On 2015 Jan 22, Yuriy Pankratov commented:

This discussion could be more enlightening and even reach a consensus of some sort if our respected opponents, instead of making ungrounded accusations and avoiding inconvenient facts, tried to address the most serious issues, raised in our comments at PubMed Common and JNS website. These issues include: stark contradiction between the EGFP and LacZ expression phenotypes shown in Fujita et al. and data shown in previous publications (all of which went through rigorous peer review by the way); lack of direct evidence of notable impairment of synaptic transmission in dnSNARE mice and existence of clear evidence of the opposite; large pool of evidence supporting physiological role of astroglial exocytosis which does not rely on the dnSNARE mice at all. Neither paper itself nor Authors’ responses to comments (which basically repeats what was said in the article) address these issues.

Still, we think that some consensus might be found. Before going to that point, we would like to clarify points raised by our opponents in their last post. 1) For the sake of unbiased discussion, citing one paper showing a lack of VAMP2 expression in astrocytes (Schubert et al.2011) one might mention at least one paper from the large pool showing the opposite (Martineau et al 2013).

More importantly, one should not swap between quantitative and “all-or-none” kind of reasoning to one’s convenience. If we assume that level of astrocytic expression of VAMP2 of tenth of that in neurons is low enough to make VAMP2 non important for function of astrocyte, than we have to assume the existence of certain level of expression below which dnSNARE transgene will not significantly affect neuronal function as compared to astrocytes. OK, it may be not tenth but hundredth fraction, dose not matter.

We thankful to our opponents for bringing up an example of tetanus and botulinum toxins. Even theses deadliest toxins act in dose-dependent manner. Both on the levels of whole organism and single presynaptic terminals, smaller doses of these toxins (as compared to LD50 and IC50) have milder effects. So, it is very likely that effects of dnSNARE expression are dose-dependent (if not to believe in homeopathy, of course).

The same is applicable to the action of doxycycline, which is also dose-dependent. So one could not expect 100% inhibition of transgenes, especially at oral administration of Dox. To answer first part of opponents comment 2), the Figure 1O-R from Halassa et al. shows efficient, but incomplete suppression by Dox, rather than “leaky” EGFP expression. To what extent the same is applicable to Fig.2C of Fujita et al, let the reader to decide. Of course, non-complete suppression by Dox is a downside of tetO/tetA system but this can be easily remedied by comparing On-Dox and Off-Dox data.

2) Theoretically speaking, concern that “neurons express the dnSNARE transgene at all “ may be applicable to any glia-specific transgenic mice. One could not a priori expect an absolute specificity of expression of neuronal and glial genes, the data of Cahoy et al. 2008 are the good illustration. This, rather philosophical, question goes far beyond the current discussion. There is no molecular genetic tool to ensure 100% glial specificity. On practice, one could only expect to obtain a negligible (again, in relative sense) level of neuronal transgene expression and verify the lack of significant impact on neuronal function.

3) Regarding the putative “dramatic and unpredictable “ effects of neuronal dnSNARE expression, the TeNTx and BoNT give a good indication of what to expect. However, dnSNARE mice do not show any notable deficit of motor or respiratory function. On a level of synapses, there was no evidence of any significant decrease (not saying about complete inhibition) of vesicular release of main neurotransmitters (Pascual et al. 2005; Lalo et al. 2014). On contrary, our data show an impairment of signals triggered by activation of Ca2+-signalling selectively in astrocytes (Lalo et al. 2014; Rasooli-Nejad et al. 2014). Let it to the reader to decide, to what extent available functional data support the opponents’ notion that “synaptic transmission may directly be suppressed by dnSNARE expression in neurons “ and that “Even very low levels of expression of dnSNARE in neurons invalidate any conclusion based on this transgenic mouse “.

One might argue that dnSNARE transgene could be expressed only in the certain subset of neurons or in some specific brain region thus strongly affecting some specific function rather than causing general, milder, functional deficit. However, this is unlikely for the supposed basal leakiness of the tet-off system and further experiments would be required to identify such regions/neuronal subsets.

4) Addressing the second half of the point 2) – One can only wonder why, in 2012, already knowing that their results contradict to data presented by that time by several studies, our respected opponents did not contact authors of those publications to request mice from them? Again, one might only wonder why PCR data generated from 2 batches of mice have sample size of n = 3 – 4 (meaning 1-2 tissues per batch) ?

5) Regarding the intrinsic limitations of dnSNARE mice, anyone working with them is aware of fact that EGFP, LacZ, and dnSNARE genes were inserted independently. However, their expression is controlled by the same factors so their expression probabilities depend on the same set of parameters and therefore are not truly independent, from mathematical point of view. The correlation in expression of these transgenes is supported by the co-inheritance. Furthermore, data of Halassa et al. show that 97% of cells expressing the dnSNARE, also express EGFP. We would like to emphasize that the opposite - the presence of true mosaic expression pattern in dnSNARE mice, i.e. existence of number of individual cells expressing dnSNARE and not expressing EGFP and number of EGFP-only cells, has not be shown so far; Fig.3 from Fujita et. al 2014 does not show this either.

Thus, even assuming the leakiness of the “tet-off” system, one might expect probability of EGFP expression to be of the same order of magnitude as that of dnSNARE, this is also agrees with data of Fujita et al. So, in case of absence of EGFP expression in a large population of neurons, the presence of even small fraction of neurons expressing dnSNARE is very unlikely. From mathematical point of view, the probability of certain population of neurons to express only dnSNARE will fall exponentially with the expected size of population.

Finally, one could hardly deny the large difference in the phenotype of the cohort of dnSNARE mice, described by Fujita et al. and the cohort of mice used by other groups. The point of some consensus could be that in some, still unidentified conditions, the tetA/tetO system may suddenly became leaky, causing some level of expression GFAP-driven transgenes dnSNARE, EGFP and lacZ genes in neurons. So, in experiments with dnSNARE mice extra care should be done to verify the lack of neuronal dnSNARE expression. This can be done by showing the absence of surrogate reporters EGFP or lacZ in neuronal populations of interest combined with electrophysiological data showing the lack of deficit of synaptic neurotransmitter release. This could be a good practice for any glia-specific inducible transgene.

On 2015 Jan 13, Maiken Nedergaard commented:

With all respect to the commentator, the misleading posted arguments and evident lack of insight into the biology and construction of the dnSNARE mice underscores the danger of such unsolicited and unreviewed posting, not subject to peer review. That said, we have clarified several points below, and will leave it to the reader to evaluate our data as published in Fujita et al., J Neurosci, 2014 and to form an unbiased opinion.

1) Our immunolabeling data does not show that astrocytes fail to express VAMP2, nor did we ever make such a claim. Rather, our analysis documents that astrocytes express VAMP2 at much lower levels than neurons, both in vitro and in vivo. Besides our own data, this notion is supported by independent sets of data – transcriptional analysis showed that astrocytic expression of Vamp2 is a tenth that of neurons (Cahoy JD, 2008), while an immunohistochemical analysis showing that VAMP2 is enriched in presynaptic terminals, and is not detectable in astrocytes (Schubert V, 2011).

The dnSNARE mice express the 3 genes (EGFP, LacZ, and dnSNARE) independently of one another; their expression cassettes were injected in the oocyte as separate genes. Thus, a mosaic pattern of expression is to be expected, and that is what Fig. 3 documents. We certainly agree that astrocytes express all 3 transgenes at higher levels than neurons do; we documented precisely this point in Fig. 2D. However, the key element of our study is to demonstrate that leaky neuronal expression, and hence low levels of dnSNARE expression in neurons, may significantly impact synaptic transmission, since VAMP2 is essential for the fusion of synaptic vesicles with the presynaptic membrane.

Incidentally, the best example of the damage that may be wrought by any neuronal expression of dnSNARE is the acute mortality associated with nanogram quantities of botulinum toxin. Botulinum toxin’s actions are analogous to those of dnSNARE; the functional consequences of both derive from the necessity of the SNARE complex to the release of synaptic vesicles.

2) We will leave it to the reader to evaluate the immunohistochemical analysis, but will note that the leaky expression of EGFP was also displayed in Halassa MM, 2009, Fig. 1O-R. Unfortunately, EGFP expression has no predictive value for expression of the dnSNARE transcript, since as noted, the genes are independently expressed. We received the dnSNARE mice from Dr. McCarthy, rather than one of the groups using the mice, because Dr. McCarthy made the dnSNARE mice. We have analyzed two independent shipments (received in 2007 and 2012) and identified neuronal expression of EGFP in both sets of mice.

3) This comment reveals a basic misunderstanding of the inherent limitation of the dnSNARE mice. Direct inhibition of vesicular fusion in neurons is expected to interfere - in dramatic and unpredictable ways - with neuronal activity in the intact animals. It is not a matter of the relative expression of dnSNARE expression in neurons versus astrocytes. Even very low levels of expression of dnSNARE in neurons invalidate any conclusion based on this transgenic mouse. Moreover, we document in Fig. 2H that neurons express the dnSNARE transgene in the presence of doxycycline, and that transgene expression is increased after removal of doxycycline. In other words, the expression of the dnSNARE transgene is also controlled by doxycycline in neurons.

4) Again, it is not a matter of the relative leakiness of dnSNARE expression in neurons. The fact that neurons express the dnSNARE transgene at all is the fundamental concern. Interfering with synaptic release is one of the most powerful manipulations that may be executed upon a neuronal network.

5) Once again, the point of our study is not to show predominant neuronal dnSNARE expression. We document that cortical neurons do express the dnSNARE transgene, and that the expression of dnSNARE in neurons is regulated by doxycycline. These observations invalidate the use of dnSNARE transgenic mice in the study of neuroglia signaling: It is not possible to attribute change in neuronal activity to gliotransmitter release, since synaptic transmission may directly be suppressed by dnSNARE expression in neurons.

6) Unfortunately, exchange speaks as much to the deficiencies of the PubMed Comment mechanism as to the self-defensive but ultimately unsupportable arguments of the commentator, as it invites a Reddit-like forum, in which informed and uniformed commentary are admixed into an unenlightening whole.

Commented by Maiken Nedergaard, Takumi Fujita, Michael J. Chen

On 2015 Jan 05, Yuriy Pankratov commented:

Article by Fujita et al. aims to put under question an importance of SNARE-dependent vesicular gliotransmission basing on their observation of “widespread “ neuronal expression of dnSNARE transgene. However, there are several inconsistences and misinterpretations in the data which seriously undermines the main conclusion on the paper.

1) The immunocitochemical analysis (Figure 3A-D), which is supposed to show “widespread neuronal expression” of b-Gal and EGFP in dnSNARE mice actually gives merely an anecdotal evidence of their expression in minor population of neurons. Neither Figure 3 nor the description of results in the text provides any statistical data. In Fig.3A, white arrows are used to draw attention to the correlation of green VAMP2- and orange MAP2-staining in neurons which is a trivial result. However, careful inspection of these images reveals a number of green puncta not associated with orange staining which might be as well located in astrocytes. To rule this out, the quantitative data on correlation of VAMP2 with neuronal and glial markers are essential. The lack of VAMP2 staining in cultured astrocytes (Fig3) is in controversy with data of Pascual et al (2005). This fast was ignored by the Authors, as well as other evidences of VAMP2 expression in astrocytes (Parpura 1995, Maienschein 1999, Montana 2004, Martineau 2013).

Similarly, careful inspection of images shown in Fig 3C,D shows that most of cells stained for NeuN do not show b-Gal signal for and EGFP fluorescence; only few cells show co-localisation of the tetO transgenes with neuronal marker. As it is, Fig.3 does not strongly support the conclusion of “widespread neuronal expression” and I have a doubt that quantitative analysis of correlation of b-Gal and EGFP signal with neuronal and glial markers will show predominance of their neuronal localisation. Authors themselves admit this implicitly, saying about strong EGFP expression in astrocytes and “low to moderate level” of EGFP expression in neurons (p.16597). Also, there is no reproducibility in the shape of cells stained for NeuN across the four columns in Fig.3C which might be an indication for the lack of specificity of antibodies.

2) Talking about reproducibility, the immunocytochemistry and EFGP data in Fig.3 are in striking controversy with previous data shown by the P. Haydon’s group (Pascual 2005; Halassa e2009, Lalo 2014). We observed more than hundred of brain slices from dn-SNARE mice and dnSNARE-negative littermates and did not see any neuronal EGFP fluorescence like that one shown in Fig3. Also, the pattern on astroglial EGFP-signals shown in Figure 3C (mainly diffuse staining with rare bright somata) is different from previous reports, showing numerous bright somata with bright bushy processes. Comparing EGFP-images shown by Fujita et al. with previous reports, one might wonder whether these images were obtained in the same strain of mice at all. The possible explanations of the discrepancy and reported “leakiness” of GFAP-tTA promoter might be a founder effect in the cohort of mice used by Fujita et al. or influence of epigenetic factors. It was reported that level of DNA methylation can strongly affect the GFAP expression in neurons and astrocytes (Barresi 1999; Hatada PLoS One 2008; Takizawa Dev Cell 2001). Again, one might only wonder why Authors imported the dn-SNARE mice not from P. Haydon’s lab, but from Ken McCarthy’s who did not publish any major paper on dn-SNAREs apart from his earlier collaboration with P. Haydon.

3) Analysis of basal leakiness of tet-Off system in Figure 3E may be misleading since qPCR data on transgenes expression are compared to the “clear” wild-type mice. No wonder that such comparison showed large, statistically significant difference. However, in physiological and behavioural experiments data recorded in dnSNARE Dox-Off mice are usually compared to the data from dnSNARE Dox-On mice or from the dnSNARE-negative littermates (Pascual et al. 2005; Halassa et al. 2009; Lalo et al. 2014). When compared in such way, the data in Fig.3E shows a different picture. Firstly, expression of dnSNARE transgene in Dox-On and GFAP-tTA/dnSNARE negative mice is much less than in Dox-Off. Secondly, expression of dnSNARE transgene in GFAP-tTA/dnSNARE negative mice is much less than Lac-Z and EGFP transgenes. Also, one can see from Fig.3C that characteristic astrocytic EGFP staining patterns disappear in the Dox-On and GFAP-tTA/dnSNARE negative mice. Combined, these data suggest that putative leakiness of tet-Off system under GFAP promoter affects mainly basal neuronal expression of transgenes whereas level of glial dnSNARE expression is much less in non-dnSNARE mice as compared to dnSNARE-Dox Off. So, even if GFAP promoter can be leaky, it can be mitigated by using the dnSNARE-negative littermates as a control.

4) Putting aside putative explanations of problems with cohort of dn-SNARE mice used by Authors, the data shown in Figures 2 and 3 are in some agreement that neuronal dnSNARE expression does not prevail even in that particular cohort. As shown in Fig.2E and stated in the Discussion, the cortical neuronal dn-SNARE expression reaches only 32% of glial level in 8-day old mice which is hardly big news since it is widely known that GFAP promoter can also be active in neurons as this stage of development. Furthermore, level of neuronal dn-SNARE expression was much less in the adult age. Although Authors do not provide a direct comparison of neuronal and glial fractions, estimation could be done using neuronal marker Rbfox3 as a reference. Comparing Figs.2 G-G, one could estimate the fraction of dn-SNARE expressing neurons as 1/16, i.e 8%. Even taking 20% as an “optimistic” estimate, one cannot draw a definitive conclusion about predominantly neuronal expression of dn-SNARE transgene in the adult mice without direct evidence of impairment of neurotransmitter release. Such evidence could be provided by demonstrating the significant decrease in the frequency of mIPSCs or mEPSCs or at least the decrease in the baseline fEPSPs in the neurons of off-DOX mice.

5) So, the paper lacks crucial evidence of “the profound suppression of synaptic transmission in Off-Dox dnSNARE mice”. In contrast, previous works on dnSNARE mice showed up-regulation of excitatory synaptic transmission in hippocampus (Pascual 2005) and up-regulation of inhibitory synaptic transmission in the neocortex (Lalo 2014) of dnSNARE mice. Thus, the dnSNARE mice (at least used in the previous work) do not have a major deficit in presynaptic release of neurotransmitters, strongly arguing against abundant neuronal dnSNARE expression. This inconvenient fact was ignored.

Authors show that removal of Dox induces the suppression of the EEG signal amplitude but attribute this effect to the neuronal expression of dnSNARE. Since Authors do no provide a convincing evidence of predominant dnSNARE expression in neurons as compared to glia (and show some evidence of the opposite) and do not provide any direct evidence of impaired synaptic signalling in neurons, this conclusion is unconvincing if not incorrect. One could argue that suppression of the EEG signal might be due to profound astrocytic dnSNARE expression, which was also observed in the present paper, causing an impairment of gliotransmitter release and changes in glial modulation of synaptic transmission. Actually, the up-regulation of GABAergic synaptic transmission, that we observed in dnSNARE mice (Lalo 2014) is an good agreement with this hypothesis.

6) Lastly, I would like to stress that in the former article we provide a several lines of evidence of exocytotic gliotransmission which cannot be affected by putative neuronal expression of dnSNARE transgene at all, in particular “sniffer-cell” detection of ATP release from isolated astrocytes and perfusion of individual astrocytes in situ

On 2015 Jan 05, Yuriy Pankratov commented:

Article by Fujita et al. aims to put under question an importance of SNARE-dependent vesicular gliotransmission basing on their observation of “widespread “ neuronal expression of dnSNARE transgene. However, there are several inconsistences and misinterpretations in the data which seriously undermines the main conclusion on the paper.

1) The immunocitochemical analysis (Figure 3A-D), which is supposed to show “widespread neuronal expression” of b-Gal and EGFP in dnSNARE mice actually gives merely an anecdotal evidence of their expression in minor population of neurons. Neither Figure 3 nor the description of results in the text provides any statistical data. In Fig.3A, white arrows are used to draw attention to the correlation of green VAMP2- and orange MAP2-staining in neurons which is a trivial result. However, careful inspection of these images reveals a number of green puncta not associated with orange staining which might be as well located in astrocytes. To rule this out, the quantitative data on correlation of VAMP2 with neuronal and glial markers are essential. The lack of VAMP2 staining in cultured astrocytes (Fig3) is in controversy with data of Pascual et al (2005). This fast was ignored by the Authors, as well as other evidences of VAMP2 expression in astrocytes (Parpura 1995, Maienschein 1999, Montana 2004, Martineau 2013).

Similarly, careful inspection of images shown in Fig 3C,D shows that most of cells stained for NeuN do not show b-Gal signal for and EGFP fluorescence; only few cells show co-localisation of the tetO transgenes with neuronal marker. As it is, Fig.3 does not strongly support the conclusion of “widespread neuronal expression” and I have a doubt that quantitative analysis of correlation of b-Gal and EGFP signal with neuronal and glial markers will show predominance of their neuronal localisation. Authors themselves admit this implicitly, saying about strong EGFP expression in astrocytes and “low to moderate level” of EGFP expression in neurons (p.16597). Also, there is no reproducibility in the shape of cells stained for NeuN across the four columns in Fig.3C which might be an indication for the lack of specificity of antibodies.

2) Talking about reproducibility, the immunocytochemistry and EFGP data in Fig.3 are in striking controversy with previous data shown by the P. Haydon’s group (Pascual 2005; Halassa e2009, Lalo 2014). We observed more than hundred of brain slices from dn-SNARE mice and dnSNARE-negative littermates and did not see any neuronal EGFP fluorescence like that one shown in Fig3. Also, the pattern on astroglial EGFP-signals shown in Figure 3C (mainly diffuse staining with rare bright somata) is different from previous reports, showing numerous bright somata with bright bushy processes. Comparing EGFP-images shown by Fujita et al. with previous reports, one might wonder whether these images were obtained in the same strain of mice at all. The possible explanations of the discrepancy and reported “leakiness” of GFAP-tTA promoter might be a founder effect in the cohort of mice used by Fujita et al. or influence of epigenetic factors. It was reported that level of DNA methylation can strongly affect the GFAP expression in neurons and astrocytes (Barresi 1999; Hatada PLoS One 2008; Takizawa Dev Cell 2001). Again, one might only wonder why Authors imported the dn-SNARE mice not from P. Haydon’s lab, but from Ken McCarthy’s who did not publish any major paper on dn-SNAREs apart from his earlier collaboration with P. Haydon.

3) Analysis of basal leakiness of tet-Off system in Figure 3E may be misleading since qPCR data on transgenes expression are compared to the “clear” wild-type mice. No wonder that such comparison showed large, statistically significant difference. However, in physiological and behavioural experiments data recorded in dnSNARE Dox-Off mice are usually compared to the data from dnSNARE Dox-On mice or from the dnSNARE-negative littermates (Pascual et al. 2005; Halassa et al. 2009; Lalo et al. 2014). When compared in such way, the data in Fig.3E shows a different picture. Firstly, expression of dnSNARE transgene in Dox-On and GFAP-tTA/dnSNARE negative mice is much less than in Dox-Off. Secondly, expression of dnSNARE transgene in GFAP-tTA/dnSNARE negative mice is much less than Lac-Z and EGFP transgenes. Also, one can see from Fig.3C that characteristic astrocytic EGFP staining patterns disappear in the Dox-On and GFAP-tTA/dnSNARE negative mice. Combined, these data suggest that putative leakiness of tet-Off system under GFAP promoter affects mainly basal neuronal expression of transgenes whereas level of glial dnSNARE expression is much less in non-dnSNARE mice as compared to dnSNARE-Dox Off. So, even if GFAP promoter can be leaky, it can be mitigated by using the dnSNARE-negative littermates as a control.

4) Putting aside putative explanations of problems with cohort of dn-SNARE mice used by Authors, the data shown in Figures 2 and 3 are in some agreement that neuronal dnSNARE expression does not prevail even in that particular cohort. As shown in Fig.2E and stated in the Discussion, the cortical neuronal dn-SNARE expression reaches only 32% of glial level in 8-day old mice which is hardly big news since it is widely known that GFAP promoter can also be active in neurons as this stage of development. Furthermore, level of neuronal dn-SNARE expression was much less in the adult age. Although Authors do not provide a direct comparison of neuronal and glial fractions, estimation could be done using neuronal marker Rbfox3 as a reference. Comparing Figs.2 G-G, one could estimate the fraction of dn-SNARE expressing neurons as 1/16, i.e 8%. Even taking 20% as an “optimistic” estimate, one cannot draw a definitive conclusion about predominantly neuronal expression of dn-SNARE transgene in the adult mice without direct evidence of impairment of neurotransmitter release. Such evidence could be provided by demonstrating the significant decrease in the frequency of mIPSCs or mEPSCs or at least the decrease in the baseline fEPSPs in the neurons of off-DOX mice.

5) So, the paper lacks crucial evidence of “the profound suppression of synaptic transmission in Off-Dox dnSNARE mice”. In contrast, previous works on dnSNARE mice showed up-regulation of excitatory synaptic transmission in hippocampus (Pascual 2005) and up-regulation of inhibitory synaptic transmission in the neocortex (Lalo 2014) of dnSNARE mice. Thus, the dnSNARE mice (at least used in the previous work) do not have a major deficit in presynaptic release of neurotransmitters, strongly arguing against abundant neuronal dnSNARE expression. This inconvenient fact was ignored.

Authors show that removal of Dox induces the suppression of the EEG signal amplitude but attribute this effect to the neuronal expression of dnSNARE. Since Authors do no provide a convincing evidence of predominant dnSNARE expression in neurons as compared to glia (and show some evidence of the opposite) and do not provide any direct evidence of impaired synaptic signalling in neurons, this conclusion is unconvincing if not incorrect. One could argue that suppression of the EEG signal might be due to profound astrocytic dnSNARE expression, which was also observed in the present paper, causing an impairment of gliotransmitter release and changes in glial modulation of synaptic transmission. Actually, the up-regulation of GABAergic synaptic transmission, that we observed in dnSNARE mice (Lalo 2014) is an good agreement with this hypothesis.

6) Lastly, I would like to stress that in the former article we provide a several lines of evidence of exocytotic gliotransmission which cannot be affected by putative neuronal expression of dnSNARE transgene at all, in particular “sniffer-cell” detection of ATP release from isolated astrocytes and perfusion of individual astrocytes in situ