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Reply to the reviewers
We thank the four reviewers for their generally positive feedback on the manuscript. Below, we provide a point-by-point response to each reviewer.
We are performing new FCS and gradient measurements as suggested by the reviewers. We are confident we can have these completed within three months (accounting for the summer break).
Reviewer #1 (Evidence, reproducibility and clarity (Required)):
*This manuscript reports a very thorough and careful study of the mobility of Bicoid in the early embryo, explored with single-point fluorescence correlation spectroscopy. Although previous groups have looked into this question in the past, the work presented here is novel and interesting because of the different Bicoid mutants and constructs the authors have examined, in particular with the goal of understanding the role of the protein DNA-binding homeodomain. The authors convincingly show that there is a significant increase in Bicoid dynamics from the anterior to the posterior region of the embryo, and that the homeodomain plays an important role in regulating the protein's dynamics. Their experiments are very well designed and carefully analyzed. The authors also modelled gradient formation to see whether this change in dynamics might play a role in setting the shape of the gradient. I am not sure I fully agree with their conclusion that it does, as mentioned in my comment below. However, it is an interesting discussion to have, and I think this paper makes a significant advance in our understanding of Bicoid's behavior in the early embryo. *
We thank the Reviewer for their positive comments and their suggestions for improving the manuscript. We will resolve the concerns raised by the reviewer with clarity in the revision. We will also add additional comment in the Discussion regarding the interpretation of our results.
*Major comments: *
- 1) Gradient profile quantification: Some of the conclusions made by the authors rely on the comparison between their model of gradient formation (as captured in the equations in lines 232 and 233) and the Bcd intensity profile measured in the embryos. Since the differences in gradient shape predicted by the different models are very small (see Fig. 3B, which is on a log scale and therefore emphasize small differences, and Fig. 3C), it is very important to understand how reliable the experimental concentration profiles are.*
This is a fair comment. It is worth noting that the key differences between the 1- and 2-component models are only apparent at large distances (and hence low concentrations) from the source.
We performed the quantification of the gradients in a manner similar to the Gregor lab, whereby the midsagittal plane is analysed. We used 488nm illumination (rather than 2-photon, as the Gregor lab does) so our measurements are likely noisier. However, we are not investigating the variability in the gradient here, but the mean extent. We currently correct background with a uniform subtraction, but we appreciate that is not the optimal method.
In the revised manuscript, we will repeat the above experiments using a 2-photon microscope. Further, we will image lines expressing His::mcherry without eGFP under the same imaging conditions to more accurately estimate the background signal. While we expect this to improve the data quality, we do not envisage significant change to the observed profiles based on prior experience.
At the moment, I do not find the evidence that [Bcd] concentration profile is more consistent with a 2-component diffusion model than a 1-component model very strong. A few comments related to this: * * 1a. Line 249, it is mentioned that: "observations ... incompatible with the SDD model". Which observations exactly are incompatible with the SDD model?
The key points are in the preceding paragraph. We will improve the model presentation in the Results and also include further contextualisation in the Discussion.
1b. In Fig. 3D, only the prediction of the 2-component model is shown. What would the simple 1-component diffusion model look like? Is it really incompatible with the data?
We agree with this comment and will provide the 1-component fit to the gradient profiles. We expect it to fit well for the anterior half of the embryo but fail at larger distances (as has been previously shown).
Regarding the FCS data, we also show one and two component fits. We will show the alternative fits – a 2 particle fit is clearly an improvement (see also related response to reviewer 2).
1c. Line 243: "The increased fraction in the fast form ... consistent with experimental observation of Bcd in the most posterior" (Mir et al.)". I am not sure how this is significant, since the simple model also predicts there will be Bcd in the posterior - the only difference is how much is there (as shown in Fig. 3C), and it's a very small difference.
The absolute differences are not large between the two models, but due to the observed clustering (Mir et al. 2018), even small differences can have very large effects. In the revision we will provide estimates of the actual concentration differences.
We are performing new experiments with the Fritzsche lab at Oxford to estimate if there is clustering of Bcd. We will also repeat our FCS experiments to validate our key conclusion of AP differences in diffusion of Bcd. These should be completed by the end of the summer.
1d. Since the difference between models is in the posterior region where Bcd concentration is very low, when comparing the models to the data the question of background subtraction is essential. How was the subtracted background (mentioned line 612) estimated?
See above response to the first comment.
1e. Along the same line, were the detectors on the Zeiss LSM analog or photon counting detectors, and how confident can we be that signal is exactly proportional to concentration?
We used PMTs and did not directly do photon counting. But the intensity is still proportional to the concentration. It is possible to estimate the absolute concentration value, e.g., Zhang et al., 2021 (https://doi.org/10.1016/j.bpj.2021.06.035). However, our main conclusions – especially regarding the spatially varying Bcd dynamics – are not dependent on this.
1f. Can the gradients created by the two Bcd mutants (FIg. 4B) be quantified as well, and are they any different from the original Bcd gradient?
We agree this would be useful. We will provide the gradient quantifications of the bcd mutants in the revision.
1e. What is the pink line in Figure 5C (I am assuming the green one is the same as in Fig. 3D)? It could be better to not use normalization here, or normalize everything respective to the eGFP::Bcd data to make comparison in relative concentrations in the posterior for different constructs more evident (also maybe different colors for the three different data sets would help clarity).
This is a fair comment, and we will create graphs with new data for better visualisation.
1f. Discussion, lines 402-403: Does the detailed shape of the Bcd in the posterior region matter at all, since the posterior is not a region where Bicoid is active, as far as we know? Could a varying Bcd dynamics have other consequences that would be more biologically relevant?
Bcd is now known to act at 70% EL (Singh et al., Cell Reports 2022). So, the gradient is relevant for a large extent of the embryo length, though it is not known if there is any effect in the most posterior region.
2) Model for gradient formation (lines 231-238): * * 2a. Whether the molecules of Bcd can change from their fast to slow form is never questioned. How do we know (or why might we suspect) they do exchange?
This is a good point. Within the nucleus, and based on our mutant data, we suspect the fast/slow forms correspond to unbound/bound DNA states.
In the cytoplasm, the dynamics are less clear. Bcd can bind to cytoskeletal elements (Cai et al., PLoS One 2017) as well as to Caudal mRNA. Therefore, it seems reasonable to have different effective dynamic modes – yet, how such switching occurs remains unclear.
Ultimately, our model approximates multiple dynamic modes that are integrated to drive Bcd motion. Including switching between states is a reasonable assumption based on what is known about cytoskeletal and protein dynamics, but we do not have a specific mechanism.
It is challenging to estimate a specific kon / koff rate, as the dynamic changes also depend on the diffusion – which itself is changing. For now, we believe our level of abstraction is appropriate given what is known about the system. It will be very interesting to explore the specific interactions underlying such behaviour in the future, but that is beyond this current manuscript.
2b. The values used in the model for alpha, beta_0 and rho_0 should be mentioned. Maybe having a table with all the parameters in the method section, or even in the supplementary section, would help. The exact values of alpha and beta matter, because if they are large (fast exchange) a single exponential gradient is to be expected, if they are 0 (no exchange) a double exponential gradient is to be expected, with intermediate behavior in between. Which case are we in here?
We agree and will add a more complete table in the revision.
3) Discussion about anomalous diffusion (lines 386-388): The 2-component model used by the authors to interpret their FCS data seems very well justified here (excellent fits with very small residuals). I agree with the authors' conclusion that "the dynamics of Bcd within the nucleus are more complicated than a simple model of bound versus unbound Bcd", but I don't see how that can lead to a diagnostic of anomalous diffusion instead. Maybe it is just a matter of exactly explaining what is meant by anomalous diffusion here (since this term is often used to mean different things). A more likely scenario I think, is that there are more than just two Bcd components in the system.
This is a good point, and we can’t easily differentiate two/multi- component fits from anomalous diffusion ones. This is a known problem. But we have recently shown in a collaboration with the Laurent Heliot lab (Furlan et al, Biophys J 2019), that anomalous diffusion is a good stable indicator of changes, even if it might not be the right model. We use anomalous diffusion as it stably predicts changes. We do not claim, however, that diffusion is anomalous. We will improve the discussion of these points in the revised manuscript.
4) Line 440 and after: What is the evidence that the transition between the two forms might vary non-linearly with Bcd concentration? How would that help adapt to different embryo sizes? It would be good to be more explicit here instead of just referring to another paper.
We will improve this discussion. The central point is that the action of Bicoid is unlikely to simply depend linearly on concentration as in that case the ratio of fast to slow forms would be constant across the embryo. Related to the above comment, it is important to emphasise that we are using a phenomenological model, not one based on a specific mechanism.
5) Since an important aspect of this work is the study of different Bcd constructs in vivo, it is important that these constructs are very clearly described, so the section on the generation of the fly lines (Methods) should be expanded. In particular: * * 5a. It seems that the eGFP:: NLS control used here was different from that first described in Ref. 64 (and used for FCS experiments in Ref. 30 and 36)? If so, what NLS sequence was used here, and precisely what type of eGFP was used (in particular, was the A206K mutation that prevents dimerization present in the eGFP used)? If it is the same construct as in Ref. 64, it should be mentioned explicitly. * * 5b. Were the mutant N51A and R54A lines gifts as well, or have they been described before? If so, previous publications should be referenced. If not, how the plasmid was introduced in the embryo should be briefly explained.
We agree and will expand on the fly lines in the revision.
6) Concentration calibration measurements (Methods Fig. 2, line 568 and on). It is well known that background noise is going to interfere with the measurement of N when the signal becomes equivalent to the background noise (Koppel 197, Phys Rev A 10:1938-1945, and for a recent discussion of this effect for morphogens in fly embryos: Zhang et al., 2021, Biophysical Journal 120,4230-4241). It is almost certain that in the low signal regions of the embryo (e.g. posterior cytoplasm) this is affecting the reported concentration, and should be at least acknowledged.
We agree with the reviewer. We will provide the SBR. We will also correct the N values based on the method followed in Zhang et al., 2021, Biophysical Journal 120,4230-4241.
*7) Reference 3 is mis-characterized in two different ways in the manuscript: * * 7a. Line 50: The conclusion in Ref. 3 was not that the gradient was due to a diffusive process, on the contrary Gregor et al. argued that Bcd was too slow to form such a long-range gradient by diffusion. Studies that do present data consistent with a morphogen gradient formation mechanism driven by diffusion are reference 5, reference 30, Zhou et al., Curr. Biol. 2012;22(8):668-75 and Müller et al., Science 336 (2012) 721-724. *
Gregor et al., do not argue against a diffusion process – indeed, they utilise a SDD model in their paper. However, they do extensively discuss how the predicted dynamics from the SDD model are not compatible with gradient formation as observed after n.c. 13. This problem was resolved to some degree by FCS measurements of Bcd (e.g., Dostatni lab, Development 2011) and the use of a Bcd tandem reporter which showed that production and degradation change during n.c. 14 (Durrieu et al., MSB 2018). We will improve the framing of these results in the revision.
7b. The diffusion coefficient estimated from FRAP measurements and reported in Ref. 3 (D = 0.4 micron^2/s) is mentioned a couple of times in the manuscript (line 66, line 395, line 411). However, this number is simply incorrect. When fast components (such as the ones clearly detected here by FCS) are present, they diffuse out of the photobleached area during the photobleaching step. If that is not corrected for during the analysis (and it wasn't in Ref. 3), then the recovery time measured is just equal to the photobleaching time, and has nothing to do with either the fast or slow fraction of the studied molecule - it has no other meaning than to give a lower bound on the value of the actual effective diffusion coefficient of the molecule. This effect (called the halo effect) is well known in the FRAP community (see e.g. Weiss 2004, Traffic 5:662-671), it has been experimental demonstrated to occur for Bcd-eGFP in the conditions used in Ref. 3 (Reference 30), and the actual diffusion coefficient that should have been extracted from the data presented in Ref. 3 has been recalculated by another group to be instead D = 0.9 micron^2/s (Castle et al., 2011, Cell. Mol. Bioeng. 4:116-121). It would therefore be better to report the corrected value from Castle et al. to help the field converge towards an accurate description of Bcd mobility.
We fully agree and will use the improved FRAP estimated value for Bcd.
*Minor comments and suggestions: *
- 8) Figure 1: From panel A, it seems that what is called "Anterior" and "Posterior" is about 150 micron away from the embryo mid-section, i.e. about 100 micron from either the anterior pole or the posterior pole (so not the tip of the embryo, but somewhere in the anterior half or posterior half). Maybe this should be made clear in the text. *
We have made changes in Figure 1A to indicate the region within which the FCS measurements are carried out. We have added the relevant details in the legend of figure 1 lines 137-138.
*9) Fig. 2A; It might be good to put this graph on a log scale, so that cytoplasmic values are seen more clearly. Also, what about reporting on nuclear to cytoplasmic ratios? *
We will rework on this graph and make necessary changes.
*10) Fig. 2: It could be interesting to plot D_effective as a function of the measured concentration of Bicoid in different locations, since the (interesting) suggestion is made several time that [Bcd] could the a determinant of the protein mobility. *
Our work provides an indication that Bcd concentration is connected to the diffusion. We did this by measuring at two locations. To extend this to a rigorous model would require substantial new measurement along the whole length of the embryo. While interesting, this represents a very large investment of time and lies beyond the current manuscript.
*11) Figure 3B&C: Is the curve for 2-component diffusion (without concentration dependence) for steady-state missing? *
We will clarify in the revision.
*12) Lines 78 and 471: What do the authors mean by "new reagents"? The word reagent evokes a chemical reaction, but there are none here. Do the authors mean new constructs? or new mutants? *
We have changed lines 78 and 479 from “new reagents” to new Bcd mutant eGFP lines”.
*13) Lines 57-59: Another good reference for FCS measurements performed to study the dynamics of a morphogen (in this case Dpp) is Zhou et al., Curr. Biol. 2012;22(8):668-75 *
We added this reference in no.70.
*14) Lines 109-111: A word must be missing. Precisely determined what? *
Precisely measure within cytoplasm, and nuclear compartments and also during interphase stages. We have changed to “precisely measure in the cytoplasmic and nuclear regions during the interphase stages of nuclear cycles (n.c.)12-14.” in line no.111-112.
*15) Line 278: The increase in the slow mode is expected. Maybe explicitly mention why. *
In line 286, we have added “due to the loss of Bcd binding to the DNA”.
*16) Line 282: "with the fast component increasing", maybe replace with "with the diffusion coefficient of the fast component increasing" or "with the fraction of the fast component increasing". *
We have changed line 289 “with the diffusion component of fast component increasing towards the posterior”.
*17) Line 517: Is there a reason why the dorsal surface is always placed in the coverslip? *
We have added these details in line 528-529 in Methods.
*18) Line 524 and on: FCS measurements: What was the duration of each individual FCS measurement? It is great that the exact number of measurements are reported in the supplementary! *
Thank you for the complement. Typically, cytoplasmic measurements are 60secs and nuclear measurements are 20-40s. We have added this in line no.528-529. We also added a column to indicate the duration of each of the measurements in the supplementary tables.
*19) An Airy unit of 120 um seems large in combination with an objective with a NA of 1.2, is there a reason for that? What was the radius of the resulting detection volume? *
Olympus microscopes have a 3x magnification stage in their confocals. This leads to the change in the Airy unit. Otherwise, it would be 40 mm.
*20) Thank you for detailing the reasons behind the choice of excitation power, an important and often omitted details. Where in the excitation path were the values of the laser power measured (before or after the objective?)? *
Thank you for the complement. The laser power is measured before the objective. We removed the objective and measured the laser power in the objective path.
*21) Line 585: "since the brightness of eGFP::Bcd..." do the authors mean the molecular brightness of a single eGFP::Bcd molecule, or the total fluorescence signal? *
It is the total fluorescence signal. We have edited line no.592.
*22) It would be good for reference to mention the approximate value of the molecular brightness recorded for these eGFP constructs at the laser power used. *
We will measure and tabulate in the revised manuscript.
*23) Reference 766: The year (and maybe other things) is missing. *
We have corrected this reference.
24) Figure 2 (Methods): The concentrations shown on the figure should be in nM not uM. * * Thanks for noticing – we have changed.
Reviewer #2 (Evidence, reproducibility and clarity (Required)):
MAJOR POINTS
- 1) FCS measurements and fits *
- a) Please state the duration of each individual FCS measurement. *
In the cytoplasm, the measurements were carried out for 60 secs and in nuclei it is between 20-40s. We could not measure for 60s in the nuclei as the nuclear position fluctuates from its initial position. We will add another column to indicate the duration of FCS measurements in the supplementary tables.
b) The authors acknowledge potential issues with fluorophore photophysics and use different lag time ranges for the calibration dye Atto-488 (0.001 ms in Method Fig. 2) and eGFP (0.1 ms in the main figures). Given the strong influence of different parameters on data interpretation and conclusions, Method Fig. 2 should be repeated with purified eGFP. This is particularly relevant for the noisy FCS measurements in posterior regions.
Performing the experiment with purified eGFP will be a volume calibration. We routinely performed this before each imaging session, and that should be fluorophore independent. As noted by Reviewer 1, it is also important to be clear about background correction. We will provide brightness data for eGFP and background values in the revised manuscript. We can then use this to estimate the corrected concentrations.
We use 0.1 ms to start, as at that point any contribution from the photo-physics should have decayed (0.1 ms is about 3-5 times the day rate of the photophysical process, Sun et al., Analytical Chem 2015).
c) Please explain why no data is shown for "AN" around 0.1 ms lag time in Fig. 1B in contrast to all other figures.
We will add the data for AN from 0.01 in the revised figures.
d) Please state what the estimated diffusion coefficients with one-component model fits are. Please also explain why the fits in Fig. S1E do not reach a value of 1 and why they plateau higher than the experimental data at long lag times. Please constrain the fits to G=1 at 0.1 ms tau and G=0 at 1 s tau to make a fair comparison.
The experimental ACF curves reach 0 at long lag times as would be expected. The one-component fits, however, don’t describe the data well and as a result they do not reach 1 and 0 at short and long lag times, respectively. The fitting is done using a mean-squared estimation of the best approximation of the particular model function to the data. Fixing the parameters can be done, but it will further reduce fit accuracy and deviations will be larger. We will perform this analysis and tabulate the one component fits in supplementary 1 with necessary corrections.
e) Please assess the validity of all multi-component fits by comparing the relative quality of the models to the number of estimated parameters using the Akaike information criterion or similar approaches.
We will provide the values denoting the quality of the fits in the revision. We will provide the 3D 1 particle fit, the 3D 1 particle fit with triplet, the 3D 2 particle fit and the 3D 2 particle fit with triple and will provide appropriate measures of fit quality.
f) Please also present the Bcd-GFP fits with 0.001 ms that are mentioned in line 590, and present the results for the data that did not give comparable tau_D1 and tau_D2 values mentioned in line 593.
We will provide all the curves from 0.001ms in the supplementary. We did not provide these details as we have followed the methods from Abu Arish et al., 2010. As our cytoplasmic and nuclear TauD values match with Abu Arish et al., 2010 and Porcher et al., 2010, we thought the excess data would be redundant.
3) Bicoid gradient and modeling * a) Little et al. 2011 observed that the Bcd gradient decreases around n.c. 13. Can the authors of the present work observe a similar concentration decrease using FCS? This is important to i) validate the FCS concentration measurements, and ii) to resolve the controversy regarding "previous claims based on imaging the Bcd profile within nuclei, which predicted decrease in Bcd diffusion in later stages".*
This is a good point regarding conclusions from the previous literature. The Little et al. paper inferred that diffusion had to decrease from fitting to the gradient profiles. However, subsequent analysis from our lab (Durrieu et al., MSB 2018 [which uses a different method involving a tandem reporter for Bicoid] and this manuscript) strongly suggest that Bicoid remains dynamic, at least through n.c. 13 and early n.c. 14. One way to test this is to use SPIM-FCS, where longer time courses can be taken (though with slower time resolution in the FCS). We have performed preliminary experiments with SPIM-FCS and we will revisit this data to see if we can find evidence for changes in the diffusion.
We will also extend the Discussion to make the results clearer in terms of previous models and literature.
b) Please explain why the experimental Bcd-GFP gradient data does not reach a value of 1 (e.g. in Fig. 3D) despite normalization. Please also explain why the fits become flatter in Fig. 5B compared to the steep fit in Fig. 3D.
Both lines were measured under identical conditions. Therefore, we normalised to the maximum value of both experiments. We will redo, normalising to each individual experiment. Regarding Fig. 5C, the Bcd::eGFP curve is identical to Fig. 3D. The flatter curve is the line with eGFP tagged to a NLS alone.
c) For modeling, please take into account observations that the Bcd source is graded with a wide distribution (30-40% EL, see Spirov et al. 2009, Little et al. 2011, Cai et al. 2017 etc.). The extent of the source used in the present work (x_s=20 um, line 620) is at least five times too small.
Care must be taken in defining the source extent. The most careful measurements are reported in Little et al., PLoS Biology 2011 who performed single molecule FISH. They conclude “We demonstrate that all but a few mRNA particles are confined to the anterior 20% of the egg”. Further, the peak in the particle density is around 20-30um from the anterior (Figure 3, Little et al., PLoS Biology 2011), with the vast majority of counts being with 10% of the anterior pole. Further, Durrieu et al. MSB 2018, showed using a Bcd tandem reporter that there was unlikely to be an extended gradient of bcd mRNA (maximum extent of around 50um). Here, we used a simple source domain, which was arguable a little narrow, but not significantly so. We will increase the value in the revision, but the claim that there is an extended bcd mRNA gradient (Spirov et al., Development 2009) has not been substantiated by later experiments.
- d) Please discuss in the paper how well the simulations in Fig. 3B agree with the experimental data.*
We will provide these details in the revision.
- e) Please provide a precise estimate for the statement "Even with an effective diffusion coefficient of 7 μm2s-1, few molecules would be expected at the posterior given the estimated Bcd lifetime (30-50 minutes)" to turn this into a quantitative argument. How many molecules are expected to reach posterior in which model, and how does it compare to experimental observations?*
This can be estimated based on the root-mean-square distance for diffusive processes. We will provide this in the revision.
- f) The sentence "we find that a model of Bcd dynamics that explicitly incorporates fast and slow forms of Bcd (rather than a single "effective" dynamic mode) is consistent with a range of observations that are otherwise incompatible with the standard SDD model" needs to be toned down and corrected since a simple SDD appears to be sufficient to account for the observed gradients. If the authors disagree, please specifically point out in the paragraph around line 249 what observations exactly are incompatible with a standard SDD model.*
This is similar to the point raised by Reviewer 1. While the standard SDD model can explain the overall gradient shape, it is not compatible with the observed time scales and Bcd puncta tracked in the posterior pole. We will improve the Discussion around this point to make the distinctions between the models clearer.
- 5) Data presentation *
- a) In line 27 and 122 it would be better to rephrase the wording "find/found" and give credit to previous papers that first made these observations. *
We will edit in the revision.
- b) For the statement "This suggests that the dynamics of the fast fraction were not captured by previous FRAP measurements", please explain why this should not be the case even though the fast fraction is shown to be larger than the slow fraction in the current work.*
We will edit in the revision.
- c) Similarly, the sentence "The dynamics of the slower mode correspond closely to measured Bcd dynamics from FRAP" likely needs to be corrected since it neglects the contribution of the faster mode, which is fluorescent as well and should also contribute to the dynamics from FRAP.*
This is similar to the point raised by Reviewer 1 and we will edit in the revision.
d) In the absence of further evidence (see above), the sentences "We establish that such spatially varying differences in the Bcd dynamics are sufficient to explain how Bcd can have a steep exponential gradient in the anterior half of the embryo and yet still have an observable fraction of Bcd near the posterior pole" and "These results explain how a long- ranged gradient can form while retaining a steep profile through much of its range" in the abstract need to be toned down.
We are not sure here what needs to be toned down. Our results show that there are (at least) two dynamic forms of Bcd and, combined, they are capable of forming a long-ranged gradient while also ensuring the gradient remains steep in the anterior (because the diffusion coefficient itself varies across the embryo). We will go through these statements and make sure the meaning is clear.
e) The authors state that "However, we show that eGFP::Bcd in its fastest form can move quickly (~18 μm2s-1), and the fraction of eGFP::Bcd in this form increases at lower concentrations", but this has not been directly shown. Please tone down this statement or directly test the prediction that Bcd has a higher fraction of the fast form in earlier nuclear cycles when Bcd concentration is smaller.
This is a good suggestion, and we will test whether early nuclear cycles of the anterior domain show faster dynamics.
*MINOR POINTS * * 1) Introduction * * a) Please explain explicitly what exactly the contention in Bcd, Nodal and Wingless dynamics is in the cited references. *
We will add in the revision. b) In line 95, it would be better to state that this is a variation of the SDD model rather than "a new model". * We changed from “a new model” to “an improved version of SDD model” in the current version of the manuscript. 2) Methods * * a) The authors state that "The same software was also used to calculate the cross-correlation function", but I couldn't find any cross-correlation analyses. Please clarify. *
It is line 538. There is no cross correlation. We changed this to the autocorrelation function.
b) Please correct the "uM" typo to "nM" in the legend of Method Fig. 2A.
We have changed this in the current version.
- c) In the sentence "Further, since the brightness eGFP:Bcd in the anterior and posterior cytoplasm is lower compared to the nuclei", "brightness" probably needs to be changed to "concentration" since the molecular brightness is unlikely to change. *
We edited the line no.591.
- d) Please explain the background-correction method mentioned in line 612. Please also state at what temperature the experiments were performed.*
We will add a better background correction in the revision. Currently, it is the non-embryo background as background noise. The measurements are carried out at 25oC.
*3) Results * * a) Please provide labels for anterior, posterior, dorsal and ventral in Fig. 1A. * * b) Please explain the colors in Fig. 5C. * * c) Please explain the dashed lines in Fig. 3C. * We have edited Figure 1A and Figure 5C. We will edit Figure 3C in further revision.
*OPTIONAL * * 1) If possible, it would be helpful to mention whether the transgenic animals have any abnormal phenotypes or whether they can rescue the bcd mutant. * We will update in the revision.
*2) To validate the concentration measurements, it would be ideal if the authors could determine the Bcd concentration gradient using FCS along the anterior-posterior axis. This would also address whether there are further unexpected changes in diffusivity in medial regions and along the anterior-posterior axis that would have to be considered for modeling. * To measure the Bcd concentration using FCS along the whole axis would be a very challenging undertaking. To get the data for the two positions analysed already represents a significant amount of work. We have done SPIM-FCS measurements, and we will be repeating our FCS measurements in the Fritzsche lab at Oxford. Combined, we believe this provides sufficient corroboration of our results.
*3) Local photoconversion experiments, e.g. in Bcd-Dendra2 embryos if available, would provide compelling support for the relevance of the measurements in the current work. * This is a nice idea, but this would represent a substantial project in its own right and lies beyond the current work.
Reviewer #3 (Evidence, reproducibility and clarity (Required)):
*In my estimation the experimental work is rigorous and the results fully support the conclusions of the authors. I was surprised, however, that the HD-only form localizes via very different and simpler dynamics than does full-length Bcd, but nevertheless forms at least a qualitatively similar gradient. That leads to the question as to whether the existence of the fast and slow forms and their different ratios in different parts of the embryo actually are physiologically relevant. I don't see a straightforward way to test this experimentally, because the mutations that effect Bcd gradient formation also affect essential functions of the protein that if abrogated produce severe downstream effects on embryonic development and lethality. However I would like to see this point at least addressed in the discussion. The data and the methods are presented in such a manner that they can be reproduced, and the number of replicates and statistical analysis is overall robust. * We thank the Reviewer for the positive and constructive review. They, like both previous reviewers, raise the issue of the model and how it fits with the data. As outlined above, we will improve this part of the data presentation and also the Discussion to make sure the main results are clear.
We agree that the underlying importance of the different dynamic forms of Bicoid – and why they change across the embryo – remains unknown. We believe that our careful characterisation of such behaviour is important nonetheless, as it reveals that: (1) morphogen dynamics are more complicated than typically modelled, and this may be just as relevant for ligands moving through extracellular space; and (2) dynamics can vary in space/time, providing an additional possible mechanism of control for regulating morphogen gradient profiles.
Of course, we would like to explore potential physiological relevance. Further exploration of the homeodomain and its role in regulating dynamics is a potential route, but that belongs in future work.
*Minor comments: *
- The presentation of the graphical data measuring Bcd levels along the a-p axis (Fig 1C, 1D, 4C-F and others) needs to be improved, because the grey lines that represent ACF curves are essentially invisible. This is partly because there is usually extensive overlap between the grey lines and other lines. This may be solved by using a more vivid colour than grey for the ACF curves, or perhaps the ACF lines could be made thicker but with some transparency so that overlapping data can be seen. In any event this aspect of the presentation needs to be improved. * We have made the ACF lines thicker to distinguish from the model fit.
*In Figs 2D and 2I measurements of statistical significance between the proportion of protein in fast and slow modes need to be added. * We will add in the revision.
*Relevant to line 174 and Fig 2, NLS should be defined when first used, the source of the NLS should be given (is it from Bcd?) and the rationale for looking at eGFP::NLS should be made explicit. *
We have added details on how the eGFP::NLS is generated in the methods.
*In Fig 3D the dashed lines need to be defined. I assume these are experimental error bars but this is not stated. *
We now state this in the legends.
*On lines 344-5, shouldn't this conclusion concern the HD rather than the NLS? * Yes, thanks for pointing it out it is related to only NLS not NLSHD. We removed this statement from line 351.
*On line 432, CAP is not an acronym, the correct term is 5' 'cap' or 'cap structure'. Also Cho et al. PMID 15882623 should be added to the references here. * We changed the corresponding section and added the references.
*On lines 446, 456, 469, and throughout: replace 'blastocyst' with 'blastoderm'. The former term is generally used for embryos that undergo full cellular divisions and cleavage in early embryogenesis, not for syncytial embryos such as Drosophila. * We have changed blastocyst to blastoderm throughout the manuscript.
Reviewer #4 (Evidence, reproducibility and clarity (Required)):
Major comments: The averaged autocorrelation curves were fitted to models of diffusion with one and two components. The one-component model was insufficient to reproduce the data and the two-component model seems to fit the data. Have the authors tested models with more than two components? Could it be possible to distinguish more Bcd populations?
While it is possible to fit with further components, it rarely provides useful further insight. In particular, the error in measuring three tau_D’s is typically very large. In addition, the improvement in the fit will be marginal, and thus the extra components cannot be justified statistically. Of course, we cannot exclude a third (or more) possible dynamic modes, but within the resolution of our FCS measurements two components with triplets are in general the maximum that can be accommodated without overfitting. We will provide evidence for this claim in the supplement of the revised manuscript.
In Figure 2E, the same concentration of eGFP::NLS is estimated to exist in the cytoplasm and nucleus. Since the NLS should target eGFP to the nucleus, what is the explanation for this observation? Is it possible that the method used to estimate the concentration of molecules is underestimating the concentration in the nucleus or the opposite in the cytoplasm?
This is a good observation. There are two possible explanations. First, the regular division cycles “reset” the nuclear levels. Therefore, differences may not be so large. Second, FCS measurements of concentration can be noisy, as they depend on the very short time scales in the measurement. We will double check our measurements and clarify this in our revision.
*In the simulation of the SDD model (Figure 3B), simulations at 10 min, 25 min and 120 min are shown. Assuming that 120 min corresponds to early nc14, are simulations at earlier timepoints corresponding to nc12 and nc13 indistinguishable from the profile at 120 min? This demonstration would further support the option to merge the data from all nuclear cycles. *
This is a good point. Here, we were primarily focused on showing the time evolution of the model, rather than directly mapping onto experiment. We will clarify in the revision.
*The results obtained with the BcdN51A mutant show an increase in diffusion speed, while retaining similar proportions of fast and slow populations. In the slow fraction, a new population is found. Assuming that the BcdN51A molecules cannot bind specifically to DNA due to the mutation, what would this newly found population correspond to? Could the authors explore the possibility of nonspecific binding to DNA? The article would also win by discussing more on this aspect or other options. *
This is an interesting question. Dslow for anterior nuclei of N51A mutants increases (Dslow from ~0.2um2/s to ~1.5 um2/s), and the proportion is similar to the slow fraction of WT Bcd in the anterior nuclei (F=50%). The Dslow values of bcdWT suggest that 0.2um2/s is a result of DNA binding. For bcdN51A, Dslow of 1.5 um2/s is suggestive of nonspecific interaction of bcdN51A to the DNA. Such a nonspecific interaction is also noticed in the case of NLS::eGFP, where we see a significant amount (Dslow~ 1-1.5 um2/s , F=20%) of slow form in the anterior nuclei, likely due to non-specific interaction with the DNA.
It is worth noting that the inactive homeodomain of transcription factor sex comb reduced (scr) also interacts non-specifically with DNA at high concentration (Vukojevic et al., PNAS 2010). Non-specific interaction of eGFP fluorophore is also noted to be higher in the nuclei of AT-1 cells that suggest “obstacle-free accessible space” is low in the nuclei (Wachsmuth et al., JMB 2000). Therefore, though we do not understand the specific mechanism, our results for N51 mutants are aligned with previous observations of intra-nuclei dynamics.
The experimental rational behind the BcdMM reporter needs to be better explained as it is not clear. It was previously shown that the N51A mutation disturbs zygotic hb activation and Caudal gradient formation (see Figure 3 in Niessing et al., 2000). Since N51A already causes a strong phenotype by disturbing hb expression and Cad gradient formation, what is the reasoning being adding extra mutations to this background? Since the mutations in the PEST domain and YIRPYL motif are involved in cad translational repression, it would be more interesting to add them to the R54A mutation and further study the repression of cad? It would also shed light on the unexpected no difference or even decrease in diffusion in the cytoplasm of the R54A mutant which should increase if indeed the cad mRNA binding is being repressed.
Our rationale was to remove more elements of Bcd to see if there was some degree of redundancy – at least in terms of the dynamics.
The Bicoid homeodomain N51A mutation is physiologically known to cause de-repression of caudal and inhibit hunchback expression. Mechanistically, nuclear Bcd activates hb transcription. However, in the cytoplasm Bcd interacts with other proteins and forms a complex to de-repress caudal. Bcd binds to caudal mRNA through its HD at one end of the complex. However, in the other end, other proteins in the complex are bound to the 5’cap region caudal mRNA. Our rationale for generating the MM mutation was that the N51A mutation may not be sufficient for Bcd to be released from the protein complex. Therefore, additional mutations to N51A may release Bcd from interactions with either DNA or with other proteins through PEST domain and YIRPYL motif.
*Have the authors confirmed that their BcdR54A indeed inhibits cad translation? *
We have not tested the eGFP:bcdR54A to inhibit cad translation. We will add the data in the revision.
*How many embryos of BcdMM were analysed? The authors should also provide a table with all the values in SI as they have done for all the other reporters. *
We will add this data with the revision.
*The claims with eGFP::NLSBcdHD need to be supported by data from multiple embryos. Even if multiple ACF curves are obtained from one embryo, analysing only one embryo is not sufficient. This would clarify the fact that this reporter seems to be able to reproduce the mobility of Bcd in the nucleus. *
We agree and we are arranging to collect more data. This should be completed by the end of the summer.
*According to the methods, all reporters were expressed in a bcd null background, made with the bcd1 allele. This allele is also known as bcd085 and according to Driever and Nusslein-Volhard, 1988 (PMID: 3383244), this allele only causes an intermediate phenotype. This indicates that a truncated version of the protein probably still exists on the embryo. Do the conclusions obtained here still hold if a truncated version of the Bcd protein exists in addition to their reporters? *
We used the bcdE1 mutant, a null mutant of bcd. This was used by Gregor et al., Cell 2007 in their generation of the original Bcd::eGFP. We have also recently generated a more complete bcdKO mutation (Huang et al., eLife 2017). Our embryos do not have a clear phenotype that we can relate to the specific bcd- background used. Nonetheless, we agree it is an important point to be clear about the genetic background and we will clarify in the revised manuscript.
Minor comments: * * In line 45: "Morphogens are signalling molecules", the authors should consider removing the word "signalling" since not all morphogens are, especially the one being studied, Bicoid. * * In lines 80-81 (and also throughout the text): "We measure the Bcd dynamics at multiple locations along the embryo AP-axis", should be more accurate and changed to anterior and posterior of the embryo. Using "multiple locations along the AP axis" is ambiguous and not exact for what was done.
Yes, this is a fair comment. We have edited these sections in the current manuscript.
*Throughout the article, the authors refer multiple times to "modes for/of Bcd transport". Since they or others have not proven that Bcd is being transported, which would involve at least another factor, the authors should replace transport by movement, diffusion or a similar word with which they are comfortable. *
We have changed transport to movement wherever relevant in the text.
*Suggestion: The authors claim that the Bcd gradient is exponential up to 60% of embryo length. Would this information allow a more precise calculation of the gradient decay length in the exponential region than the 80-100µm stated on line 202? *
This is an interesting point, but our results suggest that the idea of the decay length is not so applicable in the posterior region. There, the Bcd dynamics are generally quicker, thereby increasing l. Of course, we cannot discount possible spatial variation in degradation. However, in previous work, our Bcd tandem reporter (which is sensitive to changes in degradation) did not reveal spatial variation in degradation.
In lines 258-259, the sentence "Further, Bcd binds to caudal mRNA, repressing its expression in the cytoplasm" should be improved to clarify the role of Bcd in caudal mRNA translation repression and references should be added. This should also be corrected in the following paragraph.
We will add the necessary corrections in the revision.
*In line 262, "mutations" should be singular since it corresponds to only one amino acid mutation. *
We have corrected this.
*Figure 4J needs to be corrected as the fractions of the slow and fast populations do not correspond to what is shown in Table 3. For example, Fslow fraction of AC is ~45% in the figure while it is 36% in Table 3. The problem occurs in all fractions. *
We are sorry there is a mislabelling in the corresponding figure. AN is in the place of AC. We have edited figure 4J and removed the mislabelling.
*In the discussion, in lines 379-380, "Given the changing fractions of the fast and slow populations in space, the interactions between the populations are likely non-linear". What is the reasoning for non-linearity and not interchangeability? *
If the interactions between the two populations were linear, then the fraction in each form would be constant across the embryo. Some degree of nonlinearity is required in order to have spatially varying relative populations.
*In line 432 caudal should be italicized. *
We have edited this.
*In the discussion, the authors conclude that "In the nucleus, the two populations can be largely (though not completely) explained by Bcd binding to DNA". The discussion would win by explaining all the possible options. * We will add the necessary changes in the discussion. This is also related to above reviewer comments.
