Endocytosis at the Drosophila blood–brain barrier as a function for sleep

[Editors’ note: a previous version of this study was rejected after peer review, but the authors submitted for reconsideration. The first decision letter after peer review is shown below.]

Thank you for submitting your work entitled "Endocytosis at the blood-brain barrier as a function for sleep" for consideration by eLife. Your article has been reviewed by a Senior Editor, a Reviewing Editor, and three reviewers. The following individuals involved in review of your submission have agreed to reveal their identity: Paul Taghert (Reviewer #3).

Our decision has been reached after consultation between the reviewers. Based on these discussions and the individual reviews below, we regret to inform you that your work will not be considered further for publication in eLife. However, we do feel the work could be made acceptable but only after the essential changes noted below are handled experimentally. Should you choose to submit a new version of this work, we will endeavor to have it reviewed by the same Board member and referees.

Summary:

This paper explores the functional contributions of the blood brain barrier (BBB) to sleep regulation in Drosophila. It uses a full range of genetic cellular and imaging methods to consider the hypothesis that endocytosis/exocytosis in BBB glia changes in ways that supports the role of these cells in helping resolve levels of metabolites that increase in relation to sleep-need. Further it provides evidence for the involvement of glial Rab11 in the cellular mechanism. Experimentally analyzing glial function in sleep, the work touches an aspect of brain physiology that has just begun to be explored but that has been proposed as one of the crucial functions of sleep. Thus, this work is a potentially significant contribution of interest to a general audience.

Though work is clearly described, thorough in most aspects and also several caveats are clearly acknowledged, there are issues that need to be clarified and conclusions that need to be strengthened in order to better establish the key conclusion of the paper that inhibition of endocytosis in glia increases sleep.

Essential revisions:

1) The authors nicely describe various difficulties experienced with genetic tools to perturb endocytosis in targeted glia (e.g. temperature-independent and potentially endocytosis-independent effects of shi-ts expression, as well as leaky GsGal4 expression). In addition, they report similar effects on sleep following expression of constitutively active and dominant negative forms of Rab11 as well as perturbation of Rabs that may not participate in endocytosis (Figure 4 and Figure 4—figure supplement 1). Thus, it is important to better establish sleep phenotypes arise from changes in endocytosis rather than non-specific glial malfunction. Some suggestions of additional experiments to support the hypothesised role of endocytosis are proposed below.

1a) To better characterise sleep-associated endocytosis, it would be useful to measure rates of endocytosis at 4-6 time points to define a daily cycle, not just two time points.

1b) Given the possibility that even adult-specific expression of mutant dynamin or Rab RNAi can have long-lasting changes in glial physiology or alterations in BBB permeability, it would be useful to test if these flies revert to normal sleep behaviour if allowed to recover for an appropriate period of time.

1c) To show that a different amount of sleep deprivation (more or less) produces a proportionate change in endocytosis (i.e., two or more points on the concentration-effect curve).

1d) To show bidirectionality of regulation and to control for potential contribution of stress rather than sleep drive, the authors should test whether endocytosis following more sleep is reduced (this may require orthogonal genetics: e.g. to drive sleep-inducing FB neurons).

2) Different Gal4 lines are used to target subsets of glia. The specificity of these lines needs to be clearly documented. The logic for using one or other for different experiments needs to be clarified. And at least one case, an additional Gal4 may need to be used.

2a) The description of Gal4 expression lines (Figure 3—figure supplement 2) should be expanded Critically, to demonstrate that each one the Gal4s used is indeed expressed preferentially in glia, the figure should include counter stains with glia or neuron-specific antibodies (Repo and Elav, respectively). Glial-specific expression would be also more convincing if the authors could test how well the expression pattern of these Gal4s (Rab9-Gal4 in particular) is blocked by Repo>Gal80. (More minor, it might help if an outline of the brain were drawn).

2b) The tubGal80.ts experiments utilize Rab9-Gal4. To more convincingly implicate the glial cells presumed to be targeted, these experiments should also be repeated with Moody-Gal4 (and possibly Repo-Gal4 as well).

3) Figure 1 shows that of Shi-ts expression in glia induces resistance to mechanical stimulation during sleep. Can a control experiment be done to rule out the possibility of a sensory defect that makes these flies unresponsive to mechanical stimulation? E.g. To test the responsiveness of awake Repo>Shi flies to mechanical stimulation? On this note, are the PG and SPG drivers expressed outside the brain in sensory structures?

Other concerns and suggestions:

4) Is it necessary to dissociate cells before adding Alexa647-dextran? Why not measure before dissociation as most cellular processes including endocytosis could be more robust in an intact brain. If it is simply to allow access to Alexa647-dextran, then could an alternative smaller endocytic tracer be tried?

5) Is resistance to mechanical stimulation following SD specific only to Shi, or also seen following endocytic Rab manipulation?

6) The shi-ts expression results suggest that sleep during SD happens at both temperatures, but nighttime sleep seems to elevated sooner in both males and females at 18 degrees, than in controls. Is this impression correct? and if so, is there an explanation? This difference (if reproducible) involves latencies and time of day differences. The fly sleep literature appears to point to an increasing fragmentation of cellular mechanisms between those that affect daytime versus nighttime sleep. Is there any basis to think or expect that the cell biological mechanisms (exo- and endocytosis) should be geared to daytime versus nighttime?

7) Figure 2C suggests that the effects of Shi-ts on sleep are not due to merely overexpression of Dynamin since the expression of Shi-wt does not have a significant effect. However, for Shi-wt, only total sleep is shown, whereas the main effect for Shi-ts at 18C is on day sleep. To exclude the possibility that a Shi-wt effect on sleep is masked when only total sleep is shown the figure should be revised to include data showing the effect of Shi-wt on daytime sleep.

8) Indeed, it would useful to consistently show data for total sleep and daytime sleep for all genotypes in the paper (these data must be available).

9) In Figure 3A, to exclude possible effects due to expression of Shi in neurons (in addition to expression in the BBB glia), the authors could show that these phenotypes remain when the expression in all glia is blocked using Repo>Gal80.

10) It would be valuable to test, with existing tools, to what extent surface glia are responsible for the phenotypes observed with the pan-glial driver, Repo. Does Shi expression in surface glia also cause resistance to mechanical sleep deprivation? Is the phenotype of either NP6293 or moody >Shi weaker than that of Repo>Shi and does combining NP6293 and moody Gal4s generate a phenotype comparable to that of Repo-Gal4? Why is the 9-137-Gal4 driver (SPG & PG) that is later used in Figure 5 (subsection “Endocytosis occurs during sleep and is influenced by prior wakefulness”) not used here?

11) Figure 3 localizing effect to surface glia: In Figure 3A – which UAS-shi was used? The effect does not appear to match that of repo-Gal4. The difference is no more than 100 min; whereas. in Figure 2A, the difference is >200 min. Is this lack of quantitative matching significant? Maybe it reflects the strength of the Gal4s but alternatively it could mean that other cells contribute. This should be discussed.

12) In the same figure – the lack of effect of astrocyte expression seems to be correlated with an unusually high value for the UAS control. Is there a reason to be concerned here?

13) Regarding EM images in Figure 4A – how abundant and frequent are these ultra-structural changes and how do they correlate with sleep phenotypes?

The observations themselves (amassed ring-like structures resembling microtubules, and a thinner PG layer) are only described to the level of positioning of two arrows in one of the micrographs. There should be some definition of the phenotypes and indication of prevalence, severity or quantification (either within or between animals). Were the suspected MTs coated or bridged as originally described in the paper cited? There no details provided in the methods regarding gender, time of day, age, or "n" value.

In addition, it would be useful to know if these are also seen following induction of wild-type dynamin, because WT-dynamin expression does not cause sleep phenotypes and there is the potential to examine how relevant these ultrastructural defects might be to the sleep effects observed. (Perhaps the cited EM paper has addressed this issue in neurons?) Are there any changes in membranes or vesicular structures that could potentially be connected to a block in endocytosis? What is the predicted EM phenotype associated with Rab11 CA expression?

14) Is the overall structural integrity of BBB, as shown in Figure 4B, also preserved when Rab11CA is expressed in glia?

15) In Figure 4C, the significance is determined based on a difference between DN and CA allele of each Rab protein. Is this the best criterion? Wouldn't it be better to compare each manipulation to the parental controls? In any event, it should be made clear why only Rab11 and not others is deemed to have crossed a significance threshold.

16) The overall logic that explains the link between the manipulations, endocytosis and sleep is confusing. Glial expression of Rab11CA increases sleep, similarly to Shi-ts. Do the authors propose that Rab11CA inhibits endocytosis, similarly to Shi-ts?

17) On similar lines, the data shown in Figure 4C seem to contradict the data in Figure 4D. In Figure 4D, Repo>Rab11CA causes increased sleep, compared to parental controls. Figure 4C, shows that using the RepoGS driver, Rab11 DN induces even more sleep than Rab11CA. Thus, both of these opposing manipulations cause increased sleep. Could it be that both manipulations simply make glial cells sick, and therefore, in both cases, sleep is increased due to malfunction of glia, and not due to specific changes in endocytosis? The possibility for a non-specific effect is supported by similar data in Figure 4—figure supplement 1C, where expression of either DN or CA versions of Rab27 and Rab30 produces exactly the same phenotype of increased sleep, unless the authors believe that these also work by affecting endocytosis. These issues should be explained and addressed in a revised manuscript.

18) In Figure 4—figure supplement 1B – are the effects of Rab3, Rab9 and Rab11 that were significant in Figure 4A (without RU486) still significant in the Figure 4—figure supplement 1B (with RU486)? The significance stars in Figure 4—figure supplement 1B are shown only for Rab1, Rab5, Rab27 and Rab30.

19) The apparent contradiction between Figure 1, Figure 2, Figure 3, Figure 4 and Figure 5 should be more clearly explained. Figure 5 shows that SD (which increases sleep pressure) causes increased endocytosis, but, Figure 1, Figure 2, Figure 3 and Figure 4, show that inhibiting endocytosis actually increases sleep, suggesting that endocytosis in BBB promotes wakefulness. An explanation that connects the two observations should be included.

20) Are the changes in endocytosis that correlate with sleep state specific only to surface glia? Are there changes in endocytosis in other populations of glial cells, as function of sleep?

Reviewer #1:

In this manuscript, Artiushin et al., aim to explore the role of glia endocytosis in sleep regulation focussing on a Drosophila model of the blood-brain barrier. The work is very interesting in principle as it touches an aspect of brain physiology that has been hardly explored so far but that has been proposed as one of the crucial functions of sleep.

The manuscript is well written in general and the experiments are well reported. The main weakness of the work is that in almost all experiments the genetic tools adopted did not behave as expected. The temperature sensitive form of shibire, (which is instrumental for experiments in Figure 1, Figure 2 and Figure 3) does not appear to provide any specific insight, possibly due to a temperature insensitive activation. The repoGENESwitch tool (instrumental for experiments in Figure 4) does not seem to be properly responsive when it comes to controlling activation.

All in all, the fact that the genetic tools employs are not behaving appropriately is a major weakness for the study as it is basically impossible to understand the exact specificity of the effect in terms of timing. For instance, it is impossible to exclude that this a developmental effect.

One possibility to reinforce the findings could be to adopt different genetic tools with greater reported specificity, such as the ones described in https://pubs.acs.org/doi/10.1021/acssynbio.7b00302

Presentation of data could be improved.

For instance:

# There is no reason to limit labelling of panels within figures. Please use more letters, ideally one per panel. It facilitates discussion.

# Avoid using barplots. Barplots are uninformative and should almost always be discouraged. Use plots that are more informative, giving more insights on the distribution (such as boxplot or violin plots)

# The experiment in Figure 3—figure supplement 2 needs some kind of co-staining confirmation

# Please quantify the observations collected using electron microscopy?

Reviewer #2:

Most of the manuscript (Figure 1, Figure 2, Figure 3 and Figure 4) describes how manipulating glia affects sleep. Overall, the behavioral phenotypes are strong. However, there are multiple issues with specificity of the methods, with data representation and with the interpretation of some of the results. Another question is – is it really so surprising and interesting that manipulating large numbers of glial cells has an effect on brain function, and sleep in particular?

The second part (Figure 5) is more interesting and promising, as it provides evidence for correlation between sleep/wake states and the rate of endocytosis in BBB glia. However, this part needs further development. Also, the link between this part and the rest of the manuscript seems a bit artificial, as they do not really support or complement each other well.

Specific comments:

1) The authors show in Figure 1 that expression of the temperature sensitive allele of dynamin, Shi-ts in glia induces resistance to mechanical sleep deprivation. The authors show that the basal wake activity of these flies is not affected. However, another interpretation of the data should be considered. These flies may be unresponsive to mechanical stimulation. The authors should test the responsiveness of awake Repo>Shi flies to mechanical stimulation. The authors should also check if Repo>Shi provides resistance to sleep deprivation induced by alternative methods (thermo-genetic). Finally, the authors test the effects on SD only with Shi, but do not do it with the rest of manipulations, presented later in the paper, such as expressing mutant Rab proteins. Are the effects on resistance to SD specific only to Shi, but not to other manipulations of endocytosis?

2) The authors observe strong effects for the temperature sensitive Shi allele even at the permissive temperature of 18C. This raises the question whether Shi is a good tool in this specific system. The main concern is that the observed phenotypes are mostly due to non-specific effects that make the glial cells sick. The authors should, at least, test if knocking down the endogenous Shi using RNAi produces a phenotype similar to expressing dominant negative Shi.

3) The authors claim in Figure 2C, that the effects of Shi-ts on sleep are not due to merely overexpression of Dynamin since the expression of Shi-wt does not have a significant effect. However, for Shi-wt, only total sleep is shown, whereas the main effect for Shi-ts at 18C is on day sleep. Could it be that the effect of Shi-wt on sleep is masked when only total sleep is shown? The authors should demonstrate the effect of Shi-wt on day sleep.

4) In Figure 3A, to exclude possible effects due to expression of Shi in neurons (in addition to expression in the BBB glia), the authors should show that these phenotypes remain when the expression in all glia is blocked, using Repo>Gal80.

5) To what extent are surface glia responsible for the phenotypes observed with the pan-glial driver, Repo? For instance, does Shi expression in surface glia also cause resistance to mechanical sleep deprivation? Is the phenotype of either NP6293 or moody >Shi weaker than that of Repo>Shi? Will combining both NP6293 and moody Gal4s (SPG & PG) generate a phenotype comparable to that of Repo-Gal4? Why don't the authors use here the 9-137-Gal4 driver (SPG & PG) that is later used in Figure 5 (subsection “Endocytosis occurs during sleep and is influenced by prior wakefulness”)?

6) The images in Figure 3—figure supplement 2 should be of better quality. The outline of the brain should be drawn. The authors also should demonstrate that each one the Gal4s used in this Figure is indeed expressed preferentially in glia by co-staining with glia or neuron-specific antibodies (Repo and Elav, respectively). The glia-specific expression would be also more convincing if the authors could show the expression pattern of these Gal4s (Rab9-Gal4 in particular) when the expression of the UAS-nGFP reporter is blocked in glia, using Repo>Gal80.

7) The EM images in Figure 4A – how abundant and frequent are these ultra-structural changes? Are these changes also observed upon the expression of Rab11CA? Also, could the authors detect any accumulation of vesicles that cannot be secreted due to expression of mutant Shi?

8) Is the overall structural integrity of BBB, as shown in Figure 4B, also preserved when Rab11CA is expressed in glia?

9) In Figure 4C, the significance is determined based on a difference between DN and CA allele of each Rab protein. Is this the best criterion? Wouldn't it be better to compare each manipulation to the parental controls? Also, what would be the effect of overexpressing WT versions of these Rab proteins?

10) The overall logic that explains the link between the manipulations, endocytosis and sleep is confusing. Glial expression of Rab11CA increases sleep, similarly to Shi-ts. Do the authors propose that Rab11CA inhibits endocytosis, similarly to Shi-ts?

Do they suggest that expression of constitutively active Rab11 is equivalent to the inhibition of vesicular trafficking? If so, what would be the effect of Rab11 RNAi? Would it produce an opposite phenotype (less sleep)? Repo>Rab11 DN could be useful, but it was lethal. The authors should try using tub-gal80ts, to achieve inducible expression of Rab11 DN. Also, does Repo>Rab11CA cause resistance to mechanical sleep deprivation, just like Shi-ts?

11) One of the major claims of this paper is that inhibition of endocytosis in glia (Shi-ts, Rab11CA) increases sleep. It is important to show that an opposite manipulation of increasing endocytosis actually reduces sleep. The data shown in Figure 4C is confusing and seems to contradict the data in Figure 4D. In Figure 4D, Repo>Rab11CA causes increased sleep, compared to parental controls. The interpretation is that this happens due to inhibition of endocytosis. However, in Figure 4C, using RepoGS driver, Rab11 DN induces even more sleep than Rab11CA. It seems that both of these opposing manipulations cause increased sleep, which is counter-intuitive. Could it be that both manipulations simply make glial cells sick, and therefore, in both cases, sleep is increased due to malfunction of glia, and not due to specific changes in endocytosis? The possibility for a non-specific effect is supported by similar data in Figure 4—figure supplement 1C, where expression of either DN or CA versions of Rab27 and Rab30 produces exactly the same phenotype of increased sleep.

12) In Figure 4—figure supplement 1B – are the effects of Rab3, Rab9 and Rab11 that were significant in Figure 4A (without RU486) still significant in the Figure 4—figure supplement 1B (with RU486)? The significance stars in Figure 4—figure supplement 1B are shown only for Rab1, Rab5, Rab27 and Rab30.

13) How do the authors explain the phenotypes caused by the expression of other Rabs, besides Rab11? Do they think that they all work by affecting endocytosis?

14) In Figure 5, the authors should demonstrate that their genetic manipulations (Shi-ts and Rab11CA) actually can inhibit endocytosis in the surface glia using the 10kd dextran absorption assay. Also, could it be that the changes they see after SD are in fact caused by physical damage to the BBB? They may test if the effects of SD on endocytosis are resolved once the flies are allowed few hours of recovery after SD. They can also test how thermo-genetic SD affects their assay. They should also do EM on BBB after SD.

15) There is an apparent contradiction between Figure 1, Figure 2, Figure 3Figure 4 and Figure 5. According to Figure 5, SD causes increased endocytosis. SD of course increases sleep pressure. But, in the Figure 1, Figure 2, Figure 3 and Figure 4Figures, the authors claim that inhibiting endocytosis actually increases sleep, suggesting that endocytosis in BBB promotes wakefulness. A possible solution to this paradox is that during normal sleep, there is an increase in endocytosis. This is important to support the function of sleep because increased endocytosis eventually helps to reduce sleep pressure. This is why inhibition of endocytosis promotes sleep – because in the absence of proper endocytosis, sleep quality is compromised, and sleep is then less effective in reducing the sleep pressure.

16) Are the changes in endocytosis that correlate with sleep state specific only to surface glia? The authors should have additional control in Figure 5 – test if there are any changes in endocytosis in other populations of glial cells, as function of sleep.

Reviewer #3:

This paper explores the functional contributions of the blood brain barrier (BBB) to sleep regulation in the model system Drosophila. It is a careful study that uses a full range of genetic cellular and imaging methods to consider the hypothesis that endocytosis/exocytosis in BBB glia changes in ways that supports the role of these cells in helping resolve levels of metabolites that increase in relation to sleep-need. Further it makes a strong case for the involvement of Rab11 in the cellular mechanism. The emerging involvement of glial compartments in the fundamentals of brain physiology (here sleep regulation) makes this work a significant contribution of interest to a general audience. The work is clearly described, thorough in most aspects of the analysis and discussed in a scholarly fashion. I have a few questions and concerns that may help improve the paper.

Shibere mis-expression and effects on sleep.

The paper wisely pays careful attention to the effects (and lack of effects) of temperature with a classic ts allele of dynamin. In addition, I also commend the use of different shi isoforms to help focus on the biologically (not technically) important results. I had one question about this dataset that involved, not amount of sleep, but its temporal patterning.

The results suggest that sleep during SD happens at both temperatures but I notice that nighttime sleep is elevated sooner in both males and females at 18 degrees, than in controls. Is this impression correct? and if so, is there an explanation? This difference (if reproducible) involves latencies and time of day differences. In my reading of the fly sleep literature, there is an increasing fragmentation of cellular mechanisms between those that affect daytime versus nighttime sleep. Is there any basis to think or expect that the cell biological mechanisms (exo- and endocytosis) should be geared to daytime versus nighttime?

Dynamin and MTs

The ultrastructural work is an effective supporting body of evidence to evaluate the effects of UAS-shi at permissive temperatures. However, the results – amassed ring-like structures resembling microtubules, and a thinner PG layer – were not well-described, beyond the positioning of two arrows in one of the micrographs. There was no clear definition of the phenotypes nor any indication of prevalence, severity or quantification (either within or between animals). Were the suspected MTs coated or bridged as originally described in the paper cited? There no details provided in the methods regarding gender, time of day, age, or "n" value. On a tangential (but relevant) note, was ultrastructure observed at only a single phase point? This issue is clearly beyond the scope of the current study.

Cell Specificity

Figure 3 localizing effect to surface glia;

3A – which UAS-shi was used?

- Male or female flies?

- The effect does not appear to match that of repo-Gal4. Difference is no more than 100 m; whereas. In Figure 2A, the difference is >200 min. Is this lack of quantitative matching significant? Maybe it reflects the strength of the Gal4s but alternatively it could mean that other cells contribute. I did not find any discussion of this point.

Rab involvement

The screens were careful, unbiased, quantitative and very large in scope. I commend the authors for determining that the Gs-Gal4 line was leaky but was somewhat confused by the overall definitions of hits. There was a set of hits with no RU486 (Rab 3, 5 and 9) and a different one with RU486 (Rab1, 5, 27 and 30). Yet at the end, only Rab11 is judged to have experimental support – I was not clear why (1) only Rab11 and not others crossed threshold. Also (2) whether Rab11 is a positive or negative regulator of sleep.

“As preliminary screening compared only experimental flies (RepoGS>UAS-Rab) with or without RU, the Rabs of interest were confirmed with Repo-GAL4, including the full complement of UAS and GAL4 controls.”

1) But only Rab 11 is shown, not Rab 3 or Rab9 – follow-up on Rabs 3 and 9 were neither shown nor mentioned,

“Expression of recycling-endosome associated Rab11 CA resulted in a robust sleep increase when driven in all glia (Figure 4D) and was significant for both CA lines.”

2) Paradoxically, Rab11 activity appears to increase sleep in the follow-up but in the preliminary large scale screen the DN isoforms of Rab11 produced significantly more sleep than did the CA isoforms – by my reading that means Rab11 in glia is a negative regulator. So, I'm not sure how to interpret the combined dataset.

Endocytosis

1) Why dissociate cells before adding Alexa647-dextran? Why not measure before dissociation? The results are fortunately very clear, but I would think cellular processes like endocytosis would be more robust in an intact brain.

2) Also it would be a stronger case if a different amount of SD produces a proportionate change in endocytosis (i.e., two points on the concentration-effect curve).

Also, would it would strengthen the case to measure endocytosis following more sleep (to control for potential contribution of stress to change); This would require orthogonal genetics to drive sleep-inducing FB neurons, so I suspect the genetics would be too complicated for a two-month period of additional study.