Persistence, period and precision of autonomous cellular oscillators from the zebrafish segmentation clock

[Editors’ note: this article was originally rejected after discussions between the reviewers, but the authors were invited to resubmit after an appeal against the decision.]

Thank you for choosing to send your work entitled "Persistence, period and precision of autonomous cellular oscillators from the zebrafish segmentation clock" for consideration at eLife. Your full submission has been evaluated by Janet Rossant (Senior editor), Tanya Whitfield (Reviewing editor and reviewer), and two additional peer reviewers, and the decision was reached after discussions between these individuals. Based on our discussions and the individual reviews below, we regret to inform you that your work will not be considered further for publication in eLife.

The reviewers agreed that the study is interesting and has been done carefully, but they had significant concerns over the fit of the experimental data to the model, and the extent to which the analysis provides a true advance in our understanding of somitogenesis in vivo. Although the study uses a larger number of cells than in previous work on similar systems, it was felt that the main findings are unsurprising and largely confirm those of earlier studies. It was also felt that, should a link to in vivo data be made (as suggested by Reviewer 3), this was also likely to confirm work that has already been done, and so would be unlikely to add further understanding. The full reviews are appended below.

Reviewer #1:

This study tests the proposal that the zebrafish somite segmentation clock is characterised by autonomous cellular oscillators, which have been proposed in other studies to be present and coupled by Notch signalling. This question has been tackled before in other species (chick, mouse), although in these previous studies, a very few dissociated cells were studied as part of a cell suspension (Masamizu et al.) or were pooled for analysis (Maroto et al.). The current study provides an advance over these previous studies, as the authors have examined much larger numbers of dissociated cells within a low density suspension than in previous studies, enabling a much more thorough quantitative and statistical analysis of the data. The authors also examine a small number of cells that have been isolated completely, and show (for a small number of cells) that oscillations can occur autonomously under these conditions.

Overall, the study appears careful and thorough and will be an important addition to the literature in this field. The experimental detail is sometimes a little sparse and more information could be added for clarification – see specific comments below. In addition, the figure legends need careful revision, as there is confusing mislabelling in several places.

Specific comments:

1) The period of individual cell oscillations at 26°C (81 min) is much longer that the value that is stated to be the period of trunk segmentation in intact embryos (27 min), measured tissue explants from the Looping Tg strain (55 min) and the authors' predictions (40 min) (subsection "Inferred period of segmentation clock cells in vitro”). This needs further explanation and discussion. What is the genetic background of the Tg strain? This is not described in the Materials and methods. The authors should include a measurement of the period of trunk segmentation in intact Looping Tg strain embryos as well as the explants, rather than merely comparing to previously published work (albeit from the same group, but done in a different laboratory etc.).

2) Little information is given about the health and other characterization of the cells in the low density suspensions. In the videos, they appear to show a lot of blebbing activity – is this expected? Do they retain other characteristics (e.g. gene expression) of the PSM and are they able to divide? It would be helpful to have some more information about the general behaviour of these cells under the conditions of the experiment.

3) What happened to the cells that touched each other? Do pairs of cells in contact with one another synchronise their signalling, or oscillate with a shorter period? Is there a community effect, and what is the minimum number of cells in a group that is sufficient to maintain faster and synchronized oscillations?

4) Fgf8b has been added to the culture medium to mimic conditions in the tailbud. What happens in absence of Fgf8b? Are there oscillations at all? Or damped oscillations? or oscillations with even longer periods?

5) The legend to Figure 1—figure supplement 1 is not sufficient to understand the figure. There is both a red and a grey line on each panel, but the legend confusingly only refers to a black line. (What is the grey line? – Background levels? – This should be stated somewhere.) I presume that the grouping of each set of traces refers to the independent replicates, but this is not explained anywhere. The 'smoothed' traces should be labelled as such on the figure. Also, the colour code is not correct – the smoothed traces are in red with blue circles to indicate peaks and troughs, not in blue with red triangles as indicated in the legend. Likewise, in Figure 1—figure supplement 2 and legend, the peak finding on the traces is actually labelled with red triangles, not blue as indicated in the legend; filtering appears to be labelled with blue triangles, not red as indicated. This lack of attention to detail has made it difficult and time-consuming to review the manuscript.

6) Figure 1—figure supplement 6 – these traces show timecourses for 10 individual isolated cells. Have these data been subjected to the same smoothing, peak and trough analysis etc. as the data from the low density set? Do they behave in a similar way?

Reviewer #2:

The manuscript presents a very worthwhile data set, detailing time-course expression profiles for a Her1 reporter with high temporal resolution. These show a high degree of variability, and a range of analyses are performed to extract phase and amplitude data. The authors go on to compare these summary measures to those obtained from a generic model of a system close to a supercritical Hopf bifurcation (at the boundary between decaying and sustained oscillations). They show that reasonable (though not perfect) agreement between the two sets of measures (experimental and simulated) can be achieved for an appropriate set of model parameters.

These results are interesting in their own right, as a careful investigation of the nature of the time-courses obtained from the cultured tailbud cells. I'm less convinced that they say anything particularly important about somitogenesis in zebrafish. My primary concern here is that the Her1 expression observed in the low-density cultured cells is so distinct to that observed in tailbud cells in an intact embryo. The period of oscillation in vivo is 27min; the mean period extracted from the time-courses of the cultured cells is around three times as long as this (ca. 78min). The two sets of oscillations thus represent markedly different dynamics. The long-period noisy oscillations observed in cultured cells may (or may not) be due to a dynamical system close to a Hopf bifurcation, but if they are, it is hard to see how this relates to a dynamical system based on the same components oscillating in a tissue with almost three times the frequency! The key observation in this regard is that the somitogenesis period in explanted PSM is around 55min, rather than the 27min in the embryo at the same temperature. This is reported in this manuscript without any real discussion. But surely this is a striking and potentially important result.

My overall assessment is that the data set and data analysis are high quality and worthy of publication. The potential fit to a very generic model is also interesting, but I'm not convinced that the fit is actually that good. Given the large discrepancy between the cultures and the embryo, I'm not convinced that the data have much to say about somitogenesis.

Substantive concerns:

1) Fgf8b was added to the culture medium "to mimic the signaling environment of the tailbud". Was this necessary to see oscillations in Her1-YFP levels? What happens if it is not added?

2) Did cells in culture never divide? This is not mentioned (other reasons for discounting time-courses are mentioned). Cells in the tailbud typically undergo a single division at around 15-16hpf (see Figure 1C in Bouldin et al. (2014). Genes & Development, 28, 384-395.) It seems that this division should fall within the time window of the current study. Are the culture conditions blocking this division, and if so, might that be expected to affect the oscillations?

3) The authors state (subsection “Heterogeneity in the population of oscillating cells”) that the simulated data are "in good agreement with the experimental data (Figure 2F)" However, Figures 2B and 2F don't match very well, as noted by the authors themselves in the next sentence. There is clearly more overall variability in amplitude in the real data (2B) than in the simulated data (2F), though the correlation of neighbouring peak amplitudes is similar. So the data show similar short-time coherence of amplitude to the model, but significantly greater variability in amplitude overall.

4) The data do appear to support the idea that the main variability in the oscillations is in the amplitude rather than in the period (Figures 2B, 2C). The authors use this finding to focus their attention on a S-L model with q=0 (so, the frequency is independent of the amplitude). This restricts the type of supercritical Hopf bifurcation that could underlie the observed oscillations (the normal form does not require q=0). Does this restrict the possible molecular mechanisms underlying the observed Her1 oscillations? In particular, do noisy negative feedback oscillators behave in this way? It is my understanding that stochastic simulations of negative feedback circuits (like the ones alluded to by the authors) that exhibit sub-Hopf stochastic resonance do show amplitude-dependence of the period (increased amplitude leads to increased period). Furthermore, the authors have previously shown that the use of the Her1-Venus transgene increases the period of oscillations. Is this likely to be due to the overall increase in expression level of Her1 in the Looping line? The amplitude-dependence of period (or lack of it) is potentially important for the tissue-wide oscillations observed in the PSM, as the value and distribution of q is an important factor in the ability of oscillators to synchronise.

Reviewer #3:

Webb et al. describe segmentation clock oscillations of individual dissociated zebrafish tail bud cells. They find that oscillations are present in vitro (as expected), but that the period is longer than in vivo (as previously postulated but shown here for the first time). A noise model can account for the degeneration of oscillations.

The data is interesting for zebrafish researchers but I am not convinced that it goes beyond previous studies in chick and mouse.

It seems straightforward to compare the in vitro oscillations to the in vivo oscillations in Notch signaling mutants. This experiment would test if the differences in vitro can be explained by the absence of Notch signaling.

[Editors’ note: what now follows is the decision letter after the authors submitted for further consideration.]

Thank you for resubmitting your work entitled "Persistence, period and precision of autonomous cellular oscillators from the zebrafish segmentation clock" for further consideration at eLife. Your revised article has been evaluated by Janet Rossant (Senior editor) and three reviewers, one of whom, Tanya Whitfield, is a member of our Board of Reviewing Editors.

The reviewers agree that the manuscript has been improved and that the study is a significant advance over previous work. Although several unanswered interesting questions remain, the study will be valuable in stimulating discussion and research in this area.

However, there are also some concerns. The first, outlined by Reviewer 2, is that the oscillations you describe in single cells do not necessarily represent the 'segmentation clock' itself. This may require some re-wording or further discussion in the manuscript.

The second concern, highlighted by Reviewer 1, relates to the cell division rate in your cultures. This is perplexing, as the video that you show illustrates a mitotic index an order of magnitude higher than the value you state for the study overall (5/18 cells dividing in this field of view = 28%, whereas you state that the rate overall is only 2%). As your cells are drawn from a dividing progenitor population, and Fgf8 (a mitogen) has been added to the culture, it would be expected that the cells continue to divide, and it is reassuring to see them do so. However, the discrepancy between this and your description makes it difficult to have confidence in the numbers of dividing cells stated in the manuscript. Since this has implications for interpretation of the dataset as a whole, it is important that this is addressed.

Reviewer #1:

Firstly, and also with respect, I would like to clarify that I did not state that the previous manuscript was 'only a technical' advance over previous work; in fact, this part of my review was a positive comment in support of the paper.

The authors have addressed all the points that I raised, most of them very satisfactorily. I think the argument is clearer and that the additional data (e.g. maintenance of marker expression) help with the overall interpretation.

My one remaining concern relates to the issue of dividing cells in the low-density dataset. It is helpful that the authors have given more detail on cell divisions in a source file, and I appreciate the argument that the focus of the study is necessarily on the single cells. However, more explicit information is still needed here, especially for Video 1. The legend to Video 1 indicates that it corresponds to the field of view for the non-dividing cell in Figure 1B, C. It would help to mark the cell of interest (e.g. with a ring or arrowhead) at the start of the video. Otherwise, the text in the fifth paragraph of the subsection “Oscillations in isolated segmentation clock cells in vitro”, leads the reader to think that Video 1 is illustrating a whole field of cells that do not divide.

More importantly, however, in addition to the non-dividing cell in the lower left, Video 1 also includes no fewer than five clear examples of cell divisions, four of them YFP+ (at 00.26 (top right and lower right), 00.30 (middle left), 00.33 (extreme top right) and 00.41 (bottom right)). I find this very surprising, given the source data file (Figure 1—source data 2), which documents only 9 instances of cell division in the entire dataset from a total of 29 fields of view, which would suggest that cell division events are rare. The observation of five division events in a single field of view also suggests that Video 1 is not representative of the dataset as a whole, and is directly contradictory to the statements in the rebuttal that 'it seems that culture conditions are inhibiting division'; 'because of the very low rate of cell division in the culture' etc. In short, I am not confident that the authors have measured the rate of cell division accurately in their cultures. Further explanation is required here.

As the authors have pointed out in their rebuttal (although I could not find this in the manuscript), the pairs of daughter cells remain attached to one another. As far as I can see, there does not appear to be a consistent timing of division relative to the phase of the oscillation between the three examples, or maintenance of synchrony between daughters within a pair, although oscillation in at least one daughter can clearly continue after division. For example, after the division at 00.30, the daughter on the left of the pair has a very clear YFP peak at 00.39-00.40, while its sister on the right has very low YFP signal at the same time point. Since the dataset captures this very interesting information, it deserves some comment, even if a full analysis is beyond the scope of the current study.

For cells that did divide (including the four YFP+ cells shown in Video 1), were oscillations measured up to the point of division, or were these cells eliminated from the analysis altogether? The text is not altogether clear on this point.

Reviewer #2:

I continue to believe that the data described in this manuscript are interesting and valuable, and I think it is very positive that the authors are making the raw data available to allow others to analyse them (although I maintain that the authors have done a good job of this already).

The authors have addressed my queries and concerns. The additional data, and provision of raw data, make it easier to assess the validity of the statements made in the manuscript.

I have one remaining niggle with the conclusions drawn from the data and the corresponding nomenclature employed by the authors. The cells are derived from the tailbud and maintain tailbud markers (new data). The cells certainly exhibit oscillations, which have features that are consistent with an underlying dynamical system that is close to a Hopf bifurcation. So it is fair to say that the cells are oscillators. However, I remain to be convinced that these facts are sufficient to call the cells "single zebrafish segmentation clock cells" (e.g. sixth paragraph of the Introduction and many other places). The segmentation clock is surely a coordinated tissue-wide oscillatory operating in the tailbud/PSM. A parsimonious (though not necessary) explanation of the findings reported is that the segmentation clock results from the interaction of some noisy cell-autonomous genetic oscillators. But that is not sufficient to call the oscillations in the single cells in vitro a "segmentation clock".

I accept the argument that the period of the in vitro segmentation clock can exhibit marked temperature-dependence. But that does not lessen the difficulty of arguing that if a cell-autonomous oscillation in tailbud-derived cells is borderline-Hopf with a period of ca. 80min, then the in vivo clock, with a period of ca. 27min, has something to do with borderline-Hopf dynamics. I maintain that I do not think it is easy to explain how an oscillatory mechanism can be close to a Hopf bifurcation at two radically different periods.

It may be that the mechanisms underlying the observed in vitro cell-autonomous oscillations and the in vivo segmentation clock are closely related (and it is probably true), but that does not mean that their dynamics are similar. Just because cells can oscillate in two different conditions does not mean that one can say that the oscillations are two different versions of the same thing.

In summary, I like this study. I think the in vitro oscillations are interesting and the analysis is powerful. I just don't like the idea of calling these oscillations a segmentation clock – that is what operates in the embryo.

Reviewer #3:

Webb et al. have revised their manuscript to more clearly explain the limitations of previous studies in concluding that cell-autonomous oscillations form the basis of the segmentation clock. The differences between single cells, tissue explants and in vivo tail buds are striking but unexplained. The paper is a nice technical advance but the main conclusions were expected from previous studies, and the most interesting phenomena of different periods in vitro and in vivo remains unaddressed.

[Editors’ note: the author responses to the first round of peer review follow.]

Reviewer #1: This study tests the proposal that the zebrafish somite segmentation clock is characterised by autonomous cellular oscillators, which have been proposed in other studies to be present and coupled by Notch signalling. This question has been tackled before in other species (chick, mouse), although in these previous studies, a very few dissociated cells were studied as part of a cell suspension (Masamizu et al.) or were pooled for analysis (Maroto et al.). The current study provides an advance over these previous studies, as the authors have examined much larger numbers of dissociated cells within a low density suspension than in previous studies, enabling a much more thorough quantitative and statistical analysis of the data. The authors also examine a small number of cells that have been isolated completely, and show (for a small number of cells) that oscillations can occur autonomously under these conditions.

We would respectfully dispute the claim that our manuscript provides only a technical advance over the papers of Masmizu and Maroto. Although these pioneering papers have been cited in the primary and review literature as containing evidence for autonomous oscillators in the mouse or in the chick, in fact, neither of these papers provides direct evidence. Indeed, the authors of the papers have carefully refrained from making any conclusions about this aspect, and based on the evidence in these papers, one could just as easily conclude that cells from the chick and mouse segmentation clock cannot autonomously sustain oscillations. We argue that this is a non-trivial problem with the literature. The idea that segmentation clock cells are autonomous has been widely assumed for the purposes of theoretical modeling; this assumption was first explicitly stated in 2003 in three papers, two years before Maroto and three before Masamizu:

1) Lewis, J. (2003) Autoinhibition with transcriptional delay: a simple mechanism for the zebrafish somitogenesis oscillator. Current Biology 13(16), 1398–1408;

2) Monk, N. A. M. (2003). Oscillatory expression of Hes1, p53, and NF-kappaB driven by transcriptional time delays. Current Biology 13(16), 1409–1413;

3) Jensen, M. et al., (2003). Sustained oscillations and time delays in gene expression of protein Hes1. FEBS Letters, 541(1-3), 176–177.,

It is possible that these experimental papers were selectively interpreted by the field in the light of the earlier theoretical models, and the idea that this has somewhere been shown experimentally appears now to be widely believed.

We take some space below to detail the evidence and claims of these two important papers.

Maroto et al., 2005: In this study, cells were isolated from chick posterior PSM, then dispersed and grown in suspension culture, and fixed at subsequent time points over an interval spanning the formation of 2 somites (3 h). The fixed cells were spun down onto a slide to allow in situ hybridization with mRNA to the cyclic gene Lunatic fringe (Figure 3E). The authors observed changes in the percentage of cells expressing Lfng in these different time points, however, they were not able to distinguish between noisy autonomous oscillators and stochastic patterns of gene expression (p313): “Such fluctuating percentages are likely to correspond either to a stochastic shut down of oscillating cyclic gene expression or to asynchronous oscillations among cells of the same pool.” The authors highlighted the need for real-time reporters to investigate whether PSM cells are sustained, autonomous oscillators (p314): “The development of real-time imaging techniques to analyze cycling gene expression at single cell resolution will be required to establish whether oscillations are maintained or not in these cell cultures.”

Masamizu et al., 2006: In this study the first real-time reporter of the segmentation clock, a luciferase reporter of Hes1 expression in mouse, allowed single PSM cells to be observed in vitro. However, the arguments in this paper about oscillations and autonomy need to be treated with caution. The authors first state (p1314) “It was previously shown that expression of the chick homolog c-hairy1 oscillates even in dissected PSM fragments, suggesting that this oscillator functions in a cell-autonomous manner (7, 19).” This is mistaken reasoning by the authors, since this result says nothing at all about cell- autonomous function, only whether the PSM needs to be intact or needs a neighboring tissue to oscillate. The result is equally consistent with cell-autonomous and cell non-autonomous oscillations.

When introducing the PSM dispersal experiments, the authors write: “It was recently shown that dissociated PSM cells also become out of synchrony (19).” But, this is a conclusion that the authors of reference 19 (Maroto et al.,) did not feel confident about, as discussed above. They continue: “However, it is not clear whether each PSM cell has a stable oscillator but is reset at various phases when dissociated or has an unstable oscillator, like fibroblasts. We thus next examined Hes1 oscillation in dissociated PSM cells.” In this latter passage Masamizu assume that the cells oscillate, and couch their description in these terms.

The entire PSM except S0 was dispersed in 100% serum and cells were plated on poly-L lysine glass bottomed wells. The density of plating was not stated, and it was not reported whether cells were touching neighbors during the course of the recording. It is not stated how many cells were imaged, but expression from only 3 cells was reported, each showing 4 expression pulses with variable duration and steeply decreasing amplitude (Figure 4 D, E). The original location of these cells in the PSM prior to dispersion is not known, nor how frequent this behavior is amongst the cells in culture. A period was given as 155 ± 6 min in the text, however, it was not stated how this was calculated. It is difficult to see how this data supports the idea that mouse PSM cells are sustained autonomous oscillators.

Importantly, Masamizu never use the phrase “cell autonomous” to describe their own data. Our reading of Masamizu is that they have probably filmed rare events of PSM cells rapidly damping out oscillations, in a cultured field of otherwise non-oscillatory cells. Consistent with this interpretation is the absence of any study in the last 10 years using any of the various mouse reporter lines to show potential cell-autonomous properties of the oscillators.

In summary, Masamizu’s study proposes that PSM cells may be “unstable oscillators”, and highlights the role of inter-cellular signaling in maintaining and coordinating oscillations in vivo. Reflecting this perspective, their mathematical model of the process did not contain a sustained oscillator. Instead, the formalism is an example of an excitable system where the expression pulses are initiated by fluctuations or by signals from neighboring cells (Figure 5).

It is not our place here to be overly critical of Masamizu, as this paper was a landmark in the field because of the live reporter. However, it is important to point out exactly the strengths and limitations of their study, and to be clear about what sort of evidence is there, what sort of conclusions can be reasonably drawn, and what remains an open question. In our revised version, we have significantly modified the Introduction to more carefully describe the data from these papers and their context in the literature.

Overall, the study appears careful and thorough and will be an important addition to the literature in this field. The experimental detail is sometimes a little sparse and more information could be added for clarification –

see specific comments below. In addition, the figure legends need careful revision, as there is confusing mislabelling in several places. Specific comments:

1) The period of individual cell oscillations at 26°C (81 min) is much longer that the value that is stated to be the period of trunk segmentation in intact embryos (27 min), measured tissue explants from the Looping Tg strain (55 min) and the authors' predictions (40 min) (subsection "Inferred period of segmentation clock cells in vitro”). This needs further explanation and discussion. What is the genetic background of the Tg strain? This is not described in the Materials and methods. The authors should include a measurement of the period of trunk segmentation in intact Looping Tg strain embryos as well as the explants, rather than merely comparing to previously published work (albeit from the same group, but done in a different laboratory etc.).

We agree that this aspect of the manuscript was confusing. In response to this comment and to comment 2 and 4 below, and to very similar to comments by reviewer 2 (concerns 1 and 2), we decided to fundamentally reorganize the beginning of the Results section, and to include new experiments. We replaced the original estimates of period differences with a direct measurement of the difference between the period of the explanted tissue and the separated cells. Importantly, we combine this with describing the step-wise isolation of the cells, documenting the changes at each step from explanted tissue to isolated cells. We hope that this better illustrates the connection between the different samples, and also makes it clear exactly at which steps differences in the period appear. Note that we cannot yet explain all the differences, but we hope the new manuscript allows the reader to better understand what is known.

We include a new experiment in which we explanted and grew the tailbuds from Looping embryos in similar culture conditions to the isolated cells. These explants show persistent oscillations, but with a longer period than the intact embryo (Figure 1—figure supplement 3). We next describe the dispersed individual cells from the tailbuds in identical conditions, and show that most show very few cycles (median 2) with a twofold longer period before damping out (Figure 1—figure supplement 4). Motivated by the elevated level of FGF in the tailbud in vivo, we next describe the addition of Fgf8b to the cultures. This does not further change the period, but dramatically increases the number of cycles to a median of 5 (Figure 1—figure supplement 5). In addition, we have included a spreadsheet in which the raw and background-subtracted data from all low-density oscillating cells is presented so that other researchers may analyze this in detail (Figure 1—source data 3).

The results from each time series analysis are presented in table form in Figure 1—source data 1. Thus, explanting slows the tissue period about 1.5 times, and dissociating the cells from the tissue slows them about 2-fold. We do not understand the origin of the general slowing in culture, but we comment on the fact that this has been previously noted by others, and propose that some general property of culture may be responsible. We also point out that primary culture studies for zebrafish is in its infancy in the literature, particularly with respect to dynamics, and that obviously more work needs to be done.

A slowing of individual cells due to separation from the tissue was predicted by previous work, and we see this, but the observed magnitude is higher than expected. This is actually quite exciting, and forces us to propose the existence of a second, as yet unknown coupling system and/or a constitutive factor that elevates the period, but is lost by diffusion when the cells are separated (but is obviously not FGF).

We have added text to introduce and explain the transgenic line, which was generated in Soroldoni et al., (Science 345, 222–225, 2014), in a timely manner at the beginning of the Results and information in the Materials and methods. The new Results subsection (“Oscillations in isolated segmentation clock cells in vitro”) describes the step-wise dissociation, the observed periods, and additional measures of the cells’ properties (shape, division, gene expression etc.). We have removed the previous Results section that focused on the calculation of differences in estimated period, and have instead included a discussion of the period differences in the subsection “Heterogeneity in the population of oscillating cells”.

Please also see our response to reviewer 2, below.

2) Little information is given about the health and other characterization of the cells in the low density suspensions. In the videos, they appear to show a lot of blebbing activity –

is this expected? Do they retain other characteristics (e.g. gene expression) of the PSM and are they able to divide? It would be helpful to have some more information about the general behaviour of these cells under the conditions of the experiment.

From previous work done in the Heisenberg, Paluch and Raz lab, embryonic cells of several zebrafish lineages show blebbing phenotypes both in the embryo and in culture (Diz-Munoz et al., PLoS Biol. 8, e1000544, 2010; Maitre et al., Science 338, 253–6, 2012; Ruprecht et al., Cell 160, 673–685, 2015), so we think this is a normal phenotype. We have added information about this in the fourth paragraph of the subsection “Oscillations in isolated segmentation clock cells in vitro”.

We have included experiments investigating the expression of PSM genes. We examined whether the cells in our cultures express No tail (Ntl, a zebrafish homolog of Brachyury), a well-established marker of the posterior progenitor population (Martin and Kimelman, Genes Dev. 24, 2778–83, 2010) and Tbx16 (Spadedtail), a marker of tailbud and posterior PSM (Martin and Kimelman, Dev. Cell 22, 223– 32, 2012). Polyclonal antibodies to these proteins had been previously published (Schulte-Merker et al., Development 116, 1021-1032 (1992); Amacher et al., Development 129, 3311-3323 (2002)), but these reagents are limited or exhausted. Therefore, in the revised version of this paper we now describe the generation and validation by our group of two new monoclonal antibodies to these proteins in a new supplement (Figure 1—figure supplement 6).

During the original experiments that form the core of the manuscript, we had split the starting material: one part was imaged as reported in the manuscript, the other part was cultured in parallel and then fixed at later time points and immunostained for Ntl and Tbx16 protein. We found that 81 out of 114 cells across 10 fields of view in the culture had either elevated Ntl and/or Tbx16 staining in their nuclei after several hours of culture. Since Ntl and Tbx16 expression is lost as cells move into the anterior PSM, this finding argues that many of the cells in culture have maintained a relatively posterior progenitor state. The dissection of the tailbud posterior to the end of the notochord (see Figure 1A and Figure 1—figure supplement 1) is expected to recover cells of the neural plate, skin, endoderm and lateral plate mesoderm, in addition to cells of the PSM. Approximately 60% of the cells express Her1- YFP in culture (Figure 1B), and we therefore anticipated that ~40% of cells in the culture would not express markers of PSM. The finding that 71% of the cells express Ntl or Tbx16 is consistent with most or all of the Her1-YFP positive cells expressing these posterior markers. We have included information about the expression of Ntl and Tbx16 protein in the embryo and in vitro as a new supplement (Figure 1—figure supplement 7), and included text to summarize these findings in the fourth paragraph of the subsection “Oscillations in isolated segmentation clock cells in vitro”.

Summary information for each Fgf8b experiment in the current manuscript is provided in table form (Figure 1—source data 2), and includes the number of expressing cells, cell survival, cell division, etc. Cells that underwent division during the recordings had been previously included in the touching category, because these cells tend to remain in close contact (see below: reviewer 2, point 2), but in response to requests by reviewers 1 and 2, we have now separated these cells, creating a category of dividing cells. The frequency of dividing cells is low ~2%.

3) What happened to the cells that touched each other? Do pairs of cells in contact with one another synchronise their signalling, or oscillate with a shorter period? Is there a community effect, and what is the minimum number of cells in a group that is sufficient to maintain faster and synchronized oscillations?

We appreciate these interesting questions, but this was not measured systematically in our movies. The main problem was that the cells that touch each other usually crawled on top of each other, making it difficult to distinguish between each individual cells using wide-field imaging. We are currently exploring different culture, labeling and imaging options to address this question directly and argue that such an analysis is outside the scope of this study.

4) Fgf8b has been added to the culture medium to mimic conditions in the tailbud. What happens in absence of Fgf8b? Are there oscillations at all? Or damped oscillations? or oscillations with even longer periods?

The effect of Fgf8 was raised also by reviewer 2 (concern 1). Tailbud cells in our culture oscillate without Fgf8b, also with a range of oscillatory phenotypes, but with many fewer peaks on average. These peaks tend to occur at the beginning of the recording, and in most cases appear to damp out. To document this, we have added to the revised version traces from 52 cells from the same starting tailbud cell suspensions as reported in the manuscript (experiments 240711 and 250112), but recorded in a separate well of the divided dish without added Fgf8b. Peak counting analysis of these traces found a median of 2 peaks, in agreement with our previously published work defining the basic isolation and culture protocol (Webb et al., J Vis Exp (89) 2014), compared to a median of 5 peaks for Fgf8b-treated cells (Figure 1—source data 1). Although period estimates for the serum only cells are slightly noisier because of the fewer cycles, they are similar to those of cells treated with Fgf8b. This phenotype is consistent with the proposed role of FGF in the vertebrate tailbud as a factor that retains cells in a progenitor state (Dubrulle, J. et al., (2001). Cell, 106(2), 219–232.; Diez del Corral, R. et al., (2002). Development 129, 1681– 1691). Rather than being instructive for the period of oscillations, FGF appears to be permissive for the oscillatory state and we have now included some discussion of this result in the fourth and sixth paragraphs of the Discussion, as it is a unique test of various hypotheses about the role of FGF in the embryo.

Thus, the addition of Fgf8b to this culture system keeps the cells oscillating throughout the recording and allows us to observe more cycles per cell and improve period estimates. We have included this information now in a new supplement (Figure 1—figure supplement 4), compare the statistics of these cells directly in Figure 1—figure supplement 8, comment on the effects of FGF in the culture at the beginning of the Results section.

5) The legend to Figure 1—figure supplement 1 is not sufficient to understand the figure. There is both a red and a grey line on each panel, but the legend confusingly only refers to a black line. (What is the grey line? Background levels? This should be stated somewhere.) I presume that the grouping of each set of traces refers to the independent replicates, but this is not explained anywhere. The 'smoothed' traces should be labelled as such on the figure. Also, the colour code is not correct – the smoothed traces are in red with blue circles to indicate peaks and troughs, not in blue with red triangles as indicated in the legend.

We apologize for the mistakes in the color referencing. We have revised the figure legend to accurately reflect the figure.

Likewise, in Figure 1—figure supplement 2 and legend, the peak finding on the traces is actually labelled with red triangles, not blue as indicated in the legend; filtering appears to be labelled with blue triangles, not red as indicated. This lack of attention to detail has made it difficult and time-consuming to review the manuscript.

Again, apologies for the mistakes in the color referencing. We have revised the figure legend to accurately reflect the figure.

6) Figure 1—figure supplement 6 –

these traces show timecourses for 10 individual isolated cells. Have these data been subjected to the same smoothing, peak and trough analysis etc. as the data from the low density set? Do they behave in a similar way?

We have updated this figure (now Figure 1—figure supplement 9) to show the raw, background-subtracted data with smoothing and with peak calling using the same basic analysis pipeline as the other time series. This is described in the figure legend. The statistics from these cells are now included in tabular form (Figure 1—source data) for comparison with cells in all conditions. Although the certainty associated with these values is lower because of the smaller sample size, the cells behave in a similar way.

Reviewer #2: The manuscript presents a very worthwhile data set, detailing time-course expression profiles for a Her1 reporter with high temporal resolution. These show a high degree of variability, and a range of analyses are performed to extract phase and amplitude data. The authors go on to compare these summary measures to those obtained from a generic model of a system close to a supercritical Hopf bifurcation (at the boundary between decaying and sustained oscillations). They show that reasonable (though not perfect) agreement between the two sets of measures (experimental and simulated) can be achieved for an appropriate set of model parameters. These results are interesting in their own right, as a careful investigation of the nature of the time-courses obtained from the cultured tailbud cells. I'm less convinced that they say anything particularly important about somitogenesis in zebrafish. My primary concern here is that the Her1 expression observed in the low-density cultured cells is so distinct to that observed in tailbud cells in an intact embryo. The period of oscillation in vivo is 27min; the mean period extracted from the time-courses of the cultured cells is around three times as long as this (ca. 78min). The two sets of oscillations thus represent markedly different dynamics. The long-period noisy oscillations observed in cultured cells may (or may not) be due to a dynamical system close to a Hopf bifurcation, but if they are, it is hard to see how this relates to a dynamical system based on the same components oscillating in a tissue with almost three times the frequency! The key observation in this regard is that the somitogenesis period in explanted PSM is around 55min, rather than the 27min in the embryo at the same temperature. This is reported in this manuscript without any real discussion. But surely this is a striking and potentially important result. My overall assessment is that the data set and data analysis are high quality and worthy of publication. The potential fit to a very generic model is also interesting, but I'm not convinced that the fit is actually that good. Given the large discrepancy between the cultures and the embryo, I'm not convinced that the data have much to say about somitogenesis.

We share with the reviewer the view that the slowing of segmentation in the explant is a striking and potentially important result. Of course, any in vitro model of an in vivo situation must be viewed with caution, and zebrafish primary cell culture is in its infancy, particularly when it comes to understanding dynamics. However, we disagree that the difference in period between intact embryo and individual cell is in itself a substantive problem with the in vitro model; we argue that the differences may allow us to begin to reveal and estimate the magnitude of key interactions present in the tissue that are missing in vitro. There are a number of points raised by the reviewer in the paragraphs above, which we attempt to clarify and discuss here, as well as describe the new experiments and revisions we made.

1) Comparison of period lengths. Given the previously noted slowing of development in explanted zebrafish tissue (Langenberg et al., Dev. Dyn. 228, 464–474 (2003)), we needed a more direct measure of this slowing to get a better comparison of the differences between the genetic oscillations in the tissue and single cell. We have therefore now added a new experiment in which we estimate period directly from the YFP signal in explanted Looping1 tailbuds (Figure 1—figure supplement 3, Figure 1— source data 1). We found a period of 42 minutes in the explant, which is about 1.5 times the longer than the period of segmentation in the intact embryo. When cells are dispersed from the tailbud explants in culture, the period lengthens approximately 2-fold (regardless of the presence of FGF). We argue this is a direct measurement of the difference between tissue-level and single cell oscillations in culture. An increase in period after dissociation was expected but its magnitude was not, so these new experiments provoked by the reviewers’ critiques may have revealed a new phenomenon. We speculate that this difference might be due to an as yet unknown additional source of coupling in the tissue, and/or a tonically-expressed factor in the tailbud that elevates the frequency in the tissue, but is diluted once the cells are dispersed. Please also see the detailed response to reviewer 1, substantive concern 1, above. Thus, the revised manuscript removes the lengthy and somewhat abstract comparisons of estimates in the Results, replacing them with measurements at the beginning of the Results, and a discussion of the differences at the end.

2) With respect to the more general point about whether a system can oscillate over a range of 2-3 fold in frequency using the same components, we would point out that changes in temperature cause the whole system to shift its frequency 3-fold, while generating a normally proportioned embryo (Schröter et al., Dev. Dyn. 237, 545–553, 2008). Such reliability at different temperatures and periods is likely advantageous for an embryo that grows up without parental care and is subject to a fluctuating environment. Although this hasn’t been examined in detail, we would be hesitant to say that the oscillations at one of the temperatures do not relate to the dynamics of the system at other temperatures. Whatever the changes to the biochemistry, these end up in the parameter omega for the frequency in the model. The model is used primarily to probe the noise in the data and doesn’t describe the changes in time-scale. Thus, we argue that the change in frequency is not in itself a problem for the model or interpretations.

We don’t yet understand the 1.5-fold slowing in the explants relative to the intact embryo. Our hypothesis is that some general temperature-like factor is influencing the rate of development generally. It was reported that changes in O2 can slow zebrafish development and even temporarily arrest it (Padilla and Roth, 2001, PNAS 98(13):7331-5), so gas exchange may play a role.

Alternatively, there may be some rate influencing metabolic factor that is normally available from the yolk that is missing in the explants, causing the tissue to use an alternate energy source with a lower flux, which influences the general developmental rate. We wish to investigate this slowing in the future, as it is indeed striking and could well be more generally important, but we have argued here that it should not present an insurmountable challenge to the current analysis and interpretation of the data.

We are confused by the reviewer’s statements “…reasonable (though not perfect) agreement between the two sets of measures (experimental and simulated)” and “…I'm not convinced that the fit is actually that good”. It is rare that model and experimental data are in perfect agreement, and we are deliberately using a very simple model to try to tease apart the basic timescales in the noise. It would almost certainly be possible to add more complexity to the model (additional parameters), or change its structure altogether, and thereby improve the match between model and experiment (Note that in Figure 2, there is no fitting in the technical sense), but it is unclear what would be gained. Nevertheless, it is important to point out what the model did not do a good job of explaining, and in this respect we have revised the paragraph comparing model and data (see point 3 below).

Substantive concerns: 1) Fgf8b was added to the culture medium "to mimic the signaling environment of the tailbud". Was this necessary to see oscillations in Her1-YFP levels? What happens if it is not added?

See response to reviewer 1, specific comments 4, above.

2) Did cells in culture never divide? This is not mentioned (other reasons for discounting time-courses are mentioned). Cells in the tailbud typically undergo a single division at around 15-16hpf (see Figure 1C in Bouldin et al. (2014). Genes & Development, 28, 384-395.) It seems that this division should fall within the time window of the current study. Are the culture conditions blocking this division, and if so, might that be expected to affect the oscillations?

Cells divide during the recording, although this is at low frequency. This behavior was previously included in the “touch another cell” category, as after division the cells almost always stay in contact and crawl over each other, but Figure 1—source data 2 has now been revised to include the division category explicitly.

The number of cell divisions we see is reduced relative to what was measured in vivo by Bouldin et al., 2014, and therefore it seems that the culture conditions are inhibiting division. Importantly, Zhang et al., 2008 (Cell cycle progression is required for zebrafish somite morphogenesis but not segmentation clock function. Development, 135(12), 2065–2070) examined the emi1 mutant zebrafish that lacks cell divisions after early gastrulation and concluded that the segmentation clock was normal. Bouldin showed that a heatshock of cdc25a expression increased the mitotic rate and prolonged Tbx16 expression, but did not present evidence about the effects of reducing division on differentiation. On this basis, we wouldn’t have expected that reducing cell division would affect the cells ability to oscillate per se. In any case, we have checked Tbx16 and Ntl expression in the cells of parallel cultures (as above) and found that expression is consistent with the tailbud. We argue therefore, that although the culture system appears to reduce cell division, this has not affected the differentiation state of the cells.

From previous studies in the embryo (Delaune, E. A., et al., (2012). Single-cell-resolution imaging of the impact of Notch signaling and mitosis on segmentation clock dynamics. Developmental Cell, 23(5), 995– 1005), divisions were observed to introduce phase noise into the time series. Thus, our analysis, which excludes cells that divide, is likely to give a slightly higher measurement of precision than if we included dividing cells. Additionally, because of the very low rate of cell division in the culture, we argue that cell division cycle stage is unlikely to be a major contributor to the heterogeneity we observe. We have commented on these aspects in the first paragraph of the subsection “Precision of persistently oscillating cells”.

3) The authors state (subsection “Heterogeneity in the population of oscillating cells”) that the simulated data are "in good agreement with the experimental data (Figure 2F)" However, Figures 2B and 2F don't match very well, as noted by the authors themselves in the next sentence. There is clearly more overall variability in amplitude in the real data (2B) than in the simulated data (2F), though the correlation of neighbouring peak amplitudes is similar. So the data show similar short-time coherence of amplitude to the model, but significantly greater variability in amplitude overall.

As mentioned above, we have deliberately used a very simple model, where we did not expect an exact match to the data. In order to avoid giving the impression that we have captured all the features of the data, we have replaced the phrase “in good agreement” with “comparable to”, and then given a sentence where we point out the differences to the data:

“Slow amplitude fluctuations can drive the oscillators in and out of the oscillatory state (Figure 2E; Figure 2—figure supplement 2), and introduce correlations in the amplitude of consecutive cycles that are comparable to the experimental data (Figure 2F). Interestingly, the trend to higher amplitude variance at higher amplitude values, and the existence of a low occurrence of high relative amplitude cycles are not captured by the theory.”

4) The data do appear to support the idea that the main variability in the oscillations is in the amplitude rather than in the period (Figures 2B, 2C). The authors use this finding to focus their attention on a S-L model with q=0 (so, the frequency is independent of the amplitude). This restricts the type of supercritical Hopf bifurcation that could underlie the observed oscillations (the normal form does not require q=0). Does this restrict the possible molecular mechanisms underlying the observed Her1 oscillations? In particular, do noisy negative feedback oscillators behave in this way? It is my understanding that stochastic simulations of negative feedback circuits (like the ones alluded to by the authors) that exhibit sub-Hopf stochastic resonance do show amplitude-dependence of the period (increased amplitude leads to increased period). Furthermore, the authors have previously shown that the use of the Her1-Venus transgene increases the period of oscillations. Is this likely to be due to the overall increase in expression level of Her1 in the Looping line? The amplitude-dependence of period (or lack of it) is potentially important for the tissue-wide oscillations observed in the PSM, as the value and distribution of q is an important factor in the ability of oscillators to synchronise.

Our choice of q = 0 was made partly for simplicity, and also based on some data that we didn’t present before, which is the correlation between period and amplitude – apologies for this. We have now included this plot in Figure 2—figure supplement 1 as panel D. The reviewer is correct to point out that in general when a system is reduced to its normal form close to a Hopf bifurcation, it requires a special non-generic symmetry to get one of the parameters = 0. Thus, we do not make any claim that the underlying system has this property; in general we expect that q would not be zero. However, with noise in the system, a small value of q can easily be blurred. We show this scenario in Figure 2—figure supplement 1 panels E-I, in which we examine the effect of noise on the SL model with known values of q.

We also examined the behavior of the classical Lewis negative feedback model (Lewis, J. (2003) Autoinhibition with transcriptional delay: a simple mechanism for the zebrafish somitogenesis oscillator. Current Biology 13(16), 1398–1408). For this model also, using the parameters given in that paper noise can blur the correlation between the amplitude and period. We agree that using these new data to constrain and develop microscopic models of the segmentation clock, thereby probing the molecular mechanisms at the core of the clock is a very interesting prospect, but to do so will require a systematic examination of how different sources of noise affect the dynamics of the various models, as well as examination of various perturbations. We argue that this is a major new project, and outside the scope of the current paper.

In the interests of furthering the utility of this data, we have now included a spreadsheet in which the raw and background-subtracted data from all low-density oscillating cells is presented so that other researchers may analyze this in detail and test against other theoretical descriptions (Figure 1—source data 3).

The overall increase of period in the Looping line is unlikely to be due to the elevated levels of Her1 in the embryo. We have generated several independent lines with the same transgene and these express a range of levels, but have an identical period offset to wildtype (10 ± 2%) as the published Looping line.

Reviewer #3: Webb et al. describe segmentation clock oscillations of individual dissociated zebrafish tail bud cells. They find that oscillations are present in vitro (as expected), but that the period is longer than in vivo (as previously postulated but shown here for the first time). A noise model can account for the degeneration of oscillations. The data is interesting for zebrafish researchers but I am not convinced that it goes beyond previous studies in chick and mouse. It seems straightforward to compare the in vitro oscillations to the in vivo oscillations in Notch signaling mutants. This experiment would test if the differences in vitro can be explained by the absence of Notch signaling.

As described above, this study clearly goes well beyond previous work in mouse and chick.

We are not aware of any report of reliable imaging and tracking of oscillations in tailbud cells, the subject of this manuscript, in an intact embryo. Delaune et al. (Dev. Cell 23, 995–1005, 2012) and Shih et al. (Development 142, 1785–1793, 2015) have reported oscillations of single cells in the bulk of the PSM, where cell movement in the tissue is very limited, enabling reliable semi-manual tracking over time. These cells are all systematically slowing their oscillations (Morelli et al., HFSP J. 3, 55–66, 2009; Shih et al., 2015) and are not the relevant comparison to our cell culture. In contrast, cells are moving rapidly in the tailbud (in x, y and z) (Lawton et al. Development, 140(3), 573–582, 2013). We have not yet been able (nor have other laboratories) to extract extended tracks on the timescale of several cycles that would enable a reliable estimate of the period of tailbud cells in the intact embryo. This is why we have considered the period of oscillations at the local tissue level instead (effectively averaged over many cells moving within the tailbud) where the measurements are reliable (Soroldoni et al., Science 345, 222–225, 2014). Note that this period would include the effects of local and tissue-level collective processes such as cell-cell coupling or diffusive signaling.

[Editors’ note: the author responses to the re-review follow.]

Reviewer #1: Firstly, and also with respect, I would like to clarify that I did not state that the previous manuscript was 'only a technical' advance over previous work; in fact, this part of my review was a positive comment in support of the paper. The authors have addressed all the points that I raised, most of them very satisfactorily. I think the argument is clearer and that the additional data (e.g. maintenance of marker expression) help with the overall interpretation. My one remaining concern relates to the issue of dividing cells in the low-density dataset. It is helpful that the authors have given more detail on cell divisions in a source file, and I appreciate the argument that the focus of the study is necessarily on the single cells. However, more explicit information is still needed here, especially for Video 1. The legend to Video 1 indicates that it corresponds to the field of view for the non-dividing cell in Figure 1B, C. It would help to mark the cell of interest (e.g. with a ring or arrowhead) at the start of the video. Otherwise, the text in the fifth paragraph of the subsection “Oscillations in isolated segmentation clock cells in vitor”, leads the reader to think that Video 1 is illustrating a whole field of cells that do not divide.

We have marked the cell of interest with an arrow at the beginning of Video 1, and we have re-written the legend to Video 1 to describe what is seen and how we processed the different cellular behaviors for analysis in the paper. We hope that this description, along with other changes (see below), will help to clarify the reported cell categories and to reduce ambiguity about the decision-making process.

More importantly, however, in addition to the non-dividing cell in the lower left, Video 1 also includes no fewer than five clear examples of cell divisions, four of them YFP+ (at 00.26 (top right and lower right), 00.30 (middle left), 00.33 (extreme top right) and 00.41 (bottom right)). I find this very surprising, given the source data file (Figure 1—source data 2), which documents only 9 instances of cell division in the entire dataset from a total of 29 fields of view, which would suggest that cell division events are rare. The observation of five division events in a single field of view also suggests that Video 1 is not representative of the dataset as a whole, and is directly contradictory to the statements in the rebuttal that 'it seems that culture conditions are inhibiting division'; 'because of the very low rate of cell division in the culture' etc. In short, I am not confident that the authors have measured the rate of cell division accurately in their cultures. Further explanation is required here.

We re-counted all the divisions in the movies, and added an expanded explanation of how cells were categorized. As we now state in the legend to Figure 1—source data 2:

“Across the 29 fields recorded, we observed cell divisions in both YFP-negative (30, 5% of total cells) and YFP-positive cells (13, 2% of total cells). We found a range in the number of cell divisions from 0 to 5 cells per field, with an average of 1.5 ( ± 1 SD) divisions per field. The categories of disqualification list the first event in a recording that led to disqualification. For example, four divisions in YFP-positive cells occurred after the cell had been disqualified for another reason (movement in and out of field, touching another cell).”

In summary: (1) we re-counted the same number of YFP-positive divisions as we had previously reported (2%); (2) a slightly larger number of YFP-negative cells are dividing throughout the experiments (5%); and (3) the field with the highest number of divisions (5) was indeed the field shown in the supplementary video.

This means that Video 1 is not representative of the mean number of dividing cells per field in the data set as a whole, but if one calculates the approximate Maximum Load expectation for throwing 43 balls (cell division) into 29 pots (field of view), it’s ~4.5, so we don’t think a field with 5 events was unexpected. We argue to retain this video for illustrative purposes, with appropriate annotation, as it does give a nice, compact overview of the different behaviors that are seen in the experiment, as highlighted by Reviewer 1 (below). We hope that readers will find these interesting and it will stimulate future studies in the community.

We have now revised the Results section, Figure 1B legend, and the legend of the movie to reflect these facts, and in particular to avoid giving the impression that the field is representative of the mean division rate per field in the entire data set. Results subsection “Oscillations in isolated segmentation clock cells in vitro”, fifth paragraph, Figure 1B legend, Video 1 legend.

As the authors have pointed out in their rebuttal (although I could not find this in the manuscript), the pairs of daughter cells remain attached to one another. As far as I can see, there does not appear to be a consistent timing of division relative to the phase of the oscillation between the three examples, or maintenance of synchrony between daughters within a pair, although oscillation in at least one daughter can clearly continue after division. For example, after the division at 00.30, the daughter on the left of the pair has a very clear YFP peak at 00.39-00.40, while its sister on the right has very low YFP signal at the same time point. Since the dataset captures this very interesting information, it deserves some comment, even if a full analysis is beyond the scope of the current study.

We have commented on the cells’ tendency to remain attached after division and the interesting observation that oscillations can continue after division in the Results section, subsection “Oscillations in isolated segmentation clock cells in vitro”, fifth paragraph.

For cells that did divide (including the four YFP+ cells shown in Video 1), were oscillations measured up to the point of division, or were these cells eliminated from the analysis altogether? The text is not altogether clear on this point.

Any cell that divided at any point in the recording was disqualified from analysis. We now state this explicitly in the fifth paragraph of the subsection “Oscillations in isolated segmentation clock cells in vitro”.

Reviewer #2: I continue to believe that the data described in this manuscript are interesting and valuable, and I think it is very positive that the authors are making the raw data available to allow others to analyse them (although I maintain that the authors have done a good job of this already). The authors have addressed my queries and concerns. The additional data, and provision of raw data, make it easier to assess the validity of the statements made in the manuscript. I have one remaining niggle with the conclusions drawn from the data and the corresponding nomenclature employed by the authors. The cells are derived from the tailbud and maintain tailbud markers (new data). The cells certainly exhibit oscillations, which have features that are consistent with an underlying dynamical system that is close to a Hopf bifurcation. So it is fair to say that the cells are oscillators. However, I remain to be convinced that these facts are sufficient to call the cells "single zebrafish segmentation clock cells" (e.g. sixth paragraph of the Introduction and many other places). The segmentation clock is surely a coordinated tissue-wide oscillatory operating in the tailbud/PSM. A parsimonious (though not necessary) explanation of the findings reported is that the segmentation clock results from the interaction of some noisy cell-autonomous genetic oscillators. But that is not sufficient to call the oscillations in the single cells in vitro a "segmentation clock". I accept the argument that the period of the in vitro segmentation clock can exhibit marked temperature-dependence. But that does not lessen the difficulty of arguing that if a cell-autonomous oscillation in tailbud-derived cells is borderline-Hopf with a period of ca. 80min, then the in vivo clock, with a period of ca. 27min, has something to do with borderline-Hopf dynamics. I maintain that I do not think it is easy to explain how an oscillatory mechanism can be close to a Hopf bifurcation at two radically different periods. It may be that the mechanisms underlying the observed in vitro cell-autonomous oscillations and the in vivo segmentation clock are closely related (and it is probably true), but that does not mean that their dynamics are similar. Just because cells can oscillate in two different conditions does not mean that one can say that the oscillations are two different versions of the same thing. In summary, I like this study. I think the in vitro oscillations are interesting and the analysis is powerful. I just don't like the idea of calling these oscillations a segmentation clock –

that is what operates in the embryo.

We fully agree with the reviewer’s assessment. Indeed, our group has often argued for the use of the term segmentation clock to refer to the tissue-level rhythmic patterning system in the embryo, so we should have been aware of this connotation. We have changed the term “segmentation clock cell” to “cell isolated from the segmentation clock” or equivalent and appropriate wording throughout the paper (once in the Abstract, three times in the Introduction, eight times in the Results, and once in the Discussion (see annotated manuscript version). We have also inserted a qualifying sentence about the general slowing in the Discussion:

“Nevertheless, until the mechanism of this general slowing in vitro and its influence on the molecular and cellular processes within the segmentation clock are understood, we must remain circumspect in our interpretations.”

Reviewer #3: Webb et al. have revised their manuscript to more clearly explain the limitations of previous studies in concluding that cell-autonomous oscillations form the basis of the segmentation clock. The differences between single cells, tissue explants and in vivo tail buds are striking but unexplained. The paper is a nice technical advance but the main conclusions were expected from previous studies, and the most interesting phenomena of different periods in vitro and in vivo remains unaddressed.

We agree that the differences between single cell and tissue level activities are still not understood. We also agree that some theoretical studies gave expectations that are now supported by our work (and other theories are now disqualified), but we continue to argue that there was no previous experimental work of this kind, and that the experimental demonstration and characterization of the autonomous state is an important contribution.