conflict with prior knowledge. Under what circumstances do we accept "bad" geometry is actually the right way to model something? These are often information-rich and functionally relevant discoveries, such as Hoogsteen base pairing or very strained geometries at a catalytic site. This is worth calling attention to.

We read the opening of the "manual evaluation" section as a framing of structure solution as tedium that should be automated as much as possible, but whose results nevertheless fall short in the absence of an expert's intervention. This is unfortunate. We would rather laud both the amazing efficiency (and thereby throughput) that automating routine steps has made possible and the important role of the researcher in guiding the process and interpreting the results.

On the topic of data not deposited in the PDB, the authors describe a case of a severely radiation damaged dataset and how it was necessary to reprocess the raw data to improve it. We strongly agree that raw data should be made publicly available for exactly these sorts of reasons. Once again, separating this administrative barrier from the researchers' decisions during data collection would be helpful in setting a positive tone. The authors point out the amazing proteindiffraction.org resource and should call for more deposition there (or to SBGrid DataGrid). In EM, the EMPIAR database plays a similar role (with greater proportional adoption) and the reprocessing potential of datasets deposited there should be highlighted and celebrated.

The "supplying context", "summary" and especially "outlook" sections bring up some extremely important points that could bear to be repeated at the beginning of the manuscript to help frame this work. The tradeoff necessary under the present circumstances in particular — the fact that imperfect "first draft" structures are still useful, and much more useful when they can be quickly updated with any corrections — deserves greater emphasis, and perhaps further discussion of how the field should go about addressing and documenting problems with models and data after the pandemic. We are overall very excited to see this work in print alongside the resources already publicly available at insidecorona.net. Collectively, that resource and this manuscript represent an exciting development in peer review away from gatekeeping and toward continuous improvement!

Finally, we note a handful of points that we suggest would improve readability:<br /> SARS-CoV is now also known as SARS-CoV-1. We strongly suggest using this term throughout the manuscript to differentiate it from SARS-CoV-2.<br /> The phrase "not by experimentalists, but scientists from other fields" suggests a false dichotomy. We recommend rewording so as to recognize the existence of experimentalists in other fields. <br /> The rationale for annotating secondary structures with the Haruspex neural network is not yet clear.<br /> The COVID-19 pandemic is "unprecedented" in very recent history, but arguably not unique even in recorded history — we would favor a different term here.<br /> The abbreviation RdRp is not defined.<br /> "fulfil" is a typo.<br /> “Structures solved in a hurry to address a pressing medical and societal need _are_ even more prone to mistakes.” - suggest "may be"

James Fraser and Iris Young (UCSF)

On 2020-09-30 10:20:45, user Emilian Stoynov wrote:

Interesting article. Can you provide information how long was kept in captivity the captive bred individual with the patagial tag prior to be released again with leg-mount tag replacing the patagial one? Frequently, captive bred birds perform better when re-released after sometime of refueling/rehabilitation following the original release. This fact may bias the data from switching between different type of tags. The best would have been if this result was obtained by marking wild experienced bird first tagged with patagial and afterwards switched to leg-mount tag.

On 2020-09-18 02:09:42, user Maria Ingaramo wrote:

Summary: for now, we recommend using the S11 tag at the N-terminus of target proteins.

Details:<br /> We'd like to thank Dr. Abby Dernburg for pointing out that our S11 fragment, which ends in two glycines, might act as a C-terminal degron signal (doi.org/10.1016/j.cell.2018...:DdzbmEETvEUkkesPwEqFKBomMYw "doi.org/10.1016/j.cell.2018.04.028)"). We've successfully tagged proteins at both the N-terminus and the C-terminus, but we have not established that these yield similar expression levels. We take this concern very seriously, and we're checking this now. Results will be posted here and at andrewgyork.github.io/split_wrmscarlet. In the meantime, we recommend avoiding the potential issue by attaching the S11 fragment at the N-terminus. If C-terminus tagging is required, we suggest the alternative S11 sequence YTVVEQYEKSVARHCTGGMDELYK.

-Maria Ingaramo

On 2020-07-06 15:50:28, user OxImmuno Literature Initiative wrote:

https://www.immunology.ox.a...

On 2020-06-26 10:15:50, user Ersa Flavinkins wrote:

Major issue with the article: the vector, the pcDNA3.1-N-myc/C-C9 vector, is not found nor availible from catalogue in anywhere. All the ACE2 proteins are stained with anti-C9 antibodies--indicating that the cloned part is not the entire mRNA.

The original specification of the c-myc/c9 vector was stained by the anti-c-myc antibodies on the cell surface--so there is an additiona signal peptide in fromt of the c-myc tag in the vector.

no pcDNA3.1 vector have an AgeI site and XM_017650263.1 is not cut by either AgeI or Acc65I. As the human, civet and rat ACE2 gene is specified to have their signal peptide removed before cloning into their vector, the vector must carry it's own signal peptide--which is before the c-myc tag as the original thesis at ref.55https://www.ncbi.nlm.nih.gov/pmc/ar... and ref.34 https://www.ncbi.nlm.nih.go...

specified the staining of the cells via antibodies targeting the c-myc tag on the N terminii of the ACE2 receptors.

This leave all the receptors--the Human,Civet and the Rat--with an N-terminal C-myc tag. and the Ferret badger, Rhesus, Raccoon dog, Hog badger, Free-tailed bat, Rabbit, cat and dog ACE2 receptors may potentially contain parts of the signal peptides themselves or even the entire signal peptide. The Rs bat and pangolin ACE2 receptors were cloned into an unknown vector and there is no way of telling whether the Signal peptide, c-myc tag or other AAs were retained or not. However, as these were all marked as C9 tagged on the C-terminus, the exact cloned part must not include the C-terminal stop codon or other parts of the mRNA since the natural Stop codon will prevent C9 tag expression.

There is no indication of the N-terminal clone site for the 2 ACE2 proteins, but the Human, Civet and Rat ACE2 is specified to have the signal peptide sequence removed. and therefore an additional signal sequence must be included before the C-myc tag in the vector to enable cell surface display.

As the article specifies that the ACE2 proteins expressed from such vectors have a "N-terminal c-myc tag and a c-terminal C9 tag", the tage expressed as specified have serious issue with steric clashing with the other S1 RBD monomer and therefore downplaying the Human, Rat and Civet ACE2--this may be even more severe with the other ACE2 and the exact N-terminal status of the Rs and pangolin ACE2 receptor is impossible to tell. Over all, this experiment is heavily contaminated and there is no way to actually deduce the results by just their method section alone. As no published vector available offers simultaneousy the N-myc and C-C9 tagging capability in the protein product, it may or may not be the same vector as specified before.

At best, it may downplay the ability of hACE2 to mediate entry with the PP assay by steric clash with the Tag and potential AAs in front of them--indicating an intentional overplay of Rs bat and pangolin ACE2 receptor by handicapping the rest with a bulky protein tag and a potential antibody binding to the tag, all of which clashes with the rest of the S glycoprotein and significantly decreases the entry efficiency, at worst--if the specified N-myc/C-c9 vector is the same as the vector described before, it mean that none of the PP assays are trustable as actual, unbiased data.

Notably, the PP assay result described here is in conflict with another paper https://www.biorxiv.org/con... using the exact same protocol but specified a different N-terminal tag--the HA tag, again on the N terminus of their ACE2 proteins. Notably, the Rs bat and Rat receptor affinities, as well as the Feline and pangolin receptor affinities, as by PP assay, were inverted in the 2 publications. As well as the Feline and Rabbit receptor affinities--despite the feline and rabbit are specified as being tagged using the same protocol in both publications--c-myc in this and HA in the other.

Unless the exact cloning sequences of the vectors and the inserts are published, neither publications can be used as an exact indicator of the true affinities of the ACE2 to the S glycoprotein, and none of the publications may be used as a true indicator, in isolation or in tandem, of the true affinities of animal ACE2 to the SARS-CoV-2 Spike glycoprotein.

On 2020-06-16 21:57:53, user Fraser Lab wrote:

I am posting this review on behalf of a student from a class at UCSF on peer review: https://fraserlab.com/peer_... . The student wishes to remain anonymous. I will be happy to act as an intermediary for any correspondence.

In this manuscript Moti et. al., propose a novel way of visualizing Wnt transport from the ER to the membrane using the Retention Using Selective Hook (RUSH) system. Through use of this system, they also provide insight on the involvement of filopodia used for signaling by Wnt3A.

Overall, the authors provide a very promising system for live visualization of Wnt transport inside of a producing cell. Wnts are known to be particularly difficult to tag and visualize in a live model, and this lab was able to show that their tagged Wnt3A not only transports as expected but also is still capable of signaling.

Aside from the tool they developed, the authors state that Wnt transfer between cells via actin-based filopodia. Though they do show that Wnt-positive vesicles are seen in projections, they make the strong claim that it is being transferred to a receiving cell. The images and videos show movement in the projections, but the experiments do not show that the projections are touching the neighboring cell or transferring the vesicles. In supplemental video 5B, the Wnt-positive vesicles appear to actually be migrating into the cell body as opposed to the neighboring cell, which was not discussed.

The major success of this paper is the creation of a functional RUSH-Wnt3A construct that can be used to visualize Wnt transport in the producing cell. As Wnts are very difficult to tag or manipulate, this is a great achievement and its use will strongly help further our understanding of Wnt transport.

Minor points:<br /> The authors switched between HeLa, 293T and RKO cells for different conditions. As the RKO cells were engineered with WLS knockouts, the WT RKO cells could serve as the cell line to test for RUSH-Wnt3A alone and with the Porcupine inhibitor. If this was done intentionally, the authors should state why this was done. Otherwise, using the same cells for each condition would eliminate other factors that could affect the transport of RUSH-Wnt3A. <br /> Transfection of reporter cells (STF reporter) cells with RUSH-Wnt3A for signaling assay. These results would show self-activation of Wnt signaling. Could the STF reporter cells be co-cultured with a different cell line transfected with RUSH-Wnt3A to see the activity levels of the receiving cell? This could further support filopodia, or at least cell contact, as a way of activating cell signaling.<br /> Figure 6a is missing a label for what I suspect is LGR5834DEL.<br /> Figure 6c – would like to see filopodia quantification for LGR5(FL) and a non-transfected cell.

On 2020-05-19 00:55:54, user Fraser Lab wrote:

I am posting this review on behalf of a student from a class at UCSF on peer review: https://fraserlab.com/peer_... . The student wishes to remain anonymous. I will be happy to act as an intermediary for any correspondence.

This manuscript by Wang et al., uses tagged PKD-2 extracellular vesicles (EVs) in C. Elegans to explore the potential role of EVs in directional transfer from one organism to another.

Overall, they identify a mechanoresponsive nature of certain male sensory cilia to release EVs, which are then found to be specifically located on the vulva of his mating partner.

The authors provide compelling evidence that the male tail sensory cilia can respond to global pressure to release EVs, in that the usage of agarose-coated coverslips and slides was a robust way to perturb the forces that a male nematode feels when mounted.

Separately, they also provided evidence of directional transfer of EV cargo from male to hermaphrodite C. elegans during mating. Specifically, showing that in inseminated hermaphrodites, there was highly localized deposition of the male-specific PKD-2-carrying EVs along the hermaphrodite vulva. Though, this study was limited by the inability to perturb EV budding and determine causality between EVs and presence of PKD-2 on hermaphrodite vulvas.

The major success of this paper was in their ability to tag and visualize EVs, and use this technique to identify a candidate mechanism of release for extracellular vesicles. All in all, this paper opens a door for determining potential biological functions for extracellular vesicles, which has been largely elusive in the field.

Minor points:<br /> Figure 1B could benefit from having an inseminated control image, to visualize which signals are present as autofluorescence<br /> It was unclear how many worms were imaged in the directional transfer experiment, but having that number would be important in establishing reproducibility

On 2020-05-05 20:42:00, user Taekjip Ha wrote:

Thank you very much for sharing your interesting manuscript!<br /> We used your preprint as one of the journal club papers in the Single<br /> Molecule & Single Cell Biophysics course for graduate students of Johns<br /> Hopkins University during the Covid-19 lockdown. Students also practiced peer<br /> reviews as the final assignment. I am submitting their formal reviews here <br /> and hope you find them useful.

Taekjip Ha

Reviewer 1.

The authors develop an ?-hemolysin nanopore-based sequencing by synthesis assay<br /> which can be used to interrogate the kinetic properties of single DNA<br /> polymerases. Their method is novel and addresses the problem of increasing the<br /> throughput of polymerase screening methods. Previous techniques only allowed<br /> kinetics of polymerases to be screened one at a time. This new method is a<br /> clever integration of existing nanopore sequencing technologies that addresses a<br /> longstanding problem in development of specialized polymerases in biotechnology.<br /> The paper is interesting to read and not especially difficult for someone<br /> outside of the field to understand.

Each polymerase-pore complex could be uniquely tagged with a circular barcode<br /> template, allowing the assay to be multiplexed and scaled up to accommodate 96<br /> complexes at once. Convincing proof of concept data is shown highlighting the<br /> ability of the method to distinguish between barcodes, as well as the stability<br /> of the circular template. The title and abstract are appropriate, concise, and<br /> clearly lay out the aims of the paper. Introductory figures showing assay design<br /> and low throughput tests are very well presented and easy for the reader to<br /> follow. Low throughput tests show clear clustering, in both two-dimensional<br /> plots and PCA, of data obtained from each tested polymerase which could be used<br /> to distinguish and characterize them. Later in the paper, however, there are<br /> confusing inconsistencies between what is stated and what is shown in the data.

Figure 3a shows how each kinetic parameter is defined by the voltage trace. Only<br /> four of the five kinetic parameters are shown: dwell time, tag release rate, tag<br /> capture rate, and full catalytic rate. Tag capture dwell time (TCD) is not<br /> shown, yet it is featured in the principle components analysis and is shown to<br /> have a relatively high coefficient for some polymerases. How this parameter is<br /> defined by the trace and how it differs from dwell time is not clearly addressed<br /> in the main text of the paper. This figure (3a) and the subsequent analysis<br /> could be improved by explaining how each parameter is calculated and how they<br /> differ to clear up any ambiguity. Explanations of how each parameter correlates<br /> to polymerase fidelity, processivity, speed, etc. may also help convince the<br /> reader of the utility of their method. This is done well for some but not all of<br /> the described parameters.

Figure 5 shows the distribution of counts associated with each of 96 unique<br /> circular barcodes over three polymerases. RPol1 is associated with relatively<br /> few read counts which are not much higher from background off-target signal from<br /> RPol33. The uneven distribution of barcode counts is attributed to the low<br /> processivity of polymerase 1. Later (figure 6), in the 96-plex screen of<br /> polymerase mutants, less than twenty mutants in the screen have detectable<br /> barcode counts and those that do have few counts. This observation is again<br /> thought to be due to poor processivity of the polymerases. Polymerase fidelity<br /> very likely also plays a role in the ability of the assay to identify<br /> polymerases. Since barcode assignment is alignment based, and nanopore<br /> sequencing platforms are known to have a relatively high error rate as well, one<br /> can imagine that a more error-prone polymerase will also escape detection. There<br /> is no benchmarking data to define a polymerase detection threshold. It is clear<br /> that the efficacy of the method decreases for polymerases with lower fidelity<br /> and processivity, but what might be designated as ‘low’ is never defined. What<br /> subset of polymerases make it through this new screening process and what are<br /> their defining kinetic characteristics? How widely applicable would this method<br /> be for identifying desired features in polymerase variants? What kinds of<br /> polymerases would be expected to be missed by the screen?

There are some minor inconsistencies in the data that should be addressed.<br /> Supplemental table 5 shows the calculation of the proportion of mapped reads in<br /> the low throughput 3-plex experiments. The number of total raw reads used to<br /> calculate the 67% CBT mapping as described by the main text is 418, the value<br /> for RPol1 alone rather than a sum of the total read values for all three<br /> columns. Similarly, the text states that 20 polymerase variants were identified<br /> in the screen while figure 6a shows only 17 polymerases were associated with<br /> barcode counts.

The method described in the paper is conceptually strong and should be very<br /> helpful in identifying polymerases with desirable kinetic properties when<br /> coupled to mutagenesis screens. It has the potential to be improved upon as<br /> nanopore sequencing technology is further developed and the error rate that is<br /> currently innate to the platform is decreased. It is likely that general<br /> improvements to nanopore sequencing itself would greatly decrease false positive<br /> rates in the described method. This technique could also be more applicable if<br /> its points of failure were addressed and proper thresholds defined. The higher<br /> false positive rate observed in RPol2 (supplemental figure 11a) is more likely<br /> to be a fault of the polymerase fidelity rather than a characteristic of the<br /> barcode set. What kind of polymerase misincorporation rate is permissible to<br /> still allow confident barcode assignment? At what point does polymerase<br /> processivity become an issue and cause ambiguity in barcode identification?<br /> There appears to be a set of kinetic parameters that must be met in order for<br /> differences in polymerases to be resolved by this assay. Clearly defining what<br /> it is good at and what it is going to miss is essential before it can be used<br /> reliably for screening.

Reviewer 2.

Summary<br /> In this article, the authors expand upon their previously published system of singlemolecule<br /> nanopore sequencing-by-synthesis and investigate whether it can be scaled-up to be<br /> used as a screening method downstream of polymerase directed evolution experiments. The<br /> major advancement in this paper is that as a screening tool for polymerases, it also has the<br /> capability to provide detailed kinetic information on each of the polymerases, something that<br /> prior methods struggled to do. As a proof-of-principle, the authors simultaneously screen 96<br /> polymerases with 96 barcodes and extract kinetic data from their single-molecule profiling.<br /> This work has multiple merits. Notably, although the general framework is the same, the<br /> authors have made a series of changes to improve their system since their previously published<br /> work, that played a role in allowing them to make multiplexed measurements. The authors also<br /> creatively pull a variety of kinetic parameters from their single-molecule voltage traces that<br /> allow them to easily separate different polymerases after principle component analysis.<br /> On the other hand, the work has a couple of issues, detailed below, with regards to<br /> controls and clarity that would be helpful if addressed.<br /> Major Issues<br /> 1. The authors utilize DNA bases that are tagged to generate unique signals for recognition<br /> when captured and blocking the nanopore. From the principle component analysis<br /> tables (Supplementary Table 4a-c), it appears that the polymerases vary quite a bit with<br /> regards to processing different bases. At present, it is unclear whether these kinetic<br /> differences are being caused by differences between structures of the bases, or whether<br /> they are caused by differences between structures of the tags. One control would be to<br /> repeat one set of experiments with the tags shuffled between the bases and observe<br /> how reproducible the results are. This would give the reader a sense of how much<br /> measurements are being affected by the tags used for this technique.<br /> 2. For the experiment in Fig. 5, the authors end up showing that barcodes can be identified<br /> with a false positive rate of 13%. This is with a pilot experiment of 96 barcodes. From<br /> this data, it suggests that this technique would be difficult to scale-up any further, which<br /> may limit its usefulness – in fact even 96 barcodes may already be pushing the limit.<br /> From reading the paper, it is unclear if what is dominating this problem is the length of<br /> the barcode (i.e. limited sequence divergence due to 32-nt), or if nanopore sequencing<br /> accuracy is still a limiting factor. It would be great to see a small pilot experiment with<br /> longer barcodes to see if this could allow for improved accuracy, or some in silico<br /> statistical modeling extrapolating from their current data (e.g. length of barcode x<br /> required to accurately separate number of polymerases y with a false positive rate of z).

quite flexible, it still is unaddressed whether this repeated jostling of the tag<br /> (linked directly to the base) would affect kinetic measurements. Overall, it would be nice<br /> to see some measurements compared or benchmarked against a more well-established<br /> technique side-by-side (e.g. single-molecule optical trap), just to see if the data matches<br /> up or not. Notably with a parallel technique, you can also do the control of tagged vs.<br /> untagged nucleotides, thus unambiguously determining the potential effect of a tag on<br /> polymerase kinetics.<br /> Minor Issues<br /> 1. In the abstract the authors mention they “develop a robust classification algorithm that<br /> discriminates kinetic characteristics of the different polymerase variants.” It is unclear<br /> what this is referring to in the paper. If it is simply the principle component analysis then<br /> saying “develop” may be a bit overreaching.<br /> 2. Rather than referring to prior publications this publication should have in the<br /> supplement and/or methods the exact nucleotide + tag combinations used in this paper.<br /> 3. It is unclear after reading the methods why there are three separate PCA tables per<br /> polymerase in the supplement.<br /> 4. It is unclear what is the difference between tdwell and tag capture dwell from the written<br /> descriptions in the paper. Highlighting the difference visually in Fig. 3a (as was done<br /> with the rest of the kinetic variables) would help the reader clearly understand exactly<br /> what is being measured.<br /> 5. A table of the 96 barcodes used for Fig. 5/6 should be added to the supplementary<br /> materials.<br /> 6. The numbers in Supplementary Table 5 do not add up correctly – the authors should<br /> take a look again and make sure the correct numbers are present.<br /> 7. In Fig. 2 the authors experimentally calculate BMPI cut-offs for 3 different barcodes and<br /> get 0.8, whereas in Supplementary Fig. 8 the authors do an in-silico calculation for BMPI<br /> cut-off and still get 0.8. One would imagine that increasing the number of barcodes<br /> would require a stricter BMPI cut-off. Some sort of commentary on this, or perhaps<br /> reanalysis of the multiplexed data with a stricter BMPI cut-off could be helpful.<br /> 8. In Supplementary Fig. 12 the authors show a protein gel of their pore-polymerase<br /> conjugates. The bands show that post-linking, there is still a decent amount of nonlinked<br /> polymerase. In the methods there is no mention of a size exclusion purification<br /> step post-conjugation. Are the authors loading a mixed population onto their chips? This<br /> needs to be clarified.<br /> 9. In Supplementary Table 7 the tag capture dwell (TCD) variable missing.

Reviewer 3.

In the study titled Multiplex single-molecule kinetics of nanopore-coupled<br /> polymerases, Palla et al. developed and demonstrated the use of a<br /> single-molecule sequencing technology for the high-throughput identification of<br /> DNA polymerases with desired kinetic properties. Nanopore sequencing reactions<br /> were carried out on complementary metal-oxide-semiconductor (CMOS) chips, each<br /> of which contains over 30,000 individually addressable electrodes, thereby<br /> allowing sequencing reactions to be carried out on each chip in a multiplex<br /> fashion. Each DNA polymerase was coupled to an ?-hemolysin pore and bound to a<br /> 51 bp circular barcoded ssDNA template (CBT). The template is bound to a primer,<br /> thus enabling the incorporation of the appropriate nucleotides by the polymerase<br /> into the ssDNA template. Since each ssDNA template is circular, multiple<br /> iterations of the barcoded region can be observed during the sequencing of each<br /> template. Furthermore, each of the four nucleotides are uniquely tagged. When a<br /> nucleotide is being incorporated into the template ssDNA, the tag attached to<br /> the nucleotide is captured in the nanopore, thereby decreasing the conductance<br /> through the pore. Such a decrease in conductance is measured by an analog to<br /> digital converter (ADC) placed parallel to the sequencing circuit, and the<br /> recorded ADC values are then converted into a fraction of open channel signal<br /> (FOCS). Because the four tags are different from each other, the corresponding<br /> FOCS generated differ from each other as well, and can thus be used to<br /> distinguish the nucleotides from each other. Using a software, the FOCS is<br /> converted into raw reads. Then, using a barcode classification algorithm, each<br /> qualified raw read is compared to any template of the experimenter’s choice.<br /> Aligning a raw read to the correct template will more likely generate a higher<br /> barcode match probability index (BMPI) value for that read, while aligning a raw<br /> read to an incorrect template will more likely generate a lower BMPI value for<br /> that read. As such, for each sequencing experiment, the average BMPI value<br /> (derived from comparing raw reads to a template) can be used to identify the<br /> template to which the polymerase is bound. And if each polymerase-template pair<br /> is unique, the average BMPI value can then be used to identify the polymerase as<br /> well. Lastly, the authors defined a set of five kinetic parameters that can be<br /> measured during the course of a sequencing reaction. Because different<br /> polymerases are likely to differ from each other with respect to these kinetic<br /> parameters, comparison of the parameters between polymerases can help identify a<br /> polymerase with the desired properties.

To develop their nanopore sequencing technology, the authors first showed that<br /> the BMPI value can be used to identify a CBT. Thereafter, the authors showed<br /> that, after a polymerase is loaded with a particular CBT, the loaded CBT will<br /> not get replaced by another CBT that is present in the same reaction volume,<br /> thereby demonstrating the potential for multiplexing this sequencing platform.<br /> Then, as stated above, the authors defined five kinetic parameters that can be<br /> measured during sequencing. Using Principle component analysis (PCA), the<br /> authors showed that these kinetic parameters differ between polymerases, thus<br /> indicating the ability of this platform to distinguish polymerases based on<br /> these parameters. To demonstrate the multiplex potential of their platform, the<br /> authors conducted multiplex experiments in which different sets of CBTs were<br /> loaded onto three different polymerases. These pore-polymerase-CBT conjugates<br /> were then pooled prior to loading onto the CMOS chip. Notably, these experiments<br /> showed that CBTs can be identified in a pooled format. Finally, as a practical<br /> demonstration of the capability of the platform to identify, in a multiplex<br /> format, polymerases with properties of interest, the authors generated 96<br /> polymerases, each of which was then loaded with a unique CBT. In this multiplex<br /> reaction, the authors identified four polymerases that are potential candidates<br /> for further development for use in DNA amplification methods.

Here are some thoughts I had while going through the preprint:

1. The authors state that, in their pooled 3-plex sequencing experiment, about<br /> 67% of the raw reads (n = 418) were identified as any of the three barcodes used<br /> in the experiment. In Supplementary Table 5, it can be seen that, for total<br /> RPol-CBT, [the percent of raw reads with BMPI > 0.8] = [the number of raw reads<br /> with BMPI > 0.8] / [the total number of raw reads]. That is, 66.9% = 280 / 418.<br /> However, the table shows that the total number of raw reads for the RPol1-CBT1<br /> alone is 418. If this is the case, it is unclear to me how the total number of<br /> raw reads for all three RPol-CBTs (RPol1-CBT1, RPol2-CBT2, and RPol3-CBT3) can<br /> be 418 if that of RPol1-CBT1 alone is already 418.

2. On p19, line 1, I believe that “Experiments 1 and 3” should say “experiments<br /> 1 through 3”, since in all three of these experiments, the raw reads were<br /> compared to the correct template, as noted in the legend below the figure<br /> (Supplementary Figure 6b).

3. In Supplementary Figure 6a, the color-coding legend indicates that the<br /> barcode region of the ssDNA template is highlighted in grey. However, nothing in<br /> the ssDNA sequence was highlighted in grey.

4. The data presentation for Supplementary Figure 6b along with the associated<br /> text description are a bit confusing too me. It is stated that, in experiments<br /> 1-3, the reads were compared to the correct templates, while the reads in<br /> experiment 4-5 were compared to the incorrect templates shown in Supplementary<br /> figure 6a. In this part of the study, the three pore-polymerase-CBT conjugates<br /> (RPol1:CBT1, RPol2:CBT2, and RPol3:CBT3) were first individually assembled, and<br /> then pooled and loaded onto the CMOS chip. Assuming that this has been done for<br /> each of the five experiments indicated in Supplementary Figure 6, then there is<br /> really no universally correct template (e.g., comparing CBT1 to the raw reads of<br /> a pooled experiment would only yield higher BMPI values for a third of the reads<br /> (i.e., only for RPol1:CBT1-derived raw reads). Are the raw reads from experiment<br /> 1, 2, and 3 compared to CBT1, CBT2, and CBT3, respectively? This wasn’t<br /> specified anywhere in the text.

5. Regarding Figure 6a, the authors stated that, out of all of the 96<br /> polymerases screened in this multiplex experiment, 20 polymerases were<br /> identified as having detectable activity (p23, bottom). However, as depicted in<br /> Figure 6a, there are only 17 polymerases for which the associated barcodes were<br /> counted (i.e., there are only 17 yellow bars). Thus, it is unclear to me where<br /> the number “20” is derived from.

6. In the PCA analysis in Supplementary Figure 11, the authors tried to map the<br /> sequencing data derived from the multiplex experiment back to those derived from<br /> the singleplex experiments involving the same three polymerases. The sequencing<br /> data set for the second barcode set (CBT33-64) could not be mapped back well,<br /> and it was stated that this might be due to the high false positive rate of<br /> barcode identification for that barcode set. That being said, as indicated in<br /> Supplementary Table 6, the false positive rate for RPol1:CBT1-32 and<br /> RPol2:CBT33-64 are 11.94% and 16.06%, respectively. Thus, if the author’s claim<br /> is true, the inability to map back is due to a 16.06% – 11.94% = 4.12%<br /> difference in the false positive rate. It is unclear to me if a 4.12% difference<br /> in false positive rate would really lead to such a dramatic difference in the<br /> ability to map back. Also, it is unclear if this higher false positive rate<br /> arose due to polymerase (RPol2), the templates (CBT33-64), both, or neither.<br /> Logically, it seems unlikely that the rate would be due to the CBTs since it is<br /> unlikely that the middle third of the set of 96 CBTs would just happen to give<br /> higher false positive rates in comparison to the other two thirds. An easily<br /> accomplished comparison between two polymerases would be to load both<br /> polymerases with the exact same set of CBTs, and then compare the derived false<br /> positive rate for each polymerase. Then, one can repeat the experiment but using<br /> a different CBT set. This will help narrow down whether the observed false<br /> positive rate is due to the polymerase or the CBTs themselves.

7. Regarding Figure 5, it is unclear to me the exact differences between 5a and<br /> 5b. I see that the data presentation is a little different, but I’m not sure if<br /> both figures are necessary here given that both deal with the same three<br /> polymerases as well as the same set of 96 CBTs.

8. It is stated that the surface of each individual CMOS chip contains 32,768<br /> electrodes (p30) and that the chip contains thousands of pores (p4). Now, as<br /> mentioned in the measurement setup (Figure 1a legend), the measurement setup<br /> requires two electrodes (a counter electrode and a working electrode). Given<br /> this, it is unclear to me what proportion of those 30,000-some electrodes are<br /> working or counter electrodes. I believe that clarification on this would help<br /> the reader get a better sense of the number of pore-polymerase-CBT conjugates on<br /> each individual CMOS chip, and thus, a better sense and appreciation of the<br /> multiplex scale.

9. On p30, under the section Pore-polymerase-template complex formation,<br /> “SpyCather” should say “SpyCatcher” (i.e., a “c” is missing).

On 2020-05-05 18:33:30, user Taekjip Ha wrote:

Thank you very much for sharing your interesting manuscript!<br /> We used your preprint as one of the journal club papers in the Single<br /> Molecule & Single Cell Biophysics course for graduate students of Johns<br /> Hopkins University during the Covid-19 lockdown. Students also practiced peer<br /> reviews as the final assignment. I am submitting their formal reviews here <br /> and hope you find them useful.

Taekjip Ha

Reviewer 1.

Summary:<br /> In this study, the authors describe the development of a tool that can be used<br /> to observe and measure single-moleculeCap-dependent and Cap-independent<br /> translation, concurrently, in live cells. The authors spend a considerable<br /> portion of themanuscript on controls to rule out ribosome run-through from the<br /> first ORF to the second, swapping tags, and addressingfluorescent bleed through,<br /> which is appreciated. They also present novel measurements including translation<br /> site localizationand diffusion, ribosome occupancy, and elongation rates. The<br /> translation elongation measurements are particular striking giventhat an<br /> analogous single-molecule experiment has not been demonstrated previously.<br /> Overall, this study is elegant in its useof the bicistronic construct and has<br /> potential applications in studying endogenous eukaryotic IRES elements, such as<br /> incircRNAs.

Given that, there are certain points of clarification that should be addressed<br /> or expanded upon in the manuscript.

Major comments:

1. In the section titled “IRES and CAP translation sites stretch out as<br /> ribosomes load”, the authors show evidence thatCap-only and IRES-only<br /> translation sites “stretch out as ribosomal content increases”. However, in a<br /> different section of themanuscript where ribosome occupancy is measured, it is<br /> shown that Cap+IRES translation sites have more ribosomes per RNAmolecule than<br /> Cap-only or IRES-only translation sites. However, the “stretching” measurements<br /> do not reflect this difference:Figure 3C/D show that the single modes of<br /> translation have a greater average stretch than dual-mode translation<br /> sites.Additionally, the authors make no indication that the Cap and IRES sites<br /> should counteract each other in any way. The authorsdo not adequately address<br /> this disconnect.
2. In the discussion, the authors state “One of the most interesting<br /> observations with our biosensor was that Cap translationactually enhances that<br /> of the IRES, but not the other way around”. In Figure 6F, the authors measure<br /> fluorescent intensitiesof translation sites under stress conditions and show<br /> that Cap-only translation decreases while IRES-only translationincreases in the<br /> presence of cellular stress. In the caption for Figure 6F, the authors state<br /> “Cap + IRES intensitiesrepresent the Cap translation intensity in spots with<br /> both Cap and IRES intensities”. The data in the corresponding “CAP-IRES”panels<br /> show that the Cap intensities differ greatly (increases, especially in the<br /> presence of arsenite) when IRES translationis active. Does this not indicate<br /> that IRES translation enhances that of the upstream Cap-dependent ORF?
3. In the Results section for RNA diffusion measurements, one inconsistency<br /> that the authors should address is that Cap-onlyand IRES-only sites display<br /> indistinguishable MSDs. The authors state “this overall trend suggests the<br /> mobility of ourbiosensor is mainly dictated by the degree of translation rather<br /> than the type of translation”. However, in the ribosomeoccupancy experiments, it<br /> is shown that Cap-only translation sites contain almost triple the number of<br /> ribosomes as comparedto IRES-only. This is a clear difference in the “degree of<br /> translation” but does not agree with the MSD data.

Minor comments:<br /> 1. Under stress conditions, Figure 6D shows that Cap-only translation sites<br /> decrease in intensity while IRES-only translationsites increase in intensity.<br /> Presumably, the following analysis should be obtainable with the same data set.<br /> What is the“stretching” measurement at these sites? Given statements by the<br /> authors, Cap-only translation sites should be more compactunder stress<br /> conditions compared to Cap-only translation sites without stress. The inverse<br /> should be true for the IRES-onlytranslation sites. <br /> 2. There is no description of the method used to measure the distance for RNA<br /> stretching. From the illustration in Figure 3A,it appears that the measurement<br /> is made from the center of each fluorescent spot to the center of the other, but<br /> an explicitdescription of the method would be appreciated.

Reviewer 2

Peer review of the preprint, “Quantifying the spatiotemporal dynamics of IRES<br /> versus Cap translation with single-molecule resolution in living cells”<br /> Koch, A. et al. investigate the unknown single molecule dynamics of viruses<br /> hijacking host cells using internal ribosome entry sites (IRES). In order to<br /> determine the dynamics between IRES and Cap mediated translation, Koch, A. et<br /> al. developed a novel method in which the kinetics of IRES and Cap mediated<br /> translation can be visualized in real-time. They developed a bicistronic<br /> biosensor containing two separate open reading frames with repeated epitopes.<br /> Each of these open reading frames are differentially translated either in a Cap<br /> or IRES mediated manner. Depending on which open reading frame is translated,<br /> different fluorophore labeled antibodies will bind to the epitope<br /> co-translationally and on the emerging nascent chain. As a result, the biosensor<br /> will be decorated with different fluorophores depending on which open reading<br /> frame is being translated. From this data, Koch, A. et al. determined the mode<br /> of translation depending on which fluorophores are observed to colocalize with<br /> the transcript. Using this new technique, the authors demonstrated that two open<br /> reading frames can be simultaneously translated, and two different manners of<br /> translations can be visualized on a mRNA. Normally, two to three times more<br /> ribosomes are recruited to Cap mediated translation sites as compared to IRES<br /> mediated translation sites; however, during oxidative and ER stress, IRES<br /> mediated translation is favored. Both Cap and IRES mediated translation sites<br /> are stretched out with increasing ribosome load and both sites have similar<br /> mobilities, spatial distributions and elongation rates. Additionally, the<br /> authors also suggest that upstream translation can positively impact downstream<br /> translation. <br /> The authors ingeniously combine common techniques used in ensemble experiments,<br /> such as bicistronic transcript, with nascent chain tracking to develop a method<br /> to visualize different modes of translation in real-time in vivo with single<br /> molecule resolution. This technique was used to understand the dynamics of IRES<br /> mediated translation, but this method also has broad applications. The technique<br /> developed by Koch, A. et al. seems promising and exciting. In general, the<br /> article is well written, and I recommend this work to be published; however, a<br /> few clarifications and improvements are needed to enhance the clarity and<br /> development of the text before the work can be published. <br /> The abstract concisely explains the importance, goals, methods and conclusions<br /> of the work. The introduction nicely explains the aims of the paper and<br /> importance of the novel technique developed as well as the importance of<br /> determining the mechanism by which viruses use IRES to hijack the cell’s<br /> translational machinery. Koch, A. et al. also provide context for which the work<br /> has been done, such as previous ensemble experiments. The ensemble experiments<br /> lacked the spatial temporal resolution needed to determine the kinetics and<br /> dynamics of IRES translation in real-time; yet, the authors satisfy this gap in<br /> knowledge using a new method. However, the authors did not provide a comparison<br /> of the data collected in the ensemble experiments and the data collected in this<br /> work using the new technique. It would be important to understand if the<br /> previous ensemble experiments support the data collected using this new<br /> technique. This could provide further support and verification for the new<br /> technique. <br /> The authors provide an adequate amount of background needed to understand the<br /> importance and context of an experiment. The experiments and results are clearly<br /> described. However, there are a few points that need clarification or further<br /> explanation to determine the validity and reasoning of the experiments and<br /> conclusions, including why were lysine demethylase KDM5B or kinesin like protein<br /> Kif18b used in the open reading frame as opposed to other proteins or why did<br /> the open reading frames not encode for the same protein, but with different<br /> tags? It would have been better for both open reading frames to encode for the<br /> same protein with different tags, so that the length of open reading frame from<br /> the 5’ Cap to the first stop codon would be roughly the same size as the length<br /> of the open reading frame from the IRES site to last stop codon. This may have<br /> helped clarify and provide a fair comparison between the amount of stretching on<br /> the different translational sites and the number of ribosomes at each<br /> translation site. This would also eliminate the open reading frame size as a<br /> possible contaminating factor. This may also explain the different ratio of<br /> ribosomes recruited to the Cap and IRES translation sites when the original tag<br /> and switch tag were used in Figure 5. When the switch tag was used, the ratio of<br /> ribosomes recruited to the Cap versus IRES translation sites was 2.8, but when<br /> the original tag was used, the ratio of ribosomes recruited to the Cap versus<br /> IRES translation sites was 2.1. This could be due to the different open reading<br /> frame lengths including the 24X SunTag-Kif18b being longer at 8kb and thus<br /> allowing more space on the translation site for ribosomes as compared to the 10x<br /> flag-KDM5B’s translation site length at 5kb. Additionally, in Figure 3, the<br /> authors try to answer a difficult question by measuring the distance from<br /> actively translating ribosomes to the 3’ end of the transcript to determine how<br /> the translation sites stretch with increasing ribosome load; however, the<br /> authors do not account for the different lengths of the translation sites.<br /> Understandably, it’s difficult to measure the distance of translation site<br /> stretching. It could be useful to place stem loops labeled with fluorophore<br /> tagged antibodies or a dCas9 labeled with a fluorophore before the IRES site, so<br /> that more precise measurements of the translation site stretching can be<br /> obtained, if feasible. <br /> The authors suggest that IRES and Cap mediated translation sites stretch out<br /> with increasing ribosomal load as shown in Figure 3D. Yet, there is an outlier<br /> in the general trend when the Cap translation site is examined on Cap + IRES<br /> translation sites in Figure 3C (top plot). As the ribosome load increases, the<br /> Cap translation site stretches from 130 nm to 150 nm, but then retracts to 144<br /> nm. It is true that the general trend is that as the ribosome load increases,<br /> the translation site stretches, but this outlier should be acknowledged.<br /> Additionally, clarification or an explanation should be provided to explain why<br /> single mode translation sites, shown in Figure 3D are stretched out longer than<br /> the translation sites in the IRES + Cap translation sites, shown in Figure 3C.<br /> Additionally, the authors should address possible reasons why the Cap<br /> translation site is not two to three times more stretched than the IRES<br /> translation site given that two to three times more ribosomes are recruited to<br /> the Cap translation site.<br /> Additionally, the authors should address the precision of the technique and<br /> data, meaning how they analyzed the data when more than one ribosome was on a<br /> translation site. The authors should address how they analyzed the data when<br /> more than one fluorophore was present at single location. Did the authors<br /> measure the photobleaching steps at that location or did the authors take the<br /> average distance from a group of nearby fluorophores to measure the distance<br /> from the actively translating ribosomes to the 3’end of the transcript? It may<br /> be the case that a group of fluorophores or ribosomes may not be resolved at one<br /> location, if so, how did the authors analyze this data. The authors should<br /> acknowledge or address a limitation in the experimental design that the<br /> technique relies on upon measuring the intensity of the fluorophore labeled<br /> antibodies binding to a nascent chain that has potentially many epitope binding<br /> sites as the ribosome translates the transcripts. The longer time the ribosome<br /> translates the transcript, the more epitopes appear on the nascent chain. As a<br /> result, a higher intensity on a translation site does not always mean more<br /> ribosomes. It could mean that a ribosome has translated more of the transcript<br /> resulting in a longer nascent chain with more epitopes and possible fluorophore<br /> labeled antibodies binding to the nascent chain resulting in an increase in<br /> signal intensity. <br /> Koch, A. et al. provide proper controls to determine the total amount of<br /> transcripts in the cell by labeling transcripts at the 3’ end. However, it would<br /> behoove the authors to provide a few additional control experiments or<br /> explanations. It would be beneficial for the authors to provide an explanation<br /> of the choice and amount of tags. SunTags, specifically v1 SunTag, are known to<br /> aggregate1 which may negatively impact the data or the conclusions drawn from<br /> the data. Similar experiments can be performed with different tags as a negative<br /> control to verify that the choice of tags does not influence the data. The<br /> number of tags in each open reading frame are different, which may affect the<br /> amount of fluorophore labeled antibodies that bind to the nascent chain and<br /> could affect the observed intensity. A control experiment should be performed to<br /> account for the number of epitope tags in each reading frame and the resulting<br /> intensity, before the amount of translation or ribosomes can be determined and<br /> compared at the different translation sites. The authors do address this concern<br /> in Figure 5 by using the original and switch tag. Additionally, the authors<br /> should verify that adding MS2 stem loops to the 3’ end of transcript does not<br /> affect the stability, localization or translation of the transcript. The authors<br /> provide a control experiment to determine that ribosome is not continually<br /> translating through two open reading frames and that IRES can independently<br /> recruit ribosomes. The authors also suggest that upstream translation can<br /> enhance downstream translation of non-overlapping open reading frames. This is<br /> explained though simulations, but it would improve the authors’ credibility if<br /> this conclusion can also be verified experimentally by using a negative control,<br /> such as removing the 5’ Cap from the transcript and determining the number of<br /> ribosomes recruited or translated on the transcript, if feasible and the<br /> transcript is stable. <br /> Finally, the authors beautifully explained how physiological conditions, such as<br /> oxidative or ER stresses, during a viral infection could affect IRES and Cap<br /> mediated translation. The authors determined that IRES mediated translation was<br /> enhanced as compared to Cap mediated translation. If feasible, it would be<br /> beneficial to conduct the same stretching experiments under oxidative and ER<br /> stress conditions to further support the conclusion and provide a fair<br /> comparison to the data under normal conditions.<br /> Overall, the article is well written; however, the article’s layout can be<br /> improved to further clarity and develop main points in the paper. Initially, the<br /> authors suggest that that are three times more Cap mediated translation events<br /> as compared to IRES mediated translation events. Then the authors explain the<br /> biophysical properties of the translation sites as well as the elongation rate<br /> at these sites. Next, the authors suggest that two to three times more ribosomes<br /> are recruited to the Cap mediated translation site as compared to the IRES<br /> mediated translation site as shown in Figure 5. However, the authors reference<br /> this last point throughout the beginning of the paper. I suggest that the<br /> authors discuss and present the data in Figure 5 earlier in the paper such as<br /> after Figure 1. This would improve the flow and logical progression of a key<br /> point in the paper and would also provide an explanation as to why the authors<br /> chose to present the data in Figures 3 and 4. Additionally, Figure 5 would also<br /> support the data provided in Figure 1. <br /> In general, the authors elegantly describe a novel technique and its application<br /> in this article. This novel technique has potential to advance the field by<br /> providing single molecule analysis in real-time in living cells. The conclusions<br /> and findings of Koch, A. et al. are significant and important for determining<br /> the dynamics between IRES and Cap mediated translation. I look forward to<br /> reading the work when its published.

Reference <br /> 1. Tanenbaum, M. E.; Gilbert, L. A.; Qi, L. S.; Weissman, J. S.; Vale, R.<br /> D., A protein-tagging system for signal amplification in gene expression and<br /> fluorescence imaging. Cell 2014, 159 (3), 635-646.

On 2020-03-11 17:23:16, user Debra Hansen wrote:

Terrific paper, great work. Since obtaining structures of membrane proteins is much more difficult than most soluble proteins, including the following technical details in the final publication will be helpful to the research community. (1)How membrane proteins migrate in gels and how well they transfer in Westerns are affected by the compositions of loading buffer, running buffers, transfer buffer; acrylamide concentration (stacking & separating gel). These details seem trivial for most papers, but are important for working with membrane proteins. (2)Exact location of the His-tag in the sequence. His-tags are often not included in the FASTA sequence when the structure is entered into the Protein Data Bank. The His-tag was placed at the "N-terminus", but it can't be at the very N-terminus, since the signal peptide is cleaved in PilQ.

On 2019-12-31 18:11:21, user Paul Schanda wrote:

This is a very interesting work on the plasticity of the SurA chaperone in its apo state and binding outer-membrane proteins (OmpX, OmpF). The paper has a couple of nice experiments, and in particular the combination of techniques (smFRET, cross-linking mass spectrometry (XL-MS), mass-spec-detected hydrogen-deuterium exchange, a bit of MD simulations) is appealing.

Detecting and localizing chaperone-client protein contacts is a difficult endeavor and the authors primarily use mass-spec methods to this end. As I am not an expert with mass spectrometry I have questions, as some of the data are not entirely convincing to me.

1. the Lys-based XL-MS results are quite puzzling to me, and they even seem to be in contradiction to the "tag-transfer" XL-MS results. In particular, Figure 4 shows cross-linking of OmpX to almost all parts of SurA, including residues that are clearly turned outwards (in the structure shown, at least). In contrast, the experiment that uses MTS-diazirine and UV-cross linking shows a much more narrow cross-linking pattern. How should one interpret this?

Should one basically drop the results from the Lys-cross linking (with DSBU) altogether, as it seems to me that it may contain quite a number of false positives ?

1. the HDX-MS results are also a bit unclear to me. The mass uptake in D2O are fairly small, and the differences with/without client protein appear very small. For the shown peptide fragments (about 20 residues long) the differences in mass uptake with/without OMP are well below 1 Da (i.e. well below one hydrogen atom) over 100 minutes. In some cases, the difference is essentially zero in Figure S10 (e.g. first line second plot, or second line, plots 1 and 3, where there is even a cross-over, suggesting that the error bars are underestimated?).<br /> I do not have much experience with mass-spec detected HDX. How reliable are such data?

2. I was curious why the authors have not tried to detect FRET effects between the chaperone and the OMP, i.e. having one dye on each of these two proteins. Such an experiment may allow them to further localize the binding site.

Congratulations to this interesting paper.

On 2019-08-05 09:25:37, user Rajendra wrote:

DiExM, the next big leap in ExM development and application. Nice blog by NIH Director: https://directorsblog.nih.g.... DiExM will greatly progress nanoscale imaging and diagnostic pathology.

On 2019-08-02 17:36:17, user Kathleen wrote:

WOW! Differential Expansion Microscopy-Machine Learning (DiExM). Nice work!! Anisotropic expansion of up to 8-fold linear and >500-fold volumetric. Important study utilizing expansion microscopy (ExM) for precise nano scale imaging of cellular structures. Opinion on ExM posted by Francis Collins https://directorsblog.nih.g.... DiExM will greatly progress nanoscale imaging and greatly progress diagnostic pathology.

On 2019-07-30 15:40:13, user Ranya wrote:

WOW! Differential Expansion Microscopy-Machine Learning (DiExM). Nice work demonstrating anisotropic expansion of up to 8-fold linear expansion. Important study utilizing expansion microscopy (ExM) for precise nano scale imaging of cellular structures. DiExM will greatly progress diagnostic pathology. The scope of ExM is highlighted by NIH Director Francis Collins in his recent blog https://directorsblog.nih.g...

On 2019-06-24 21:29:29, user ThePatrickWatsonLab wrote:

Hello! Very nice paper-- we are also interested in post-translational modification of SR proteins. I am wondering if you could provide more clarity regarding your phos-tag gels. They way they are currently labeled, they are difficult to interpret. Is it possible to include size markers?

On 2018-12-10 17:29:30, user Christopher Ryan Douglas wrote:

The research goal of the manuscript: ‘CRISPR/Cas12a-assisted PCR tagging of mammalian genes’, is to demonstrate the efficiency of a CRISPR/Cas12a endonuclease system using PCR cassettes and endogenous homologous recombination mechanisms for readily tagging genes in mammalian cell lines. Previous methods often use extensive cloning techniques that are expensive and/or laborious, while the pursued method incorporates pre-designed plasmids with tags that can then be used with unique M1 and M2 oligos for easy PCR cassette development and CRISPR/Cas12a, gene-specific tag integration. In the paper they hypothesize that (1) successful, on-target integration is equivalent to current models in yeast using the CRISPR/Cas9 system, (2) is dependent on homology dependent repair mechanisms, (3) that efficiency can be further improved through the use of different modifications, including: removing the ATG start codon of the fluorescent tag (i.e. mNeonGreen), increasing the length of the homology arms, adding bulky protein modifications at the 5’ end of M1 and M2 oligos; and (4) the tested system can obtain human genomic coverage of 98.1% by including different species-specific CRISPR/Cas12a variants. They used tag-specific immunofluorescence localization and Anchor-Seq to assess on-target integration success; and they utilized PCR and PAGE to create and purify the PCR cassettes used for integration. <br /> (1) The findings state that for the tested genes there was an observed 0.2-13 % with correct tag-specific localization as imaged using the tag fluorescence. This could be further increased up to 60% using previously established antibiotic selection with Zeocin (Puromycin also tested). The authors used a restriction digest approach utilizing DpnI or FspEI to target and eliminate Dam methylated plasmids, which is assumed to be those plasmids existing prior to amplification. It would be useful if they provided some reference demonstrating that the non-methylated site isn’t targeted. If it was targeted to some extent, this could result in significantly more fragments of the selection marker plasmid being present. It is possible that these could ligate together and form plasmids that could confer resistance without the target gene sequence being present. Further information clarifying the purification procedure of these samples would eliminate this concern. <br /> Another criticism is that it is never directly stated how it compares to the current CRISPR/Cas9 system used in yeast. What are the comparable efficiencies both compared to the CRISPR/Cas9 system in yeast and mammalian systems? The use of resistance tags helps with amplification and population percentages expressing correctly is relatively high, but if the paper could provide some more context for comparing the relative efficiency of the system compared to other approaches in yeast and mammalian systems, it would elevate the impact of the paper.<br /> (2) The role of HDR is demonstrated by first removing the homology arms of the M1 and M2 oligos and then altering them to include 5’ overhangs compatible with CRISPR/Cas12a integration. Only residual amounts of non-homologous end-joining (NHEJ) or other DNA repair mechanisms were observed, indicating the importance of HDR. It was also observed that the homology arms would work for 30nt and optimally greater than 60nt.<br /> By removing the ATG start codon for the mNeonGreen protein, the diffuse non-specific cytoplasmic fluorescence could be reduced significantly. The residual amount of expression observed is explained as coming from start codons in the homology arms or the crRNA within the open reading frame of the mNeonGreen. It could also be possible that the system is promiscuous and targeting multiple dependent sites dependent on the crRNA, which has been reported to a limited extent for certain targets in the CRISPR/Cas9a system1. Despite abounding evidence of the kinetic specificity of the alternative CRISPR/Cas12a system employed here, there may be residual off-target effects that persist for specific sequences2. While not relevant for creating new cell lines using this system, it may be worth discussion for future work and in more complex systems, such as, in vivo.<br /> (3) With further modifications of the nucleotides using phosphorothioate bonds and biotinylating 5’ ends of the M1/M2 oligos, they assessed the efficiency of tagging of several genes, including: CLTC, and DDX21. They observed a 2-3x fold increase in efficiency and a decrease of observed diffuse cytoplasmic, non-specific fluorescence. Based on the data presented in Figure 3C, it appears that the phosphorothioate bonds were far more important for both increasing the on-target integration efficiency and reducing the non-specific diffuse, cytoplasmic fluorescence. While omitted, it may be worth including data for the phosphorothioate bond (i.e. 10S) and Biotin combination, as it might have provided some idea about the limitation of such modifications to increase the efficiency of the system. <br /> (4) In most tagging systems, C-terminal tagging is used and the CRISPR/Cas12a system needs to cut a protospacer associated motif (PAM) within a potentially short 17nt sequence on either side of the gene stop codon in humans. Given that the authors used a Lachnospiraceae bacterium ND2006 (i.e. TTTV) for all previous experiments, they confirmed that it could only obtain 43.2% genomic coverage. When adding the genomic coverage of AsCas12a_TATV and the AsCas12a_TYCV/LbCas12a_TYCV combination, only 71.6% was collectively covered. Upon using an extended search space in the 3’-UTR region, 98.1% coverage was observed. To compensate for this extended search, the authors noted the need to adjust the M2 oligo so that a small deletion occurs at the cleavage site to prevent additional cleavage events at the site by the CRISPR/Cas12a. For future studies, it would be worth considering the relative efficiency and specificity of these different species-specific CRISPR/Cas12a variants to create a rule for differing to one of the variants in the case overlapping genomic coverage by two or more. Another criticism would be that the expanded search into the 3’-UTR does not necessarily account for the possibility of disrupting post-transcriptional regulatory units within the region. This could provide the need for additional variants that provide more collective coverage using the limited search space provided by the PAM.<br /> Overall, the paper carries significant impact and capably demonstrates the applicably of this PCR-based CRISPR/Cas12a system to mammalian systems, in vitro. Despite some small, potential issues with the specificity of the observed efficiency, the only major area of concern would be the possibility that the expansive genomic coverage obtained by including sites in the 3’-UTR could in practice compromise key post-transcriptional regulatory units in this region. This can be easily avoided through additional experiments demonstrating the lack of an effect on overall expression with the use of some or all observed PAM sites, and/or using additional Cas12a variants to obtain more genomic coverage without using the 3’-UTR regions.

References<br /> 1. Henriette O’Geen, Abigail S Yu, David J Segal. ‘How specific is CRISPR/Cas9 really?’. Current Opinion in Chemical Biology, Volume 29, 2015, Pages 72-78, ISSN 1367-5931, https://doi.org/10.1016/j.c....<br /> 2. Isabel Strohkendl, Fatema A. Saifuddin, James R. Rybarski, Ilya J. Finkelstein, Rick Russell. ‘Kinetic Basis for DNA Target Specificity of CRISPR-Cas12a’. Molecular Cell, Volume 71, Issue 5, 2018, Pages 816-824.e3, ISSN 1097-2765. https://doi.org/10.1016/j.m....

On 2018-07-05 14:19:41, user Scott Scholz wrote:

Fascinating. Aside from the tag effect on any particular protein, do you have any ideas about why N-terminally tagged proteins are more likely to be punctate in general? Or why C-terminally tagged are more likely to be vacuolar...etc?

On 2018-05-29 17:57:50, user TeresitaMPorter wrote:

CO1 reference sets have been updated to version 3:<br /> https://github.com/terrimpo...

Contains more species, more sequences, and more outgroup taxa including eukaryotes and bacteria.

On 2018-03-30 13:00:18, user Markku Varjosalo wrote:

This preprint was published in Nature Communications on 22th of March titled as “An AP-MS- and BioID-compatible MAC-tag enables comprehensive mapping of protein interactions and subcellular localizations”

On 2018-01-27 01:19:32, user Casey Greene wrote:

I reviewed this paper at a journal. I thought that the journal in question would make the review public, but perhaps that is only after the paper is accepted. In the interests of improving the discussion of papers before they become published, I'm posting my review here as well.

Confidential Competing Interests (required):<br /> None

Reveal reviewer identity to authors (required): Yes

General assessment and major comments (Required):<br /> The authors describe HAWK, a k-mer based approach to association analysis. The idea is certainly clever, and I can imagine this work as a jumping off point for other approaches to the analysis of genetic variants that differ between groups.

I have some concerns about how the work is presented. The method discusses k-mer association analysis as a technique for "sequencing data." Within the manuscript, the method is applied to simulated E. coli genomic data and to the 1k genomes dataset.<br /> - If the authors want to suggest that this works for E. coli, or other bacterial, data they should apply the method to real genome sequencing data from these organisms. It seems like plasmids that vary with the test condition could make the approach somewhat computationally expensive (they would need to be built from k-mers). It'd be nice to see A) if this works in practice; and B) how scaling is affected. If this is not intended to be used for real microbial data, then perhaps the authors should note this.<br /> - The only application in the manuscript is to whole genome data. It seems like this approach would be a relatively inefficient way to deal with RNA-Seq data. Should the domain be refined?<br /> - Is the approach expected to work with exome sequencing data? If so, it would be nice to see an example showing that the capture process doesn't introduce any systematic biases that affect the method's false positive rate.

I downloaded the software and it compiled successfully. It is a bit difficult to use. The documentation is also sparse. It would be helpful to have a wrapper script that would handle the most common workflow as well as documentation with one fully worked example. The version of the source code associated with the published paper should be archived to figshare, zenodo, or a similar service.

Some assertions are made with regard to computational cost of competing methods in the intro. It would be helpful to me to see some benchmarking of HAWK.

"We provide scripts to lookup number... as future work." This is fine to leave for the future, but can you at least provide some documentation of these scripts in the repository's README?

Lines 277-280: is it possible that certain samples have different contamination? I'm not disputing that this is one possible explanation, but it doesn't seem like other possibilities (contamination, etc) have been ruled out to this point.

Minor Comments:<br /> In "Counting k-mers", what is a sample for "appear once in a sample." Is this once in a condition, or is there a first stage of sample filtering before the k-mers are aggregated?

The github repo contains DS_Store files. This should be added to .gitignore

Both the GPL v2 and v3 licenses appear to be included with the CPP source code.

The source code on the website has a version number, but there are no tags in the github repository. Please tag with the version number.

In "verification with 1k genomes data": I think line #169 is referring to significant differences between the YRI and TSI samples using the standard calling algorithm. This paragraph could be reworded for clarity.

typo: "While upto 20%"

On 2017-10-28 16:51:14, user Lionel Christiaen wrote:

Student #4<br /> 1. Genetic design: Homie-dependent long-distance regulation<br /> a. What is the background knowledge?<br /> Homie-homie self-pairing interactions can orchestrate enhancer activation of a reporter<br /> b. What is the question or hypothesis addressed?<br /> Is physical proximity central to enhancer-promoter communication?<br /> c. What is the approach? Which methods does it employ?<br /> A transgene consisting of the eve promoter and the lacZ coding sequence is inserted at an attP site located 142 kb upstream of the eve gene.<br /> d. What were the observations and analysis? (i.e the raw data and analyses)<br /> Sporadic expression of LacZ mRNA is observed solely within the limits of the endogenous eve stripes.<br /> e. What are the interpretations?<br /> Activation of the lacZ reporter depends on the enhancers in the eve locus 142 kb away.

1. Visualization of transcription and enhancer-promoter dynamics<br /> a. What is the background knowledge?<br /> b. What is the question or hypothesis addressed?<br /> What is the connection between enhancer action and physical enhancer-promoter proximity?<br /> c. What is the approach? Which methods does it employ?<br /> Insertion of tags. An MS2 stem loop cassette and MCP fused to a blue fluorescent protein to visualize nascent eve transcripts. A PP7 stem loop and PCP fused to a red fluorescent protein to visualize nascent transcripts of lacZ and ParS/ParB DNA labeling system to mark the position of the lacZ reporter whether it's active or not.<br /> d. What were the observations and analysis? (i.e the raw data and analyses)<br /> In the blue channel it can be observed the transcriptional dynamics of the eve gene in the characteristic seven-striped pattern. The green channel trace the movement of the lacZ reporter within the nucleus and in the red channel lacZ expression is observed as a subset of nuclei in the eve stripes<br /> e. What are the interpretations?<br /> LacZ expression is restricted to nuclei that reside within one of the seven eve stripes.<br /> f. What are the conclusions about the biological processes being studied?<br /> There is a close connection between transcription and physical proximity

2. Spatial proximity is necessary for enhancer action<br /> a. What is the background knowledge?<br /> b. What is the question or hypothesis addressed?<br /> How enhancer action is related to spatial proximity?<br /> c. What is the approach? Which methods does it employ?<br /> Analysis of live images and replacing the homie sequence with lambda DNA of the same length<br /> d. What were the observations and analysis? (i.e the raw data and analyses)<br /> For the parS-lambda-lacZ they observe a bimodal distribution for the time-averaged physical distance but when the homie sequenced is replaced with lambda the distribution of the RMS distance is unimodal. None of the nuclei in control parS-lambda-lacZ embryos express lacZ.<br /> e. What are the interpretations?<br /> Homie pairing creates a local chromatin conformation that is permissive to transcription events by ensuring physical proximity between the eve enhancers and the promoter of lacZ<br /> f. What are the conclusions about the biological processes being studied?<br /> Eve enhancers must be in close proximity to the lacZ promoter in order to activate transcription.

3. Necessity for sustained physical association<br /> a. What is the background knowledge?<br /> b. What is the question or hypothesis addressed?<br /> What is the temporal relationship between enhancer-promoter proximity and transcriptional activation?<br /> c. What is the approach? Which methods does it employ?<br /> Measure of the mean distance between the green parS tag and the eve gene as a function of time and alignment of the nuclei with respect of time point when nascent transcripts could first be detected.<br /> d. What were the observations and analysis? (i.e the raw data and analyses)<br /> There is a convergence until the onset of transcription at which point the mean distance corresponds to an average separation of about 340 nm. Also, a drop in transcriptional activity of the lacZ reporter is accompanied by an increase in the mean distance between the ParS transgene and the eve gene.<br /> e. What are the interpretations?<br /> There is a close connection between the establishment of enhancer-promoter proximity and enhancer activation of transcription. <br /> f. What are the conclusions about the biological processes being studied?

4. Physical enhancer-promoter engagement leads to distinct topological conformation<br /> a. What is the background knowledge?<br /> Independent eve enhancers regulate individual stripes of the eve pattern along the embryo<br /> b. What is the question or hypothesis addressed?<br /> Is transcriptional activation associated with an additional step that promotes physical enhancer-promoter engagement?<br /> c. What is the approach? Which methods does it employ?<br /> Examination of nuclei from different stripes separately to explore the topology of the locus under different activating enhancers.<br /> d. What were the observations and analysis? (i.e the raw data and analyses)<br /> Different distances in nuclei belonging to different stripes are observed. The distance between the eve gene and the parS tag of the inactive lacZ reporter in stripe 5 is shorter than the observed for nuclei in stripes 4/6 and 3/7 for which the enhancers are located farther away from the parS tag<br /> e. What are the interpretations?<br /> Eve enhancers directly engage the endogenous eve promoter to activate transcription and that in each eve stripe a distinct topological conformation is adopted<br /> f. What are the conclusions about the biological processes being studied?

5. Promoter compositions has phenotypic consequences<br /> a. What is the background knowledge?<br /> The eve stripe enhancer drives expression from two different eve promoters, one for the endogenous eve gene and the other for the lacZ reporter.<br /> b. What is the question or hypothesis addressed?<br /> Is promoter competition occurring in the genomic setup?<br /> Does the reduction in eve transcription have any phenotypic consequences?<br /> c. What is the approach? Which methods does it employ?<br /> Comparison of eve transcription in individual nuclei in which lacZ is active ann nuclei in which lacZ is silent<br /> Crossing males carrying a homie-lacZ transgene at -142 kb to females heterozygous for a wt eve gene and an eve deficiency.<br /> d. What were the observations and analysis? (i.e the raw data and analyses)<br /> When lacZ is also transcribed there is a 5-25% reduction in endogenous eve transcription <br /> The presence of the homie-LacZ transgene exacerbates eve haploinsufficiency<br /> e. What are the interpretations?<br /> Competition between two promoters at the transcriptional level in the early embryo has phenotypic consequences for patterning in the adult<br /> f. What are the conclusions about the biological processes being studied?<br /> Manipulating topological chromatin structures can interfere with developmental programs.

Review.<br /> By designing a transgene consisting of the eve promoter and the lacZ coding sequence located 142 kb upstream of the eve gene and taking advantage of the homie insulator, which self-pairing interactions can orchestrate enhancer activation of a reporter, the authors created a system where the activation of the lacZ reporter depend on the enhancer in the eve locus 142 kb away. By introducing tags using the MS2-MCP, PP7-PCP and the parS-parB systems and by measuring the mean distance between the green parS tag and the eve gene as a function of time and they found that there is a convergence until the onset of transcription at which point the mean distance corresponds to an average separation of about 340 nm. By modifying their construct (eliminating homie or reversing the homie sequence) they conclude that the eve enhancers must be in close proximity to the lacZ promoter to activate transcription; however, a possible explanation on why reversing the orientation of homie prevents lacZ expression while there is still close proximity between enhancer and promoter. Also, a drop in transcriptional activity of the lacZ reporter is accompanied by an increase in the mean distance between the ParS transgene and the eve gene, suggesting that there is a close connection between the establishment of enhancer-promoter proximity and enhancer activation of transcription. The authors provide evidence that suggests that manipulating topological structures can interfere with developmental programs; for this part (Figure 6, panel A) I would suggest to make a separate figure for measure of % eve activity reduction for each stripe since the way it is shown makes it harder to appreciate the figure.

On 2017-10-28 16:50:57, user Lionel Christiaen wrote:

Student #3<br /> • Summary of work presented<br /> o Introduction<br /> • Focus on the mechanism through which enhancers act over distance<br /> • 3C-based experiments have revealed enhancer-promoter interactions that are conserved among developmental stages, cell fates, or evolution, suggesting a permissive role of the physical enhancer-promoter interactions on transcriptional activity<br /> • Lineage specific enhancer-promoter interactions are found to be prevalent in many developmental contexts – instructive role?<br /> • Direct dynamic link between enhancer-promoter proximity and transcriptional activation is needed<br /> • Devised an assay that uses a combo of genome editing, genetics, and live single-cell imaging to visualize the relationship between enhancer activation of transcription and physical proximity in real time<br /> o Figure 1 – an endogenous genomic construct is designed to investigate long-distance enhancer-promoter interactions<br /> • Background knowledge<br /> • Enhancers act on promoters over distance<br /> • Hypothesis<br /> • Physical proximity is central to proper enhancer-promoter communication<br /> • Homie-homie self-pairing interactions can orchestrate enhancer activation of a reporter at distances of at least 2 Mb<br /> • Experimental approach<br /> • Constructed a transgene consisting of the eve promoter (no enhancers) with a LacZ reporter at an attP site 142 kb upstream of the eve gene<br /> o Homie is a boundary element (insulator) which marks the 3’ end of the eve locus<br /> o Needed to be able to be able to visualize the location of the promoter, the location of the enhancers, and monitor the transcriptional activity in living embryos<br /> • Observations, data<br /> • In fixed embryos expression of lacZ mRNA is seen only within the limits of endogenous eve stripes<br /> • Interpretations<br /> • The activation of the lacZ reporter depends on the enhancers in the eve locus 142 kb away<br /> • Conclusions<br /> • At this stage of development, the eve promoter has no spontaneous activity and does not respond to nearby enhancers

o Figure 2 – visualization of enhancer-promoter movements producing transcriptional activity using 3-color live imaging<br /> • Background knowledge<br /> • The preliminary construct in figure 1 works as expected<br /> • Hypothesis<br /> • Examining how spatial proximity relates to enhancer action<br /> • Experimental approach<br /> • Introduced tags into the initial transgene from figure 1<br /> • MS2 loops – in first eve intron, used to mark nascent eve transcripts and the nuclear location of the eve gene and the associated eve enhancers<br /> • PP7 stem loops – near 5’ end of the lacZ coding sequence to visualize transcriptional activity of the lacZ reporter<br /> • parS/parB DNA labeling system – mark the position of the lacZ reporter independent of whether the reporter is active<br /> o parS DNA sequences nucleate the binding of a ParB-GFP<br /> • Performed 3-color time-lapse confocal imaging on 2 hour old embryos carrying the tagged eve locus and the parS-homie-lacZ reporter<br /> • Observations, data<br /> • Individual fluorescent foci are observable in 70-100 nuclei simultaneously<br /> • lacZ expression is restricted to nuclei that reside within one of the eve stripes<br /> • In nuclei in which the reporter is active, the reporter is separated from the eve gene<br /> o In nuclei where the green focus (parS) and the blue focus (active eve gene) are far from each other, there is no red focus (lacZ reporter)<br /> o In nuclei where there is a red focus, the three colored foci appear to be attached together<br /> • Interpretations<br /> • The eve gene and the reporter come together to generate transcription<br /> • Conclusions<br /> o Figure 3 – physical proximity between enhancers and promoter is required to activate transcription<br /> • Background knowledge<br /> • The genetic constructs from figure 2 allow simultaneous visualization of the location of the promoter, the location of the enhancer, and transcriptional activity<br /> • Hypothesis<br /> • Needed more detailed quantification of how enhancer activity is related to spatial proximity<br /> • Experimental approach<br /> • Measured the physical separation between the eve gene and the lacZ reporter in embryos carrying the construct in embryos over a 30 min period in cycle 14<br /> • Replaced the homie sequence with lambda DNA of the same length to confirm that linkage of the reporter to eve is dependent on homie<br /> • Reversed the orientation of homie in the original transgene such that the lacZ reporter is downstream<br /> • Scored nuclei with respect to the transcriptional activity of the lacZ reporter<br /> • Observations, data<br /> • Normal construct<br /> o Bi-modal distribution for the time averaged physical distance that could be modeled as a mixture of two Gaussians<br /> • Homie replaced with lambda<br /> o The distribution of the MS2-parS RMS distance is unimodal with a mean at 743 nm<br /> o There is no instance in which there is sustained close proximity<br /> • Homie reversed<br /> o Pairing still occurs but the regulation of the reporter by the eve enhancers is disrupted<br /> o Bi-modal distribution resembling that of the regular transgene<br /> • Scored nuclei<br /> o All of the parS-homie-LacZ transgene nuclei showing lacZ transcription have a degree of physical separation that falls within the distribution corresponding to the bound conformation – there are no nuclei in the unbound conformation in which there is lacZ transcription<br /> • Interpretations<br /> • Homie pairing is responsible for creating the chromatin conformation needed for transcription events to occur by bringing the enhancers and the promoter together<br /> • Conclusions<br /> • Eve enhancers must be in close proximity to the lacZ promoter in order to activate transcription<br /> o Figure 4 – dynamics of chromatin movement underlies kinetics of enhancer-promoter interactions and transcriptional activation<br /> • Background knowledge<br /> • Previous experiments show the spatial requirements between enhancers and promoters for gene expression but not the temporal relationship<br /> • Hypothesis<br /> • Chromatin movement dynamics play a role in the interaction between enhancers and promoters<br /> • Experimental approach<br /> • All nuclei displaying a switch from off to on were aligned with respect to the time point when nascent transcripts could be detected<br /> • Measured the mean distance between the parS tag and the eve gene as a function of time<br /> • Did the above two steps but in nuclei that go from on to off

• Observations, data<br /> • Off to on<br /> o Sharp switch in activity state<br /> o There is a continuous spatial convergence until the onset of transcription when there is an average separation of 340 nm<br /> • On to off<br /> o A drop-off in transcription is accompanied by an increase in the distance between the enhancer and the promoter<br /> o There is a 4 min gap between the time when the enhancer and promoter separate and when transcriptional activity declines – this is largely due to the length of the reporter gene and how long RNAPII takes to clear it<br /> • Interpretations<br /> • There is a close connection between the establishment of enhancer-promoter proximity and the activation of transcription<br /> • Conclusions<br /> • Results fit with the idea that the enhancer and promoter must maintain close proximity to each other for continuous initiation of transcription<br /> o Figure 5 – activation from endogenous enhancers is governed by enhancer-promoter distances<br /> • Background knowledge<br /> • The pairing of homie is not sufficient to generate the sustained physical proximity between enhancer and promoter needed for transcription initiation<br /> • Different eve enhancers regulate individual stripes of the eve pattern in the embryo<br /> • Hypothesis<br /> • Additional compaction is needed (in addition to homie pairing) in order to cause initiation of transcription<br /> • Experimental approach<br /> • Examine nuclei from different stripes separately to explore the topology of the locus under different enhancers<br /> • Observations, data<br /> • Distance of the eve-MS2 gene relative to the parS tag in nuclei where homie pairing occurs but there is no lacZ transcription<br /> o Different distances in nuclei belonging to different stripes (different enhancers)<br /> o The distance to the homie pair should depend on the distance between the activating enhancer and the endogenous homie<br /> o The distance between the eve gene and the parS tag in stripe 5 is shorter than that observed in stripes 4/6 and 3/7 where the enhancers are located farther away<br /> • For the two enhancers that control stripes 4/6 and 3/7 the distance between the eve gene and the parS tag match within the stripe pairs<br /> • The nuclei with the active reporter show significant shortening of the distance between the eve enhancers and the promoter<br /> • The fraction of transcriptionally active reporters decreases with increasing distance between the stripe enhancer and the lacZ promoter<br /> • Interpretations<br /> • Eve enhancers directly engage the eve promoter to activate transcription – the chromatin in the nuclei in each eve stripe adopts a distinct conformation<br /> • The shortening of distance between enhancer and promoter in nuclei with active transcription support the idea of additional compaction of the locus for transcription<br /> • The activation probability of the promoter driving lacZ expression goes down as the distance between enhancer and promoter increases<br /> • Conclusions<br /> • Transcriptional activation requires direct physical engagement between the enhancer and the promoter – associated with topological compaction of the gene locus<br /> o Figure 6<br /> • Background knowledge<br /> • The eve enhancer drives expression from two different eve promoters (endogenous and lacZ reporter)<br /> • Hypothesis<br /> • The activity of the enhancers could be limiting, if that’s the case, the lacZ reporter will reduce transcription of the eve gene<br /> • Is promoter competition occurring?<br /> • Experimental approach<br /> • Compare eve transcription in individual nuclei in which lacZ is active and nuclei in which lacZ is silent<br /> • Cross males carrying a tagless homie-lacZ transgene with females heterozygous for wt eve and eve deficiency – weakly haploinsufficient<br /> o See if the lacZ transgene exacerbates eve haploinsufficiency<br /> • Observations, data<br /> • For each stripe there is a 5%-25% reduction in endogenous eve transcription in nuclei where the lacZ reporter is being expressed<br /> • The presence of the homie-lacZ transgene causes a 4-fold increase in eve defects in eve deficient flies<br /> o Having the homie-lacZ transgene exacerbates eve defects<br /> • Interpretations<br /> • Competition between two promoters in the early embryo has phenotypic consequences for patterning in the adult<br /> • Conclusions<br /> • Disrupting chromatin structures can interfere with developmental programs if doing so interferes with the interaction between enhancers and their promoters<br /> • Merits<br /> o Very clever system built to test hypotheses<br /> • Potential improvements<br /> o Figure 3<br /> • Schematics are a little misleading<br /> o Figure 4<br /> • Causality is not firmly established in this figure – what is the order of events between transcription termination and increase in distance?<br /> • See what happens when you inhibit polymerase or promoter?<br /> o May be beyond the scope of this figure<br /> • Minor problems<br /> o Language concerning the lacZ reporter may be misleading sometimes…they say lacZ is active when I think they mean lacZ is actively transcribed. At no point were they doing histochemical staining so they never tested lacZ activity

On 2017-10-28 16:50:25, user Lionel Christiaen wrote:

Student #1<br /> Chen et al. set out through to determine the dynamics of promoter enhancer interactions through a series of biochemical and genetic assays paired with confocal in vivo time lapse imaging. The authors developed an elegant system to tag genetic loci, enhancer-promotor dependent transcriptional activity of lacZ, and endogenous expression of eve mRNA. Additionally, they were able to provide quantitative data to accompany to support their claims. <br /> Highlights of the work<br /> - employed different well-established methods to interrogate an experimental question that is lacking experimental validation. <br /> - single cell data was obtained to account for population heterogeneity. <br /> -Time lapse live in-vivo assays that return a more complete scenario (both proximity and expression measured simultaneously) compared to prior studies that measured either transcriptional activity or chromatin dynamics independently providing only a static view.

Recommended improvements<br /> - The authors claim because that there is no expression of lacZ at the locus in which it was inserted means that it does not respond to nearby enhancers. “These findings indicate that the activation of the lacZ reporter depends on the enhancers in the eve locus 142 kb away, and that at this stage in development, the promoter of the reporter has no spontaneous activity nor does it respond to enhancers near the site of insertion.” I think I know what the author is trying to convey in the latter part of this statement however it can be interpreted as “in this developmental stage, even if you insert an enhancer at this locus it won’t activate lacZ “please clarify this sentence or add a reference. <br /> - Also, I would like the authors to address the threshold of molecules required to obtain fluorescent signal, this is important for the transcription on/off experiments. <br /> -The promoter competition experiments are missing p values that are mentioned in the figure legend.

On 2017-10-28 16:48:42, user Lionel Christiaen wrote:

Student #10<br /> 1- Enhancers are thought to act as static regulatory modules defined by their transcription factor binding sites that modulate their activity through space and time. However, not all binding sites are created equal, with multiple transcription factors showing weak binding activity at “degenerate” binding sites. To investigate the contribution of these weaker sequences, the authors looked at the activity of a well-known transcription factor, Ultrabithorax at the enhancer for shavenbaby. The authors theorize that the activity of these enhancers is modulated by their nuclear microenvironment, allowing a higher number of transient associations of weakly associated transcription factors in order to drive robust expression. <br /> 2- The imaging techniques in this paper are advanced, and may not be as sensational as light sheet microscopy, but each technique serves to answer the question that it seeks to answer. The first is the “expansion” technique, which physically enlarges the sample through the introduction of a polyacrylamide solution. This improves the effective resolution, but may be prone to artifacts. The second is using halo-tag fusion proteins with high intensity dyes to achieve single molecule resolution which allows the previous results to confirmed using the expansion technique, mainly that there are local increases in concentration of Ubx in nuclei. This effect disappears by mutagenesis of the Ubx DNA binding site, suggesting that Ubx’s association with DNA is driving the increase in local concentrations.<br /> One of the most impressive techniques is to use florescence in-situ hybridization with antibody co-stains to demonstrate that there is a high correlation of the Ubx transcription factor with gene expression. This is done using an intronic probe which will specifically localized to the locus of transcription.<br /> Finally, the authors use a synthetic enhancer network to test the hypothesis that low affinity binding sites at enhancers serve to increase the local concentration of the transcription factor that responds to that motif. <br /> 3- I don’t like the expansion technique, but the authors use live imaging to demonstrate their observations are valid. Although it may have been interesting to image transcription live in concert with their single molecule imaging, I understand that the authors had a set of defined questions that their experiments address sufficiently. I also think it would have been interesting to test a suite of genes in the in-situ assay instead of using only one probe. This could identify loci that may have varying degrees of transcriptional response to Ubx.<br /> 4- Showing the weakened enhancer binding sites in the final figure with red “X”s gives the impression that the binding site has been deleted, making it a bit hard to understand.

On 2017-10-28 16:48:02, user Lionel Christiaen wrote:

Student #7<br /> Prior to this paper, it was known that transcription factors (TFs) only stay bound for a few seconds before dissociating from DNA, and that low affinity binding sites are necessary for TFs to distinguish between binding sites with a similar sequence. The authors wanted to answer the question of how these brief TF contacts could allow for transcription from low affinity sites. They hypothesized that multiple low affinity sites could act together to “trap” TFs and create “microenvironments” with high TF concentration that would allow for transcription. To address this question, they used the svb locus in Drosophila which contains multiple distinct enhancers that have low affinity binding sites for Ubx. Techniques they used included: super-resolution confocal microscopy, FISH, immunofluorescence, and live imaging of specially prepped (~4x expanded) transgenic embryos.<br /> The authors first found that Ubx was localized to distinct regions of the nucleus that did not overlap with unrelated TFs, which suggested that Ubx is not localized by a general mechanism that limits the distribution of all TFs. They also showed that Ubx did no co-localize with repressive chromatin and it only partially overlapped with active transcription sites, providing evidence that Ubx has specificity in its localization and is not found at all active loci. Since these results were found in fixed embryos, the authors wanted to confirm it wasn’t just an artifact of the fixation process, so they performed live imaging of Ubx using a Halo tag and a fluorescent dye ligand, JF635. They found the same results, in which Ubx was localized to specific regions at high concentration, and they further showed that its localization was dependent on DNA binding by mutating the homeodomain. They next wanted to determine if the regions of high Ubx concentration co-localized with sites of active svb transcription using FISH. Indeed, they found that Ubx was enriched at sites of svb transcription, but it was not enriched at sites of active transcription driven by a synthetic enhancer, providing more evidence that its localization has specificity. They next wanted to determine if binding site affinity affected the localization of Ubx by either changing a low-affinity site to a high-affinity site, or by removing multiple low-affinity sites. They found that the switch to a high-affinity site led to decreased enrichment of Ubx microenvironments, and the removal of low-affinity sites resulted in active transcription only occurring in regions with high Ubx concentration. This inverse correlation between affinity and Ubx concentration led them to conclude that binding site affinity determines the enhancer’s response to local Ubx concentration. Lastly, they found that the Ubx co-factor, Hth, was co-enriched around active transcription sites, suggesting that high concentrations of TFs and their co-factors are required for transcription. The authors concluded that clustered binding sites for the same TF, cooperative interactions between TFs and their co-factors, and clustering of enhancers could all result in increased local concentration of TFs by acting as a “trap” to increase their time near low-affinity enhancer sites.

Technically innovative with their use of methods to expand embryos, as well as their use of Halo-tagged Ubx and the dye, JF635, for live imaging.

Major<br /> Fig. 2 A/B don’t seem to match up.

How did they quantify [Ubx] at svb loci in fig 3 f, h, j, l, n, p, r when they used lacZ reporters for the above images?<br /> Why use lacZ reporters rather than FISH of endogenous svb?<br /> There seems to be large variability in their results (i.e. enrichment of Ubx at TALEA driven enhancers of 0.02 ± 0.63), so how significant are any of these results?

Maybe check other Ubx regulated loci with FISH to see if the same concepts hold true.

On 2017-07-01 22:41:59, user David Galbraith wrote:

Hi Naomi:

Nice work! However, you indicate "To address this challenge, we3 and others4 developed single nucleus RNA-seq....". The first report of single nucleus RNA-seq was in fact a couple of years prior to these two references, by Grindberg et al. (2013). RNA-Seq from single nuclei. Proceedings of the National Academy of Sciences U.S.A. 110:19802-19807, and it would be very courteous if you would include that citation in your publication. Further, if you wish to comprehensively attribute analysis of polyadenylated RNA as a surrogate for total cellular polyadenylated RNA, you might consider citing: Macas, J., Lambert, G.M., Dolezel, D., and Galbraith, D.W. (1998). NEST (Nuclear Expressed Sequence Tag) analysis: a novel means to study transcription through amplification of nuclear RNA. Cytometry 33:460-468, and Zhang, C.Q., Barthelson, R.A., Lambert, G.M., and Galbraith, D.W. (2008). Characterization of cell-specific gene expression through fluorescence-activated sorting of nuclei. Plant Physiology 147:30-40.

Thanks for this consideration.

David

On 2017-04-03 01:43:01, user Juha Kere wrote:

This manuscript was first submitted to Nature Genetics 20 Sep 2012 and the same date returned to authors without review. We reanalyzed later the same RNA sequencing data referred to here using transcript 5' tag mapping to the genome, and it served as the basis for conclusions regarding new PRDL transcription factor genes upregulated at 4-cell and 8-cell stages (Töhönen, Katayama & al. Nature Communications 6:8207, 2015; DOI: 10.1038/ncomms9207). Our analysis and conclusions regarding DUX4 as an early regulator of human Embryo Genome Activation are published for the first time here. For correspondece, please contact juha.kere@ki.se.

On 2016-12-22 16:32:01, user Vijay Jayaraman wrote:

Does the order in which the DDD and the HA is placed after the gene matter? In the original construct of pGDB HA tag was 3' to the DDD unlike in the design mentioned in this paper.

On 2016-03-17 19:29:25, user Fabien Campagne wrote:

I disagree with the recommendation to use BioConductor as stated by the authors (section 3, page 11, frameworks). BioConductor is a great option in R, but it is not easy to obtain previous releases of BioConductor and the packages that it offers. If you need computational reproducibility, it is not trivial at all to obtain specific versions of a BioConductor environment. I recommend that the authors try to put their solutions to the test before recommending them. My group experienced many dependency installation issues with BioConductor, including the inability of the release servers to tag URLs with versions, so that even source code cannot be retrieved reliably in the future. <br /> We now routinely create docker images that contain R, BioConductor and a specific set of packages. This is the best way we found to achieve computational reproducibility with R.

On 2015-11-30 14:55:42, user Raphael Levy wrote:

PNAS rejected the letter: "After careful consideration, the Board has decided that your letter does not contribute significantly to the discussion of this paper." (https://raphazlab.wordpress...

More info on our work and analysis of SmartFlare can be found at my blog (https://raphazlab.wordpress....

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer 1 (Public review):

(1) "The timescales of the peptide recognition and unbinding process are much longer than what can be sampled from unbiased simulations. Therefore, the proposed mechanism of recognition should only be considered a hypothesis based on the results presented here. For example, peptides that do not dissociate within one one-microsecond MD simulation are considered to be stable binders. However, they may not have a viable way to bind to the narrow protein cleft in the first place."

We thank the Reviewer for this valuable feedback and we agree with the Reviewer. Our work on the IRE1 cLD activation mechanism is focused on generating a hypothesis of the binding mechanism driven by MD simulations. We recognize the limitations in defining a stable binder due to the time scales sampled. However, our primary focus was to sample and characterize a possible binding pose in the center of the cLD dimer. We contextualized our statements about stable binders and limited our claims to stating that the protein-peptide complex is stable within 1 µs-long simulations. However, we believe that our finding that the cLD dimer groove is not able to accommodate peptides is solid, as the steric impediment described is present in all our replicas, both with and without peptides, in a cumulative sampling time of 24 µs without peptides and 66 µs with peptides. Additionally, we included a plot showing the distribution of groove width across all replicas.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) The title was changed from “Unfolded polypeptides can stably bind to hIRE1α cLD dimer” to “Unfolded polypeptides bind to hIRE1α cLD dimer surface”

Addition to the text. (Figure 15 A legend) “(A) Distributions of the groove width of peptide-bound cLD dimers throughout all simulations performed. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(2) Oftentimes, representative structures sampled from MD simulation are used to draw conclusions (e.g., Figure 4 about the role of R161 mutation in binding affinity). This is not appropriate as one unbinding event being observed or not observed in a microsecond-long trajectory does not provide sufficient information about the binding strength of the free energy difference.

We thank the Reviewer for the insightful comment. As explained in the previous point, we believe that our simulations provide useful hypotheses. We are aware of the limitations due to the timescale and agree that these limitations cannot be overcome with standard equilibrium simulations. To address these limitations, used orthogonal methods, specifically MM/PB(GB)SA calculations, to calculate binding free energies from existing trajectories. We added predictions of all the peptides using AlphaFold 3, to confirm the binding region. Importantly, we now provide experimental results to assess the binding affinity of cLD dimer mutants E102R and Y161R.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. 16A). We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Figure 16 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT). (B) Difference in enthalpy (enthalpy of binding, ∆H) as an estimate of the binding free energies of unfolded polypeptides to hIRE1α cLD dimer derived from MM/PBSA calculations of our peptide simulations.”

Addition to the text. (Figure 4 G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Results section: Point mutations destabilize unfolded peptide binding to cLD) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102 K_1/2= 6.35 µM and Y161R K_1/2= 5.4 µM, Supplementary Table 3) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 3), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary Table 3)

Reviewer 2 (Public review):

(1) Improving presentation to include more computational details.

We thank the Reviewer for raising this critical point. We agree that the manuscript is tailored for a biology audience, as the data are particularly relevant for that community. Nevertheless, we also understand the importance of providing sufficient methodological detail for computational readers. We added more references to the methods for computational information in the main text.

(2) More quantitative analysis in addition to visual structures.

We added an uncertainty estimate for the HDX calculations using bootstrapping and included additional information on bond distances for E102 and Y161. We also incorporated time-series data showing the distance of the peptide from the groove across all replicas.

Addition to the text. (Figure 1C legend) “(C) The deuterated fraction obtained from experimental results (dashed line, shaded area indicates the error we calculated from bootstrapping) published by Amin-Wetzel et al. and the fraction computed from MD simulations (solid lines, blue for TIP3P water and orange for TIP4PD water) for the PDB and AF model at incubation time point 0.5 min. This time point corresponds to experimental incubation times, not MD simulation time. Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping. Below each absolute value plot, we report the discrepancy, which is defined as the difference between the simulated and experimental deuterated fractions, with the shaded area indicating the corresponding error.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

Reviewer 3 (Public review):

A potential weakness of the study is the usage of equilibrium (unbiased) molecular dynamics simulations, so that processes and conformational changes on the microsecond time scale can be probed. Furthermore, there can be inaccuracies and biases in the description of unfolded peptides and protein segments due to the protein force fields. Here, it should be noted that the authors do acknowledge these possible limitations of their study in the conclusions.

We appreciate the Reviewer’s thoughtful comment. As noted in our response to Reviewer 1, we addressed the concern about sampling by applying orthogonal methods and experimental techniques. We agree with the Reviewer that some form of enhanced sampling is necessary if we want to assess binding in a more quantitative way, e.g., via free energy calculations. However, we also realize that applying any enhanced sampling scheme to our system is very challenging, given its large size and the complex peptide-protein interactions, which are not easily captured in a few collective variables. After a careful assessment and some preliminary tests, we decided that estimating free energies using enhanced sampling would necessitate a separate paper due to both the conceptual complexity of the project and the size of the necessary sampling campaign.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Some enhanced sampling or path sampling simulations may be carried out to identify the peptides’ binding and unbinding mechanisms to the protein. This can show whether the disordered peptides studied in this work do indeed bind to the protein.

We thank the Reviewer for this constructive criticism. We acknowledge the limitations associated with investigating binding and unbinding mechanisms of disordered peptides within the time scales accessible to our equilibrium simulations. However, the primary objective of our study was to sample and characterize a plausible binding pose at the center of the cLD dimer. We wanted to understand if unfolded model peptides require an open groove able to contain them to bind to IRE1’s core luminal domain or if binding also in the absence of an open groove.

Enhanced sampling is, of course, an important strategy to overcome the limits of equilibrium simulations. However, we note that implementing enhanced sampling approaches in this system poses significant challenges due to its large size and the complexity of peptide–protein interactions, which cannot be easily captured using a limited set of collective variables. We decided that a thorough application of enhanced sampling would therefore constitute a separate study. Instead, we decided to validate our simulations in two ways: 1) we ran a new set of free energy calculations, and 2) we tested key predictions in experiments, adding significant new data to strengthen the conclusions of our manuscript.

To evaluate whether the binding free energies of MPZ-derived peptides to human IRE1α cLD dimers are consistent with experimentally reported binding constants, we employed the MM/PBSA (Molecular Mechanics/Poisson–Boltzmann Surface Area) method. Calculations were performed over the final 250 ns of each simulation replica using the Single Trajectory Protocol (STP), which avoids the need for additional simulations. This approach provides an estimate of the effective binding free energy (i.e., enthalpy of binding) by accounting for bonded and non-bonded interactions, as well as solvation contributions. The entropic contribution, being computationally more demanding and subject to additional approximations, was not included. Binding enthalpies were obtained for MPZ1-N (in different initial orientations), MPZ1-C, MPZ1-N-2X, and MPZ1-N-2X-RD. The results indicated small differences in effective binding energies between the shorter peptides (MPZ1-N and MPZ1-C), whereas MPZ1-N-2X exhibited the lowest binding energy and MPZ1-N-2X-RD the highest, consistent with experimental trends. These findings support the reliability of our model and sampling strategy as a framework for analyzing peptide binding conformations to cLD.

We identified residues E102 and Y161 as key contributors to the binding of unfolded peptides in our simulations. Contact analysis revealed these residues as binding hotspots, centrally located within the observed interaction regions. To probe their relevance, we conducted simulations of cLD dimers with single arginine mutations in these residues, aimed at disrupting these hotspots through charge repulsion. These simulations revealed increased instability of the MPZ1N2X on the cLD dimer surface. We further validated these findings experimentally using fluorescence anisotropy assays. Fluorescently labeled MPZ1N-2X was titrated with purified cLD mutants (E102R and Y161R), and anisotropy measurements were fitted to derive  K_1/2 values. Both mutations resulted in approximately a two-fold reduction in binding affinity relative to the wild-type cLD, confirming the importance of these residues in stabilizing peptide binding.

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “Thus, we investigated how the point mutations of two key residues, E102R and Y161R, would affect peptide binding by simulating the cLD mutant in complex with MPZ1N-2X (Fig. 4C-E). We initialized the systems in the pose described for the other peptide-cLD systems described earlier (Fig. 3B, t = 0 µs). In simulations of the wild-type (WT) cLD dimer, the peptide generally remained near the center (Fig. 4C,F). By contrast, MPZ1N-2X displayed reduced binding to E102R, fully dissociating in one TIP4P-D replica (Fig. 4E,F). A similar trend was observed for Y161R, where one partial dissociation event occurred (Fig. 4D,F). Comparative analysis of MPZ1N-2X contact sites on the WT and mutant cLD dimers (Supplementary Fig. 17B-D) revealed that, in the presence of mutations, the peptide engages a broader surface region rather than remaining centrally localized, while forming fewer contacts with the specific residues (Supplementary Fig. 18A-B).”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102  K_1/2= 6.35 µM and Y161R  K_1/2= 5.4 µM, Supplementary Table 1) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 1), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4 legend) “(E) Side view snapshot after 1 µs of simulation of E102R hIRE1α cLD dimer (gray) in complex with MPZ1N-2X (orange). The amino acid R102 on both monomers is represented in magenta sticks. (F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Methods section: Binding free energy calculations (MM/PBSA)) “The binding free energy of noncovalently bound complexes of human IRE1 cLD and peptides was calculated with MM/PBSA (Molecular mechanics/PoissonBoltzmann Surface Area) method via gmx_MMPBSA (version 1.6.4)[1, 2]. The Poisson-Boltzmann method was used to estimate the electrostatic contribution to solvation free energy as recommended for data obtained with the CHARMM force field. The contribution of the entropic term was omitted, obtaining effective binding free energy values, or enthalpy of binding (∆H). We used the Single Trajectory Protocol (STP), using the cLD-peptide simulations as input. The calculations were performed on the last 250 ns of each replica. Single-term total non-polar solvation free energy (inp = 1) was used. The charmm_radii (PBRadii= 7) was used to build amber topology files [3]. The default parameters were applied for other terms.”

Addition to the text. (Methods section: Protein purification) “To express hIRE1α LD (24-443) human cDNA sequences were cloned into pET47b(+) to create a coding sequence with N-terminal His6-tag. Mutations of hIRE1α LD were introduced by overlap extension PCR and restriction cloning into pET47b(+). For expression of the proteins, the plasmid of interest was transformed into Escherichia coli strain BL21DE3* RIPL (Agilent Technologies). Cells were grown in Luria Broth until OD600=0.6-0.8. Protein expression was induced with 0.6 mM IPTG, and cells were grown in 20°C overnight. For purification, cells after harvesting were resuspended in Lysis Buffer (50 mM HEPES pH 7.2, 400 mM NaCl, 20 mM imidazole, 5% glycerol, 5 mM β-mercaptoethanol) and were lysed in Constans Systems cell disruptor at 25 000 psi. The supernatant was collected after centrifugation for 45 minutes at 48000×g in 4°C. Supernatant was loaded onto Ni-NTA column (Cytiva) and the protein eluted with a linear gradient of imidazole from 20 to 500 mM. Fractions containing the protein were diluted 1:8 with anion exchange wash buffer (50 mM HEPES pH 7.2, 5 mM β-mercaptoethanol), loaded onto HiTRAP-Q ion exchange column (Cytiva) and eluted with a linear gradient from 50 mM to 1 M NaCl. Afterwards, the His6tag was removed by cleavage with Precission protease (GE Healthcare, 1 µg of enzyme per 100 µg of protein). The cleavage was performed overnight in 4°C. The protein sample after cleavage was loaded onto a Ni-NTA column, and the flow-through containing protein without the tag was collected. The protein was further purified on a Superdex 200 10/300 gel filtration column equilibrated with Buffer A (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT). Protein concentrations were determined using extinction coefficient at 280 nm predicted by the Expasy ProtParam tool (http://web.expasy.org/protparam/).”

Addition to the text. (Methods section: Fluorescence anisotropy) “For fluorescence anisotropy measurements, the MPZ1-N-2X peptide attached to 5 carboxyfluorescein (5-FAM) at its N-terminus was obtained from GenScript at >95% purity. Binding affinities of hIRE1α LD mutants to FAM-labeled peptides were determined by measuring the change in fluorescence anisotropy on a Tecan CM Spark Micro Plate Reader with excitation at 485 nm and emission at 525 nm with increasing concentrations of hIRE1α LD variants. Measurements were performed in Buffer A supplemented with Tween 20 (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT, 0.025% Tween 20). Fluorescently labeled peptides were used in a concentration of 90 nM. The reaction volume of each data point was 25 µL and the measurements were performed in 384-well, black flat-bottomed plates (Corning) after incubation of peptide with hIRE1α LD variants for 30 min at 25◦C. Binding curves were fitted using Prism Software (GraphPad) using the following equation: F_bound = r_free +( r_max − r_free)/(1+10((Log K_1/2 −x)·n_H)), where F_bound is the fraction of peptide bound, r_max and r_free are the anisotropy values at maximum and minimum plateaus, respectively. n_H is the Hill coefficient and x is the concentration of the protein in log scale. Curve-fitting was performed with minimal constraints to obtain K_1/2 values with high R² values. However, as this equation does not consider the equilibria between hIRE1α LD dimers/oligomers, these apparent K_1/2 values do not reflect the dissociation constant.”

(2) Wherever possible, conclusions related to binding affinity should not be drawn from single unbinding events. For example, the title of Figure 4, "Single point mutation of cLD alters the binding affinity of unfolded peptide," should be softened. Similar changes should be made throughout the manuscript where such claims have been presented.

We thank the Reviewer for highlighting this important point. In the revised manuscript, we have adjusted the text to remove or soften conclusions related to binding affinity that were based on single unbinding events in the MD simulations.

Addition to the text. (Figure 4 title) “Single point mutations of cLD alter the binding of unfolded peptide MPZ1N-2X.”

Addition to the text. (Results section title: Unfolded polypeptides can stably bind to hIRE1α cLD dimer) “Unfolded polypeptides bind to hIRE1α cLD dimer surface.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1αα cLD dimer surface) “Our goal was to elucidate a potential binding pose and identify the relevant features of unfolded proteins and the cLD that affect the binding.”

Reviewer #2 (Recommendations for the authors):

(1) A table of all simulated trajectories, including simulation conditions, number of replicas, box size, number of atoms, equilibration length, recording time step, number of frames for further analysis.

We thank the Reviewer for this helpful suggestion. We have added a summary table of all simulations, including the requested details, to the Supplementary Information (Table 1).

Addition to the text. (Supplementary figures and tables: Table 2)

(2) The current NVT equilibration time was 0.125ns, and then no productive NPT simulations were mentioned as equilibration. Even though this is a simulation of mostly folded structures, it still takes some time for these amino acids to relax within the force field.

We thank the Reviewer for this constructive comment and acknowledge the validity of the concern. However, our simulations were extensively sampled, and equilibration was achieved within the first 50 ns of the production runs. Therefore, the segments of the trajectories from which we draw conclusions correspond to equilibrated states (see RMSD analysis, Figure 1). Additionally, binding free energy calculations (MM/PBSA) were carried out on the last 250 ns of the simulation replicas.

(3) At least three histograms were presented in Figure 2C, which I guess is from multiple simulations, and does not seem to be discussed.

We thank the Reviewer for pointing out the lack of reference to Figure 2C. We added the correct reference to the text where the groove width of luminal domains of human and yeast is discussed.

Author response image 1.

RMSD analysis of human IRE1_α_ cLD dimer simulated in complex with unfolded peptides.

Addition to the text. (Results section: The putative groove of human IREα cLD is dynamic but unable to contain peptides ) In simulations of the dimeric structures, the average groove width was 7.3 ± 0.1 Å for the human cLD and 8.9 ± 0.1 Å for the yeast cLD, averaged over three TIP3P and three TIP4P-D replicas per system (Fig. 2C).

(4) The comment regarding the CHARMM force field on Page 6 is not justified. Actually the force field the authors used (CHARMM36m, Jing et al Nat Methods 2016) did include scaling of TIP3P LJ parameters to correctly capture the dimensions of the intrinsically disordered proteins (IDPs). However, the authors cited a couple of examples of literature of previous versions of CHARMM force fields and commented that it cannot capture IDP dimensions with TIP3P.

We thank the Reviewer for pointing out this source of confusion. We cited the main papers of CHARMM as [4, 5], which were misleading, and following the Reviewer’s advice, we removed these citations.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “Current all-atom force fields used in MD simulations are mainly designed to reproduce the dynamics of folded and globular proteins [6].”

(5) I am fine that the authors used TIP4PD with CHARMM36m, but caution should be taken for such a combination of protein and water force fields. Note that when optimizing force fields for IDPs, one often has to balance protein-water interactions by either enhancing protein-water interactions, enhancing water dispersions, or reducing protein-protein interactions. So, all such optimization is dependent on both protein and water force fields. TIP4PD was designed to pair with Amber99sb-ildn or, most recently, Amber99sb-disp instead of CHARMM36m. This could result in rescaling of LJ parameters.

We thank the Reviewer for raising this issue. We argue that the TIP4P-D water model has been used in combination with the CHARMM36m force field [7] and has been shown to yield satisfactory results for disordered regions.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “The TIP4P-D water model was developed to address limitations of existing force fields in reproducing the structural ensembles of intrinsically disordered proteins and regions. It incorporates enhanced dispersion and moderately stronger electrostatic interactions to improve the balance between water dispersion and electrostatics [8]. Zapletal et al. [7] showed that for proteins containing both folded and disordered regions, the CHARMM36m force field [9] in combination with the TIP4P-D water model provides a robust framework, preventing collapse of disordered regions while preserving folded regions. Acknowledging that the behavior of disordered regions can be case-specific, we conducted molecular dynamics simulations of the two cLD dimer models using the CHARMM36m force field with both TIP3P and TIP4P-D water models.”

(6) I suggest referring to the methodology part for simulation details as much as possible when presenting the story.

We thank the Reviewer for this suggestion. In the revised manuscript, we now refer the reader to the Methodology section for detailed descriptions of the HDX-MS data analysis and the MM/PBSA free energy calculations.

Addition to the text. (Results section: Hydrogen-deuterium exchange experimental data validate the cLD dimer structure) “From our simulations, we calculated the theoretical deuterated fraction using the method by Bradshaw et al.[10] and compared it to the experimental data (Fig. 1C-D and Supplementary Fig. 10) (see Methods).”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

(7) Error bars and methodology of error analysis should be provided for all cases of all-atom simulations if possible, since convergence is always an issue when considering these conformational changes within microseconds of all-atom simulations.

We thank the Reviewer for the important observation. We agree and added error methodology for the estimation of theoretical deuterated fractions (Fig. 1C).

Addition to the text. (Figure C legend) “Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping.”

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To reproduce the time points after incubation in deuterium (D₂O), we computed deuterated fractions separately for each of the two monomers constituting a dimer for the time points 0.5 min (30 s) and 5 min (300 s). Then, we computed the mean and standard deviation over the data coming from replicas of the same cLD dimer model (AF or PDB model) and the same water model (TIP3P or TIP4P-D). To estimate the uncertainty of the mean values obtained from our datasets and the dataset from Amin-Wetzel et al. ([11] Figure 3—source data 1), we applied a non-parametric bootstrap resampling procedure. For each sequence range from HDX-MS analysis, we treated the measurements from the N=6 independent datasets as independent samples, accounting for 3 replicas each with two monomers (6 monomers total). We then generated 10,000 bootstrap replicates by sampling the datasets with replacement, maintaining the same number of samples N in each resample. For each replicate, we calculated the mean at each sequence position. The resulting distribution of bootstrap means was used to compute the standard deviation as an estimate of the standard error. We computed the difference between simulation and experimental data (deuterated fraction discrepancy), and for each residue, we selected as the ‘best structure’ the model with the discrepancy closest to zero among PDB-TIP3P, PDB-TIP4P-D, AF-TIP3P, and AF-TIP4P-D systems.”

(8) Technically I would call DR1 and DR2 linker regions within a folded structure. Their motions are quite restrained by the fold part. I therefore, am not sure how much TIP4PD really helps in contrast to a scaled TIP3P. A plot of structures colored with PLDDT score or b-factor within the PDB should be provided. Quantitative metrics of these regions (e.g. chi chi-squared) might help justify the choice of the AF model against the PDB model. Currently, the two models look very similar in Figures 1c and 1d. Similarly, quantitative metrics as a function of different simulation time windows will help justify the convergence of the simulation and indicate the flexibility of these regions.

We thank the Reviewer for this thoughtful comment. In response, we analyzed the AlphaFold2 and AlphaFold3 predictions, which consistently assign very low pLDDT values (<50) to the DR2 region, while DR1, is predicted with higher but still low confidence (50 < pLDDT < 70). These scores indicate intrinsic uncertainty in the structural definition of both regions, supporting their flexibility despite being located within a folded context.

Addition to the text. (Results section: The hIRE1_α_ cLD forms a stable dimer) “All five AlphaFold 2 predictions closely resembled the top-ranked model used for our simulations (Supplementary Fig. 7C). In contrast, the five AlphaFold 3 predictions yielded greater variability in DR2 organization and longer helices in DR2, but still consistently maintain low pLDDT scores in this region, indicating disorder (Supplementary Fig. 7D).”

Addition to the text. (Figure 7 C-D legend) “(C) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT). (D) Superposition of the 5 structures predicted by AlphaFold 3 for the cLD dimer and colored by confidence prediction score (pLDDT).”

(9) Fluorescence anisotropy seems to be an important set of experimental data to justify the binding of multiple unfolded peptides to IRE. I suggest the authors include a bar plot of binding affinity of different variants in Figure 3. The raw titration curves should also be included in SI.

We thank the Reviewer for this valuable suggestion. The binding affinities reported in previous studies are summarized in Table 2; the reader is referred to those works for the corresponding raw titration curves. The binding affinities for the cLD mutants analyzed in the present study are provided in Table 3, and the associated titration curves are shown in Figure 4G.

Addition to the text. (Figure 4G legend) “Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary figures and tables: Table 3) See Tab. 1

(10) The authors should discuss the dependence of initial orientations of unfolded peptides on the final results. The authors claimed that after 1 microsecond simulations, the orientation of these peptides to IRE changed. Quantitative metrics showing both the binding (e.g., number of contacts) and binding orientation (contact region or angles) should be provided to tell whether the simulation is converged. The comparison to the experimental data lacks quantitative metrics. The authors mentioned the dissociation of MPZ1N-2X-RD in half of the simulations; they might want to provide such a metric for all peptides. Technically, 1 microsecond brute-force simulation is quite short for observing such a binding event, and enhanced sampling methods (e.g. metadynamics) might be necessary for investigating binding. However, at least the presentation and interpretation of the current results should be improved for comparing simulations and experiments.

We thank the Reviewer for the insight. We expanded the discussion of the peptide orientation and added an analysis of the peptide angle with respect to the cLD central groove and contacts. Additionally, we inserted AlphaFold 3 predictions of all the simulated complexes.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0◦ orientation", as the peptide forms a 0 ◦ angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0◦) orientation (Supplementary Fig. 14). We refer to these poses as the "90◦ orientation" and "270◦ orientation".”

Addition to the text. (Supplementary Figures and Tables Fig. 14) “(A) Peptide orientation with respect to the central groove principal axis. The angle was computed as the dihedral angle described by the Cα atoms of Y161 residues (groove principal axis) and the C_α_ atoms of residues L1 and A12 of the MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 10 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between hIRE1α cLD dimer and MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 50 frames, while the shaded lines indicate the value per frame. The analysis were performed on three sets of simulations: "90 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis; "270 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis but flipped 180 degrees with respect to the 0 degree; "0 degrees" orientation, the peptide is placed parallel to the groove principal axis.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. ??A).”

Addition to the text. (Supplementary Figures and Tables Fig. 16A) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT).”

(11) I also have a couple of questions regarding the point mutant Y161R. a) The motivation of mutating Y161 to R is more speculative (Figures 4a,b) than quantitative. The authors might want to show an intermolecular contact map between IRE and unfolded peptides or IRE contact probability along residue indexes to show the interaction hotspots. Figure S11 only showed the structure instead of any metrics for such a purpose. b) It might be better to also show a histogram of the distances of Figure 4e and 4f. Figure 4f actually suggested 1 microsecond simulation is quite short to observe the dissociation event. c) Testing the mutation within the experiment, if possible, would clearly strengthen this part of the manuscript.

We thank the Reviewer for these constructive suggestions. We have added an analysis of intermolecular contacts for the Y161R and E102R mutants (Fig. 18A–B), which highlights the interaction hotspots between IRE1 residues and the unfolded peptides. To further characterize peptide–groove interactions, we now provide minimum peptide–groove distance time series for all peptides (Fig. 15B). Moreover, to experimentally support our simulations, we performed fluorescence anisotropy measurements on the MPZ1N-2X peptide with cLD WT and mutant constructs. These experiments confirm our computational observations (Fig. 4F–G and Fig. 18C).

Addition to the text. (Figure 18 legend) “(A) Number of contacts between residues 102 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between residues 161 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (C) Protein purification of WT hIREα LD and mutants E10R and Y161R.”

Addition to the text. (Figure 4F-G legend) “(F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(12) Similar comments of quantitative analysis (e.g. contact map as a function of simulation time) apply to the last part of results when discussing the intermolecular interactions. Observations such as "the interface predicted by AlphaFold showed stability across MD simulation replicas lasting 200 ns" were provided, but there is no quantitative analysis. How consistent was this observation across multiple replicas of simulations, and how many replicas were used?

We thank the Reviewer for this valuable suggestion. To provide a quantitative assessment, we performed new triplicate simulations of the BiP–cLD monomer complex and plotted the fraction of native contacts over time. These results, which demonstrate the consistency of the interface across replicas, are now included in the Supplementary Material.

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Figure 20 legend) “Fraction of native contacts between BiP and cLD monomer in simulations of the structures predicted by AlphaFold 3 without ligands or in complex with ADP or ATP. The dark lines indicate the rolling average of the fraction of native contacts over 100 frames, while the shaded lines indicate the value per frame. The fraction of native contacts (Q) was calculated according to the definition of Best et al. [12]: . For N pairs of native contacts (i, j), where is the distance of the pair in the initial configuration (here the AlphaFold 3 prediction), r_(i,j)(X) is the distance at frame X, β is a smoothing parameter (β = 50 nm⁻¹), λ is the tolerance of the reference distance (λ \= 1.8) and the cutoff used to define a contact between heavy atoms was 0.45 nm.”

(13) The figure legends are noted using lowercase letters but are described using uppercase.

We thank the Reviewer for pointing that out, and we changed everything to capital letters.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1: I am confused about the HDX-MS results shown in Figure 1. Here, I must also mention that I am not familiar with comparing HDX-MS experiments with MD simulations. The authors mention that they show the deuterated fraction computed from MD simulations for the PDB and AF model at time points 0.5 min and 5 min. However, this time certainly does not correspond to the MD simulation time, thus, it is unclear to me where the difference between the results comes from. Are the two time points some input parameters to the script used to calculate the deuterated fraction? Thus, I would ask the authors to better explain what is the difference in the results between the two time points. Especially, since the general reader might not be familiar with comparing HDX-MS experimental results to MD simulations. Furthermore, I would ask the authors to clarify in the Figure 1 caption that these time points do not correspond to the MD simulation time.

We thank the Reviewer for pointing us to this possible source of confusion. The time points are effectively input parameters to the calculations of theoretical deuterated fractions from MD simulations. We expanded the explanation of the method in the method section and clarified in the Figure 1 caption that these time points do not correspond to the MD simulation time.

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To determine the deuterated fraction of a peptide segment from simulations, the protection factor for each residue i, Pi, must be computed from the simulation snapshots, following the approach of Best and Vendruscolo [13]: . Here, N_C,i and N_H,i are the number of H-bonds and heavy-atom contacts of the backbone amide of residue i, and the scaling factors β_C and β_H are set to 0.35 and 2.0, respectively. The simulated deuterated fraction of a peptide segment, , defined by residues m_j +1 to n_j, was then calculated at any exchange time point t as:

Where m_j and n_j are the first and last residue numbers of the j-th protein fragment, respectively. The intrinsic exchange rate constants for each residue type () were obtained from Bai et al. with updated acidic residues and glycine [14, 15].”

Addition to the text. (Figure 1 legend: ) “This time point corresponds to experimental incubation times, not MD simulation time.”

Addition to the text. (Figure 10 legend: ) “Time points correspond to experimental incubation times, not MD simulation time.”

(2) For AlphaFold 2 Multimer prediction, the authors only considered the top predicted structure. However, AF2-M, one generally obtains 5 structures, and it is also possible to obtain more structures by using an additional random seed. Thus, it would be interesting if the authors would consider the difference between the 5 structures they obtained from the AF2-M prediction. Are they all very similar? (Especially considering the DR1 and DR2 segments, that is the main difference between the PDB and AF2 structures). Analyzing the different predicted AF2 structures would give more insight into the accuracy of the AF2-M predicted model.

We thank the Reviewer for this insightful suggestion. All AF2-M predicted structures were found to be highly similar, and we now include them in Figure 7E for comparison.

Addition to the text. (Figure 7E legend) “(E) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT).”

(3) On Page 6, the authors talk about a "an early PDB model". First, I find the nomenclature "early" confusing here; perhaps it would be better to talk about "an initial PDB model", but I leave it up to the authors to think about if they want to change that. More importantly, reading the Comp. detail on Page 23, it is not so clear what the difference is between the "early" and "final" PDB models, and how the difference in their setups leads to different results. The information is somewhat there on Page 6 and Page 23, but it can be made much clearer. Thus, I would ask the authors to better explain the difference between the early and final PDB models.

We thank the Reviewer for this helpful comment. In the revised manuscript, we have clarified the terminology and provided a more explicit explanation of the differences between the two IRE1 models, both in the Results section and in the Methods.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “An initial PDB model with modified side chain orientations in residues L116 and Y166 due to the modelling of neighbouring missing DR1, caused the dimer to dissociate in one-third of the replicas. [...] The final PDB model, with correctly oriented L116 and Y166 (Supplementary Fig. 9B), was stable in simulations in both TIP3P and TIP4P-D water (Supplementary Fig. 7B).”

Addition to the text. (Methods section: IRE1_α_ core Luminal Domain (cLD) structural models - Human PDB dimer) “An initial PDB model was briefly equilibrated in NPT, and a conformation with a groove width of approximately 0.6 nm was selected. This snapshot was used as the initial structure for the initial “PDB model” simulations, in which the dimer dissociates.”

(4) Page 12: "In early simulations", again, I find the nomenclature "early" confusing here. Perhaps it would be better to talk about "In initial simulations" or "In preliminary simulations", but I leave it up to authors to think about this.

We thank the Reviewer for pointing out this possible source of confusion. We improved the text by referring to these simulations based on the different orientations of the peptide on the cLD dimer in the modeled complex.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0° orientation", as the peptide forms a 0° angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0°) orientation (Supplementary Fig. 14). We refer to these poses as the "90° orientation" and "270° orientation".”

Here, we provide a detailed description of the additional changes made to the manuscript.

Additional edits to the manuscript

Following discussions with Prof. Dr. David Ron, we refined our BiP model by removing the signal peptide (residues 1–18). Using AlphaFold 3, we predicted BiP–cLD heterodimeric complexes in the presence of ADP, ATP, or without nucleotide. Each of the three complexes was simulated in TIP3P water, in three independent replicas of 1 µs each.

Addition to the text. (Results section: hIRE1α cLD intermolecular interactions guide the activation process) “We used AlphaFold 3 to model the interaction between a cLD monomer and BiP (residues E19–L654) in the presence of ATP and ADP (Fig. 5B, Supplementary Fig. 19A). Prediction quality was limited in the apo and ADP-bound states (pTM = 0.48, ipTM = 0.59; pTM = 0.49, ipTM = 0.61, respectively), whereas ATP binding improved accuracy (pTM = 0.66, ipTM = 0.72). The predicted interfaces involved DR2, particularly residues 314PLLEG-318, forming a short parallel β-sheet with the substrate-binding domain (SBD) of BiP through two hydrogen bonds. All AlphaFold 3 models were stable across three 1-µs simulations (Supplementary Fig. 19B), with cLD–BiP interfaces retaining 60–80% of initial contacts (Supplementary Fig. 20). In the apo and ADP-bound states, the nucleotide-binding domain (NBD) showed high Predicted Aligned Error (PAE) relative to the cLD, indicating uncertain positioning of the two domains relative to each other. Notably, in the ADP-bound state, which is thought to interact with hIRE1α cLD, the NBD remained mobile but proximal to the αB-helices, thereby restricting access to this region. Together, the AlphaFold 3 predictions suggest that BiP engages hIRE1α cLD by sterically hindering the oligomerization interface defined by DR2 and the αB-helices [16].”

Addition to the text. (Figure 5 legend) “(B) BiP-cLD monomer complex as predicted by AlphaFold (BiP in shades of purple, cLD in orange) before the simulation (t = 0 µs) and at the end of the simulation (t = 1 µs). The SBD (residues E19-D408) is colored in light purple, and the NDB (residues C420-E650) in dark purple, and the interdomain linker (residues D409-V419) and KDEL motif (residues K651-L654) in light purple.”

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Methods section: cLD monomer in complex with BiP) “The BiP-cLD heterodimer systems were predicted with AlphaFold 3 using the AlphaFold server[17] at https://alphafoldserver.com/. The hIRE1α cLD sequence used is the same used for predicting the dimer: the PDB 2HZ6 sequence, Uniprot identifier O75460 with mutations C127S and C311S, and residues P29-P368. The BiP sequence used is taken from UniProt identifier P11021, residues E19L654. We predicted three complexes: one without any nucleotide, one containing ADP, and another containing ATP. Simulations of the BiP-cLD complex were run in TIP3P water.”

We have updated the Zenodo repository with additional data and calculations, and the corresponding link is provided in the manuscript.