Author response:
The following is the authors’ response to the original reviews.
Public Reviews:
Reviewer #1 (Public review):
Summary:
Al Asafen and colleagues apply a set of scanning fluorescence correlation spectroscopic approaches (Raster Image Correlation Spectroscopy (RICS), cross-correlation RICS, and pair-correlation function spectroscopy) to address the nuclear-cytoplasmic kinetics of the Dorsal (Dl) transcription factor in early Drosophila embryos. The Toll/Dl system has long been appreciated to establish dorsal-ventral polarity of the embryo through Tolldependent control of Dl nuclear localization, and provides an example of a morphogen gradient produced with high enough precision to yield robust biophysical measurements of general transcription factor activity and function. By measuring GFP-tagged Dl protein, either in wild-type embryos or in mutant embryos with low/medium/high levels of Toll signaling, the authors report diffusivity of Dl in nuclear and cytoplasmic compartments of the embryo, as well as the fraction of mobile and immobile Dl, which can be correlated with DNA binding through cross-correlation RICS. A model is presented where Cactus/IkB is implicated in preventing Dl from binding to DNA.
Strengths:
The experiments on wild-type GFP-tagged Dorsal are performed well, are mostly reported well, and are interpreted fairly.
Weaknesses:
The discrepancy between experiment and theory as pertains to Michaelis-Menten kinetics is not fully motivated in the text, and could benefit from a more clear presentation. The experiments performed to distinguish between the contribution of Toll-dependent phosphorylation and Cactus interaction models for limiting Dorsal DNA binding are possibly confounded by the presence of wild-type, GFP-tagged Dorsal protein.
Thank you for your thoughtful feedback. Regarding the discrepancy between experiment and theory in relation to Michaelis-Menten kinetics, we recognize that our initial explanation may not have been explicit enough. Our intent was to illustrate that if DNA binding is a saturable process, then while the absolute concentration of Dl bound to DNA will increase with total Dl levels, the fraction of Dl bound to DNA will decrease. We used Michaelis-Menten kinetics only as a familiar example to convey this concept but did not intend to suggest that the system strictly follows Michaelis-Menten behavior. To clarify this point, we removed mention of Michaelis-Menten as an illustrative analogy and stuck specifically with discussing the system as “saturating.” This primarily affected text in the paragraph starting on Line 204, but also Lines 323-325.
Regarding the concern about potential confounding effects due to the presence of wildtype GFP-tagged Dorsal (Dl[wt]-GFP): we understand the importance of addressing this point more directly. Therefore, we have imaged the Dorsal-GFP gradient in embryos expressing the UAS-dl[S280P]-GFP or the UAS-dl[S317A]-GFP constructs in the absence of the BAC-recombineered Dl-GFP construct. In both cases, the dl mutants by themselves were not able to recapitulate enough of the Dl gradient to test our hypotheses. We have added this analysis to Supplemental Figure 4 and mentioned this figure on Lines 333-336 and 354-358. Furthermore, we explicitly mention that it is possible the reason why we failed to reject the null hypothesis in the Toll phosphorylation mutant case may be due to the additional copy of Dl[wt]-GFP (the BAC recombineered construct), with text added to Lines 343-345, 365-369 (Results) and 408-418 (Discussion).
Reviewer #2 (Public review):
Summary:
In this manuscript, Al Asafen, Clark et al., use fluorescence correlation spectroscopy (FCS) to quantitatively analyze the mobility of Dl along the DV axis of the early Drosophila embryo. Dl is essential for dorsal-ventral (DV) patterning and its gradient initiates the activation of several genes and thereby orchestrates the formation of the Drosophila body plan. While the mechanisms underlying the formation of the Dl gradient have been extensively studied by this group and others, there are some observations for which there is not yet a mechanistic explanation. For example, the peak of the Dl gradient grows continuously during nuclear cycles 10-14. This is likely due to Cact-dependent Dl diffusion and Dl binding to DNA. However, the biophysical parameters governing Dl nuclear dynamics that would support these claims have not been previously measured. In this work, the authors provide evidence that GFP-tagged Dl may be separated into a mobile pool and an immobile pool. Interestingly, the fraction of immobile Dl is position-dependent along the DV axis, revealing more binding to DNA in the ventral than in the dorsal nuclei. This is either due to higher binding affinity in ventral locations (due to Toll-dependent Dl phosphorylation) or to higher Dl-Cact binding in dorsal nuclei that would prevent Dl from binding to DNA. Using dl-mutant alleles, the authors support the latter hypothesis.
Strengths:
The manuscript is well written and their conclusions are convincingly supported by their methodology and analysis. As a quantitative study, the biophysical analysis seems rigorous, in general.
Although this is not the first study that employs FSC to investigate the dynamics of a morphogen, it further exemplifies how these quantitative tools can be used to uncover mechanistic aspects of morphogen dynamics during development. In particular, the manuscript reports novel biophysical parameters of Dl dynamics that will be helpful in future hypotheses-driven modeling studies.
Weaknesses:
In my opinion, the main weakness of the manuscript is that the main biological implication of the study, namely that the asymmetry in the fraction of immobile Dl is a result of nuclear Dl-Cact binding which prevents Dl from binding DNA (Figure 5), occurs in a region of the embryo where there is very little Dl anyways (Figure 1A, 5A). While it is interesting that the fraction of immobile Dl increases (just a little, but significantly) in dorsal nuclei in mutants expressing a form of Dl with reduced Cact binding it is unclear what is the biological impact of this effect in a location where Dl is nearly absent. As can be seen in Figure 3F, the fraction of immobile is unaffected in Dl-mutant forms with reduced DNA binding, because it is already very low. It is unlikely that Dl binding to Cact in dorsal nuclei would affect shuttling as well since the fraction is very low anyway.
We thank the reviewer for pointing out the places where we could strengthen our explanations. Here we first address the criticism, also raised by the other reviewer, that the fraction of immobile Dl increases only a small amount (Fig. 5A). [In our reply to the next comment, we address the question of biological implications.] We attempted to explain this small effect size in the manuscript; however, we understand that we could clarify further and, given the fact that eLife has no restraints on space, we added more explanation in the main text.
In essence, even though the effect was statistically significant, the effect size was small because the mutation was “diluted” by the presence of a wildtype Dl protein tagged with GFP. We were willing to deal with this dilution because the alternative was that, according to previous literature, without any wildtype Dl, no Dl gradient would be present in the reduced Toll phosphorylation mutants, and only a very weak Dl gradient (weakened on both ends) would be present in mutants that reduced Cact binding. We were confident that, with our quantitative approaches, we would be able to detect the diluted effect.
However, because both reviewers have criticized this diluted effect, in this resubmission, we have included analysis of GFP-tagged mutants without the presence of wildtype Dl protein. Unfortunately, these embryos lack a discernible Dl gradient and cannot be analyzed in such a way as to test the hypotheses that the mutants were generated for.
Even so, the effect of the Cact-binding mutant was strong enough that we were able to statistically distinguish it from embryos expressing only wildtype Dl-GFP, even with the dilution effect. On the other hand we have also included a caveat that our failure to statistically distinguish Toll phosphorylation mutants from wildtype may be due to the dilution effect. We now also explicitly state the concerns about a lack of a discernible Dl gradient and have included figures of full mutants in the supplement. See also our discussion of Reviewer 1’s similar comment.
While the authors have a very clear understanding of the biology of the Dl gradient, I feel that the manuscript is more written as a 'tools' paper (i.e., to exemplify how FSC methods and analysis can be used for biological discovery). This is ok, but I think that the authors should discuss further what are the biological implications of these findings other than the contribution to uncovering the biophysical parameters.
Here we underscore the biological implications of our discovery that Cact is present in the nucleus on the dorsal side. The reviewer mentioned that Cact in the nucleus on the dorsal side appears to have little overall effect, because this is the location of the embryo where there is very little Dl in the first place, which raises the question of whether this discovery is impactful.
While we previously used the final paragraph of the discussion to touch on the implications of this discovery, we acknowledge that we could have spent more time on the explanation. As such, we have expanded this final paragraph into two paragraphs. In the first of the two, we discuss in more detail the implications specifically of the Dl/Cact interactions in the dorsal-most nuclei, as understood by the results of this paper. In brief, knowing that Dl in the dorsal-most nuclei is bound by Cact results in an updated understanding of the Dl gradient, with increased dynamic range, robustness, and precision (but unknown shape).
In the second of the two paragraphs, we discuss this result in light of our recent work on imaging Cact in live embryos, in which we have shown that Cact is present in all nuclei at roughly uniform levels. Taken together, we suggest that it is possible that Cact is bound to Dl in all nuclei (not just the dorsal-most), which would allow us to estimate the shape of the overall Dl gradient by subtracting off the fluorescence that stems from Dl/Cact complex.
For example, I think that the implications of the rejected hypothesis (i.e., that Tolldependent Dl phosphorylation does not seem to have an impact on Dl binding affinities to DNA) are important and should be further discussed (even if no additional experiments are performed). What is then the role of Dl phosphorylation? Perhaps it could have an impact on patterning robustness in lateral regions. The authors should report in Figure 5 also what happens to the fraction of Dl bound to DNA in lateral regions in the reduced Cact binding and reduced Toll phosphorylation mutants.
We appreciate the reviewer’s suggestion that the rejection of the hypothesis that phosphorylation of Dl by Toll impacts Dl/DNA binding could be expanded upon further. For the role of Dl phosphorylation by Toll: we previously mentioned that this phosphorylation is known to enhance the nuclear import or retention of Dl, and that mutation of serine 317 to an alanine abolishes Toll-mediated phosphorylation of Dl, which results in embryos with no Dl gradient. We had also mentioned that phosphorylation of Dl is not known to affect its DNA binding, which is the hypothesis we sought to test by creating the dl[S317A]-GFP mutants. We did not image any mutants, or the UAS-dl[wt]-GFP control, in the lateral regions, for two reasons. First, this region is easily the smallest of the three regions, in terms of the percentage of the DV axis (see Fig. 1A). Second, because of the dilution effect, we knew the effect size would be small, and as such, we imaged only on the extreme ends of the gradient so that the most clear conclusion could be drawn about the effect that Toll phosphorylation might have on DNA binding of Dl.
The way that position along the DV axis is reported using the nuclear-cytoplasmic-ratio (NCR) in Figures 1-3 is not incorrect, but I wonder if it is the best way of doing it. The reason is that it spreads out a relatively small region of the embryo (the ventral-most locations) and shrinks a relatively large region of the embryo (lateral and dorsal regions), see Figure 1A. Perhaps reporting the NCR in log_2 units would be more appropriate.
We agree that there is some distortion of the relative spatial extents of the Dorsal gradient when NCR is used as an independent variable on a plot. However, we prefer the NCR on the horizontal axis because it is closer the functional variable (Dl concentration, rather than spatial location) for the properties we studied.
Recommendations for the authors:
Reviewer #1 (Recommendations for the authors):
I really enjoyed the first part of this paper and have only minor suggestions for improvement of the presentation. I am confused about the experimental approach for the final figure, distinguishing phosphorylation and cactus-dependent effects. I'll divide my comments between "First Part/General Suggestions", "Last Part", and finish with some minor typo observations.
The gist of the issues with the last part of the paper could boil down to insufficient detail/explanation of the section. The discrepancy with expectation with Michaelis-Menten kinetics is presented in a total of three sentences and is not necessarily obvious to the general readership of eLife. The mutants chosen to distinguish the phosphorylation and cactus mechanisms could be described more (why these? aren't other residues phosphorylated?) and possibly why also having wild-type GFP-Dl in the measurements isn't confounding. Since there is unlimited space in this journal, it may be advisable to use this space to fill out these rationales and ideas.
First part/General Suggestions:
(1) For the RICS data, (Figures 1 and 2) there is a nice correlation between WT NC ratio and the selected low/med/hi Dl activity mutants. More-or-less the median values in, say, Figure 1E-G are reflected in Figure 1H. However, with the ccRICS data (Figure 3), it looks like there is less correspondence between the range of fraction bound estimates in, for instance, "ventral" in Figure 3D and '10b' in Figure 3E. Can the authors comment on this? Should the reader be able to make this kind of comparison, or does something about data collection for the wt/NCR measurements preclude direct comparison of magnitudes with the panel of mutants? (imaging setup, laser power, etc)?
The reviewer is correct that there seems to be a discrepancy in the values of ψ between the wt embryos (ventral side) and the Toll10B embryos. It should be noted that the Toll10B embryos are not “ventral-like” in every way, in part because they have unknown activated Toll levels that might be above or below what is seen at the ventral midline in wildtype embryos, and in part because there is no DV gradient, and thus no shuttling in these embryos that would accumulate total Dorsal on the ventral midline. As such, comparisons between Toll10B embryos and the ventral side of wildtype embryos are not exactly one-toone, and we are more confident in comparing among the mutants in an allelic series. To address this question, we have added a sentence to the end of the second paragraph of the “Dorsal/DNA binding exhibits a spatial gradient” subsection of the Results (Lines 233235).
(2) Materials and methods: Mounting and imaging of Drosophila embryos: the authors cite the "488 nm laser intensity ranged from 0.5% to 3.0%..." The values presented here are not useful for the general reader or an individual looking to replicate these conditions, as emission power produced from such values will vary from instrument to instrument. It is standard in these cases to report an estimated laser power (measured in watts) for each laser line, and a clear description of how such measurements were made (stationary beam, under scanning conditions, with what detector, etc). These measurements are valuable and the authors are strongly encouraged to report such measurements for their setup.
We appreciate the reviewer’s suggestion and understand the importance of providing absolute laser power values for reproducibility. We have now included the laser power (in watts) for the laser lines on both microscopes used in this study. The revised text can be found in the Materials and Methods section, in the Lines 535-536 and 540.
(3) The presentation of the data in Figure 4 is difficult to understand. Are the kymographs (A lower) representing the entire length of the big white arrow in A upper? Or do the dashed lines indicate the x-axis limits of the kymograph? It is difficult to tell from the figure legend, where the dashed lines are described as "areas where Dl-GFP movement is measured out of the nucleus." I believe that the authors can make these measurements and that Figure 4B reflects properties of "movement" of Dl out of the nucleus, but how they get there from these data is not clear to this reader. Perhaps a cartoon explaining the green lines and the orange lines in the kymograph or tightening the legend would help.
We thank the reviewer for their feedback and understand the need for greater clarity in the text of the pCF section and in Figure 4. The widths of the kymographs in the lower panels correspond to the full widths of the images in the upper panels. The pCF measurements were taken at the y-coordinates at the level of the white arrows. The dashed vertical lines connecting the upper and lower panels illustrate two cases of locations along the x-axis of the image where Dl is crossing from inside a nucleus to outside. In the two illustrated cases, these crossings are accompanied by either zero Dl molecules being observed to cross the nuclear barrier (ventral image/kymograph on left) or delayed crossing of Dl molecules (dorsal image/kymograph on right). To address this concern, we have added more detail to the Fig. 4 legend and greatly expanded on a discussion of what pCF does in the text (the second and third paragraph of the section). We have also updated Fig. 4 to align with new explanations from the text: namely, describing the y-axis of the kymographs as Δt (instead of log(time)) and explicitly showing that the pair correlation is for pairs of pixels that are Δx = 6 pixels apart. Further details were also added to the relevant Methods section.
(4) DV position in the wild-type imaging experiments is operationally determined through measurement of the Dorsal NC ratio. This makes sense, but the strategy is buried in the first paragraph of the results, and not discussed in the M & M. For readers unfamiliar with imaging the fly embryo or the nuances of the Dl gradient, perhaps a sentence or two explaining that embryos were oriented randomly along the DV axis, and DV positions of the imaging region were estimated by measuring the Dl NC ratio.
We thank the reviewer for this helpful suggestion. To improve clarity, we have added a description of how DV position was determined to the Materials & Methods section (paragraph starting on Line 520). Specifically, we now state that embryos were randomly oriented along the DV axis and that we used the Dorsal NC ratio of intensity as a proxy for measuring the DV position in imaging experiments. Additionally, we have added a statement to the Results section to ensure that this strategy is more clearly introduced (Lines 143-144). We appreciate this recommendation, as it will help readers unfamiliar with fly embryo imaging better understand our approach.
(5) It would be nice to report the corresponding NC-ratio values for Dl in each of the mutant conditions, perhaps as a supplement to Figure 1. Currently, Figure 1H relies on the (admittedly well-established) properties of the three mutants, but it feels that an additional nice quantitative link in the data can be drawn out here. Do the authors see the strict correlation between the wt and mutant diffusivity measurements at specific NC-ratios?
We are hesitant to try to draw direct comparisons between the mutants and the behavior of the wildtype embryo at the corresponding NCR. This is because, in the context of these uniform mutants, the NCR is determined by a combination of at least three factors that we cannot measure or control for: the unknown strength of Toll signaling, the unknown capacity of Toll signaling (ie, the potential saturation of the cytoplasmic enzymes controlled by Toll signaling), and, most importantly, the lack of a shuttling mechanism that concentrates Dl on the ventral side of the embryo. As such, the NCR does not represent a continuous variable that transforms the behavior of one mutant into another (or from mutants into wt DV coordinates), as it does along the DV axis in wildtype embryo. This is why the mutant studies are presented as boxplots. At best, we were comfortable only in using the uniform mutants as an allelic series to produce gross trends. We have added a brief statement describing the shuttling caveat to the Results section (Lines 173-177).
(6) In the section related to Dl nuclear export, the language used to describe Dl kinetics is ambiguous. The term "movement" is used seemingly as a catch-all for nuclear-importexport as distinguished from diffusion. However, diffusion is also a form of movement. Could this section be reworked to explicitly distinguish nuclear import-export and diffusive movements?
We appreciate the reviewer’s suggestion and agree that the language used to describe Dl kinetics could be more precise. By way of explanation, the pCF analysis calculates the time scale on which Dl can exit the nucleus. pCF only gives a signal if it sees the same Dl molecule twice, at two different locations after some Δt amount of time has passed. Because of this, if a given Dl molecule in a ventral nucleus is being tracked, then that molecule has some probability that it is bound to DNA initially, which means it will take, on average, longer to exit the nucleus than a Dl molecule not initially bound to DNA. Therefore, on the ventral side, the time scale on which Dl exits the nucleus is longer than on the dorsal side (where DNA binding is not happening). This can be true even if the nuclear export rate constants are the same on the ventral side vs the dorsal side. As such, we were careful to choose language that did not imply that we were talking about a nuclear export rate constant. We have added this discussion to the end of the relevant Results section (Lines 308-315).
We have also revised this section to explicitly distinguish between the mobility associated with exiting the nucleus and diffusive movement, while still trying to distinguish between the time scale of exiting the nucleus vs the nuclear export rate. Specifically, we now refer to ‘time scale of nuclear export’ when discussing transport across the nuclear envelope and reserve the term ‘diffusion’ for passive intracellular movement. Furthermore, we have edited a sentence in this section (Lines 291-293) to describe the distinction we are making between the time scale measured by pCF and the time scale commonly associated with nuclear export (that is, the reciprocal of the rate constant). We hope this clarification improves readability and conceptual clarity.
Last Part:
(1) There is an undersold argument centered on Michaelis-Menten kinetics that needs to be explicitly presented, especially since it motivates the final experiments of the paper, which are challenging. In the two sections describing how the data do not adhere to expectations based on Michaelis-Menten Kinetics, the assertion that "the fraction of immoble Dl is expected to decrease with increasing nuclear total Dl concentration" is only intuitively true if the system is saturated. Is the system demonstrably saturated? Another interpretation of this would be that these results demonstrate that the system is likely not saturated. In any case, the authors need to devote some space in the introduction and/or results and/or discussion to fully motivate this point.
We agree that the reviewer has raised an important point: if the system is very far from saturation, then the fraction of immobile Dl is not expected to decrease with increasing nuclear total Dl concentration. But neither would it increase; it would instead stay flat. To correct this mistake, we have edited the sentences in question to acknowledge the farfrom-saturation scenario, saying “at best, [the fraction bound] remain[s] constant” (Line 209). As such, our original point, which is that in no case would the fraction immobile increase [unless something else is going on besides affinity-based binding to DNA], it still valid.
(2) Wouldn't any argument on the basis of Michaelis-Menten need to rely on the assumption that the system is at steady-state? Reeves 2012 concludes that during the times measured here, Dl does not reach a steady state. It would be good, in the context of the point above, for the authors to clarify how this impacts the expectations of saturation and the application of M/M kinetics.
We thank the reviewer for raising this important point. We apologize for not being clear on our points about M/M kinetics and would like to stress again that we are not claiming the system is has M/M kinetics. We appealed to M/M kinetics only as a simple, intuitive example of a saturating system to point out the difference between bound concentration vs bound fraction as functions of total concentration. We did this because previous feedback on our manuscript suggested that the difference between these two variables needed to be made clearer. Because this point seemed controversial with both reviewers, we removed all mention of M/M kinetics and simply refer to the system as “saturating.” For further explanation, see the first paragraph of our response to Reviewer 1’s “weaknesses” in the public review.
(3) It is not clear to me how the inclusion of wild-type, GFP-tagged dorsal in the experimental setup for Figure 5 is not confounding. For the S317 (phospho-) mutant, GFPtagged alleles of both phospho- and wild-type Dl are expressed. The reasoning is that not enough phospho-mutant Dl gets into the nucleus, and this makes it difficult to distinguish the dorsal from the ventral side of the embryo, so in a dl mutant background, there is expression of wt GFP-dl from a BAC, and nos>Gal4 driven expression of a GFP-tagged S317A mutant dl. The measurements show that on the ventral side of the embryo, there is no difference in the fraction of bound Dl. Couldn't this be predominantly binding of wildtype GFP-Dl? How is this interpretable? Wouldn't it be easier to perform these measurements in a Tl 10b background (or to cross in UAS>Tl[10b]) and for the only GFPtagged dl to be S317A? The same goes for the S234 mutant (could be done in the pelle mutant background).
We thank the reviewer for raising the point that the confounding effect of wildtype Dl makes it difficult to interpret the results from the 317A mutant. Under the circumstances of the experimental design, we can best conclude that, if the null hypothesis is incorrect, the effect size was too small to detect with our sample size. As such, we have modified our discussion of the results of this experiment to carefully explain this caveat (rather than confidently saying that Toll phosphorylation has no effect). For further explanation, see the second paragraph of our response to Reviewer 1’s “weaknesses” in the public review, as well as our response to the related question raised by Reviewer 2 in the public review.
Minor issues/typo stuff:
(1) This reviewer notes that the submitted materials contain neither line numbers nor page numbers.
We appreciate the reviewer’s feedback. We have now included line numbers and page numbers in the revised manuscript for easier reference.
(2) First paragraph of results: "We imaged small regions of the embryo..." The parenthetical statement only cites pixel size and directs the reader to the methods. Without the total number of pixels, the pixel size value does not clarify how "small" the imaged region is. Consider including the xy area, pixel dimensions, and pixel size here to assert the smallness of the imaged area.
We have added the requested information.
(3) Second paragraph, Introduction: "Dorsal, one of three (Drosophila) homologs to mammalian NF-kB" (Add Drosophila). Also, aren't these orthologs?
We have made these changes.
(4) Last sentence of last paragraph in the introduction: Kind of a throw-away sentence. Consider revising.
We thank the reviewer for making this point; the sentence was originally constructed to state that our quantitative measurements resulted in a biologically significant discovery. However, because Reviewer 2 also mentioned the question of biological significance, we have changed this final sentence to explicitly mention of what the biological significance is: namely, an understanding of the Dl gradient that has superior dynamic range, spatial range, robustness, and precision.
(5) Where is the median line in the S317A boxplot in Fig 5C?
The median line is at ψ = 0. We have added an explanation of this to the Figure legend.
(6) Materials & Methods: Fly transformation, typo: Drosophila embryos were injected with 0.5 µl of each pUAST construct..." The volume of an entire Drosophila embryo is less than 0.5 µl, please revise the units to reflect the value injected. Most likely an absolute volume unit was stated when rather a concentration of an injection solution, delivered at significantly smaller volumes was intended.
We thank the reviewer for catching this typo. It was intended to indicate a concentration of 0.5 ng/μL, and we have made the appropriate changes.
Reviewer #2 (Recommendations for the authors):
(1) Perhaps this has been described in a prior publication (if this is the case, please simply state this somewhere in the Methods section where Dl-GFP embryos are described), but since Dl-GFP embryos have one copy of endogenous dl and one copy of Dl-GFP, how do potential differences in tagged vs. non-tagged Dl interactions with DNA or Cact affect their findings?
The reviewer brings up a good point, and we acknowledge that any time a protein is tagged with GFP, the behavior of the protein may be affected. We have now explicitly added this caveat to our discussion in a new paragraph on Lines 420-429.
(2) In the Discussion section, the authors argue that a major implication of their findings is the possibility that Cact binds Dl in the nuclei would imply that the true (active) Dl gradient may be unknown unless the unbounded Dl is separated from the Dl/Cact (inactive form). While this is an interesting point, this idea is not supported by the findings of Figure 5B where there is no effect in the fraction of Dl bound to DNA in the reduced Cactus binding mutants. The authors should report what happens in lateral regions in Figure 5 because perhaps there is an effect there (see comment on this in the Public Review).
We thank the reviewer for the insight, as we did not directly discuss the implications of the middle column of Fig. 5B on our hypothesis. Indeed, our hypothesis is not supported by Fig. 5B; it is instead inconclusive (failure to reject H0). This is why we designed the second experiment (Fig. 5C) to test the Cactus hypothesis, because the effect size would be greater on the dorsal side.
Furthermore, as pointed out by both reviewers, the presence of wildtype Dl-GFP in these experiments is confounding. We have discussed this elsewhere in our rebuttal, but briefly, this problem resulted in needing larger effect sizes to detect a statistically significant difference between wt and the mutant populations. This was a necessary evil that we were willing to deal with in order to ensure the Dl gradient could be established so that the dorsal vs ventral sides would be distinguishable. We have added a fuller discussion of these issues to the relevant Results section (Lines 333-336, 343-345, 354-359, 365-369) and also the Discussion section (Lines 412-418), including underscoring the fact that, from a falsification standpoint, the results in Fig. 5B do not allow us to reject either null hypothesis, possibly due to the confounding effect of wildtype Dl. We appreciate the reviewer’s point about this, and believe the changes suggested by the reviewer have improved the manuscript.
On the other hand, we respectfully disagree with the reviewer that investigating either mutant in the lateral regions of the embryo would bear fruit. To the first approximation, it would be the average between the behaviors on the ventral vs. dorsal sides. For the S317A mutant, neither the ventral nor the dorsal side was conclusive in regards to our hypotheses. (Although we admit here that further investigation into why the S317A column in Fig. 5C was statistically different from wildtype, in the opposite direction from the S234P mutant, may be interesting in future work.) For the S234P mutant, the data were more conclusive on the side of the embryo where the effect size was expected to be large enough to detect a difference. In the lateral regions, the expectation would be that the effect size would be intermediate, which would make the interpretation of the results more difficult (i.e., more likely to be inconclusive). In contrast, as Fig. 5C is already conclusive, we are not confident there would be more information gained by imaging the lateral regions.
(3) Is Figure 5A a wild-type embryo? If so, I think that the labels are misleading or unclear. Also, is it the same image as in Figure 1A? If so, I suggest replacing this with a schematic since it does not add any new data.
We have eliminated the labels for the mutants and have added the following comment to the figure 5 legend “Same embryo as in Fig. 1A”.
(4) Also in Figure 5, I suggest using labels to indicate the schematics instead of simply using their location. You could use 5A', 5A' and 5A', for example.
We have made the suggested changes.
(5) The use of some technical labels makes some figures difficult to read. I suggest using more simple labels for mutants in Figure 3F (replace R063C) or Figure 5B, C (replace S234P and S317A).
We have made changes to Fig. 3F, Fig. 5B,C, and the corresponding places in the figure legends. We have labeled R063C as ↓DNA, S317A as ↓Toll, and S234P as ↓Cact.
(6) I suggest reporting p-values consistently. For example, in Figure 4B, they use one or two asterisks to denote p-values less than 0.07 and 0.05, respectively, which is somehow arbitrary and unconventional. Why not report the actual values as in Figure 5C, for example? (By the way, I would report in Figure 5B the actual p-values as well, since a nonsignificant value is also reported in Figure 5C. Also in Figure 5C, report values in the same notation (decimal or scientific), i.e., either put 0.005 as 5x10^-3 or 10^-3 as 0.001).
We have made the suggested changes.
