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Referee #2

Evidence, reproducibility and clarity

Summary:

Carl et al present an application of a deep learning-based image analysis able to segment and classify individual yeast colonies by their phenotype in a special plate. They evaluated the method and show that it provides the accuracy similar to the one achieved by experts' manual classification.

Major comments:

The key conclusions are convincing. The evaluation is performed on 3 datasets showing different properties (strong presence of phenotype, almost lack of the phenotype, gradual change of the phenotype).

The claims are carefully formulated. The deep learning methodology (training, validation, using modern technologies such as transfer learning, Unet, augmentation) is carefully designed and carried out. The evaluation is sound. The limitations are discussed.

For a short paper as it's formulated currently, no additional experiments are necessary.

The methods are implemented and are available on GitHub.

However, I'd strongly recommend to share also the data used in the paper, to make possible the reproduction of the results as well as to be used as examples for future users.

No replicates are provided unfortunately. The manuscript would benefit from showing results from replicates, especially because they should be easily obtainable.

Minor comments:

I'm not familiar with the state of the art to judge on whether prior studies are referenced.

The text and fitures are very clear and well formulated.

Significance

Despite the conceptual innovation is average, the method is well-developed and seems to be very useful for yeast analysis.

I'm not an expert in the application area to judge the state of the art. The carried out deep learning methodology is top notch.

The manuscript can be interesting and useful for experts using the described assay for yeast.

My expertise is in omics, image analysis, and machine learning.

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Referee #1

Evidence, reproducibility and clarity

This study aims to develop tools for yeast researchers to automatically segment and classify yeast colonies. The machine learning method enables rapid classification compared to manual counting.

MAJOR CONCERNS:

Please include additional details about the types of images that must be captured for segmentation and categorization. It is important to provide details of what level of magnification might be needed during image capture. We anticipate that providing clear protocols for altering thresholds to classify colonies might be one way to overcome this challenge

While the program crops colonies and segments them accurately, there is no spatial information of where these colonies are located in the image. This loss of spatial information limits the ability to use this platform to identify colonies of interest following experiments such as a genetic screens.T

The inability to accurately recognize sectored colonies as sectored (rather than red) is a significant limitation to the usage of this program for quantitative assays. While differentiating between red and white colonies is useful, the conclusion by the authors about its value for quantitative assays is limited unless variegation can be accurately defined. The authors should either soften this conclusion or qualify what quantitative measurements might mean given the limitations of their classification program. This somewhat diminished our overall enthusiasm.

This program must be benchmarked with other colony classifiers. Cell Profiler is an example of a popular yeast colony segmentation program. How does this machine learning based tool compare with other colony segmentation and categorization programs. One possibility is to include an additional figure that compares their program with clear benchmarks. The outcome of effort based on benchmarking is not as important since we believe it is useful to have many alternatives for yeast segmentation and categorization. We think this revision would be essential to the manuscript and would add significant value.

MINOR CONCERN

The program currently saved cropped images of each segmented colony. This takes up a lot of storage space. It might be useful to provide an option to save or not save these cropped images. This flexibility will be valuable for users but does not detract from the major conclusions of the manuscript.

The authors have provided excellent examples of colonies they believe are red, white or sectored. More accurately defining a pink colony would be valuable for users of this program. How much of red is classified as pink by this program?

Providing an example data set with the protocol would be helpful for users with limited Python experience. In combination with their protocol on Protocol exchange, this would serve as a valuable resource for novices in programming.

One technical issue of the program is that the program tries to open all files in the specified folder even if they aren't jpg. This causes problems if there are additional or hidden files in the folder and the program cannot process the additional files.

Significance

This manuscript describes a machine learning approach to segment and categorize yeast colonies based on a red/white selection assay. The approach has been implemented using Python which makes this widely accessible to many researchers. Their detailed protocol on Protocol Exchange is a valuable resource which made it possible for us to evaluate its performance. The program meets its goals of reducing user time via manual counting. It is also reasonably accurate in discriminating between red and white colonies based on our initial tests. However, there are several important concerns that the authors will need to address before this manuscript can become a valuable resource for the yeast community. It is important to note that our framework is one where we have a great interest in quantitative yeast genetics but cannot evaluate the strengths and weakness of the computational approach. So much of the review is focussed on what would be needed to make this tool more user appropriate.

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Reply to the reviewers

We are grateful to all three reviewers for their careful analysis of the manuscript, and for their constructive comments. Two common critiques were:

(1) that assaying origin firing via an independent method would strengthen the conclusions, and (2) that additional analysis of ribonucleotide incorporation to exclude the retention of lagging-strand primers would allow us to definitively determine whether Pol ɛ plays a role in lagging-strand synthesis.

We will include experiments to address both critiques in a revised manuscript. To independently verify changes in origin efficiency, we will sequence nascent BrdU-containing DNA across a time course from cells released into S-phase: we will also use the last timepoint of our Okazaki sequencing analysis to control for potential cell-cycle differences. To further test the contribution of Pol ɛ and ascertain whether lagging-strand primers are retained, we will analyze ribonucleotide incorporation in both wild-type and pol2-M644L (Pol ɛ ribonucleotide hypo-incorporating) strains. We address individual specific comments and our planned revisions in more detail below.

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

This study examined the consequences of limiting levels of DNA polymerase d (Pol d) in yeast. The authors first reported multiple genome instability consequences following lowered Pol d level, including defect in S phase progression, growth defect, elevated spontaneous DNA damage, accumulation of ssDNA and activation of replication and DNA damage checkpoint. These observations are solid but not unexpected. By genome wide analysis using the Okazaki fragment (OF) mapping and ribonucleotide mapping (for polymerase usage), the authors claim a few potentially novel and striking observations that lowered Pol d differentially impact efficiencies of early vs. late origins, and that lowered Pol d results in Pol e participating in lagging strand synthesis around late origins. However, I remained unconvinced based on the data presented. These observations need to be further substantiated and alternative interpretations should be considered.

\*Main concerns:** *

One of major conclusions the authors tried to make is that the early vs. late origins are differentially affected by low level of Pol d. First, they used OF mapping data to examine origin efficiency. Asynchronous "Cultures were treated with IAA for 2h before the addition of rapamycin for 1h to deplete DNA ligase I (Cdc9) from the nucleus via anchor-away". IAA concentrations used were of 0, 0.2 mM, 0.6 mM, and 1 mM. The problem is that Figure S1 clearly showed that treating asynchronous cultures with >0.1 mM of IAA for as short as 30 min significantly alters the cell cycle profiles, mainly resulting in accumulation of S phase cells, to different extent. Presumably Okazaki fragments accumulated from these cultures suffering from the synchronizing effect may not be representative of the real change in global replication profile. For instance, it is not difficult to predict that the Okazaki fragments enrichment may be skewed towards late origins if more cells are accumulated in mid S phase following Pol d depletion. For this reason, I don't believe the result is conclusive. The experiment may be re-designed for samples at different time points following release from G1.

We agree that altered cell-cycle profiles might affect the number of Okazaki fragments sequenced in late vs early replicating regions of the genome. As noted by reviewer 3 in cross-commenting, these differences should not affect origin efficiency calculations as these are based on the ratio of reads on each strand (and therefore normalized). To more directly address this question, we will calculate origin firing efficiencies from the final timepoint of the arrest-release experiments shown in Figure 4 as suggested by the reviewer. We will also analyze origin efficiency using BrdU over a time course.

This concern also should preclude the authors from drawing conclusion about Pol e usage on lagging strands based on comparison between HydEn-seq data and OF mapping data shown in Figure 6. In fact, the rNMP incorporation change is very similar between early and late origins. The only evidence that the author rely on is the discrepancy in OF data between the two groups origins, which makes the reliability if origin efficiency measurement the central piece of data in this study. Thus, alternative approaches should also be considered to map origin efficiencies.

As noted above, we agree that an independent method of tracking origin firing efficiencies would be helpful to strengthen our conclusions. To this end, we will analyze time courses of BrdU incorporation from cultures released into S-phase.

Even if Pol e strand bias is lowered at late origins, as the authors tend to believe, there are still alternative models other than Pol e being used for lagging strand synthesis. For instance, if TLS polymerases are used on lagging strands, it could result in more ribonucleotide incorporation on the lagging strand, as they are lower-fidelity polymerases. Alternatively, if Pol d scarcity leads to more Pol e synthesis or lower RNA primer processing, it might also contribute to more apparent ribonucleotide incorporation on the lagging strands.

We feel that the widespread use of TLS polymerases is unlikely, especially given the data in figure 6A that show no growth or viability change upon deletion of all three TLS polymerases in the Pol ∂ depletion strain, even at very low levels of Pol ∂. We agree with the reviewer that our data do not conclusively rule out increased retention of lagging-strand primers – as we state in the text. We aim to test this possibility by analyzing ribonucleotide strand bias in a pol2-M644L strain that incorporates fewer ribonucleotides than the wild-type Pol ɛ. In this case, increased lagging-strand primer retention would lead to a lagging-strand bias of ribonucleotides upon Pol ∂ depletion, while increased Pol ɛ usage would not. An analogous experiment with wild-type POL2 is potentially harder to interpret because the wild-type polymerase is the predominant source of ribonucleotides in a wild-type strain (Nick McElhinny et al, 2010 - PMID:20729855), but we now have the data for this strain in hand and ready to analyze.

In Figure S5, the two HydEn-seq replicates are very different, where replicate1 shows very low strand bias. I suspect perhaps the strain used for replicate 1 does not contain pol2-M644G or rnh202 deletion.

The change in ribonucleotide incorporation is indeed substantially stronger in one replicate than the other. We have additional time-course data from a Pol ∂ depletion showing that ribonucleotide strand bias decreases over time as Pol ∂ is depleted, and will include this in a revised manuscript.

Reviewer #1 (Significance (Required)):

Given that different aspects of Pol d deficiency have been implicated in various human diseases and cancer, this type of analysis is of interest to the field.

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

\*Summary** *

In this manuscript the authors explore the basis of the deleterious effects of reduced levels of the replicative Polymerase delta. This polymerase plays several important roles in the replication process: it synthesizes most of the lagging strand, but also extends the first primer during the synthesis of the lagging strand, and it contributes to the removal of the RNA and most of the DNA synthesized by primase/Polymerase alpha during Okazaki fragment maturation. In this study, the authors systematically analyze the impact of Pol delta depletion in S. cerevisiae. They use a degron-tagged allele to modulate the levels of the polymeraes and apply mainly NGS methods and classical genetics to explore the consequences for survival, checkpoint signalling and replication features such as fork speed, origin firing efficiency and Okazaki fragment length and distribution. They report that Pol delta depletion leads to a checkpoint activation via the Rad9-dependent damage signalling pathway (but not the Mrc1-dependent replisome-associated signalling) and an accumulation of single-stranded DNA. Phosphorylation of histone H2A is taken as a marker of DNA double-strand breaks, and from the observation that deletion of recombination factors, but not end-joining factors aggravate the fitness of Pol delta-depleted cells they conclude that homologous recombination is responsible for the repair of these breaks. Analysis of replication by Okazaki fragment sequencing indicates a slight decrease in the firing efficiency of early/efficient origins, but an increase in the firing efficiency of late origins. They also observe a reduction in fork speed, although they are not able to attribute this to either a globally slower fork movement or an increase in the stalling of individual forks. They find that Pol delta depletion does not change the size of Okazaki fragments, but causes defects in the nick translation during Okazaki fragment maturation. Finally, they use NGS technology to show that the leading strand Polymerase epsilon engages in lagging strand replication particularly at late origins when Pol delta is depleted. From their observations, the authors develop a model where depletion of Pol delta primarily affects late replicating regions. They explain this by invoking a stable association of Pol delta with early replisomes, which sequesters the enzyme, thus causing an under-supply at replisomes that assemble later during S phase. This then leads to the involvement of Pol epsilon on the lagging strand. Based on the observation that fork speed and Okazaki fragment maturation are both affected, they propose that these two reactions normally compete for Pol delta, suggesting that optimal replication would require two molecules of the polymerase per fork.

\*Major comments** *

The experiments shown here are largely clean and well controlled, and the manuscript is written nicely and well-structured.

Compared to the Okazaki fragment analysis, the treatment of double-strand breaks appears somewhat cursory and remains inconclusive. Phosphorylation of H2A seems insufficient evidence for double-strand breaks, as other structures could also give rise to that signal. These lesions should be detected in a more direct manner, e.g. pulsed-field gel electrophoresis. The authors also don't provide a mechanism by which such breaks would emerge. Related to the minor effect of the ku mutant, I am wondering about the altered appearance of the colonies in Figure 2F (concerning both ku70 and rad51) - what is different about these, and could their „denser" appearance explain the slight suppression effect observed?

We agree that our treatment of double-strand breaks is limited: consistent with comments from all three reviewers about which aspects of this work are most novel, we intend to focus as much as possible on replication enzymology here. We will tone down the language around double-strand breaks in the manuscript.

Concerning the damage signalling: it is surprising to see a damage signal at concentrations of IAA that do not lead to a significant depletion of Pol delta yet (0.05 mM). At this point, it is hard to imagine DSBs to form. Could the authors explain this discrepancy?

We note that, as observed in Figure 1A and to a slightly lesser extent in Fig. 2E, Pol ∂ levels are already substantially reduced in 0.05 mM IAA. This reduction appears sufficient to induce damage

The notion that late origin firing is enhanced despite checkpoint activation is counterintuitive. Do the authors think that this effect overcomes the suppression of late origins that is normally associated with checkpoint activation? It would be helpful to test whether abolishing that phenomenon (e.g. by a mec1-100 mutant) would enhance the effect and render late origins even more active.

We thank the reviewer for this excellent suggestion: we will test the effects of a mec1-100 mutant and include the results in a revised manuscript.

It would be important to characterise the fork speed defect better, using alternative methods rather than just relying on Okazaki fragments. A differentiation between slower fork progression and more frequent fork stalling would be relevant and might help to evaluate the contribution of Pol epsilon. This might be accomplished by DNA fibre analysis. Alternatively, BrdU incorporation could serve to observe replication over the entire genome rather than only in the vicinity of replication origins. It would also be important to differentiate fork speeds in early versus late replicating regions - according to the authors' model, the defects should be most obvious in the late regions (Fig. 4 concerns only early origins).

As noted above in our response to reviewer 1, we will use BrdU incorporation to independently verify changes in fork speed and origin firing. Analysis of fork speed in late-replicating regions is challenging regardless of the methodology used, due to contributions from converging forks, but we will try to do this

Figure S3: Considering the differences in cell cycle progression, it would make more sense to compare equivalent stages of the cell cycle / S phase rather than identical time points.

We can include this analysis, although the changes in cell cycle progression and origin firing efficiency make such comparisons somewhat subjective

Considering that the Okazaki fragment analysis was done with non-synchronised cultures, is it possible that the skew in the cell cycle profile could influence the Okazaki fragment pattern?

(copy-pasted from our response to a similar query by reviewer 1)… We agree that altered cell-cycle profiles might affect the number of Okazaki fragments sequenced in late vs early replicating regions of the genome. As noted by reviewer 3 in cross-commenting, these differences should not affect origin efficiency calculations as these are based on the ratio of reads on each strand (and therefore normalized). To more directly address this question, we will calculate origin firing efficiencies from the final timepoint of the arrest-release experiments shown in Figure 4 as suggested by the reviewer.

Would it be possible to monitor not only total Pol delta levels, but also the level of Pol delta bound to the chromatin? It is shown that the level of Pol delta is depleted in the whole cell extracts, but it would be interesting to see how severe the depletion is on the chromatin.

We agree that the relative fraction of chromatin-bound vs free Pol ∂ is an interesting question, and will attempt this experiment. However, we note that extensive depletion of Pol3 makes it hard to detect by Western blot, so the results are likely to be most informative at modest depletion levels. Regardless, these data should give us an idea of the size of the ‘free’ Pol ∂ pool in cells with normal or mildly reduced Pol ∂.

Figure 6 is confusing and should be clarified: - Figure 6B: assigning the Watson and Crick strands in the schematic would make that figure easier to understand; - Figure 6B-C: the axes are labeled as 'Fraction of rNMP on Watson strand', but would it not make more sense if they were labeled 'Fraction of rNMP in Crick strand'? - Figure 6D-E: the right side scale is labelled as 'increase in rNMP on Crick strand' while in the figure legend is says it is 'change in the fraction of ribonucleotides mapping to the Watson strand. That description should be clarified; - Figure 6D: using 'Change in Okazaki fragments strand bias' to label the black line (description in the box above the figure) instead 'Change in Okazaki strand bias' would be more appropriate; - Figure 6F: the authors seem to have subtracted strand bias measured for Okazaki fragments from the strand bias measured for rNMP. It is valid to subtract these biases from each other, considering that the two structures arise independently and with different frequencies?

We can make changes to figure 6 as suggested. Regarding the validity of subtracting strand biases, we think this is sufficient to give at least a semi-quantitative view of Pol ɛ usage since both of our sequencing approaches produce quantitative readouts that directly report on replication direction or polymerase usage, respectively.

\*Minor comments:** *

Can the authors conclude that Pol delta deficiency/ incompleteness of lagging strand synthesis affects the nucleosome deposition onto DNA? (Figure 5-A)

We cannot rule out that this is occurring, and we agree that this is an interesting question for future studies. But the changes that we observe Okazaki fragment terminus location are very similar to our previously published observations from cells lacking Rad27 function, consistent with decreased nick translation.

Why did the authors use rnh202Δ and not a mutant in the catalytic subunit of RNase H2?

Deletion of any subunit of the heterotrimeric RNase H2 complex completely abolishes its function in yeast, so RNH202 was a somewhat arbitrary choice

An extra control might be useful: comparing POL3-AID rnh202Δ with the POL3-AID pol2M644G rnh202Δ triple mutant could further confirm that the observed effect is Pol epsilon-dependent.

We agree (see also our response to reviewer 1). In addition to the wild-type, we will analyze pol2-M644L – a mutant in which Pol ɛ incorporates fewer than normal ribonucleotides. An increase in ribonucleotide density on the lagging strand in pol2-M644L would support increased primer retention on the lagging strand.

Figure 2H: It would be good to see the cell cycle distribution corresponding to the western blot images.

We can include this

Various spelling, grammar or precision of expression issues: - Pg. 4, line 4: endonucleolytically instead of nucleolytically. - Pg. 6, line 10: Remove 'was'. - Pg. 6, line 12: Remove 'in vivo' from the subtitle. - Pg. 6, line 14: 'an C-terminal' should be 'a C-terminal' - Pg 16, line 13: Phrasing implies that the synthesis of both leading and lagging strands by Pol delta in regions in the vicinity of replication origins is essential - please quote any paper testing its essentiality. - Please follow standard yeast genotype nomenclature, remove ';' when listing the yeast genotypes (e.g. POL3-AID mec1Δ sml1Δ instead of POL3-AID;mec1Δ;sml1Δ- example from Figure 2-B). - Concentrations of IAA are missing in few places (e.g. legend of Figure 1-C, page 24). - Figure 1A: add the label 'IAA (mM)' - Figure 2G: pleae provide a shorter exposure of the H4 blot in addition to the one shown. - Figure 6: adding a schematic presenting the events at actively and passively replicating late origins (and the predictions about leading and lagging strand bias) would help to understand the figure. - The format of the references is inconsistent. - 'On Watson/Crick strand' should be replaced with 'in Watson/Crick strand' We will fix typos, etc

Reviewer #2 (Significance (Required)):

This is a nice piece of work that provides in vivo confirmation of several observations that have been made in purified recombinant systems. In that sense, the overall novelty is limited, but this type of study is still important to do, as biochemical assays do not always reflect what is happening in cells, and this study gives insight into basic activities of the replisome. The participation of Pol epsilon in lagging strand synthesis is an interesting observation. Overall, the study will be of interest for the DNA replication field. My own expertise is in replication, predominantly in yeast. I have experience in NGS analysis of replication as well as in genetic analysis of the DNA damage response. I therefore feel competent to evaluate all aspects of the manuscript.

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

This manuscript describes the consequences of reducing the cellular concentration of a pol-delta subunit in S. cerevisiae. Pol-delta plays multiple cellular roles at both the replication fork (it is one of two DNA polymerases responsible for lagging strand synthesis) and during repair synthesis after DNA damage. The authors combine genetic and genomic methodologies to characterise how reduction in pol-delta concentration impacts on cellular fitness and specifically lagging strand synthesis. Overall it is technically a well executed study that is clearly presented and the data are predominantly appropriately interpreted.

\*I have a number of major comments:** *

1) The authors apply OK-seq (a methodology first developed by the senior author and therefore they are clearly experts at this) to study the consequence of pol-delta depletion on genome replication. OK-seq requires isolation of Okazaki fragments and this in turn requires removal of DNA ligase (Cdc9) - the authors achieve this with the anchor away system. My concern is that in these experiments the authors are depleting two factors required for lagging strand synthesis: pol-delta and ligase; it is unclear to me how the authors can determine the relative contribution of each depletion to the observed phenotypes. Could some of the observed phenotypes (e.g. fork slowing, 5' and 3' ends of Okazaki fragments, etc) be a consequence of the double depletion, rather than just pol-delta depletion as concluded by the authors? The authors present this as a method to determine genome replication timing, but really it is an assay to look at fork direction. Given the need for an addition mutation in OK-seq (cdc9), I would encourage the authors to consider a more direct assay for replication dynamics upon pol-delta depletion, such as a copy number measure (or BrdU-ip) of DNA replication or DNA combing - these methods don't require Cdc9 depletion and could therefore ensure that observed phenotypes are a consequence of pol-delta depletion (rather than the double depletion).

As outlined in our response to the first two reviewers, we will do BrdU-IP experiments. We agree that the double depletion may have an effect on fork speed, and that BrdU-IP will allow us to test this possibility. However, we note that our analysis of Okazaki fragment initiation/processing requires the depletion of Cdc9, so for this we are limited to looking at differences between Cdc9 depletion alone vs Cdc9 depletion + Pol3 depletion.

2) One major conclusion reached by the authors is that pol-epsilon can contribute to lagging strand synthesis upon pol-delta depletion (at least during late replication). This conclusion comes from the authors use of HydEn-seq to measure rNTP incorporation from which the contribution of a polymerase (pol-epsilon in this case) to strand synthesis can be determined. In a manner analogous to OK-seq, this requires the introduction of additional mutations (both in the polymerase and by the removal of RNaseH activity). The authors interpretation that pol-epsilon can play a role in lagging strand synthesis is dependent upon there being no temporal change in pol-delta strand-displacement activity, despite continued pol-delta depletion through S phase. It is not clear to me that the data presented in Fig 5 & 6 has the sensitivity to conclude this (and the OK-seq data is also subject to the potential bias of the double depletion of pol-delta and Cdc9). I feel that a necessary control to support this conclusion, would be to undertake the HydEn-seq experiment in the absence of the pol-epsilon mutation (just pol-delta depletion in the absence of RNaseH activity). This would allow the authors to measure any increase is residual rNTPs (likely from pol-alpha primase) on the lagging strand as a consequence of pol-delta depletion and determine whether they are equally likely in early and late S phase.

As discussed in our response to the first two reviewers, we will analyze analogous data from both a POL2 wild-type and a pol2-M644L strain that incorporates fewer ribonucleotides than the wild-type.

\*The following comments are more minor:** *

-for the experiment in Fig S1B, the growth in 1.0 mM IAA is somewhat surprising given how sick the cells appear on equivalent plates. I couldn't find in the methods a description of the experimental conditions.

The cells grow very slowly in 1 mM IAA (doubling time doubles). We think this is quite consistent with the poor growth on plates

-there is considerable variability in the S phase kinetics from bulk DNA analysis (flow cytometry) when comparing Fig 1C, 2D, S3. Fig 1C appears to be the exception, with all the other figures showing poor S phase progress by comparison. It would be useful for the authors to recognise these differences and comment upon them. E.g. they appear to all be identical experiments, but are there experimental differences that could explain the different kinetics?

We see some variability in our release, but generally cells enter S-phase at around 30 minutes. The release in figure S3 was carried out at 25 ˚C rather than 30 ˚C, which accounts for the additional delay in these data

-Fig 2F, why is the rad51-deletion less severe that rad52-deletion - should they not be identical?

We agree that these should logically be very similar: we do not know why the two mutants behave slightly differently at some (but not all) IAA concentrations

-Fig 2H - could the authors show the flow cytometry (in a supplemental figure) for this experiment?

We can show this

-Fig 3B-E: OEM is described as a measure of origin efficiency - how is possible for this to have negative values?

OEM describes Okazaki fragment strand bias around previously identified origins. If such an origin does not fire in our strain background, a negative OEM can result.

-pp9: "Analysis of Okazaki fragment strand bias across the genome suggested that the average direction of replication was relatively similar at most loci across all Pol3 depletion conditions". The authors data is quantitative and they should be able to quantify how similar their data are across the various conditions, rather than making a qualitative statement: "relatively similar".

We apologize and can re-phrase this. The intention of this statement is simply to draw the reader’s attention to the fact that global distributions of Okazaki fragments are not completely altered (e.g. only 1-2 origins per chromosome) as a prelude to the more quantitative analysis that follows in figure 3.

-pp9: "origin firing efficiency in S. cerevisiae correlates strongly with replication timing"; it would be useful for the authors to support this statement with a citation.

We will add 1-2 citations to support this statement

-Fig 4A: it would help the reader if the authors could show 'zoomed in' examples of the points that the authors make (in addition to the whole chromosome view): slowed fork progression, reduced early origin activity, increased late origin activity (e.g. an origin that is normally passively replicated, that upon pol-delta depletion is no longer passively replicated and therefore becomes more efficient), etc.

We agree that this would be helpful, and can add examples in the supplement

-pp11: "An analogous global decrease in replication-origin firing efficiency has been observed in Pol ∂-deficient human fibroblasts" - but the authors are reporting a global increase in origin firing efficiency (Fig 3B).

We can re-phrase this.

-the nucleosomal ladder in Fig 5A is only weakly apparent from the gel and not particularly apparent from the density trace, this makes it's disappearance upon IAA treatment hard to interpret. Is the weak nucleosomal ladder what the authors had anticipated (in the absence of IAA)?

We do not expect a weaker nucleosomal ladder than normal in the absence of IAA. In our experience these gels just sometimes give better ladders than others, and we hope that the traces help with interpretation

-I found the effects being described by the authors in Fig 5B & C difficult to see, particularly for the transcription factors. Furthermore, why are these data differently normalised to those in Fig 4B & C (median vs. maximum)

In figure 4 we normalize to maximum since all DNA should eventually be replicated, and we therefore think that showing coverage relative to a maximum value of 1 is most informative. In figure 5 we compare distributions of termini around obstacles, and therefore feel that normalizing to the median is a more appropriate way to compare enrichment around a given meta-element. The shapes of the graphs would be unchanged by choosing a different normalization point. In order to make changes easier to see, we can make the lines thinner in figure 5 and/or change the y-axis scale.

-the final sentence of the results section returns to an analysis of the OK-seq data and is essentially a temporally segregated analysis (Fig S6) otherwise equivalent to that presented in Fig 5B. Given the importance placed on these data by the authors in the interpretation of the HydEn-seq data, I feel that it would help the reader to have been presented with these data earlier in the results section.

We can move these data up

-p22: OK-seq methods. The authors should indicate the culture conditions for these experiments.

We can include this

-p22: Computational analyses: the authors should indicate which reference genome assembly they used.

We can include this

-Fig 6B & C: the y-axis labels are confusing - do the authors mean Crick strand here?

Oops. Yes, we do. We thank the reviewer for catching this

\*REFEREE CROSS COMMENTING:** *

All three reviewers seems to be in broad agreement about this manuscript. There is one significant concern raised by the other reviewers that I'd missed: that some of the Okazaki fragment analysis was done with non-synchronised cultures. I agree with this concern, however I don't think that there is necessarily a problem with the alternative explanation suggested by reviewer #1 ('Okazaki fragments enrichment may be skewed towards late origins'). While the accumulation of S phase cells might well be expected to lead to a bias towards isolating more Okazaki fragments from around late origins, the authors calculate the fraction of reads (i.e. Okazaki fragments) mapping to each strand. The potential presence of more late S phase cells would give greater sequence coverage over late replicating regions, but alone would not alter the fraction of reads mapping to each strand. However, I agree that interpretation of this experiment is not as simple as suggested by the authors and there may well be alternative explanations along the lines suggested by reviewer #1.

There was a subsequent Okazaki fragment experiment performed with synchronised cells (Fig 4) and it might be possible to use these data to assess any differential impact on early vs late origins.

We agree, and will do this analysis

Reviewer #3 (Significance (Required)):

My expertise is in DNA replication and genome stability, particularly replication timing and replication origin function.

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Referee #3

Evidence, reproducibility and clarity

This manuscript describes the consequences of reducing the cellular concentration of a pol-delta subunit in S. cerevisiae. Pol-delta plays multiple cellular roles at both the replication fork (it is one of two DNA polymerases responsible for lagging strand synthesis) and during repair synthesis after DNA damage. The authors combine genetic and genomic methodologies to characterise how reduction in pol-delta concentration impacts on cellular fitness and specifically lagging strand synthesis. Overall it is technically a well executed study that is clearly presented and the data are predominantly appropriately interpreted.

I have a number of major comments:

1) The authors apply OK-seq (a methodology first developed by the senior author and therefore they are clearly experts at this) to study the consequence of pol-delta depletion on genome replication. OK-seq requires isolation of Okazaki fragments and this in turn requires removal of DNA ligase (Cdc9) - the authors achieve this with the anchor away system. My concern is that in these experiments the authors are depleting two factors required for lagging strand synthesis: pol-delta and ligase; it is unclear to me how the authors can determine the relative contribution of each depletion to the observed phenotypes. Could some of the observed phenotypes (e.g. fork slowing, 5' and 3' ends of Okazaki fragments, etc) be a consequence of the double depletion, rather than just pol-delta depletion as concluded by the authors? The authors present this as a method to determine genome replication timing, but really it is an assay to look at fork direction. Given the need for an addition mutation in OK-seq (cdc9), I would encourage the authors to consider a more direct assay for replication dynamics upon pol-delta depletion, such as a copy number measure (or BrdU-ip) of DNA replication or DNA combing - these methods don't require Cdc9 depletion and could therefore ensure that observed phenotypes are a consequence of pol-delta depletion (rather than the double depletion).

2) One major conclusion reached by the authors is that pol-epsilon can contribute to lagging strand synthesis upon pol-delta depletion (at least during late replication). This conclusion comes from the authors use of HydEn-seq to measure rNTP incorporation from which the contribution of a polymerase (pol-epsilon in this case) to strand synthesis can be determined. In a manner analogous to OK-seq, this requires the introduction of additional mutations (both in the polymerase and by the removal of RNaseH activity). The authors interpretation that pol-epsilon can play a role in lagging strand synthesis is dependent upon there being no temporal change in pol-delta strand-displacement activity, despite continued pol-delta depletion through S phase. It is not clear to me that the data presented in Fig 5 & 6 has the sensitivity to conclude this (and the OK-seq data is also subject to the potential bias of the double depletion of pol-delta and Cdc9). I feel that a necessary control to support this conclusion, would be to undertake the HydEn-seq experiment in the absence of the pol-epsilon mutation (just pol-delta depletion in the absence of RNaseH activity). This would allow the authors to measure any increase is residual rNTPs (likely from pol-alpha primase) on the lagging strand as a consequence of pol-delta depletion and determine whether they are equally likely in early and late S phase.

The following comments are more minor:

-for the experiment in Fig S1B, the growth in 1.0 mM IAA is somewhat surprising given how sick the cells appear on equivalent plates. I couldn't find in the methods a description of the experimental conditions.

-there is considerable variability in the S phase kinetics from bulk DNA analysis (flow cytometry) when comparing Fig 1C, 2D, S3. Fig 1C appears to be the exception, with all the other figures showing poor S phase progress by comparison. It would be useful for the authors to recognise these differences and comment upon them. E.g. they appear to all be identical experiments, but are there experimental differences that could explain the different kinetics?

-Fig 2F, why is the rad51-deletion less severe that rad52-deletion - should they not be identical?

-Fig 2H - could the authors show the flow cytometry (in a supplemental figure) for this experiment?

-Fig 3B-E: OEM is described as a measure of origin efficiency - how is possible for this to have negative values?

-pp9: "Analysis of Okazaki fragment strand bias across the genome suggested that the average direction of replication was relatively similar at most loci across all Pol3 depletion conditions". The authors data is quantitative and they should be able to quantify how similar their data are across the various conditions, rather than making a qualitative statement: "relatively similar".

-pp9: "origin firing efficiency in S. cerevisiae correlates strongly with replication timing"; it would be useful for the authors to support this statement with a citation.

-Fig 4A: it would help the reader if the authors could show 'zoomed in' examples of the points that the authors make (in addition to the whole chromosome view): slowed fork progression, reduced early origin activity, increased late origin activity (e.g. an origin that is normally passively replicated, that upon pol-delta depletion is no longer passively replicated and therefore becomes more efficient), etc.

-pp11: "An analogous global decrease in replication-origin firing efficiency has been observed in Pol ∂-deficient human fibroblasts" - but the authors are reporting a global increase in origin firing efficiency (Fig 3B).

-the nucleosomal ladder in Fig 5A is only weakly apparent from the gel and not particularly apparent from the density trace, this makes it's disappearance upon IAA treatment hard to interpret. Is the weak nucleosomal ladder what the authors had anticipated (in the absence of IAA)?

-I found the effects being described by the authors in Fig 5B & C difficult to see, particularly for the transcription factors. Furthermore, why are these data differently normalised to those in Fig 4B & C (median vs. maximum)

-the final sentence of the results section returns to an analysis of the OK-seq data and is essentially a temporally segregated analysis (Fig S6) otherwise equivalent to that presented in Fig 5B. Given the importance placed on these data by the authors in the interpretation of the HydEn-seq data, I feel that it would help the reader to have been presented with these data earlier in the results section.

-p22: OK-seq methods. The authors should indicate the culture conditions for these experiments.

-p22: Computational analyses: the authors should indicate which reference genome assembly they used.

-Fig 6B & C: the y-axis labels are confusing - do the authors mean Crick strand here?

REFEREE CROSS COMMENTING:

All three reviewers seems to be in broad agreement about this manuscript. There is one significant concern raised by the other reviewers that I'd missed: that some of the Okazaki fragment analysis was done with non-synchronised cultures. I agree with this concern, however I don't think that there is necessarily a problem with the alternative explanation suggested by reviewer #1 ('Okazaki fragments enrichment may be skewed towards late origins'). While the accumulation of S phase cells might well be expected to lead to a bias towards isolating more Okazaki fragments from around late origins, the authors calculate the fraction of reads (i.e. Okazaki fragments) mapping to each strand. The potential presence of more late S phase cells would give greater sequence coverage over late replicating regions, but alone would not alter the fraction of reads mapping to each strand. However, I agree that interpretation of this experiment is not as simple as suggested by the authors and there may well be alternative explanations along the lines suggested by reviewer #1.

There was a subsequent Okazaki fragment experiment performed with synchronised cells (Fig 4) and it might be possible to use these data to assess any differential impact on early vs late origins.

Significance

My expertise is in DNA replication and genome stability, particularly replication timing and replication origin function.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this manuscript the authors explore the basis of the deleterious effects of reduced levels of the replicative Polymerase delta. This polymerase plays several important roles in the replication process: it synthesizes most of the lagging strand, but also extends the first primer during the synthesis of the lagging strand, and it contributes to the removal of the RNA and most of the DNA synthesized by primase/Polymerase alpha during Okazaki fragment maturation. In this study, the authors systematically analyze the impact of Pol delta depletion in S. cerevisiae. They use a degron-tagged allele to modulate the levels of the polymeraes and apply mainly NGS methods and classical genetics to explore the consequences for survival, checkpoint signalling and replication features such as fork speed, origin firing efficiency and Okazaki fragment length and distribution. They report that Pol delta depletion leads to a checkpoint activation via the Rad9-dependent damage signalling pathway (but not the Mrc1-dependent replisome-associated signalling) and an accumulation of single-stranded DNA. Phosphorylation of histone H2A is taken as a marker of DNA double-strand breaks, and from the observation that deletion of recombination factors, but not end-joining factors aggravate the fitness of Pol delta-depleted cells they conclude that homologous recombination is responsible for the repair of these breaks. Analysis of replication by Okazaki fragment sequencing indicates a slight decrease in the firing efficiency of early/efficient origins, but an increase in the firing efficiency of late origins. They also observe a reduction in fork speed, although they are not able to attribute this to either a globally slower fork movement or an increase in the stalling of individual forks. They find that Pol delta depletion does not change the size of Okazaki fragments, but causes defects in the nick translation during Okazaki fragment maturation. Finally, they use NGS technology to show that the leading strand Polymerase epsilon engages in lagging strand replication particularly at late origins when Pol delta is depleted. From their observations, the authors develop a model where depletion of Pol delta primarily affects late replicating regions. They explain this by invoking a stable association of Pol delta with early replisomes, which sequesters the enzyme, thus causing an under-supply at replisomes that assemble later during S phase. This then leads to the involvement of Pol epsilon on the lagging strand. Based on the observation that fork speed and Okazaki fragment maturation are both affected, they propose that these two reactions normally compete for Pol delta, suggesting that optimal replication would require two molecules of the polymerase per fork.

Major comments

The experiments shown here are largely clean and well controlled, and the manuscript is written nicely and well-structured.

Compared to the Okazaki fragment analysis, the treatment of double-strand breaks appears somewhat cursory and remains inconclusive. Phosphorylation of H2A seems insufficient evidence for double-strand breaks, as other structures could also give rise to that signal. These lesions should be detected in a more direct manner, e.g. pulsed-field gel electrophoresis. The authors also don't provide a mechanism by which such breaks would emerge. Related to the minor effect of the ku mutant, I am wondering about the altered appearance of the colonies in Figure 2F (concerning both ku70 and rad51) - what is different about these, and could their „denser" appearance explain the slight suppression effect observed?

Concerning the damage signalling: it is surprising to see a damage signal at concentrations of IAA that do not lead to a significant depletion of Pol delta yet (0.05 mM). At this point, it is hard to imagine DSBs to form. Could the authors explain this discrepancy?

The notion that late origin firing is enhanced despite checkpoint activation is counterintuitive. Do the authors think that this effect overcomes the suppression of late origins that is normally associated with checkpoint activation? It would be helpful to test whether abolishing that phenomenon (e.g. by a mec1-100 mutant) would enhance the effect and render late origins even more active.

It would be important to characterise the fork speed defect better, using alternative methods rather than just relying on Okazaki fragments. A differentiation between slower fork progression and more frequent fork stalling would be relevant and might help to evaluate the contribution of Pol epsilon. This might be accomplished by DNA fibre analysis. Alternatively, BrdU incorporation could serve to observe replication over the entire genome rather than only in the vicinity of replication origins. It would also be important to differentiate fork speeds in early versus late replicating regions - according to the authors' model, the defects should be most obvious in the late regions (Fig. 4 concerns only early origins).

Figure S3: Considering the differences in cell cycle progression, it would make more sense to compare equivalent stages of the cell cycle / S phase rather than identical time points.

Considering that the Okazaki fragment analysis was done with non-synchronised cultures, is it possible that the skew in the cell cycle profile could influence the Okazaki fragment pattern?

Would it be possible to monitor not only total Pol delta levels, but also the level of Pol delta bound to the chromatin? It is shown that the level of Pol delta is depleted in the whole cell extracts, but it would be interesting to see how severe the depletion is on the chromatin.

Figure 6 is confusing and should be clarified:

• Figure 6B: assigning the Watson and Crick strands in the schematic would make that figure easier to understand;
• Figure 6B-C: the axes are labeled as 'Fraction of rNMP on Watson strand', but would it not make more sense if they were labeled 'Fraction of rNMP in Crick strand'?
• Figure 6D-E: the right side scale is labelled as 'increase in rNMP on Crick strand' while in the figure legend is says it is 'change in the fraction of ribonucleotides mapping to the Watson strand. That description should be clarified;
• Figure 6D: using 'Change in Okazaki fragments strand bias' to label the black line (description in the box above the figure) instead 'Change in Okazaki strand bias' would be more appropriate;
• Figure 6F: the authors seem to have subtracted strand bias measured for Okazaki fragments from the strand bias measured for rNMP. It is valid to subtract these biases from each other, considering that the two structures arise independently and with different frequencies?

Minor comments:

Can the authors conclude that Pol delta deficiency/ incompleteness of lagging strand synthesis affects the nucleosome deposition onto DNA? (Figure 5-A)

Why did the authors use rnh202Δ and not a mutant in the catalytic subunit of RNase H2?

An extra control might be useful: comparing POL3-AID rnh202Δ with the POL3-AID pol2M644G rnh202Δ triple mutant could further confirm that the observed effect is Pol epsilon-dependent.

Figure 2H: It would be good to see the cell cycle distribution corresponding to the western blot images.

Various spelling, grammar or precision of expression issues:

• Pg. 4, line 4: endonucleolytically instead of nucleolytically.
• Pg. 6, line 10: Remove 'was'.
• Pg. 6, line 12: Remove 'in vivo' from the subtitle.
• Pg. 6, line 14: 'an C-terminal' should be 'a C-terminal'
• Pg 16, line 13: Phrasing implies that the synthesis of both leading and lagging strands by Pol delta in regions in the vicinity of replication origins is essential - please quote any paper testing its essentiality.
• Please follow standard yeast genotype nomenclature, remove ';' when listing the yeast genotypes (e.g. POL3-AID mec1Δ sml1Δ instead of POL3-AID;mec1Δ;sml1Δ- example from Figure 2-B).
• Concentrations of IAA are missing in few places (e.g. legend of Figure 1-C, page 24).
• Figure 1A: add the label 'IAA (mM)'
• Figure 2G: pleae provide a shorter exposure of the H4 blot in addition to the one shown.
• Figure 6: adding a schematic presenting the events at actively and passively replicating late origins (and the predictions about leading and lagging strand bias) would help to understand the figure.
• The format of the references is inconsistent.
• 'On Watson/Crick strand' should be replaced with 'in Watson/Crick strand'

Significance

This is a nice piece of work that provides in vivo confirmation of several observations that have been made in purified recombinant systems. In that sense, the overall novelty is limited, but this type of study is still important to do, as biochemical assays do not always reflect what is happening in cells, and this study gives insight into basic activities of the replisome. The participation of Pol epsilon in lagging strand synthesis is an interesting observation. Overall, the study will be of interest for the DNA replication field. My own expertise is in replication, predominantly in yeast. I have experience in NGS analysis of replication as well as in genetic analysis of the DNA damage response. I therefore feel competent to evaluate all aspects of the manuscript.

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Referee #1

Evidence, reproducibility and clarity

This study examined the consequences of limiting levels of DNA polymerase d (Pol d) in yeast. The authors first reported multiple genome instability consequences following lowered Pol d level, including defect in S phase progression, growth defect, elevated spontaneous DNA damage, accumulation of ssDNA and activation of replication and DNA damage checkpoint. These observations are solid but not unexpected. By genome wide analysis using the Okazaki fragment (OF) mapping and ribonucleotide mapping (for polymerase usage), the authors claim a few potentially novel and striking observations that lowered Pol d differentially impact efficiencies of early vs. late origins, and that lowered Pol d results in Pol e participating in lagging strand synthesis around late origins. However, I remained unconvinced based on the data presented. These observations need to be further substantiated and alternative interpretations should be considered.

Main concerns:

One of major conclusions the authors tried to make is that the early vs. late origins are differentially affected by low level of Pol d. First, they used OF mapping data to examine origin efficiency. Asynchronous "Cultures were treated with IAA for 2h before the addition of rapamycin for 1h to deplete DNA ligase I (Cdc9) from the nucleus via anchor-away". IAA concentrations used were of 0, 0.2 mM, 0.6 mM, and 1 mM. The problem is that Figure S1 clearly showed that treating asynchronous cultures with >0.1 mM of IAA for as short as 30 min significantly alters the cell cycle profiles, mainly resulting in accumulation of S phase cells, to different extent. Presumably Okazaki fragments accumulated from these cultures suffering from the synchronizing effect may not be representative of the real change in global replication profile. For instance, it is not difficult to predict that the Okazaki fragments enrichment may be skewed towards late origins if more cells are accumulated in mid S phase following Pol d depletion. For this reason, I don't believe the result is conclusive. The experiment may be re-designed for samples at different time points following release from G1.

This concern also should preclude the authors from drawing conclusion about Pol e usage on lagging strands based on comparison between HydEn-seq data and OF mapping data shown in Figure 6. In fact, the rNMP incorporation change is very similar between early and late origins. The only evidence that the author rely on is the discrepancy in OF data between the two groups origins, which makes the reliability if origin efficiency measurement the central piece of data in this study. Thus, alternative approaches should also be considered to map origin efficiencies.

Even if Pol e strand bias is lowered at late origins, as the authors tend to believe, there are still alternative models other than Pol e being used for lagging strand synthesis. For instance, if TLS polymerases are used on lagging strands, it could result in more ribonucleotide incorporation on the lagging strand, as they are lower-fidelity polymerases. Alternatively, if Pol d scarcity leads to more Pol e synthesis or lower RNA primer processing, it might also contribute to more apparent ribonucleotide incorporation on the lagging strands.

In Figure S5, the two HydEn-seq replicates are very different, where replicate1 shows very low strand bias. I suspect perhaps the strain used for replicate 1 does not contain pol2-M644G or rnh202 deletion.

Significance

Given that different aspects of Pol d deficiency have been implicated in various human diseases and cancer, this type of analysis is of interest to the field.

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Reply to the reviewers

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

In this article, the authors characterize a complex formed by sec22b-stx1-Esyt2. They investigate how such interactions are involved in the modulation of dynamics of the plasma membrane in the context of neuritogenesis. They conclude that the contact sites between the ER and the plasma membrane, mediated by the afore-mentioned complex, contribute the expansion of the plasma membrane.

**Major comments:**

Overall, the article clearly shows that in mammalian cells there is an interaction between sec22b-stx1-Esyt2 which appears to be important for filopodia formation and possibly neuritogenesis in neurons. However, performing additional experiments to better clarify some links and assumptions made by authors could strengthen the article.

The manuscript relies on work performed either on cell lines (HeLA, PC12) or primary neuronal cultures. Although it is clear the value of the findings obtained using cell lines, they should be seen as a complementary rather than an exclusive approach. This is particularly important as the authors often make claim about neuron-related cellular biology.

For instance, the biochemistry-based findings on the interaction and characterization of the protein complex (Figure 1) are all derived from experiments perfomed in Hela or PC12. As the authors have the capacity to culture and manipulate primary neuronal cultures, such findings should be validates in neuronal cells. The authors could also consider performing biochemical experiments (i.e. co-ip) of the endogenous proteins in neuronal cultures or brain tissue.*

->Endogenous Co-IP has been tried in E18 brain tissue. One experiment using brain tissue demonstrated co-immunoprecipitation of endogenous Sec22b and E-Syt2. Unfortunately, repetitions of this experiment failed due to high background in negative control (naïve Rabbit IgG). We agree with the reviewer that this data is worth trying again. We will carry out this co-immunoprecipitation experiment from cultured neurons to answer the reviewer’s request.

The authors do show some evidence regarding the complex in neuronal cells using PLA (proximity ligation assay, figure 2) or super resolution microscopy, however, these findings should be corroborated by stronger findings targeting interaction and not based on simple proximity.

->We agree with this reviewer that PLA is limited in demonstrating the occurrence of a protein complex. We would like to stress that we have used PLA complementarily to immunoprecipitation and that we already have shown STED super-resolution data (Figure 3). In order to strengthen the STED data, we will include more details in the figure, as a supplementary movie and a supplementary spreadsheet with the quantification of the distance between the E-Syt2/Sec22b clusters to the plasma membrane stained using WGA. The STED data demonstrate that 50% of the clusters are closer than 33.6nm to the plasma membrane, a distance in the range of ER-PM contact sites.

A similar critique regards the experiments using RNA-interference of Figure 4. Performing loss-of-function experiments in neuronal cultures would strengthen and complement the results obtained via over-expression approaches shown in Figure 5.

->The loss-of-function experiments in neuronal cultures using siRNA were attempted unsuccessfully. The three E-Syts have largely different cDNA sequences thus three distinct siRNAs must be transfected in order to silence all three simultaneously. This is quite challenging in neuronal cultures and we were never able to get strong silencing of the three E-Syts. In the following points, we plan to carry out further experiments using expression of a fragment of Sec22b (Longin domain). We are confident that this is a better approach to demonstrate the importance of Sec22b/E-Syt interaction.

*Given that the authors have already in place all the necessary technology for the suggested biochemical and morphological-related experiments, these could be carried out swiftly within 3-4 months.

**Minor comments:**

The manuscript is really technical and at times tough to follow; it could benefit from key sentences to better guide the reader, particularly if not coming from the specialist field, in the appreciation of the experiments and results.

Authors should submit the manuscript to a severe round of proofreading. There are several inconsistencies and sometimes what looks like internal comments: i.e. in the methods "STED Missing" or the fact that "LTP" is used everywhere but not defined and considering that the targeted audience is most likely neuroscience-based could easily lead to confusion.

*

->We fully agree with this reviewer and apologize for leaving behind such errors. We will carefully proofread the revised ms.

*The experiments appear to have been repeated a sufficient number of times and the statistics seem adequate. It would be advisable to show in dot-plots the findings rather than in bar graphs all findings and not just the morphometrics-relative ones.

*

->We will modify the figures according to this reviewer’s suggestion.

Reviewer #1 (Significance (Required)):

*This work closely follows the excellent previous work from the Galli laboratory. As such, it is mostly incremental from a technical perspective and does not present particularly novel findings. An interesting aspect would be in addressing directly the influence of the described interactions in the lipid transfer between ER and the plasma membrane but in that sense the manuscript falls short. Although it is to be appreciated the functional readouts in terms of neuritogenesis, in the present state the manuscript features findings suitable for a very specific audience.

I believe that the appropriate audience for the present manuscript lies within the neuroscientific community interested in development, specifically neuritogenesis, and/or membrane dynamics. Additionally, it might be interesting also for researchers outside of the neuroscience community and interested in the dynamics between ER and plasma membrane.

*

->We are happy to read the comments of this reviewer. Nevertheless, we would like to stress the importance of deciphering precise molecular mechanisms in any biological process. Here, we are the first to demonstrate an interaction between lipid-transfer proteins E-Syts and ER v-SNARE Sec22b. As an example, the molecular mechanism connecting synaptic SNAREs and synaptotagmin has been the topic of more than 500 publications since seminal articles in the early 1990’s. We think that the first article linking E-Syts to SNAREs cannot be considered as a mere increment from our previous work.

The activity of E-Syts to transfer lipids in vitro has been well established __(1–3) In addition, recent work by the De Camilli lab using Origami showed that reducing the distance between liposomes enhanced the lipid transfer mediated by E-Syt2 (3). Therefore, we did not carry out experiments such as combining SNAREs and E-Syt2 in artificial membranes in vitro because we considered that there would not be much more to demonstrate than what has already been done. Furthermore, we considered the experiments in cells, particularly neurons, much more critical at this point. Demonstrating transfer of glycerophospholipid between ER and PM in cells cannot be performed like other lipids’ transfer at other membrane interfaces for the following reasons: phospholipids are very abundant (4) and they are not modified upon transfer (1)__, there are no specific dyes to detect glycerophospholipids (unlike phosphoinositides), and ER and PM are too close to distinguish if a glycerophospholipid is in one or the other membrane. Such a challenging experiment would require the ability to setup a specific biochemical assay circumventing these constraints. We think that this is out of the scope of the present study focused on the role of E-Syt/Sec22b complex.

Nevertheless, in order to get further insights on this question, we will express WT and mutant E-Syt2, purify the PM using the protocol of Figure 4 in Saheki et al __(1)__, followed by lipidomics analysis. We hope that this approach further supports our idea that E-Syts mediate an important lipid transfer mechanism towards the PM.

* Keywords regarding my expertise: Molecular and Cellular Neuroscience, Morphometrics, Dendrite, Neurons, Dendritogenesis, Biochemistry, Imaging, Microscopy.

__

Reviewer #2 (Evidence, reproducibility and clarity (Required)): *This manuscript identifies and characterises a novel interaction between E-Syts and Sec22b and demonstrates that lipid transfer between the ER and PM contributes to the development of filopodia and neuronal expansion. This interaction with E-Syt2 occurs through the Longin domain of Sec22b Sec22b association. The authors suggest a continuum with further interactions with syntaxin1, that mediates neurite outgrowth. Overall I find this study very interesting and convincing. The experimental analysis is well carried out and the claims are well aligned with their results.

I only have minor issues:

Figure 1. Some of the western blots have several bands and it is difficult to know which band is the relevant one. They should be indicated in the fig panel. Further panel E and F are barely readable and should be redrawn with the appropriate line and font size.*

->We will make the changes requested by this reviewer in Figure 1.

• *

Figure 2: is there a difference between the number of dots in axons and dendrites? Can the author elaborate on this aspect as it is not clear from the image presented.

->We could not combine PLA with further staining of MAP2 and TAU. Indeed, to perform PLA, neurons are already double labelled to detect the proteins of interest. At the stage of the neurons used in this study, both axons and dendrites are growing. Therefore, we did not invest in distinguishing between axons and dendrites. Because growth cones are known to be the major sites of membrane growth, we instead distinguished dots within neurites and in growth cones. We will make the other changes requested by this reviewer in Figure 2.

Figure 7: statistical analysis should be indicated from the BoNT/A and BoNT/C as BoNT/A represent an appropriate control cleaving SNAP25 but not Syntaxin.

->We agree with this request and we will add statistical analysis as suggested, using BoNT/A as an additional control.

On top of controlling fusion and neuronal outgrowth, syntaxin has a role in survival and its cleavage leads to neuronal death. Is this pathway mediated by E-Syts interactions?

->We have stated in the ms: “Since exposure to BoNT/C1 at high concentrations and for long incubation periods causes degeneration of neurons in culture __(5,6)__, various concentrations and incubation times were tested, and a 4-hour treatment of neurons with 1nM BoNTs was chosen to avoid such deleterious effects.” Accordingly, we did not see any degeneration in our experimental conditions.__ __

Reviewer #2 (Significance (Required)): This papers identifies the molecular mechanism of neuronal outgrowth. It is highly significant. ->We are very grateful to this reviewer for pointing out the high significance of our article.

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

__*1. The evidence for the claim that the Sec22b/Stx1 complex and E-Syts colocalize in native cells (neurons) and bind in heterologous cells is strong (3 independent lines of evidence: co-immunoprecipitation, Proximity Ligation (PLA) and STED super-resolution microscopy) However, the current title of the paper makes a claim beyond this interaction/proximity, based on evidence that is obtained with E-Syt over-expression in wildtype cells. The physiological relevance of the effects remain elusive with over-expression in wildtype cells only.

Furthermore, it is plausible that overexpression of membrane binding/bending C2-domains promotes neurite outgrowth and ramifications by a non-specific effect (as shown for copine C2 domains, PMID:25450385 and indirect evidence for synaptotagmins1,2,7).*

* This issue is especially relevant in the light of the fact that loss of all 3 Extended Synaptotagmins does not affect normal mouse development and viability (PMID: 27399837)

It would be more appropriate to choose a more descriptive title*

• *

->We agree with this reviewer that the original title may be too strong and are now proposing the following, more descriptive title:

Role of the Sec22b/E-Syt complex in neurite growth and ramification

We are fully aware that proteins harbouring C2 domains could potentially promote non-specific effects when overexpressed. However, we do not think this is the case here because none of the morphological effects of E-Syt2 expression in neurons and HeLa cells were reproduced by mutants lacking the SMP or the membrane-anchoring domains. Based on work on Copine __(7)__, a cytosolic protein, E-Syt2 still containing 3xC2 domains but lacking the membrane-anchoring domain should have shown a morphological effect if non-specific binding to phosphoinositides was the mechanism of action. We will discuss this point in the ms.

• The evidence for the working model that the morphological effects of E-Syt2 depends on the Sec22b/Stx1 complex is not strong. Although plausible, the positive effect on neurite outgrowth (E-Syt2 overexpression) and the negative effects (inhibition by Stx1 cleaveage, Sec22b-Longin or Sec22b extended linker expression) may in fact be independent

  The evidence could be strengthened by PLA measurements in neurons over-expressing Myc-E-Syt2 and Sec22b to assess MSC density. It is predicted that in both conditions, MCS density increases. MCS density by PLA measurements could also be performed in Sec22b-P33 and DLongin overexpressed and BoNT/C1 treated neurons. According to the model, the number of MCS should go down. This is of special interest for BoNT/C1 treatment, as it is important to show that the altered morphology is not purely caused by a pre-state of degeneration that is known to be induced by BoNT/C1. In addition, EM measurements of ER-PM distances might provide an independent line of evidence.*

->We agree with this reviewer that additional experiments could strengthen the description of the molecular mechanism. To this end, we will carry out the following experiments:

1/Co-immunoprecipitation experiments of endogenous Syntaxin, Sec22b and E-Syt2 in cells expressing GFP as control or Longin-GFP to demonstrate that expression of the Longin domain perturbs the association of Sec22b with E-Syt2 and Syntaxin.

2/PLA measuring the association between E-Syt2 and Syntaxin in cells expressing GFP as control or Longin-GFP to demonstrate that expression of the Longin domain perturbs the association between E-Syt2 and Syntaxin using a complementary approach.

Unfortunately, membrane-associated, BoNTC1-cleaved syntaxin corresponds to a short fragment undetectable by available antibodies whereas the fragment detected by the antibody after BoNTC1 cleavage lacks the transmembrane domain (Figure 7a). Therefore, we cannot perform PLA in BoNTC1-treated neurons.

We are confident that further exploring the mechanism of action of the Longin domain, together with the data already in the ms, will make it very clear that the morphological effects of E-Syt2 depends on the Sec22b/Stx1 complex.

1. • Link between neurite outgrowth and lipid transfer is weak. The authors argue that functional E-syt/Sec22b/Stx interaction is important for neurite outgrowth by mediating lipid transfer. The only line of evidence they provide is the absence of outgrowth effects in E-syt mutants lacking SMP or membrane spanning domains. However, from the data it is unclear whether these mutants are correctly folded, expressed and/or localized. Additional ICC stainings of the mutants in neurons are necessary to drive this point home. *

• *

->The mutants and siRNA have been already used and validated in Giordano et al. 2013 __(8)__, therefore we did not carry out experiments aiming at basic characterization of these reagents. To answer this request, we will show images of the subcellular localization by ICC of WT and mutant E-Syt2 in the revised Figure 6 or in a Supplementary Figure.

In addition, the authors might make the link between neurite outgrowth and lipid transfer stronger by examining PM lipid levels and distribution in control, Myc-E-Syt2 and E-Syt2 mutant neurons.

->We agree with this reviewer that this question is of high relevance. In order to answer this request, we will express WT and mutant E-Syt2, purify the PM using the protocol of Figure 4 in Saheki et al __(1)__, followed by lipidomics analysis. We hope that this approach further supports our idea that E-Syts mediate an important lipid transfer mechanism towards the PM.

1. • There is no clear evidence that E-syt first binds to Sec22b, after which Stx1 leaves SNAP25 and joins the interaction. This should be indicated as speculation.

   * ->We will make it clear that our model in Figure 9 is a hypothetical model.

• An apparent discrepancy exists between the TKD E-syts effects (i.e. reduced MSC density, Fig 4) and the lack of neurite outgrowth defects in TKO E-syts. According to the proposed model, the levels of E-syt correlate with the number of MSCs and thereby neurite outgrowth. Furthermore, to knock down E-Syts, single siRNAs against the three E-syts were used in Fig4. Off-target effects are not controlled in this approach. Using multiple siRNAs and/or siRNA resistant rescues would be required for robust conclusions.

  *

->The mutants and siRNA have already been used and validated in Giordano et al. 2013 __(8)__, therefore we did not carry out experiments aiming at basic characterization of these reagents. In addition, we would like to stress the complexity of carrying out a rescue experiment of a triple KD of proteins.

Statistical analysis is incomplete. It is not clear whether statistical assumptions (e.g. normal distribution) were checked before performing the tests, and whether non-parametric alternatives where used if assumptions were not met.

->We thank this reviewer for making this important alert. We would like to stress that we have always checked whether samples followed the normal distribution and made non-parametric tests__. We will include this comment in the methods.__

In Fig4, a T-test is used between multiple groups. This test can only be used when comparing two groups. Number of (independent) measurements is not clear in Fig1, 2, 4

->In all the figure legends the number of repetitions is specified

All figures: display all individual data points in all bar graphs (as shown in 5c)

*

*

\*Minor comments:**

1. Inconsistencies on distances in model. Syts are enlongated proteins and thought to be found in MSCs of ~20 nm (Fernandez-Busnadiego, 2015). Trans-SNARE complexes start to interact when the distance between membranes is ~8 nm (Liu, 2007). In the introduction, the authors suggest that incomplete zippering might occur between Stx and Sec22b, resulting in a distance between 10 and 20 nm, which would allow E-Syt localization. In the discussion, however, the authors suggest a model where Sec22b/Stx interaction is important to bring the membranes in ~10 nm distance to enhance LTP activity. Proof for either model is lacking. Please clarify.*

Fig1A: Please clarify the multiple bands? for Stx3 (anti-eGFP).

• *

->These additional bands are recognised by the anti-GFP antibody, the tag being N-terminal, thus they represent proteolytic fragments. We consistently observe these in our experiments.

Fig2: There is no size marker for panels C1-C6

• *

->We will make the appropriate correction.

Fig3: Both proteins seem to show a diffuse pattern. Please specify the validity of measuring average distance. A higher magnification zoom of staining pattern in the growth cone and visualization of the calculation could benefit interpretation.

• *

->We agree with this reviewer that Figure 3 was not optimal to show all the extent of our STED data. In order to strengthen this part, we will include more details in both the figure and as a supplementary movie and supplementary spreadsheet with the quantification of the distance between the E-Syt2/Sec22b clusters to the plasma membrane stained using WGA. The STED data demonstrate that 50% of the clusters are closer than 33.6nm to the plasma membrane, a distance in the range of ER-PM contact sites.

• E-Syt2 and E-Syt3 are used interchangeably throughout the manuscript and E-Syt1 is left out completely. It would help the reader if the authors could elaborate on their interpretation on the similarities and differences in structure and functionality between the three E-Syts.

1. Why is there a red line in Fig 7b?*

__->We added the red line to highlight the shift of SNAP25 band in BoNTA samples. If misleading, it can be removed

Reviewer #3 (Significance (Required)):__

A growing body of literature recognizes the importance of close proximities between membranes, facilitating direct interaction between organelles (Scorrano et al., 2019). Membrane Contact Sites (MCSs) are shown to be important for a wide range of cellular functions, such as lipid and calcium transfer. E-Syts have been recognized as one of the key players in neuronal MCSs, mediating lipid transport (Fernández-Busnadiego et al., 2015). A study published in 2014 by the authors of the current study revealed another two proteins important for MSCs in neurons (Petkovic et al., 2014). ER protein Sec22b and PM SNARE Syntaxin1 were shown to form a non-fusogenic trans-SNARE complex, important for lipid-transfer mediated neurite outgrowth. Gallo and colleagues have now provided important new evidence that these two components (E-Syts and Stx1/Sec22b) are together and may work together at MSCs.

->We thank this reviewer for stressing the importance of our article and agree with the conclusion of __Fernández-Busnadiego et al. (9) on E-Syts being one of the key players in neuronal MCSs, mediating lipid transport. We think that our work is a further key piece of evidence in the demonstration of the importance of E-Syts in neuronal development.__

Bibliography

Saheki Y, Bian X, Schauder CM, Sawaki Y, Surma MA, Klose C, et al. Control of plasma membrane lipid homeostasis by the extended synaptotagmins. Nat Cell Biol. 2016 Apr 11;18(5):504–515. Yu H, Liu Y, Gulbranson DR, Paine A, Rathore SS, Shen J. Extended synaptotagmins are Ca2+-dependent lipid transfer proteins at membrane contact sites. Proc Natl Acad Sci USA. 2016 Apr 19;113(16):4362–4367. Bian X, Zhang Z, Xiong Q, De Camilli P, Lin C. A programmable DNA-origami platform for studying lipid transfer between bilayers. Nat Chem Biol. 2019 Jul 18;15(8):830–837. Alberts B, Johnson A, Lewis J, Raff M. The lipid bilayer. Molecular Biology of …. 2002; Osen-Sand A, Staple JK, Naldi E, Schiavo G, Rossetto O, Petitpierre S, et al. Common and distinct fusion proteins in axonal growth and transmitter release. J Comp Neurol. 1996 Apr 1;367(2):222–234. Igarashi M, Kozaki S, Terakawa S, Kawano S, Ide C, Komiya Y. Growth cone collapse and inhibition of neurite growth by Botulinum neurotoxin C1: a t-SNARE is involved in axonal growth. J Cell Biol. 1996 Jul;134(1):205–215. Park N, Yoo JC, Lee Y-S, Choi HY, Hong S-G, Hwang EM, et al. Copine1 C2 domains have a critical calcium-independent role in the neuronal differentiation of hippocampal progenitor HiB5 cells. Biochem Biophys Res Commun. 2014 Nov 7;454(1):228–233. Giordano F, Saheki Y, Idevall-Hagren O, Colombo SF. PI (4, 5) P2-dependent and Ca2+-regulated ER-PM interactions mediated by the extended synaptotagmins. Cell. 2013; Fernández-Busnadiego R, Saheki Y, De Camilli P. Three-dimensional architecture of extended synaptotagmin-mediated endoplasmic reticulum-plasma membrane contact sites. Proc Natl Acad Sci USA. 2015 Apr 21;112(16):E2004–13.

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Referee #3

Evidence, reproducibility and clarity

1. The evidence for the claim that the Sec22b/Stx1 complex and E-Syts colocalize in native cells (neurons) and bind in heterologous cells is strong (3 independent lines of evidence: co-immunoprecipitation, Proximity Ligation (PLA) and STED super-resolution microscopy) However, the current title of the paper makes a claim beyond this interaction/proximity, based on evidence that is obtained with E-Syt over-expression in wildtype cells. The physiological relevance of the effects remain elusive with over-expression in wildtype cells only.

Furthermore, it is plausible that overexpression of membrane binding/bending C2-domains promotes neurite outgrowth and ramifications by a non-specific effect (as shown for copine C2 domains, PMID:25450385 and indirect evidence for synaptotagmins1,2,7).

This issue is especially relevant in the light of the fact that loss of all 3 Extended Synaptotagmins does not affect normal mouse development and viability (PMID: 27399837)

It would be more appropriate to choose a more descriptive title

1. The evidence for the working model that the morphological effects of E-Syt2 depends on the Sec22b/Stx1 complex is not strong. Although plausible, the positive effect on neurite outgrowth (E-Syt2 overexpression) and the negative effects (inhibition by Stx1 cleaveage, Sec22b-Longin or Sec22b extended linker expression) may in fact be independent

The evidence could be strengthened by PLA measurements in neuronsover-expressing Myc-E-Syt2 and Sec22b to assess MSC density. It is predicted that in both conditions, MCS density increases. MCS density by PLA measurements could also be performed in Sec22b-P33 and Longin overexpressed and BoNT/C1 treated neurons. According to the model, the number of MCS should go down. This is of special interest for BoNT/C1 treatment, as it is important to show that the altered morphology is not purely caused by a pre-state of degeneration that is known to be induced by BoNT/C1. In addition, EM measurements of ER-PM distances might provide an independent line of evidence.

a. Link between neurite outgrowth and lipid transfer is weak. The authors argue that functional E-syt/Sec22b/Stx interaction is important for neurite outgrowth by mediating lipid transfer. The only line of evidence they provide is the absence of outgrowth effects in E-syt mutants lacking SMP or membrane spanning domains. However, from the data it is unclear whether these mutants are correctly folded, expressed and/or localized. Additional ICC stainings of the mutants in neurons are necessary to drive this point home. In addition, the authors might make the link between neurite outgrowth and lipid transfer stronger by examining PM lipid levels and distribution in control, Myc-E-Syt2 and E-Syt2 mutant neurons.

b. There is no clear evidence that E-syt first binds to Sec22b, after which Stx1 leaves SNAP25 and joins the interaction. This should be indicated as speculation.

c. An apparent discrepancy exists between the TKD E-syts effects (i.e. reduced MSC density, Fig 4) and the lack of neurite outgrowth defects in TKO E-syts. According to the proposed model, the levels of E-syt correlate with the number of MSCs and thereby neurite outgrowth. Furthermore, to knock down E-Syts, single siRNAs against the three E-syts were used in Fig4. Off-target effects are not controlled in this approach. Using multiple siRNAs and/or siRNA resistant rescues would be required for robust conclusions.

Statistical analysis is incomplete. It is not clear whether statistical assumptions (e.g. normal distribution) were checked before performing the tests, and whether non-parametric alternatives where used if assumptions were not met. In Fig4, a T-test is used between multiple groups. This test can only be used when comparing two groups. Number of (independent) measurements is not clear in Fig1, 2, 4. All figures: display all individual data points in all bar graphs (as shown in 5c)

Minor comments:

1. Inconsistencies on distances in model. Syts are enlongated proteins and thought to be found in MSCs of ~20 nm (Fernandez-Busnadiego, 2015). Trans-SNARE complexes start to interact when the distance between membranes is ~8 nm (Liu, 2007). In the introduction, the authors suggest that incomplete zippering might occur between Stx and Sec22b, resulting in a distance between 10 and 20 nm, which would allow E-Syt localization. In the discussion, however, the authors suggest a model where Sec22b/Stx interaction is important to bring the membranes in ~10 nm distance to enhance LTP activity. Proof for either model is lacking. Please clarify.
2. Fig1A: Please clarify the multiple bands? for Stx3 (anti-eGFP).
3. There is no size marker for panels C1-C6
4. Fig3: Both proteins seem to show a diffuse pattern. Please specify the validity of measuring average distance. A higher magnification zoom of staining pattern in the growth cone and visualization of the calculation could benefit interpretation.
5. E-Syt2 and E-Syt3 are used interchangeably throughout the manuscript and E-Syt1 is left out completely. It would help the reader if the authors could elaborate on their interpretation on the similarities and differences in structure and functionality between the three E-Syts.
6. Why is there a red line in Fig 7b?

Significance

A growing body of literature recognizes the importance of close proximities between membranes, facilitating direct interaction between organelles (Scorrano et al., 2019). Membrane Contact Sites (MCSs) are shown to be important for a wide range of cellular functions, such as lipid and calcium transfer. E-Syts have been recognized as one of the key players in neuronal MCSs, mediating lipid transport (Fernández-Busnadiego et al., 2015). A study published in 2014 by the authors of the current study revealed another two proteins important for MSCs in neurons (Petkovic et al., 2014). ER protein Sec22b and PM SNARE Syntaxin1 were shown to form a non-fusogenic trans-SNARE complex, important for lipid-transfer mediated neurite outgrowth. Gallo and colleagues have now provided important new evidence that these two components (E-Syts and Stx1/Sec22b) are together and may work together at MSCs.

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Referee #2

Evidence, reproducibility and clarity

This manuscript identifies and characterises a novel interaction between E-Syts and Sec22b and demonstrates that lipid transfer between the ER and PM contributes to the development of filopodia and neuronal expansion. This interaction with E-Syt2 occurs through the Longin domain of Sec22b Sec22b association. The authors suggest a continuum with further interactions with syntaxin1, that mediates neurite outgrowth. Overall I find this study very interesting and convincing. The experimental analysis is well carried out and the claims are well aligned with their results.

I only have minor issues:

Figure 1. Some of the western blots have several bands and it is difficult to know which band is the relevant one. They should be indicated in the fig panel. Further panel E and F are barely readable and should be redrawn with the appropriate line and font size. Figure 2: is there a difference between the number of dots in axons and dendrites? Can the author elaborate on this aspect as it is not clear from the image presented. Figure 7: statistical analysis should be indicated from the BoNT/A and BoNT/C as BoNT/A represent an appropriate control cleaving SNAP25 but not Syntaxin. On top of controlling fusion and neuronal outgrowth, syntaxin has a role in survival and its cleavage leads to neuronal death. Is this pathway mediated by E-Syts interactions?

Significance

This papers identifies the molecular mechanism of neuronal outgrowth. It is highly significant.

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Referee #1

Evidence, reproducibility and clarity

In this article, the authors characterize a complex formed by sec22b-stx1-Esyt2. They investigate how such interactions are involved in the modulation of dynamics of the plasma membrane in the context of neuritogenesis. They conclude that the contact sites between the ER and the plasma membrane, mediated by the afore-mentioned complex, contribute the expansion of the plasma membrane.

Major comments:

Overall, the article clearly shows that in mammalian cells there is an interaction between sec22b-stx1-Esyt2 which appears to be important for filopodia formation and possibly neuritogenesis in neurons. However, performing additional experiments to better clarify some links and assumptions made by authors could strengthen the article.

The manuscript relies on work performed either on cell lines (HeLA, PC12) or primary neuronal cultures. Although it is clear the value of the findings obtained using cell lines, they should be seen as a complementary rather than an exclusive approach. This is particularly important as the authors often make claim about neuron-related cellular biology.

For instance, the biochemistry-based findings on the interaction and characterization of the protein complex (Figure 1) are all derived from experiments perfomed in Hela or PC12. As the authors have the capacity to culture and manipulate primary neuronal cultures, such findings should be validates in neuronal cells. The authors could also consider performing biochemical experiments (i.e. co-ip) of the endogenous proteins in neuronal cultures or brain tissue.

The authors do show some evidence regarding the complex in neuronal cells using PLA (proximity ligation assay, figure 2) or super resolution microscopy, however, these findings should be corroborated by stronger findings targeting interaction and not based on simple proximity.

A similar critique regards the experiments using RNA-interference of Figure 4. Performing loss-of-function experiments in neuronal cultures would strengthen and complement the results obtained via over-expression approaches shown in Figure 5.

Given that the authors have already in place all the necessary technology for the suggested biochemical and morphological-related experiments, these could be carried out swiftly within 3-4 months.

Minor comments:

The manuscript is really technical and at times tough to follow; it could benefit from key sentences to better guide the reader, particularly if not coming from the specialist field, in the appreciation of the experiments and results.

Authors should submit the manuscript to a severe round of proofreading. There are several inconsistencies and sometimes what looks like internal comments: i.e. in the methods "STED Missing" or the fact that "LTP" is used everywhere but not defined and considering that the targeted audience is most likely neuroscience-based could easily lead to confusion.

The experiments appear to have been repeated a sufficient number of times and the statistics seem adequate. It would be advisable to show in dot-plots the findings rather than in bar graphs all findings and not just the morphometrics-relative ones.

Significance

This work closely follows the excellent previous work from the Galli laboratory. As such, it is mostly incremental from a technical perspective and does not present particularly novel findings. An interesting aspect would be in addressing directly the influence of the described interactions in the lipid transfer between ER and the plasma membrane but in that sense the manuscript falls short. Although it is to be appreciated the functional readouts in terms of neuritogenesis, in the present state the manuscript features findings suitable for a very specific audience.

I believe that the appropriate audience for the present manuscript lies within the neuroscientific community interested in development, specifically neuritogenesis, and/or membrane dynamics. Additionally, it might be interesting also for researchers outside of the neuroscience community and interested in the dynamics between ER and plasma membrane.

Keywords regarding my expertise: Molecular and Cellular Neuroscience, Morphometrics, Dendrite, Neurons, Dendritogenesis, Biochemistry, Imaging, Microscopy.

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Reply to the reviewers

Authors’ response to reviewers for manuscript “Bacterial killing by complement requires direct anchoring of Membrane Attack Complex precursor C5b-7” (reference #RC-2019-00125)

Our manuscript entitled “Bacterial killing by complement requires direct anchoring of Membrane Attack Complex precursor C5b-7” has been reviewed by Review Commons. We thank the referees for their interest in our study and are very pleased that the referees consider our findings novel, important and well-designed. Based on the comments given by the referees, we have revised our manuscript and have included two new experimental figures:

-Experimental data validating that our gating strategy with Sytox blue correlates well with bacterial killing on plate (Fig S1-B)

-Experimental data validating that non-bactericidal MAC complexes damage the bacterial OM (Fig. S1-C).

In the response letter below, we respond to the comments raised by the reviewers and explain how we have revised our paper accordingly. All changes into the revised manuscript are clearly highlighted in yellow.

POINT-TO-POINT REPLY

Reviewer #1

(Evidence, reproducibility and clarity (Required)): The paper by Doorduijn et al. addresses a question rarely touched upon in modern studies of the complement system, namely the stability and time-resolved functions of complement component. It extends two earlier reports from the same laboratory, however, with a clear, novel point concerning especially the function of C7. The study embodies several techniques and modes of investigation. From these experiments, the paper contributes significantly to our understanding of the MAC complex is formed and why some bacteria escape this host defense mechanism. Over all the study is very well performed and written. I have only a few major comments.

Reviewer #1 raises 3 points:

POINT 1. The AFM pictures shown in Fig. 6D are of outstanding quality. However, it is a disappointment that the outcome of complement incubation was shown only for a complement-resistant E. coli strain. Would it be possible to show the location on the bacterial surface of MAC complexes, or holes, on a complement-susceptible strains? Comparing the visual outcome for such bacteria with locally formed MAC versus C7 replenished would be quite interesting and perhaps important.

ANSWER 1. Since Fig. 6D represents AFM images of MAC on complement-susceptible E. coli bacteria, we assume that the reviewer is asking why we did not perform AFM experiments on complement-resistant strains? To address this question, it is important to note that we have thus far not succeeded in robustly visualizing MAC complexes under conditions at which bacteria were not killed by MAC complexes (Heesterbeek et al., EMBO J, 2019). While non-bactericidal MAC complexes are present on the bacterial surface as demonstrated with C9 deposition by flow cytometry, we hypothesize that they are not well inserted into the membrane (demonstrated by sensitivity to trypsin) and therefore difficult to resolve by AFM. This is consistent with previous AFM experiments on related pore-forming proteins (Leung et al, 2014, 2017), in which inserted pores were readily detected on supported lipid bilayers, but mobile, non-inserted pores were harder to resolve due to the invasiveness of the AFM measurement and/or insufficient temporal resolution. In the revised manuscript we now better clarify this in line 298-301.

POINT 2. The flow cytometric analysis of bacterial killing is somewhat simplistic. Usually, staining of BOTH live and dead bacteria is performed. This permits better gating of the relevant populations. Specifically, the gating seems to fit the population in Fig. S1 only poorly, with the gate in some cases simply dividing what otherwise appears to uniform population ("C9 at t=0")

ANSWER 2. In the revised manuscript, we have now included additional data demonstrating that our gating strategy with Sytox blue correlates well with bacterial killing on plate (new Fig S1-B referred to in line 78-79, 92-93, 96-98 and Supplementals text line 21-24 shows cfu data for Sytox data of Fig 2D). These data correspond with our earlier findings showing that cells gated to be positive for Sytox blue are indeed the relevant population of dead cells (Heesterbeek, EMBO J, 2019). We disagree with the reviewer that the use of a ‘live’ stain is of added value here. Because the outer membrane of Gram-negative bacteria is also a permeability barrier for ‘live’ stains like Syto9, MAC-dependent outer membrane perforation also results in increase in ‘live’ stain during the process of bacterial lysis (also described in Stiefel et al, BMC Microbiol, 2015 PMID: 25881030). We have therefore chosen to only use the Sytox stain in this study as this is a very reliable marker for killing.

POINT 3. The cited literature is, in general, pertinent and comprehensive. I was surprised, however, that none of the many contributions to field of MAC formation by AF Esser was cited. For instance, the studies over C9 conformation (PMID: 2475785) seem not far away in topic from some of the points raised in the present paper.

ANSWER 3. The reviewer is correct that the work of AF Esser has indeed focused on the contribution of C9 and C9 polymerization to the lytic activity of the MAC pore. In the revised manuscript, we have therefore now included some of the work done by AF Esser (references 34, 36 and 37) and have discussed this in our discussion (line 305-309). However, it is important to note that much of the work on the importance of C9 polymerization by AF Esser has been performed erythrocytes and single-membrane particles (also the suggested paper by the reviewer). Translation of these studies to the role of C9 conformation and polymerization on bacterial killing is therefore limited, although it does provide clues to what differences might cause the discrepancy observed between lysis of erythrocytes and bacterial killing by MAC pores.

Reviewer #1 (Significance (Required)): Insight into the concept of locally formed MAC complexes is lacking and the paper clearly adds novel and quantitative data to this point. The paper probably mostly reaches out to an audience interested in the complement system and researchers interested in large protein complexes with conformational changes as part of their function. My own interest lies with complement-mediated protection against bacteria with a special focus on pattern recognition and protein-bacterial surface interactions.

Reviewer #2

(Evidence, reproducibility and clarity (Required)): Doorduijn et al. present a study illustrating the importance of rapid C7 interaction with C5b6 for MAC-dependent killing of complement sensitive bacteria. The absence of direct C7 interaction results in a MAC which i) doesn't kill the bacteria, and ii) is sensitive to trypsin. The authors have step by step investigated this issue by using common in vitro-methods with different strains of bacteria, serum, and/or purified complement proteins. Bacterial killing is evaluated by sytox blue influx in flow cytometry. I like this work. The experimental strategy is sound, and the conclusions are convincing are based on the presented data. The data and the methods presented in such a way that they can be reproduced. I have no concerns regarding the design, execution or conclusions.

Reviewer #2 RAISES 3 POINTS

POINT 1. My only criticism is on the number of replicates and following statistical analysis: • Overall, the experiments are conducted only three times. With the, in general, large differenced seen between the condition, this may still be acceptable. However, the statistic testing using only N=3 is of low value.

ANSWER 1. As the reviewer pointed out, with these in vitro studies where the experimental conditions are highly controlled it is common practice to perform three independent experiments when the differences are large.

POINT 2. The authors have sometimes used paired testing, and sometimes unpaired. For example, Fig. 5A-B is based on paired testing, whereas data in C, which are based on A-B, is tested using unpaired testing. Why so is unclear to me.

ANSWER 2. We thank the reviewer for this comment, as also for Fig. 5C we should have used a paired analysis, so we have done so accordingly in the revised manuscript (line 725-726).

POINT 3. Further on in Fig. 5 A-B., ANOVA with Tukey multiple comparison tests is used, which implements testing between all conditions; still, only significance is reported for blue vs. red. If the intention was to only test red vs. blue, a t-test would be better.

ANSWER 3. As with the previous comment, we have now performed a paired t-test since we only intended to compare C7 at t=0 vs C7 at t=60 in Fig. 5A-B (line 725-726). Moreover, for consistency in our statistical analyses we’ve also applied this to Fig. 3C (line 706-707).

Reviewer #2 (Significance (Required)): As far as I understand, the presented data is of high significance for the conceptual understanding of the buildup of MAC for bacterial killing on Gram-negative bacteria. I work partly with complement but is not an expert on the terminal pathway.

Reviewer #3

(Evidence, reproducibility and clarity (Required)): The study is a follow-up on the paper the same group of scientists published in EMBO J last year. That paper showed that rapid interaction between C5b6 and C7 is necessary for effective killing of Gram negative bacteria. The follow-up this paper makes is to make that case for a series of E. coli strains, showing as part of this that strains of clinical isolate E. coli resistant to complement attack prevent the rapid C5b6-C7 interaction. The story goes that C5 convertase engagement on the surface of targeted bacteria is the necessary context for effective C5>C5b conversion and thence interaction with C6 and C7. The rapid interaction with C7 is necessary because it prevents release/shedding of C5b6 from the bacterial cell surface. Overall, the conclusions seem justified - that C5b6 interaction with C7 stabilises its interaction with the surface and is needed to prevent C5b6 shedding. But this observation needs a mechanical or biophysical framework to be understood properly.

Reviewer #3 RAISES 5 POINTS

POINT 1. The authors do not observe non-bactericidal MAC pores/non-lytic MAC by AFM and so I think in this study there is no evidence for their existence. Their depiction in Figure 8b is therefore misleading and I think should be deleted. Indeed, the authors do not know what the structure of the non-bactericidal MAC pores could be, so depicting them in this specific way isn't appropriate. They have no idea what they might be like, if they exist.

ANSWER 1. We agree with the referee that we do not know the structure of a non-bactericidal MAC pore, and have therefore deleted the speculative structures in Fig. 8B (explained in line 784-785). Although we have no structural information, we do think that non-bactericidal MAC pores exist and our revised manuscript now includes new data to better explain this (Fig S1-C). While our initial manuscript showed that a delayed interaction between C5b6 and C7 results in MAC complexes that cannot perturb the bacterial inner membrane, we now show that these MAC complexes effectively damage the outer membrane (evidenced by leakage of mCherry from the periplasmic space (Fig. S1-C, explained in line 97-98 and Supplementals text line 24-31). This leads us to conclude that there are pores formed in the outer membrane that are not capable of damaging the inner membrane. We think that within this context we can name these ‘non-bactericidal MAC pores’.

POINT 2. This brings me to another point: it is really unclear to me from this study how the authors envisage the inner bacterial membrane be damaged by MAC attack. Do MAC pores formed in the OM deliver MAC components to the IM? Or what happens - is the damage to the IM indirect? The reason why this is relevant to the possibility of non-bactericidal MAC pores is that it could be these are inserted just like bactericidal pores into the OM but the IM attack is deficient in some way.

ANSWER 2. Although we agree with the reviewer that exact mechanism by which MAC pores perturb the inner membrane is unanswered, we think this is beyond the scope of this paper which mainly deals with the time-resolved functions of MAC assembly. However, to meet the referees’ critique, we have now more clearly addressed this question in our discussion and speculate on several mechanisms by which the MAC pore could induce bacterial inner membrane damage (line 277 - 288). In short, we hypothesize that OM damage could indirectly trigger IM damage by affecting regulation of osmosis, overall cell envelope stability and/or envelope stress.

POINT 3. (Significance (Required)). I am intrigued by the difference between MAC assembly on erythrocytes and bacteria. What do the authors believe to be the basis of this difference? It would help understanding of the significance of their work if they could make this clear. Without this kind of attempted explanation the results seem phenomenological - an observation has been made but why this observation occurs, what the important environmental difference is between erythrocyte membranes and the outer membranes of Gram negative bacteria is not addressed. I am looking for some kind of biophysical explanation - specific lipid properties, for example.

ANSWER 3. We agree that this is intriguing and in our revised manuscript we have included different hypotheses on why MAC assembly on erythrocytes and bacteria could be different. Although differences in composition between the erythrocyte membrane and outer membrane can definitely play a role, our data suggest that the difference is mainly a consequence of the fact that Gram-negative bacteria have two membranes (the outer and inner membrane). In the revised manuscript, the newly added figure (Fig S1-C) supports this, since this figure reveals that MAC pores generated from C5b6 that is generated in the absence of C7 can still damage the bacterial OM. However, despite observing OM damage by measuring leakage of a periplasmic protein, this does not lead to bacterial killing and IM damage. Since we here observe that rapid interaction between C5b6 and C7 is required for bacterial killing and IM damage, we think that efficient anchoring of C5b-7 is primarily relevant in damaging the bacterial IM and subsequently causing bacterial cell death. Finally, we have also mentioned this more specifically in the discussion of the revised manuscript (line 277-288).

POINT 4. Related, at the end of the Results section the authors say "Altogether, these data indicate that complement-resistant E. coli can prevent complement-dependent killing by MAC pores by preventing efficient anchoring of C5b-234 7 and insertion of MAC pores into the bacterial cell envelope." My immediate response was: 'How? The Discussion needs to consider this.' But it doesn't.

ANSWER 4. In the revised manuscript, we now explain this more extensively (line 322 – 326). In short, we hypothesize that the composition of the OM, mostly in terms of capsular polysaccharides and lipopolysaccharides, could affect this. We have added additional references supporting the role of these components in complement resistance in multiple Gram-negative species (reference 45-48 and 50).

POINT 5. I was confused by the term "metastable lipophilic domain" at line 262 on page 10. Do the authors mean the MACPF domain?

ANSWER 5. We have now more explicitly named this in our discussion as being the MACPF domain and have further elaborated what we meant by metastable (line 263-267).

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Referee #3

Evidence, reproducibility and clarity

The study is a follow-up on the paper the same group of scientists published in EMBO J last year.

That paper showed that rapid interaction between C5b6 and C7 is necessary for effective killing of Gram negative bacteria. The follow-up this paper makes is to make that case for a series of E. coli strains, showing as part of this that strains of clinical isolate E. coli resistant to complement attack prevent the rapid C5b6-C7 interaction.

The story goes that C5 convertase engagement on the surface of targeted bacteria is the necessary context for effective C5>C5b conversion and thence interaction with C6 and C7. The rapid interaction with C7 is necessary because it prevents release/shedding of C5b6 from the bacterial cell surface.

Overall, the conclusions seem justified - that C5b6 interaction with C7 stabilises its interaction with the surface and is needed to prevent C5b6 shedding. But this observation needs a mechanical or biophysical framework to be understood properly.

The authors do not observe non-bactericidal MAC pores/non-lytic MAC by AFM and so I think in this study there is no evidence for their existence. Their depiction in Figure 8b is therefore misleading and I think should be deleted. Indeed, the authors do not know what the structure of the non-bactericidal MAC pores could be, so depicting them in this specific way isn't appropriate. They have no idea what they might be like, if they exist.

This brings me to another point: it is really unclear to me from this study how the authors envisage the inner bacterial membrane be damaged by MAC attack. Do MAC pores formed in the OM deliver MAC components to the IM? Or what happens - is the damage to the IM indirect? The reason why this is relevant to the possibility of non-bactericidal MAC pores is that it could be these are inserted just like bactericidal pores into the OM but the IM attack is deficient in some way.

Significance

I am intrigued by the difference between MAC assembly on erythrocytes and bacteria. What do the authors believe to be the basis of this difference? It would help understanding of the significance of their work if they could make this clear. Without this kind of attempted explanation the results seem phenomenological - an observation has been made but why this observation occurs, what the important environmental difference is between erythrocyte membranes and the outer membranes of Gram negative bacteria is not addressed. I am looking for some kind of biophysical explanation - specific lipid properties, for example.

Related, at the end of the Results section the authors say "Altogether, these data indicate that complement-resistant E. coli can prevent complement-dependent killing by MAC pores by preventing efficient anchoring of C5b-234 7 and insertion of MAC pores into the bacterial cell envelope." My immediate response was: 'How? The Discussion needs to consider this.' But it doesn't.

I was confused by the term "metastable lipophilic domain" at line 262 on page 10. Do the authors mean the MACPF domain?

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Referee #2

Evidence, reproducibility and clarity

Doorduijn et al. present a study illustrating the importance of rapid C7 interaction with C5b6 for MAC-dependent killing of complement sensitive bacteria. The absence of direct C7 interaction results in a MAC which i) doesn't kill the bacteria, and ii) is sensitive to trypsin.

The authors have step by step investigated this issue by using common in vitro-methods with different strains of bacteria, serum, and/or purified complement proteins. Bacterial killing is evaluated by sytox blue influx in flow cytometry.

I like this work. The experimental strategy is sound, and the conclusions are convincing are based on the presented data. The data and the methods presented in such a way that they can be reproduced. I have no concerns regarding the design, execution or conclusions.

My only criticism is on the number of replicates and following statistical analysis:

• Overall, the experiments are conducted only three times. With the, in general, large differenced seen between the condition, this may still be acceptable.

• However, the statistic testing using only N=3 is of low value.

• The authors have sometimes used paired testing, and sometimes unpaired. For example, Fig. 5A-B is based on paired testing, whereas data in C, which are based on A-B, is tested using unpaired testing. Why so is unclear to me.

• Further on in Fig. 5 A-B., ANOVA with Tukey multiple comparison tests is used, which implements testing between all conditions; still, only significance is reported for blue vs. red. If the intention was to only test red vs. blue, a t-test would be better.

Significance

As far as I understand, the presented data is of high significance for the conceptual understanding of the buildup of MAC for bacterial killing on Gram-negative bacteria.

I work partly with complement but is not an expert on the terminal pathway.

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Referee #1

Evidence, reproducibility and clarity

The paper by Doorduijn et al. addresses a question rarely touched upon in modern studies of the complement system, namely the stability and time-resolved functions of complement component. It extends two earlier reports from the same laboratory, however, with a clear, novel point concerning especially the function of C7.The study embodies several techniques and modes of investigation. From these experiments, the paper contributes significantly to our understanding of the MAC complex is formed and why some bacteria escape this host defense mechanism. Over all the study is very well performed and written. I have only a few major comments.

Major Comments

1.The AFM pictures shown in Fig. 6D are of outstanding quality. However, it is a disappointment that the outcome of complement incubation was shown only for a complement-resistant E. coli strain. Would it be possible to show the location on the bacterial surface of MAC complexes, or holes, on a complement-susceptible strains? Comparing the visual outcome for such bacteria with locally formed MAC versus C7 replenished would be quite interesting and perhaps important.

2.The flow cytometric analysis of bacterial killing is somewhat simplistic. Usually, staining of BOTH live and dead bacteria is performed. This permits better gating of the relevant populations. Specifically, the gating seems to fit the population in Fig. S1 only poorly, with the gate in some cases simply dividing what otherwise appears to uniform population ("C9 at t=0")

Minor point

The cited literature is, in general, pertinent and comprehensive. I was surprised, however, that none of the many contributions to field of MAC formation by AF Esser was cited. For instance, the studies over C9 conformation (PMID: 2475785) seem not far away in topic from some of the points raised in the present paper.

Significance

Insight into the concept of locally formed MAC complexes is lacking and the paper clearly adds novel and quantitative data to this point. The paper probably mostly reaches out to an audience interested in the complement system and researchers interested in large protein complexes with conformational changes as part of their function. My own interest lies with complement-mediated protection against bacteria with a special focus on pattern recognition and protein-bacterial surface interactions.

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Reply to the reviewers

We are very grateful to the three reviewers for their useful and constructive comments on our manuscript. All reviewers appreciated that our manuscript provides a good characterization of the KKT2/3 functional domains, especially in solving crystal structures of the KKT2 central domain and revealing the importance of KKT2/3 central domains for their centromere targeting. They also commented that additional experiments (e.g. testing DNA-binding activities using recombinant proteins and examining whether ectopically expressed KKT2 fragments localize at kinetochores transiently) would significantly strengthen the manuscript. In the revised manuscript, we are going to address their comments as follows.

Reviewer #1:

From the information presented, it seems like there are only two possibilities to explain the role of the zinc finger domains in directing centromere targeting. First, this could mediate a protein-protein interaction. The authors attempt to assess this using their mass spec experiments, but this does not absolutely rule this out as this interaction may not persist through their purification procedure (low affinity or requires the presence of DNA, such as for a nucleosome).

Response: We agree with the reviewer’s comment. We will add a sentence to discuss this possibility in the revised manuscript.

Second, this could reflect direct DNA binding by the zinc finger. Although the existing paper is solid and highlights a role for the zinc finger domains in the localization of these proteins, it would be even better if the authors were to at least assess DNA binding in vitro with their recombinant protein. Comparing its behavior to a well characterized DNA-binding zinc finger protein would be powerful for assessing whether direct DNA binding could be responsible for its centromere localization.

Response: We have tested DNA-binding activities for the KKT2 central domain from T. brucei, Bodo saltans, and Perkinsela using a fluorescent polarization assay. We tested three different DNA probes (50 bp each) that were fluorescently-labelled: a 50 bp DNA probe from the CIR147 sequence, which is the unit sequence of centromere repeats of several chromosomes in T. brucei (36% GC content), as well as two random DNA sequences of 25% and 74% GC content. We found that the Perkinsela KKT2a central domain binds these three different DNA probes with similar affinities (Kd ~100 nM), suggesting that the Perkinsela KKT2a central domain binds DNA in a sequence-independent manner. Although we have not been able to obtain reliable results for T. brucei and Bodo saltans proteins thus far (due to quenching of fluorescent signals by these proteins), it is likely that the T. brucei KKT2 central domain also binds DNA in a sequence-independent manner given the similarity of the Znf1 structure/sequence among kinetoplastids. This is consistent with the observation that there is no DNA sequence that is commonly found in the centromere of all chromosomes in T. brucei and other kinetoplastids. We are going to add the DNA-binding assay results for the Perkinsela KKT2a central domain in the revised manuscript. We do not feel it is informative to compare the KKT2 Znf1’s behavior to a well characterized DNA-binding zinc finger protein (that binds specific DNA sequence), because Perkinsela KKT2a binds DNA in a sequence-independent manner.

The code for KKT2 and KKT3 localization is complicated by the multiple regions that contribute to their targeting. This includes both the zinc finger domain that the authors identify here, as well as a second region that appears to act through associations with other constitutive centromere components. Due to this, it feels that there are several aspects of these proteins that are incompletely explored. First, the authors show that the Znf1 mutant in KKT2 localizes apparently normally to centromeres, but is unable to support KKT2 function in chromosome segregation. This suggests that this zinc finger domain could have a separable role in kinetochore function that is distinct from centromere targeting.

Response: We agree with the reviewer that the mechanism of KKT2 kinetochore localization is complicated because there are at least three distinct domains that contribute to its targeting (Figure 2 in the original manuscript), but we showed that the centromere targeting of the ectopically-expressed KKT2 central domain fragment depends on Znf1 (Figure 6B in the original manuscript). Together with the finding that the Znf1-equivalent domain is essential for the localization of the full length KKT3 protein, we think that a function of the KKT2 Znf1 domain is to promote its centromere localization. In the future, it will be critical to understand the molecular mechanism of how the KKT2 central domain localizes specifically at centromeres.

Second, although the authors identify these minimal zinc finger regions as sufficient for centromere localization, they do not test whether this behavior depends on the presence of other KKT proteins. This seems like a very important experiment to test whether recruitment of the zinc finger occurs through other factors, or whether it could act directly through binding to DNA or histones.

Response: We do not have an experimental setup to test whether the centromere localization of KKT2/3 central domains depends on other KKT proteins (i.e. we cannot keep the expression of the central domain to a low level while inducing RNAi constructs at a high level). As an alternative approach, we have been testing the localization dependency of endogenously-tagged full-length KKT2/3 proteins using RNAi against various KKT proteins but our preliminary results have not found any kinetochore protein whose depletion affects the localization of KKT2 or KKT3 at centromeres. Although these results could be explained by inefficient protein depletion, they are consistent with the possibility that KKT2 and KKT3 central domains directly interact with centromere DNA. We could consider adding these data in the revised manuscript, although a significant amount of additional work will be necessary to confirm these results.

• Based on the description of kinetoplastid centromeres that the authors provide, it is actually unclear to whether these are indeed sequence independent. The authors state that "There is no specific DNA sequence that is common to all centromeres in each organism [Trypanosomes and Leishmania], suggesting that kinetoplastids also determine their kinetochore positions in a sequence-independent manner." However, it remains possible that there are features to this DNA that are responsible for defining the centromere. In principle, enriched clustering of a short motif that may elude sequence comparisons could be responsible for specifying these regions. It would be helpful to use caution with this statement, and I would also encourage the Aikyoshi lab to test this directly in future work, such as using strategies to remove a centromere or alter its position. *

Response: We agree with the reviewer that we cannot exclude the possibility that there might be an enrichment of a short motif that promotes the localization of kinetochore proteins. We will discuss this possibility in the revised manuscript.

• It would be helpful to provide a schematic of kinetoplastid kinetochore organization based on their studies to date (possibly in Figure 1) to provide a context for the relationships between the different KKT proteins tested in this paper.*

Response: While we agree with the referee that a model figure would be helpful, we feel that drawing a model for the overall organization of kinetoplastid kinetochores at this stage could be misleading because we still know very little about it. In fact, our published data (e.g. the microtubule-binding kinetochore protein KKT4 localizes at centromeres throughout the cell cycle and has DNA-binding activities) and our unpublished observations suggest that the design principle of kinetoplastid kinetochores may well be fundamentally different from that of canonical kinetochores in other eukaryotes. We therefore would like to obtain more data before drawing a model of kinetoplastid kinetochores. Instead of a model, we are going to include a summary of localization patterns for kinetoplastid kinetochore proteins in Figure 1 to help orient readers.

Reviewer #2: The experiments are in general well presented but some could be better controlled: - localization of KKT2 and KKT3 mutants is never verified to be centromeres, we have to believe the dots in the DAPI region are centromeres.

Response: We have assumed that the KKT2 and KKT3 mutants that had dots very likely localized at centromeres because they behaved similarly to wild-type proteins (i.e. align at metaphase plate in some 2K1N cells and localize at the leading edge of separating chromosomes). We will confirm this assumption by imaging the KKT2/3 mutants with a kinetochore protein marker (e.g. tdTomato-KKT1).

in some cases mutants are made in full-length (FL) background (viability, sometimes localization), but in other cases only in isolated domains. The former should be done for all assays. This is also important to show that central domain of KKT2 and KKT3 is necessary for localization.

Response: It is very laborious to create point mutants in full-length background at an endogenous locus. This is why we first tested a number of mutants in our ectopic expression of truncated (for KKT2) or full-length (for KKT3) proteins to identify the most critical mutations, which were subsequently tested in the endogenous context. Although not included in the original manuscript, we have performed an ectopic expression of additional KKT2 mutants (C597A/C600A, C616A/C619A, C624A/C627A, C640A/C643A, and H656A/C660A) in the full-length protein and found that all of them had apparently normal localization pattern, which is consistent with the results we obtained in the endogenous expression experiments (C576A, D622A, and C640A/C643A: Figure 6c in the original manuscript).

The data of F2 are interpreted to mean that PDB-like domain and middle region get to kinetochores by binding transient KT components, even though KKT2 itself is constitutive. That interpretation would really be strenghthened by showing the KKT2 fragments are now transient also. **

Response: Our observations suggest that these KKT2 fragments indeed localize at centromeres transiently (from S phase to anaphase). We will confirm this result by imaging with a transiently-localized kinetochore protein, KKT1 tagged with tdTomato, and include in the revised manuscript.

The paper could do with some attempts to get to this, based on the presented data. For example, does Znf1 bind centromeric DNA, does it bind nucleosomes, is it essential for recruiting the other KKTs, etc.

Response: As we responded to Reviewer 1, we have found that Perkinsela KKT2a central domain Znf1 has DNA-binding activities. We agree that it will be important to test whether KKT2 binds nucleosomes but it will be necessary for us to reconstitute nucleosomes using recombinant T. brucei histones. It will also be important to test whether KKT2/3 are essential for recruiting other kinetochore proteins but we think that they are beyond the scope of this manuscript.

Reviewer #3: \*Major Comments:** - No page numbers - this makes it difficult to refer to different parts of the text... *

Response: We sincerely apologize for the lack of page numbers in the original manuscript. We will add page numbers and line numbers in the revised manuscript.

Introduction (page 2), fourth-from bottom line: the authors refer here to "regional centromere" but have not defined this term (I assume, as opposed to point-centromeres of budding yeast?). I suggest rephrasing.

Response: We thank the reviewer for pointing it out. We will rephrase it in the revised manuscript.

Page 4, bottom: The discussion of KKT2 kinetochore localization brings up a lot or questions. First, can the authors use an assay like yeast two-hybrid to test for pairwise interactions between KKT2 domains and other kinetochore proteins? This could provide direct functional data on the role of these various domains in kinetochore localization.

Response: Based on the mass spectrometry of immunoprecipitated KKT2 fragments that localized at kinetochores, we are currently trying to identify direct protein-protein interactions between the KKT2 domains and other kinetochore proteins (e.g. does KKT2-DPB directly interact with KKT1, KKT6, or KKT7 proteins?). While we agree that it is important to address these questions, we think that it is beyond the scope of this manuscript because its focus is the characterization of KKT2/3 central domains. As we mentioned in the manuscript, these central domains failed to co-purify with other kinetochore proteins, and the experiment therefore did not give us any clue about how they might localize specifically at centromeres.

Second, if individual domains are being recruited to kinetochores by their non-constitutive binding partners, wouldn't this be evident if the authors looked at localization at different points in the cell cycle, and/or with dual localization tracking the putative binding partners? Could transient localization of some of the domains explain the intermediate localization phenotype observed for some domains in KKT2?

Response: As we responded to Reviewer 2, our observations suggest that these KKT2 fragments indeed localize at centromeres transiently (from S phase to anaphase). We will confirm this result by imaging with a transiently-localized kinetochore protein, KKT1 tagged with tdTomato.

Page 6: The authors note that KKT2 Znf2 bears strong similarity to DNA-binding canonical Zinc fingers, and even note the high conservation of some putative DNA-binding residues. Have the authors tested for DNA binding by this protein?

Response: As we responded to Reviewer 1 and 2, we used a fluorescence polarization assay and found that the Perkinsela KKT2a central domain binds DNA in a sequence-independent manner.

Can the authors at least model DNA binding and see if that would result in a clash, given the packing of Znf2 against the larger Znf1?

Response: As suggested, we superimposed the structure of Bodo saltans KKT2 Znf2 with that of a zinc finger 268 bound to DNA (PDB:1AAY), which shows a possible mechanism by which Znf2 might bind DNA. It also revealed a clash between DNA and Znf1 (in the crystal packing of the solved structure), implying that the position of Znf2 would need to change in order to bind DNA. We will add a supplementary figure showing a hypothetical DNA-binding mechanism by Znf2 and discuss the possibility of a necessary structural change in the Znf1 position to accommodate the DNA binding by Znf2.

\*Minor Comments:** - Page 5: I'm skeptical as to whether these zinc-binding domains, especially Znf1, should really be referred to as "fingers". *

Response: To our knowledge, the word “zinc finger” could be used for any protein that binds one or more zinc ions. Given that we still do not understand the molecular mechanism by which this domain functions, we wanted to use a very general term, Znf1. However, we do appreciate the reviewer’s point that calling this domain as a zinc finger could be misleading, so we will refer Znf1 and Znf2 in the original manuscript as the CL domain (for centromere localizing domain) and a classic C2H2 zinc finger in the revised manuscript.

Page 8: At the beginning of the section describing KKT3 cellular experiments, I think the authors need to make it much more explicit that T. brucei KKT3 shares both Znf1 and Znf2 with KKT2.

Response: We will add the suggested sentence before describing the functional assay for KKT3.

Figure S1A: The gap between lanes in the middle of the major peak is really confusing (it's not even clear that this is two different SDS-PAGE gels next to one another). I initially thought that KKT2 was in both peaks, given the labeling of this figure. I suggest labeling the lanes specifically, or cropping the picture, to avoid confusion.

Response: As suggested, we will prepare an image that shows only those lanes (from two separate gels) that were used for loading protein samples. We also like to retain the whole gel images in the same figure because those gels have rather low background signal (even without any contrast manipulation).

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Reply to the reviewers

Response to Reviewers Comments

We would like to thank all reviewers for carefully considering our manuscript and providing useful suggestions/ideas. The general consensus was that our study provides an important conceptual advance that reveals a new way of thinking about kinetochore phosphatases. However, in light of our surprising findings, it was suggested that additional experiments would be required to fully validate our conclusions. In particular, it was seen as important to test whether PLK1 can activate MPS1 from the BUB complex and to confirm that PP1 and PP2A are effectively inhibited in situations where MELT dephosphorylation can occur normally (Figure 3).

In general, we agree with these and the other points raised by the reviewers, therefore we plan to address all comments as outlined in detail below.

The major new additions to the final paper will be the following:

1) Experiments to test how BUB-bound PLK1 affects MPS1 activity.

2) Experiments to determine the efficiency of phosphatase inhibition in figure 3.

3) Experiments to test whether maintaining PLK1 at the BUB complex causes SAC silencing defects

4) Evolutionary analysis demonstrating that the PLK1 and PP2A-binding modules have co-evolved in the kinetochore BUB complex. This analysis, which has been performed already, strengthens our manuscript because it provides additional independent evidence for a functional relationship between PLK1 and PP2A on the BUB complex.

Reviewer #1

Minor comments:

1) The authors propose that PP1-KNL1 and BUBR1-bound PP2A-B56 continuously antagonise PLK1 association with the BUB complex by dephosphorylating the CDK1 phosphorylation sites on BUBR1 (pT620) and BUB1 (pT609). It is therefore expected that converting these residues to aspartate would increase PLK1 recruitment. It would be interesting to verify if this hypothesis fits with the proposed model.

Response: The general idea to maintain PLK1 at the BUB complex is a good one, but unfortunately polo-box domains do not bind to acidic negatively charged residues. Instead we will attempt to maintain PLK1 at the BUB complex using alternatively approaches (as suggested by reviewer 2).

2) In Figure 1E, are the mean values for BubR1WT+BubWT and BubR1WT+Bub1T609 both normalized to 1? If so, this fails to reveal the contribution of Bub1 T609 for the recruitment of PLK1 when PP2A-B56 is allowed to localize at kinetochores.

Response: The values will be updated and normalised to the BubR1WT+BUB1WT control. We have also performed additional experiments already and overall the results reveal a small reduction in kinetochore PLK1 following BUB1-T609A mutation and a larger reduction upon combined BUBR1-T620A mutation.

3) What underlies the increase in Bub1 levels at unattached kinetochores of siBubR1 cells (Figure S1C?) Is this caused by an increase in Bub1 T609 phosphorylation and consequently unopposed PLK1 recruitment, which consequently increases MELT phosphorylation?

Response: We suspect that PLK1 is not the cause of the increased BUB1 levels because PLK1 kinetochore levels are actually decreased in this situation (Figure S1A).

4) Although the immunoblotting from Figure S1D indicates that BubR1T620A and Bub1T609A are expressed at similar levels as their respective WT counterparts, some degree of single-cell variability is expected to occur. As a complement to Figure 1B,C and Figure S1E,F could the authors plot the kinetochore intensity of BubR1 pT620 and Bub1T609 relative to the YFP-BubR1 and YFP-Bub1 signal, respectively?

Response: There is indeed variability in the level of re-expression of BUBR1/BUB1 on a single cell level, which can at least partially explain the variation on BUBR1-pT620 and BUB1-pT609 observed within in each condition. We can upload these scatter plots at resubmission and include in the supplementary, if required.

5) The authors nicely show that excessive PLK1 levels at the BUB complex are able to maintain MELT phosphorylation and the SAC (independently of MPS1) when KNL1-localised phosphatases are removed (Figures 2A,B). However, it should be noted that PLK1 is able to promote MPS1 activation at kinetochores and so, whether AZ-3146 at 2.5 uM efficiently inhibits MPS1 under conditions of excessive PLK1 recruitment should be confirmed. Can the authors provide a read-out for MPS1 activation status or activity (other than p-MELTs) to exclude a potential contribution of residual MPS1 activity in maintaining the p-MELTs and SAC?

Response: This is a good point because although PLK1 can phosphorylate the MELTs it can also activate MPS1, although it is unknown whether it can do this from the BUB complex. We had left a dotted line in Figure 4B to include this possibility, but we will now test this directly with additional experiments.

6) To examine whether PLK1 removal is the major role of PP1-KNL1 and PP2A-B56 in the SAC or whether they are additionally needed to dephosphorylate the MELTs, the authors monitored MELT dephosphorylation when MPS1 was inhibited immediately after 30-minute of BI2356. This revealed similar dephosphorylation kinetics, irrespective of compromised PP1-KNL1 or PP2A-B56 activity, thus suggesting that these pools of phosphatases are not required to dephosphorylate MELTs. To confirm this and exclude phosphatase redundancy, the authors simultaneously depleted all PP1 and B56 isoforms or treated cells with Calyculin A to inhibit all PP1 and PP2A phosphatases. In both of these situations, the kinetics of MELT dephosphorylation was indistinguishable from wild type cells if MPS1 and PLK1 were inhibited together. These observations led to the conclusion that neither PP1 or PP2A are required to dephosphorylate the MELT motifs. Instead they are needed to remove PLK1 from the BUB complex. This set of experiments is well-designed and the results support the conclusion. However, it would be of value if the authors provide evidence for the efficiency of PP1 and B56 isoforms depletion and for the efficiency of phosphatase inhibition by Calyculin A. An alternative read-out for the activity of PP1 and PP2A-B56 (other than p-MELT dephosphorylation) clearly confirming that both phosphatases are compromised when MPS1 and PLK1 are inhibited together could make a stronger case in excluding the contribution of residual PP1 or PP2A to the observed dephosphorylation of MELT motifs.

Response: This is also a good point. We had attempted many different combinations in Figure 3 to inhibit PP1/PP2A activity as efficiently as possible. This is especially important considering the “negative” results on pMELT are very surprising. However, we will now test how efficiently we have inhibited PP1 and PP2A phosphatase function in these experiments.

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

Major comments:

1) In its current state I am not convinced that the key conclusions are fully supported by the experiments and alternative conclusions/interpretations can be drawn. For example the level of MELT phosphorylation will be determined by the balance of kinase and phosphatase activity and if they do not achieve 100% inhibition of Mps1 in their assays then they are not strictly monitoring dephosphorylation kinetics in their assays. If the combination of Mps1 and Plk1 inhibition then more strongly inhibits Mps1 then dephosphorylation kinetics becomes faster. Thus subtle differences in Mps1 activity under their different conditions could lead to misleading conclusions but in its present state a careful analysis of Mps1 activity is not provided. This lack of complete inhibition also applies to the phosphatases and the experiments in Figure 3E indicates that their Calyculin preparation is not really active as at steady state MELT phosphorylation levels are much less affected than in for instance BubR1 del PP2A (Figure 2A as an example). Thus they likely still have phosphatase activity in the experiment in figure 3E making it difficult to draw the conclusions they do. A more careful analysis of kinase and phosphatase activities in their different perturbations would be recommendable and should be possible within a reasonable time frame.

Response: These are good points and we will now more carefully assess MPS1 and PP1/PP2A activities.

2) A more stringent test of their model would also be needed. What happens if Plk1 is artificially maintained in the Bub complex? The prediction would be that SAC silencing should be severely delayed even when Mps1 is inhibited. This is a straightforward experiment to do that should not take too long. If the polobox can bind phosphoSer then one could also make BubR1 T620S to slow down dephosphorylation of this site (PPPs work slowly on Ser while Cdk1 have almost same activity for Ser and Thr).

Response: These are good suggestions and we will try to see if maintaining PLK1 at the BUB complex produces effects on the SAC.

3) Another issue is the relevance of Plk1 removal under normal conditions. As their quantification shows in figure 1D-E (I think there is something wrong with figure 1E - should likely be Bub1) the contribution of BubR1 T620 and Bub1 T609 to Plk1 kinetochore localisation seems minimal. Thus upon SAC satisfaction there is not really a need to remove Plk1 through dephosphorylation as it is already at wild type levels. It is only in their BubR1 and KNL1 mutants that there is this effect so one has to question the impact in a normal setting. This is consistent with the data in Figure S1D showing no phosphorylation of these sites under unperturbed conditions.

Response: The major finding of this study is that kinetochore phosphatases are primarily needed to supress PLK1 activity on the BUB complex and thereby prevent excessive MELT phosphorylation. The relevance of this continued PLK1 removal under normal conditions is clear, because when it cannot occur (i.e. if the phosphatases are removed) then the SAC cannot be silenced unless PLK1 is inhibited. Therefore, whilst it is true that PLK1 localisation to the BUB complex is low under normal conditions, that is because the phosphatases are working to keep it that way. The relevance of that continual removal is an interesting, but in our opinion, separate question that will require a new body of work to resolve. One possibility is that PLK1 recruitment is a continual dynamic process, that is perhaps coupled to a particular stage in MCC assembly. For example, PLK1 could bind the BUB complex to recruit PP2A to BUBR1, before being immediately removed by PP2A. In this sense, PLK1 binding could still be functionally important even if it is only occurs transiently and steady state PLK1 levels are low. We will add a line to the discussion to highlight that it would be interesting to test PLK1 dynamics on the BUB complex in future.

4) They write that in the absence of phosphatase activity Plk1 becomes capable of supporting SAC independently (of Mps1 is implied). They do not show this - only that MELT phosphorylation is maintained. As Mps1 has other targets required for SAC activity I would rephrase this.

Response: Good point, this will be rephrased.

Reviewer #2 (Significance (Required)):

The advance is clearly conceptual and provides a new way of thinking about the kinetochore localized phosphatases. These phosphatases and the SAC have been immensely studied but this work brings in a new angle. The discussion would benefit from some evolutionary perspectives as the PP1 and PP2A-B56 binding sites are very conserved but the Plk1 docking sites on Bubs less so. This will be of interest to people in the field of cell division and researchers interested in phospho-mediated signaling.

Response: Since the paper was submitted, we performed evolutionary analysis to examine this point. We discovered that the PLK1 docking sites are surprisingly well conserved and, in fact, they appear to have co-evolved within the same region of MAD/BUB along with the PP2A-B56 binding motif. We believe this new data strengthens our manuscript because it argues strongly for an important functional relationship between PLK1 and PP2A. A new figure containing this evolutionary analysis will be included in the final version.

Reviewer #3

Major comments:

1. An important limitation of this study is that KNL1 dephosphorylation at MELT repeats is monitored only by indirect immunofluorescence using phospho-specific antibodies. Thus, reduction of phospho-KNL1 kinetochore signals could be due to protein turnover at kinetochores, rather than to dephosphorylation. This is a serious issue that could be addressed by checking KNL1 dephosphorylation during time course experiments by western blot using phospho-specific antibodies, as previously done (Espert et al., 2014).

Response: This is an important point that we feel is best addressed by examining total KNL1 levels at kinetochores (instead of simply total cellular levels by western blots). The reason is that KNL1 could potentially still be lost from kinetochores even if the total protein is not degraded. In all experiments involving YFP-KNL1 we observe no change in kinetochore KNL1 levels and this data will be included in the final version. We will also perform new experiments to examine total KNL1 levels in the BUBR1-WT/DPP2A situation to test whether KNL1 kinetochore levels are similarly maintained in these cells following MPS1 inhibition.

1. For obvious technical reasons, the shortest time point at which authors compare KNL1 dephosphorylation upon MPS1-PLK1 inhibition is 5 minutes. Based on immunofluorescence data, authors conclude that kinetics of KNL1 dephosphorylation are similar when kinases are inhibited, independent of whether or not kinetochore-bound phosphatases are active. However, in most experiments (e.g. Fig. 3B, 3C, 3E) lower levels of MELT phosphorylation are detected after 5 minutes of kinase inhibition when phosphatases are present than when they are absent, suggesting that phosphatases likely do contribute to KNL1 dephosphorylation. I suspect that differences between the presence and absence of phosphatases might even be more obvious if authors were to look at shorter time points, when phosphatases conceivably accomplish their function. I would therefore suggest that the authors tone down their conclusions, as their data complement but do not disprove the previous model.

Response: We appreciate that small differences can be seen in figure 3B and 3E at the 5-minute timepoint (between the WT and phosphatase inhibited situations). This may reflect a role for the phosphatases in dephosphorylation or in the ability of drugs such as BI-2536 (3B) or Calyculin A (3E) to fully inhibit their targets in the short timeframe. We will perform additional experiments to examine MPS1 and phosphatase activity under these conditions, in response to comments by reviewers 1 and 2. In the final version we will carefully interpret the new and existing data and, if required, modify the conclusions appropriately.

1. In all experiments cells are kept mitotically arrested through nocodazole treatment, which is not quite a physiological condition to study SAC silencing. This could potentially mask the real contribution of phosphatases in MELT dephosphorylation. Indeed, it is possible that higher amounts of phosphatases are recruited to kinetochores during SAC silencing than during SAC signalling (e.g. during SAC signalling Aurora B phosphorylates the RVSF motif of KNL1 to keep PP1 binding at low levels; Liu et al., 2010). What would happen in a nocodazole wash-out? Would phosphatases be dispensable in these conditions for normal kinetics of MELT dephosphorylation and anaphase onset if PLK1 is inhibited?

Response: All SAC silencing assays where performed in nocodazole for 2 main reasons: 1) PP2A-B56, PP1 or PLK1 can all regulate kinetochore-microtubule attachments, and thereby control the SAC indirectly. Therefore, performing our assays in the absence of microtubules allows us to make specific and direct conclusions about SAC regulation; 2) Previous work on pMELT regulation by PP1/PP2A in human cells was also performed following MPS1 inhibition in nocodazole (Espert et al 2014, Nijenhuis et al, 2014). Therefore, we are able to directly compare the contribution of PLK1 to the previously observed phenotypes, which allowed us to conclude that PLK1 has a major influence. Nevertheless, we appreciate the point that the influence of PLK1 could, in theory, be different during a normal mitosis when microtubule attachment can form. Therefore, we will attempt to address whether PLK1 inhibition can bypass a requirement for PP1/PP2A in SAC silencing during an unperturbed mitosis.

Other data are overinterpreted. For instance, the evidence that CDK1-dependent phosphorylation sites in Bub1 and BubR1 is enhanced when PP1 and PP2A-B56 are absent at kinetochores suggests but does not "demonstrate that PP1-KNL1 and BUBR1-bound PP2A-B56 antagonise PLK1 recruitment to the BUB complex by dephosphorylating key CDK1 phosphorylation sites on BUBR1 (pT620) and BUB1 (pT609)(Figure 1F)". Similarly, the claim "when kinetochore phosphatase recruitment is inhibited, PLK1 becomes capable of supporting the SAC independently" referred to Fig. 2C-D is an overstatement, as residual MPS1 kinase could be still active in the presence of the AZ-3146 inhibitor.

Response: These are good points and the indicated statements will be reworded.

Minor comments:

1. In many graphs (Fig. 1A-C, Fig. 2A,C) relative kinetochore intensities are quantified over "CENPC or YFP-KNL1". Authors should clarify when it is one versus the other.

Response: This will be clarified in the axis and in the methods.

1. The drawing in Fig. 1F depicts the action of PP1 and PP2A-B56 in antagonising PLK1 at kinetochores. Thus, the output should be SAC silencing, rather than activation.

Response: The SAC symbol will be removed from the schematic to avoid confusion and because it is not actually the focus of figure 1 anyway.

1. In the Discussion authors speculate that KNL1 dephosphorylation relies on a constitutive phosphatase with unregulated basal activity. Would a phosphatase be needed at all when MPS1 and PLK1 are inhibited? Could phosphorylated KNL1 be actively degraded?

Response: We will insert total KNL1 immunofluorescence quantification so show that KNL1 KT levels are not decreased in this situation. KNL1 remains anchored at kinetochore but the MELTs must be dephosphorylated to remove the BUB complex.

1. What happens to MPS1 when KNL1-bound PP1 and BUBR1-bound PP2A are absent? Do its kinetochore levels increase as observed for PLK1? And what about the kinetochore levels of Bub1 and BubR1?

Response: We have demonstrated previously that BUB1/BUBR1 increase in this situation in line with the pMELTs (Nijenhuis et al 2014;l Smith et al, 2019) – these papers will be referenced in relation to this. We will also address the effect of phosphatase removal on MPS1 activity, in response to comments by reviewers 1 and 2.

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Referee #3

Evidence, reproducibility and clarity

The Spindle Assembly Checkpoint (SAC) is a conserved surveillance device that responds to errors in kinetochore-microtubule attachments to ultimately prevent the onset of anaphase until all chromosomes are bipolarly attached. Current models of SAC posit that the Mps1 kinase initiates the SAC signalling cascade by phosphorylating the KNL1/Blinkin kinetochore scaffold at MELT repeats, in order to create phospho-docking sites for the hetero-tetrameric BUB complex made by BUB1-BUB3-BUB3-BUBR1. The BUB complex, in turn, promotes the assembly the Mitotic Checkpoint Complex (MCC), which prevents anaphase onset by inhibiting the E3 ubiquitin ligase Anaphase-Promoting Complex bound to its activator Cdc20 (APCCdc20). The polo-like kinase PLK1, which is recruited to kinetochores through its binding to BUBR1, contributes to the robustness of SAC signalling in human cells by cooperating with Mps1 in KNL1/Blinkin phosphorylation and by phosphorylating MPS1 itself, thereby enhancing its catalytic activity. While in human cells MPS1 is the predominant kinase in SAC signalling, aided by PLK1, in other organisms where MPS1 is absent, such as in nematodes, PLK1 functionally replaces MPS1 and is necessary for SAC activation. Once all chromosomes are bipolarly attached, SAC signalling is extinguished. Key to this process are the PP1 and PP2A-B56 phosphatases that antagonise KNL1 phosphorylation by MPS1 and PLK1 and also dephosphorylate the T-loop of MPS1 to lower its catalytic activity. Current models envision that PP1 and PP2A-B56 dephosphorylate the MELT repeats of KNL1 directly. Importantly, this has been formally tested for both PP2A-B56 in human cells (Espert et al., 2014) and PP1 in yeast (London et al., 2012).

In the present manuscript, the above model is challenged with the proposal that the main contribution of PP1 and PP2A-B56 to SAC silencing is to lower the levels of PLK1 at kinetochores, rather than to dephosphorylate KNL1. By interfering with the levels of these opposing kinases and phosphatases at kinetochores the authors describe an interesting interplay that confirms an overlapping function of PLK1 and MPS1 in KNL1 phosphorylation and highlights a role for the phosphatases in dampening PLK1 kinetochore levels. Consistently, inhibition of both Mps1 and PLK1 is sufficient to bring about KNL1 dephosphorylation upon inhibition of both phosphatases at kinetochores. The hypothesis is interesting and experiments are in general carefully designed and performed. It is clear from the presented data that PP1 and PP2A-B56 antagonize PLK1 kinetochore localisation and that the MELT repeats of KNL1 can be dephosphorylated even in the absence of phosphatases, provided that MPS1 and PLK1 are inhibited. However, in my opinion the results do not rule out that phosphatases actually have a primary and direct role in KNL1 dephosphorylation.

Major comments:

1. An important limitation of this study is that KNL1 dephosphorylation at MELT repeats is monitored only by indirect immunofluorescence using phospho-specific antibodies. Thus, reduction of phospho-KNL1 kinetochore signals could be due to protein turnover at kinetochores, rather than to dephosphorylation. This is a serious issue that could be addressed by checking KNL1 dephosphorylation during time course experiments by western blot using phospho-specific antibodies, as previously done (Espert et al., 2014).
2. For obvious technical reasons, the shortest time point at which authors compare KNL1 dephosphorylation upon MPS1-PLK1 inhibition is 5 minutes. Based on immunofluorescence data, authors conclude that kinetics of KNL1 dephosphorylation are similar when kinases are inhibited, independent of whether or not kinetochore-bound phosphatases are active. However, in most experiments (e.g. Fig. 3B, 3C, 3E) lower levels of MELT phosphorylation are detected after 5 minutes of kinase inhibition when phosphatases are present than when they are absent, suggesting that phosphatases likely do contribute to KNL1 dephosphorylation. I suspect that differences between the presence and absence of phosphatases might even be more obvious if authors were to look at shorter time points, when phosphatases conceivably accomplish their function. I would therefore suggest that the authors tone down their conclusions, as their data complement but do not disprove the previous model.
3. In all experiments cells are kept mitotically arrested through nocodazole treatment, which is not quite a physiological condition to study SAC silencing. This could potentially mask the real contribution of phosphatases in MELT dephosphorylation. Indeed, it is possible that higher amounts of phosphatases are recruited to kinetochores during SAC silencing than during SAC signalling (e.g. during SAC signalling Aurora B phosphorylates the RVSF motif of KNL1 to keep PP1 binding at low levels; Liu et al., 2010). What would happen in a nocodazole wash-out? Would phosphatases be dispensable in these conditions for normal kinetics of MELT dephosphorylation and anaphase onset if PLK1 is inhibited?
4. Other data are overinterpreted. For instance, the evidence that CDK1-dependent phosphorylation sites in Bub1 and BubR1 is enhanced when PP1 and PP2A-B56 are absent at kinetochores suggests but does not "demonstrate that PP1-KNL1 and BUBR1-bound PP2A-B56 antagonise PLK1 recruitment to the BUB complex by dephosphorylating key CDK1 phosphorylation sites on BUBR1 (pT620) and BUB1 (pT609)(Figure 1F)". Similarly, the claim "when kinetochore phosphatase recruitment is inhibited, PLK1 becomes capable of supporting the SAC independently" referred to Fig. 2C-D is an overstatement, as residual MPS1 kinase could be still active in the presence of the AZ-3146 inhibitor.

Minor comments:

1. In many graphs (Fig. 1A-C, Fig. 2A,C) relative kinetochore intensities are quantified over "CENPC or YFP-KNL1". Authors should clarify when it is one versus the other.
2. The drawing in Fig. 1F depicts the action of PP1 and PP2A-B56 in antagonising PLK1 at kinetochores. Thus, the output should be SAC silencing, rather than activation.
3. In the Discussion authors speculate that KNL1 dephosphorylation relies on a constitutive phosphatase with unregulated basal activity. Would a phosphatase be needed at all when MPS1 and PLK1 are inhibited? Could phosphorylated KNL1 be actively degraded?
4. What happens to MPS1 when KNL1-bound PP1 and BUBR1-bound PP2A are absent? Do its kinetochore levels increase as observed for PLK1? And what about the kinetochore levels of Bub1 and BubR1?

Significance

The nature of the advance is conceptual. This paper challenges (although I would rather say "integrates") the prevailing model of spindle checkpoint silencing.

The current model of SAC silencing envisions that PP1 and PP2A-B56 phosphatases oppose SAC kinases (Mps1 and Polo kinase) by directly dephosphorylating some of their targets (e.g. the kinetochore scaffold KNL1 and MPS1 itself). This work proposes instead that the main function of the above phosphatases is to keep low levels of the polo kinase PLK1 at kinetochores, which would otherwise boost KNL1 phosphorylation and assembly of SAC complexes.

People working in the fields of mitosis, chromosome segregation, aneuploidy, spindle checkpoint, kinases/phosphatases could be interested by these findings.

Reviewer's field of expertise: Cell cycle, mitosis, spindle assembly checkpoint

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Referee #2

Evidence, reproducibility and clarity

Summary:

The work focuses on the role of kinetochore localized protein phosphatases in the dephosphorylation of MELT motifs and SAC silencing. The focus is on PP1 bound to KNL1 and PP2A-B56 bound to BubR1 and uses largely RNAi rescue experiments in human cell lines combined with immunofluorescence analysis and time-lapse imaging. The authors show that kinetochore localized phosphatases antagonize the localization of the Plk1 mitotic kinase to kinetochores. This is due to the dephosphorylation of BubR1 T620 and Bub1 T609 that are binding sites for Plk1 on the kinetochore. The main conclusion is that if Plk1 kinetochore localisation is prevented then there is no longer a need for kinetochore phosphatases for SAC silencing and MELT dephosphorylation.

Major comments:

1) In its current state I am not convinced that the key conclusions are fully supported by the experiments and alternative conclusions/interpretations can be drawn. For example the level of MELT phosphorylation will be determined by the balance of kinase and phosphatase activity and if they do not achieve 100% inhibition of Mps1 in their assays then they are not strictly monitoring dephosphorylation kinetics in their assays. If the combination of Mps1 and Plk1 inhibition then more strongly inhibits Mps1 then dephosphorylation kinetics becomes faster. Thus subtle differences in Mps1 activity under their different conditions could lead to misleading conclusions but in its present state a careful analysis of Mps1 activity is not provided. This lack of complete inhibition also applies to the phosphatases and the experiments in Figure 3E indicates that their Calyculin preparation is not really active as at steady state MELT phosphorylation levels are much less affected than in for instance BubR1 del PP2A (Figure 2A as an example). Thus they likely still have phosphatase activity in the experiment in figure 3E making it difficult to draw the conclusions they do. A more careful analysis of kinase and phosphatase activities in their different perturbations would be recommendable and should be possible within a reasonable time frame.

2) A more stringent test of their model would also be needed. What happens if Plk1 is artificially maintained in the Bub complex? The prediction would be that SAC silencing should be severely delayed even when Mps1 is inhibited. This is a straightforward experiment to do that should not take too long. If the polobox can bind phosphoSer then one could also make BubR1 T620S to slow down dephosphorylation of this site (PPPs work slowly on Ser while Cdk1 have almost same activity for Ser and Thr).

3) Another issue is the relevance of Plk1 removal under normal conditions. As their quantification shows in figure 1D-E (I think there is something wrong with figure 1E - should likely be Bub1) the contribution of BubR1 T620 and Bub1 T609 to Plk1 kinetochore localisation seems minimal. Thus upon SAC satisfaction there is not really a need to remove Plk1 through dephosphorylation as it is already at wild type levels. It is only in their BubR1 and KNL1 mutants that there is this effect so one has to question the impact in a normal setting. This is consistent with the data in Figure S1D showing no phosphorylation of these sites under unperturbed conditions.

4) They write that in the absence of phosphatase activity Plk1 becomes capable of supporting SAC independently (of Mps1 is implied). They do not show this - only that MELT phosphorylation is maintained. As Mps1 has other targets required for SAC activity I would rephrase this.

5) The method section is extensive and contains sufficient information for reproducing data.

6) Data and statistical analysis is ok.

Significance

The advance is clearly conceptual and provides a new way of thinking about the kinetochore localized phosphatases. These phosphatases and the SAC have been immensely studied but this work brings in a new angle. The discussion would benefit from some evolutionary perspectives as the PP1 and PP2A-B56 binding sites are very conserved but the Plk1 docking sites on Bubs less so. This will be of interest to people in the field of cell division and researchers interested in phospho-mediated signaling.

Field of expertise: kinetochore/phosphatases/bub proteins Jakob Nilsson

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Cordeiro et al provides a series of compelling evidences to support a provocative conclusion: PP2A-B56 and PP1 are critical for SAC silencing mainly by restraining and extinguishing autonomous kinase activity at kinetochores. This finding challenges the prevailing view of PP2A-B56/PP1-mediated KNL1-MELT dephosphorylation as a major SAC silencing event. This represents a paradigm change in the field and opens an important goal for future research: determine the phosphatases that dephosphorylate the MELTs. In my view this paper delivers an important clarification on how PP1-KNL1 and PP2A-B56 actually drive SAC silencing. This is a nice study and will move the field forward. The manuscript is globally solid, very well written and the conclusions are generally supported by the experimental data. However, I do have some issues with the following points, which in my view, if unaddressed, may leave the conclusion a bit fragile:

Minor comments:

1) The authors propose that PP1-KNL1 and BUBR1-bound PP2A-B56 continuously antagonise PLK1 association with the BUB complex by dephosphorylating the CDK1 phosphorylation sites on BUBR1 (pT620) and BUB1 (pT609). It is therefore expected that converting these residues to aspartate would increase PLK1 recruitment. It would be interesting to verify if this hypothesis fits with the proposed model.

2) In Figure 1E, are the mean values for BubR1WT+BubWT and BubR1WT+Bub1T609 both normalized to 1? If so, this fails to reveal the contribution of Bub1 T609 for the recruitment of PLK1 when PP2A-B56 is allowed to localize at kinetochores.

3) What underlies the increase in Bub1 levels at unattached kinetochores of siBubR1 cells (Figure S1C?) Is this caused by an increase in Bub1 T609 phosphorylation and consequently unopposed PLK1 recruitment, which consequently increases MELT phosphorylation?

4) Although the immunoblotting from Figure S1D indicates that BubR1T620A and Bub1T609A are expressed at similar levels as their respective WT counterparts, some degree of single-cell variability is expected to occur. As a complement to Figure 1B,C and Figure S1E,F could the authors plot the kinetochore intensity of BubR1 pT620 and Bub1T609 relative to the YFP-BubR1 and YFP-Bub1 signal, respectively?

5) The authors nicely show that excessive PLK1 levels at the BUB complex are able to maintain MELT phosphorylation and the SAC (independently of MPS1) when KNL1-localised phosphatases are removed (Figures 2A,B). However, it should be noted that PLK1 is able to promote MPS1 activation at kinetochores and so, whether AZ-3146 at 2.5 uM efficiently inhibits MPS1 under conditions of excessive PLK1 recruitment should be confirmed. Can the authors provide a read-out for MPS1 activation status or activity (other than p-MELTs) to exclude a potential contribution of residual MPS1 activity in maintaining the p-MELTs and SAC?

6) To examine whether PLK1 removal is the major role of PP1-KNL1 and PP2A-B56 in the SAC or whether they are additionally needed to dephosphorylate the MELTs, the authors monitored MELT dephosphorylation when MPS1 was inhibited immediately after 30-minute of BI2356. This revealed similar dephosphorylation kinetics, irrespective of compromised PP1-KNL1 or PP2A-B56 activity, thus suggesting that these pools of phosphatases are not required to dephosphorylate MELTs. To confirm this and exclude phosphatase redundancy, the authors simultaneously depleted all PP1 and B56 isoforms or treated cells with Calyculin A to inhibit all PP1 and PP2A phosphatases. In both of these situations, the kinetics of MELT dephosphorylation was indistinguishable from wild type cells if MPS1 and PLK1 were inhibited together. These observations led to the conclusion that neither PP1 or PP2A are required to dephosphorylate the MELT motifs. Instead they are needed to remove PLK1 from the BUB complex. This set of experiments is well-designed and the results support the conclusion. However, it would be of value if the authors provide evidence for the efficiency of PP1 and B56 isoforms depletion and for the efficiency of phosphatase inhibition by Calyculin A. An alternative read-out for the activity of PP1 and PP2A-B56 (other than p-MELT dephosphorylation) clearly confirming that both phosphatases are compromised when MPS1 and PLK1 are inhibited together could make a stronger case in excluding the contribution of residual PP1 or PP2A to the observed dephosphorylation of MELT motifs.

To summarize, this is a very good paper and will definitely cause an important impact in the field of mitosis.

Significance

This manuscript provides an important conceptual advance for the field of mitosis, specifically to the topic of mitotic checkpoint regulation. It remains elusive how the spindle assembly checkpoint is silenced. While previous studies have shown that PP1-KNL1 and PP2A-B56 contribute to suppress SAC signaling, how they do so is unclear. This study provides important insight into this matter. Cordeiro and colleagues demonstrate that in contrast with previous expectations, PP1 and PP2A promote SAC silencing, not by directly dephosphorylating MELT motifs on KNL1, but instead by removing PLK1 from the Bub complex. The authors find that these phosphatases antagonise CDK1- phosphorylations on BubR1 and Bub1 to dampen PLK1 levels. This activity is crucial to prevent PLK1 from maintaining MELT phosphorylation in an autocatalytic manner, thus (probably) allowing prompt SAC silencing following stable kinetochore-microtubule attachments. The described mechanism extends our view of how the SAC is regulated and should be of interest to those in the field of mitosis. The findings described in this paper allow us to better understand how cells silence the SAC. This is a top priority in the field, as the inability to timely quench SAC signaling can result in chromosome segregation errors. Determining the phosphatases that actually dephosphorylate the MELT motifs will be an essential next step forward

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Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript "Unconventional kinetochore kinases KKT2 and KKT3 have a unique zinc finger that promotes their kinetochore localization" by Marciano et al. describes functional and structural work on two unique kinetochore-localized proteins in kinetoplastids, KKT2 and KKT3. While the kinetochores of most eukaryotes are built on top of a histone H3 variant known as CENP-A (or CenH3), kinetoplastids lack CENP-A. Kinetoplastids also lack homologs of most conserved kinetochore proteins and instead possess an unique complement of kinetochore proteins, as described in earlier work by the lead author, B. Akiyoshi.

The current manuscript follows up this earlier work and seeks to understand how two putative kinases, KKT2 and KKT3, localize to the kinetochores of kinetoplastids. They begin by mapping the regions of both proteins (in Trypanosoma brucei) that are required for kinetochore localization. In both cases, a conserved "central domain" is sufficient for kinetochore localization. They then purify and determine the structure of a KKT2 central domain from a related species (Bodo saltans), and show that it possess two zinc-binding domains, termed Znf1 and Znf2. A more diverged KKT2 from Perkinsela has Znf1, but not Znf2. The authors go on to show that the Znf1 region in particular is important for localization of both KKT2 and KKT3 to kinetochores, and for long-term cell survival, in Trypanosoma brucei.

Major Comments:

• The work is well done, well described, and described in such a way that it should be reproducible.

• No page numbers - this makes it difficult to refer to different parts of the text...

• Introduction (page 2), fourth-from bottom line: the authors refer here to "regional centromere" but have not defined this term (I assume, as opposed to point-centromeres of budding yeast?). I suggest rephrasing.

• Page 4, bottom: The discussion of KKT2 kinetochore localization brings up a lot or questions. First, can the authors use an assay like yeast two-hybrid to test for pairwise interactions between KKT2 domains and other kinetochore proteins? This could provide direct functional data on the role of these various domains in kinetochore localization. Second, if individual domains are being recruited to kinetochores by their non-constitutive binding partners, wouldn't this be evident if the authors looked at localization at different points in the cell cycle, and/or with dual localization tracking the putative binding partners? Could transient localization of some of the domains explain the intermediate localization phenotype observed for some domains in KKT2?

• Page 6: The authors note that KKT2 Znf2 bears strong similarity to DNA-binding canonical Zinc fingers, and even note the high conservation of some putative DNA-binding residues. Have the authors tested for DNA binding by this protein? Can the authors at least model DNA binding and see if that would result in a clash, given the packing of Znf2 against the larger Znf1?

Minor Comments:

• Page 5: I'm skeptical as to whether these zinc-binding domains, especially Znf1, should really be referred to as "fingers"

• Page 8: At the beginning of the section describing KKT3 cellular experiments, I think the authors need to make it much more explicit that T. brucei KKT3 shares both Znf1 and Znf2 with KKT2.

• Figure S1A: The gap between lanes in the middle of the major peak is really confusing (it's not even clear that this is two different SDS-PAGE gels next to one another). I initially thought that KKT2 was in both peaks, given the labeling of this figure. I suggest labeling the lanes specifically, or cropping the picture, to avoid confusion.

Significance

This work is interesting, well done, and described nicely. It highlights how unique and different the kinetochores of kinetoplastid species are, and brings up a number of questions about how these kinetochores are specified and how they function. The structural work is also interesting and well-done. Unfortunately, the work as a whole does not make any strong mechanistic conclusions, leading to a somewhat dissatisfying conclusion.

The work could be significantly strengthened if the authors were able to make a direct functional conclusion about the roles of the Znf regions of KKT2 and/or KKT3, for example detecting DNA binding in vitro, or detecting a specific pairwise interaction between this region and another kinetochore protein.

This work will most likely appeal to researchers in the cell division and kinetochore architecture fields, although since kinetoplastids are so unique the link between this work and most other kinetochore work is unclear. This is in a way exciting: we don't yet know much about how these kinetochores relate to other eukaryotes' kinetochores.

My field of expertise is structural biology and biochemistry, with experience in kinetochore architecture and structure.

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Referee #2

Evidence, reproducibility and clarity

Kinetoplastids have unconventional kinetochores that lack CENPA nucleosomes that normally dictates the position of the kinetochore in most other eukaryotes. Marciano and colleagues analyse KKT2 and KKT3, two consistutively localized kinetoplastid kinetochore proteins that may contribute to kinetochore positioning on centromeric DNA. They find that in both proteins the central, cysteine-rich domains are sufficient to support centromere localization but that in KKT2 also other domains can do so by themselves. They then obtain crystal structures of the KKT2 central domain from bodo saltans and show it consists of 2 Zinc-finger structures (Znf1 and Znf2) of which the first is conserved in Perkinsella. Mutations of Znf1 and Znf2 in KKT2 and homologous mutations in KKT3 show that Znf1 is crucial for centromere localization and viability, while Znf2 is dispensible for both.

The paper presents a pretty straighforward characerization of functional domains in KKT2 and KKT3 with respect to centromere localization. The authors nicely show a unique Zn-finger structure (Znf1) of KKT2 and show it is crucial for localization. The study does not end up delivering an answer to the questions posed in the manuscript, namely how centromeres and therefore kinetochores are specified in kinetoplastids. The paper could do with some attempts to get to this, based on the presented data. For example, does Znf1 bind centromeric DNA, does it bind nucleosomes, is it essential for recruiting the other KKTs, etc.

The experiments are in general well presented but some could be better controlled:

• localization of KKT2 and KKT3 mutants is never verified to be centromeres, we have to believe the dots in the DAPI region are centromeres.
• in some cases mutants are made in full-length (FL) background (viability, sometimes localization), but in other cases only in isolated domains. The former should be done for all assays. This is also important to show that central domain of KKT2 and KKT3 is necessary for localization.
• The data of F2 are interpreted to mean that PDB-like domain and middle region get to kinetochores by binding transient KT components, even though KKT2 itself is constitutive. That interpretation would really be strenghtened by showing the KKT2 fragments are now transient also.

Significance

The paper presents a pretty straighforward characerization of functional domains in KKT2 and KKT3 with respect to centromere localization. The authors nicely show a unique Zn-finger structure (Znf1) of KKT2 and show it is crucial for localization. The study does not end up delivering an answer to the questions posed in the manuscript, namely how centromeres and therefore kinetochores are specified in kinetoplastids. The paper could do with some attempts to get to this, based on the presented data. For example, does Znf1 bind centromeric DNA, does it bind nucleosomes, is it essential for recruiting the other KKTs, etc.

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Referee #1

Evidence, reproducibility and clarity

Although most studied eukaryotes display similarities in their overall kinetochore structures to mediate chromosome segregation, kinetoplastid species display highly divergent kinetochores with no clear relationships to canonical kinetochore components. Prior work from the Akiyoshi lab and others has identified kinetochore proteins in Trypanosomes and other kinetoplastids. The identification of these proteins has provided a toolkit to begin to reveal the features that guide the function and assembly of these structures during chromosome segregation. Despite differences in protein composition, all kinetochores must display key properties including their ability to bind to both microtubules and chromosomal DNA. This paper focuses on the mechanisms by which kinetoplastid kinetochore components are targeted to centromere regions, an exciting question due to the apparent DNA sequence-independent nature of these associations. In other eukaryotes, this sequence independent association is specified through the action of histone variants. In contrast, it is unclear how DNA interactions occur in kinetoplastids.

This paper begins by reasoning that the proteins responsible for DNA interactions and defining the location of the centromere would localize persistently to centromeres. Thus, they focus on two constitutively localized proteins with sequence similarity to each other, KKT2 and KKT3. The authors analyze these proteins using a combination of domain analysis to test the localization requirements for these proteins, mass spectrometry analysis of interacting proteins, mutational analysis to test specific residues for localization and function, and most importantly determination of the structure of a kinetochore targeting domain, which reveals a zinc finger structure. The structural work in particular is both interesting and reveals a feature of these proteins that was not obvious based on initial sequence analysis. Overall, this paper appears to be carefully executed, rigorous, and well controlled, but could benefit from additional experiments that would extend the impact of their findings.

1. From the information presented, it seems like there are only two possibilities to explain the role of the zinc finger domains in directing centromere targeting. First, this could mediate a protein-protein interaction. The authors attempt to assess this using their mass spec experiments, but this does not absolutely rule this out as this interaction may not persist through their purification procedure (low affinity or requires the presence of DNA, such as for a nucleosome). Second, this could reflect direct DNA binding by the zinc finger. Although the existing paper is solid and highlights a role for the zinc finger domains in the localization of these proteins, it would be even better if the authors were to at least assess DNA binding in vitro with their recombinant protein. Comparing its behavior to a well characterized DNA-binding zinc finger protein would be powerful for assessing whether direct DNA binding could be responsible for its centromere localization.
2. The code for KKT2 and KKT3 localization is complicated by the multiple regions that contribute to their targeting. This includes both the zinc finger domain that the authors identify here, as well as a second region that appears to act through associations with other constitutive centromere components. Due to this, it feels that there are several aspects of these proteins that are incompletely explored. First, the authors show that the Znf1 mutant in KKT2 localizes apparently normally to centromeres, but is unable to support KKT2 function in chromosome segregation. This suggests that this zinc finger domain could have a separable role in kinetochore function that is distinct from centromere targeting. Second, although the authors identify these minimal zinc finger regions as sufficient for centromere localization, they do not test whether this behavior depends on the presence of other KKT proteins. This seems like a very important experiment to test whether recruitment of the zinc finger occurs through other factors, or whether it could act directly through binding to DNA or histones.
3. Based on the description of kinetoplastid centromeres that the authors provide, it is actually unclear to whether these are indeed sequence independent. The authors state that "There is no specific DNA sequence that is common to all centromeres in each organism [Trypanosomes and Leishmania], suggesting that kinetoplastids also determine their kinetochore positions in a sequence-independent manner." However, it remains possible that there are features to this DNA that are responsible for defining the centromere. In principle, enriched clustering of a short motif that may elude sequence comparisons could be responsible for specifying these regions. It would be helpful to use caution with this statement, and I would also encourage the Aikyoshi lab to test this directly in future work, such as using strategies to remove a centromere or alter its position.
4. It would be helpful to provide a schematic of kinetoplastid kinetochore organization based on their studies to date (possibly in Figure 1) to provide a context for the relationships between the different KKT proteins tested in this paper.

Significance

This paper provides a nice advance in understanding the molecular architecture and functional organization of kinetoplastid kinetochores. As these remain understudied, this work is valuable for revealing the chromosome segregation behaviors in these medically-relevant parasites. In addition, due to the divergence in overall kinetochore function from other eukaryotes, this work will help provide insights into the logic by which kinetochores function and are organized. The existing paper represents a solid advance in understanding the structure and requirements for KKT2 and KKT3 kinetochore targeting through this novel zinc finger domain. However, conducting some of the additional experiments made above, such as testing DNA binding and the requirements for other KKT proteins for zinc finger localization, would allow the authors to make stronger statements and a more impactful advance.

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