Astroglial CD38 regulates social memory and synapse formation through SPARCL1 in the medial prefrontal cortex

  1. Tsuyoshi Hattori
  2. Stanislav M Cherepanov
  3. Ryo Sakaga
  4. Jureepon Roboon
  5. Dinh Thi Nguyen
  6. Hiroshi Ishii
  7. Mika Takarada-Iemata
  8. Takumi Nishiuchi
  9. Takayuki Kannon
  10. Kazuyoshi Hosomichi
  11. Atsushi Tajima
  12. Yasuhiko Yamamoto
  13. Hiroshi Okamoto
  14. Akira Sugawara
  15. Haruhiro Higashida
  16. Osamu Hori

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Abstract

Social behavior is essential for the health, survival and reproduction of animals, yet the role of astrocytes in social behavior is largely unknown. CD38 is critical for social behaviors by regulating oxytocin release from hypothalamic neurons. On the other hand, CD38 is most abundantly expressed in astrocytes especially in the postnatal cortex, and is important for astroglial development. Here, we demonstrate that astroglial CD38 plays a pivotal role in the social behavior. Selective deletion of CD38 in postnatal astrocytes, but not in adult astrocytes, specifically impaired social memory without any other behavioral abnormalities. Morphological analysis revealed reductions in spine numbers, mature spines and excitatory synapse numbers in the pyramidal neurons of the medial prefrontal cortex (mPFC) due to deletion of astroglial CD38 in the postnatal brain. Astrocyte-conditioned medium (ACM) of CD38 KO astrocytes reduced synaptogenesis of cortical neurons by reducing extracellular SPARCL1, a synaptogenic protein. Finally, the release of SPARCL1 from astrocytes is regulated by CD38/cADPR/calcium signaling. Our data indicate that astroglial CD38 developmentally regulates social memory and neural circuit formation in the developing brain by promoting synaptogenesis through SPARCL1.

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    Reply to the reviewers

    'The authors do not wish to provide a response at this time.'

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    Referee #3

    Evidence, reproducibility and clarity

    Hattori et al. assessed the role of astrocytic CD38 by generating astrocyte-specific conditional CD38 knockout mice and discovered defects in social memory, synapse, and spine density in the mPFC. They further showed that conditioned media from CD38-deficient astrocytes are defective in promoting synapse formation. A known astrocyte-derived synapse promoting protein, Sparcl1, is reduced in the conditioned medium from CD38 KO astrocytes and pharmacological experiments suggest that CD38 and calcium signaling regulates Sparcl1 secretion by astrocytes.

    The discoveries are novel and important and will be of broad interest to readers. However, the following concerns need to be addressed to improve the manuscript.

    Major comments:

    1. It's unclear if experiments were conducted while the experimenters are blinded to the genotype of the mice. This is essential for behavior tests.
    2. Hippocampus is also important for memory formation. Do synapse and spine densities change in the hippocampus?
    3. The proposed model of CD38 inducing Ryr3-mediated calcium release from internal stores is interesting. However, the Barres database showed that Ryr3 is not expressed by mouse astrocytes. Could the authors demonstrate the presence of Ryr3? That's a key link in their model that hasn't been demonstrated to operate in astrocytes.
    4. The authors demonstrated reduced synapse and spine density in mPFC. Interestingly, a battery of behavior tests showed no defect, except for the social memory test. Reducing synapses in mPFC should affect a range of behaviors. Why that is not the case here?
    5. The authors only tested very short-term memory (30 minutes delay). Does CD38 regulate long-term memory? It would be important to know but I realize that a single paper cannot address all questions and therefore do not think addressing this point is a prerequisite for publication.

    Minor comments:

    1. Fig. 2F, multiple comparison adjustment is needed.
    2. Fig. 3A, scale bar is 10 micrometers, not millimeters
    3. Fig. 4C, D, it is unclear if the quantification is normalized to actin loading control. BDNF levels appear lower in KO, though not significantly different, raising the question of whether an equal amount of samples was loaded.
    4. Need to validate whether CD38 levels are reduced in P42-46-injected adult knockout before concluding that CD38 is required only during development

    Significance

    Astrocytic contribution to social memory has not been reported. This study is thus the first report on the role of astrocytes in social memory. Their discovery of CD38-regulation of Sparcl1 release is also novel and important for synapse formation, although more evidence is needed to support this point (see major comments above). This study will be of broad interest to neuroscientists. I have expertise in cellular and molecular neurobiology and can evaluate all parts of the paper.

    Referees cross-commenting

    I agree with the issues that the other reviewers pointed out, especially the need for improving data reporting and consistency/accuracy. Overall, I think this manuscript has potential and the issues are addressable.

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    Referee #2

    Evidence, reproducibility and clarity

    Summary

    In their manuscript, Hattori et al., put forward evidence that the knock-out of CD38 expression in astrocytes at approximately post-natal day 10 (referred to as CD38 AS-cKO P10) leads to a specific deficit in social memory in adult mice, while other types of memory remain unaltered. Using immunohistochemistry (IHC), the authors found a reduced number of excitatory synapses in the medial prefrontal cortex (mPFC) of CD38 AS-cKO P10 mice. Switching to in vitro primary cell culture models, the authors identify the astrocyte secreted protein SPARCL1 as a relevant synaptogenic factor. Using pharmacological dissection of relevant signaling pathways, Hattori et al., propose that cADPR formation and calcium released from intracellular stores, is essential for SPARCL1 secretion from astrocytes. Finally, the authors analyzed the transcriptome of primary CD38 KO astrocytes using bulk mRNA sequencing, and found that genes related to calcium signaling were downregulated in these cells.

    Major commments:

    • Are the key conclusions convincing?
      1. From a global perspective, the multiple lines of evidence provided by the authors strongly suggest that expression of CD38 in astrocytes is important for synaptogenesis in the mPFC of P10 mice, with ablation of CD38 and reduced synapse formation leading to social memory deficits at P70. However, the data concerning the role of astrocyte-secreted SPARCL1 is not particularly strong: further experiments are needed to support this claim (see below).
    • Are the claims preliminary or speculative?
      1. As it stands, there is no proof that the claimed astrocyte-specific deletion of CD38 is actually astrocyte specific. This evidence is crucial: without it the reported effects could be due to non-specific CD38 knock-out in other CNS cells. In this respect, the Western Blot in Supplementary Figure 1A does not provide information on astrocyte-specific deletion, merely that CD38 was globally reduced in the mPFC. Interestingly, the authors have previously published data (Hattori et al., 2017, 10.1002/glia.23139) showing that CD38 expression is mostly astrocyte-specific, peaking at p14, which coincides with the peak period of synaptogenesis. The degree of CD38 heterogeneity is also an issue that I think the authors need to consider. Do they information on this? Is CD38 expressed in every astrocyte of the CNS, or are there some astrocytes that are CD38 negative at P14? Is the mPFC a region specifically enriched in CD38 positive astrocytes and does this explain the observed behavioral deficit? I think if this is known, the authors should mention it in the "Introduction" or "Discussion". If this is not known, maybe the authors could provide data addressing the issue.
      2. I think the authors should take more caution in claiming that SPARCL1 is the main factor secreted through the CD38 signaling pathway and responsible for increased synaptogenesis. This is for several reasons, all centered on data displayed in Figure 4 and Supplementary Figure 6:
        • a) Western Blot (WB) data: The "Materials and Methods" section for WB does not indicate how protein loading and transfer efficiency were controlled for. Normalizing to β-Actin levels is an acceptable way to control for loading and transfer efficiency when using cell lysates. However, in the absence of such an abundant structural protein in conditioned media it is unclear how loading and transfer was controlled for under these conditions. Do the authors normalized the CD 38 KO AS ACM data by expressing protein levels relative to those from WT AS ACM? Is BDNF being used as a control, based on proteomics data? If so, why is proteomics data not given in the manuscript and why is this control not shown for all ACM blots? I realize that (quantitative) blotting using ACM is difficult, but I am also not convinced that the methodology used is sufficiently rigorous. Simple steps to give confidence would be Coomassie staining of gels both before and after membrane transfer, to show that i) the total protein amount loaded was the same in each lane of the gel and ii) the transfer to the nitrocellulose membrane was complete. In addition, Ponceau S staining of the nitrocellulose membrane should also have been performed and displayed, to show (roughly) equal amounts of protein were transferred for each lane. In summary, the WB data quantification needs to be better controlled. The values of the Y axis in these graphs (and throughout the manuscript) are simply too small to be read properly. Finally, I want to highlight the general lack of precision regarding the nature of the replication unit (the "n"). For example, the legend of Figure4C-D states "n = 6", but we have no idea if these are 6 independent primary cultures originating from 6 mice, 6 independent cultures from the same mouse, 6 repeats of the Western Blot using the same sample etc. This issue is valid for the whole manuscript: in my opinion, the authors should be more much careful when it comes to these crucial elements of scientific reporting.
        • b) While the data hint at an important role of SPARCL1 in synapse formation, when the authors tested if ACM from CD38 KO astrocytes supplemented with exogenous SPARCL1 could rescue synapse formation, the effect was incomplete, with only a trend to an increase in synapse number (Figure 4J-K). Perhaps the authors simply forgot to indicate the statistical significance of differences between the experimental groups (Figure 4K)? However, if there really were no statistically significant differences observed, the authors should reduce the strength of their conclusions regarding SPARCL1. This protein may well be pro-synaptogenic but, as it stands, other factors could well be in play. Perhaps the authors should have tried higher concentrations of SPARCL1 to further boost synaptogenesis? In this respect, the SPARCL1 knockdown (KD) experiment in Supplementary Figure 6B-D is an important addition, but should be supplemented by rescue with an siRNA-resistant recombinant SPARCL1? If SPARCL1 is a major player in synaptogenesis, the prediction is that synapse numbers would be close to wild type levels with this approach.
        • c) In my opinion, there are also issues with the data displayed in Figure 4H-I. The authors want to convince the reader that SPARCL1 is mostly an astrocytic protein using immunohistochemistry on mouse mPFC sections, co-labelled with antibodies against neuronal and astrocytic markers. In these panels, we are presented with images showing a few cells, in which it seems SPARCL1 is absent from NeuN positive cells, present in WT astrocytes and reduced in CD38 AS-cKO P10 astrocytes. However, the numbers of cell counted and lack of quantification severely impact on the strength of this conclusion. In my opinion, the authors should have quantified their IHC data by counting cells and establishing the ratios of SPARCL1 positive over NeuN or S100β positive cells, in both control and CD38 AS-cKO P10 animals. This experiment would provide critical information that the conditional gene targeting strategy is robust. The authors should also consider quantifying the intensity of the SPARCL1 signal in astrocytes. This is recommended as the image displayed in Figure 4I for the CD38 AS-cKO is problematic: are the authors really claiming that the reduction in SPARCL1 expression following cKO of CD38 in astrocytes is at best only partial? Is 11 days between the first tamoxifen injection and tissue fixation actually sufficient to allow for CD38 turnover? With low levels of protein turnover, the possibility exists that residual levels of CD38 are still sufficient to impact SPARCL1 levels. What would happen if there is a greater interval between tamoxifen administration and tissue recovery? Would levels of synaptogenesis be further reduced? Is this an issue of production versus secretion or a combination of factors?
      3. The heatmap (Figure 5E-F) is simply too small to interpret. The color choice is also not accessible for colorblind readers. The authors might consider displaying this heatmap in a separate figure. The authors should also provide a supplementary table where all the genes detected are listed along with their respective counts. Furthermore, it is surprising that the authors only found genes being downregulated in CD 38 KO astrocytes. Were they really no genes up-regulated? The authors might also want to indicate the genes belong to each of the ontological categories listed in Figure 5F. On p. 11, Figure 5E: The authors should indicate in the main text they performed bulk RNA-sequencing and not another type of RNA sequencing (like single cell RNA sequencing for instance). The authors indicate n = 2 but we have no indications of the nature of the replicate (also see earlier comments). Please amend.
    • Are additional experiments necessary? I think supplementary experiments are essential to support the claims of the paper. Most are described in the section above, but to summarize:
      1. Show data to prove that the CD38 AS-cKOP10 model is astrocyte-specific and leads to a total loss of CD38 in these cells.
      2. WB data: The issue of protein loading and transfer efficiency should be dealt with. Quantifications should be revisited.
      3. The authors should quantitatively analyze the different IHC performed in Figure 4H-I.
      4. The authors should provide more information on their RNA sequencing data: list of genes detected with their FPKM values etc. The authors should display the RNA sequencing data in a separate figure, allowing the heatmap to be enlarged.
      5. LC-MS/MS data: the authors should provide the list of all the proteins they identified in their LC-MS/MS experiment. As a supplementary table for instance? The majority of these experiments should be able to be performed with pre-existing samples/tissue slices. If not, the experimental pipeline necessary exits and these supporting experiments should not be too burdensome.
    • Data and methods presentation Methods: The authors need to work on this aspect of the manuscript. Most of the important details are already described, but some crucial ones are missing, while the phrasing used to describe methods is sometimes misleading. I will give some examples here, but this is not an exhaustive list. The fact that the manuscript is riddled with small mistakes, inconsistencies and/or oversights makes it difficult to read and creates a negative impression. The whole manuscript would benefit from a thorough proof-reading, preferably by a native speaker.
      1. in the "Immunohistochemistry and Synaptic Puncta Analysis" section on p. 21-22, we have no indication of which antibodies against "GFAP, NDRG2, VGlut1, PSD95, S100β, NenN(?) and SPARCL1" were used. It is standard practice to indicate the company, product number and lot number. The authors must also indicate the dilution at which they use these antibodies. On p.22, the authors write the cells were incubated with "Alexa- or Cy3-conjugated secondary antibodies". The excitation wavelengths of the Alexa dyes used need to be given.
      2. The authors need to provide more details on the microscope they used. Merely writing "using a 63× lens on a fluorescence microscope" (p.23) is insufficient.
      3. In the "LC-MS/MS" method the authors wrote: "Briefly, these proteins were reduced, alkylated, and digested by trypsin". I think that in the reduction and alkylation steps, chemicals other than trypsin were actually used. This sentence should be modified to reflect this.
      4. p.19: "uM" is written when the authors very likely mean "µM". Please check the whole manuscript for repeat examples. I know this is often lab "short-hand", but it should be avoided in scientific publications.
      5. The authors should be careful when describing their data to always indicate whether they referring to experiments performed using cultured astrocytes or not. As it stands, the text is confusing: for instance, when describing RNA-sequencing data in Figure 5, the main text appears to indicate that these astrocytes were acutely isolated from adult mice, when in fact they were obtained from primary cultures. Given concerns in the literature about potential differences between acutely isolated and cultured astrocytes (Foo et al., Neuron, 2011), this is essential. Data presentation: The figures appear to have been produced in a rush - and almost have a "screenshot" feel to them. This is not a scientific issue per se, but does impact on the overall impression given by the manuscript. The following is a non-exhaustive list of issues with the figures. I list the major ones that the authors should correct.
      6. Almost all Y axis labels are too small. The authors should comply to the basic journal requirements in terms of font sizes. Some axes do not end on a tick (e.g. Figure 3R). This is not dramatic, but should be corrected. Globally, the authors need to display bigger bar plots - most of them are extremely hard to read. Labeling should also be checked: Figure 4K, the Y axis label indicates values displayed are in %, when I think the axis graduation displays ratio values. Some of the IHC pictures are also too small to be easily interpreted.
      7. The heatmap in Figure 5E is impossible to read and, as such, has little or no value for the manuscript.
      8. Scale bars: where is the scale bar in Figure 2A? Figure 3A-H: Is the scale bar really representing 10 millimeters? Supplementary Figure 3A: scale bar is missing. Please check for similar issues throughout the manuscript.
      9. Figure Legends are problematic, and often contain incorrect or incomplete information. Examples include: Supplementary Figure 1: The description of panels J, L and N appears to be missing. Please also use the Greek letter beta and not 'b' for S100β. Supplementary Figure 5: I think the term "KO" is missing after CD 38 in the legend title. Figure 3: why state that nuclei were counterstained with DAPI in Figure 3P,Q, when this precision is not given for panels Figure 3A-H? Figure 3A-H: If the authors choose to explicitly state PSD95 is a post-synaptic marker, why not indicate that VGlut1 is a pre-synaptic marker? Same issue in Supplementary Figure 4.
      10. There are multiple instances of panels being wrongly referred to in the main text. On p.10, Figure 4H is referenced, when I think the authors mean Figure 4I; on p.10, Figure 4I-J are referred to when the authors clearly describe data found in Figure 4J-K. These types of mistakes are problematic and recur throughout the manuscript.
    • Statistical analysis As mentioned above, the exact nature of the replicates is often not stated, when the "n" number is indicated. The authors must correct this issue and give the information either at the appropriate point in the main text or in the figure legend.

    The authors should also be more consistent in the way they indicate which statistical tests were performed. This should also be indicated either at the appropriate point in the main text or in the figure legend. Furthermore, care should be taken to ensure statistics are presented in an appropriate manner: at the end of legend for Figure 4, it is indicated #p < 0.05 vs. CD38 KO ACM. This hashtag symbol is completely absent from the figure. In Figure 4F-G, the lack of statistical symbols seems to indicate no statistical tests were performed on these data, when the legend covering these panels states "*p < 0.05 versus P70", indicating some tests were done. We cannot interpret this panel without knowing which comparisons were done exactly and which were significant.

    In the "Materials and Methods", the authors give no indication that the assumptions of the statistical test they used were met (normality of data distribution for t-tests, homogeneity of variances for ANOVA...). This needs to be checked, and if not met, appropriate non-parametric tests should be used instead.

    Minor commments:

    • Specific experimental issues that are easily addressable. Most of the experimental issues that need to be addressed are given in previous sections and should be easily addressable.
    • Citation of previous studies? Adequate
    • Clarity and accuracy of text and figures There are issues with the clarity and accuracy of text and figures - which are described above. The text is also often problematic in its phrasing and other, more fundamental aspects. For instance, the authors spent a considerable amount of time speaking about the role of oxytocin, when they only performed one measurement of oxytocin levels in mice.
    • Suggestions to improve the presentation of data and conclusions? All my suggestions to improve the presentation of data can found in previous sections. As for improving the authors presentation of their conclusions, the authors should make a considerable re-drafting effort, particularly for the "Discussion", which lacks clarity in how supporting arguments are built and presented. For example, on p.13, I am confused with the argument made by the authors. Their data are focused on synapses onto pyramidal neurons of the mPFC, but here the discussion states that the behavioral phenotype they observed in CD38 AS-cKOP10 might be explained by a lack of mPFC neurons synapsing onto neurons in the Nucleus Accumbens (assuming that "NAc" really refers to this brain region, as the definition is missing from the text). I think the authors should make it clear if this is their interpretation of their own result, which essentially renders their focus on mPFC pointless, or a speculation on possible other mechanisms that could also explain their behavioral results. Personally, given the data shown, I believe the authors should focus on explaining how their data in mPFC might explain the behavioral output observed. The authors could also provide perspectives on how the hypothesis laid down in this paragraph would be tested. When the authors write on p.14 "We identified SPARCL1 as a potential molecule for synapse formation in cortical neurons" why use the word "potential"? Does this mean the authors consider their data on SPARCL1 (one of the key messages of the paper) invalid? If the authors themselves think the role of SPARCKL1 is ambiguous based on their own data, they should perform further experiments. P. 13, the authors write: "Moreover, many studies have shown that astrocyte-specific molecules, including extracellular molecules such as IL-6, are involved in memory function"; Interleukin 6 (Il-6, abbreviation not defined in the manuscript) is definitely not an astrocyte-specific molecule (see, for example, Erta et al., 2021 10.7150/ijbs.4679).

    Significance

    NATURE AND SIGNIFICANCE OF THE ADVANCE: I think that despite the issues described above, this manuscript, once revised, could have a strong impact in the field. It would fuel the current paradigm shift which puts astrocytes at the forefront of neuronal circuit wiring during development with links to adult behavior. By identifying clear molecular targets involved in astrocyte-driven synaptogenesis, this article could help the clinical field to find new druggable targets, which may help reverse aging-related cognitive decline.

    COMPARISON TO EXISTING PUBLISHED KNOWLEGDE: This work adds new data in the specific and growing line of research that study how astrocytes control synaptogenesis. Recent reviews have summarized advances in this field (Shan et al., 2021, 10.3389/fcell.2021.680301; Baldwin et al., 2021, 10.1016/j.conb.2017.05.006).

    AUDIENCE: Neuroscientists in general, clinicians interested in cellular and molecular causes of neurodevelopmental disorders leading to social dysfunctions.

    REVIEWER EXPERTISE: Astrocyte biology; Astrocyte-neuron interactions and synapse assembly; Neuronal circuit formation and plasticity

    Referees cross-commenting

    After careful reading of the other comments, I feel that there is considerable agreement/overlap between the reviewers on the main issues with this manuscript. Perhaps the major difference relates to the amount of further work necessary for the manuscript to be publication ready.

    As Reviewer 3 rightly points out, this is always a moot point: how much is it reasonable for reviewers to ask authors to do? While I agree with all of Reviewer 1's comments regarding the rigour of the mass-spec/western blot analysis, it seems to me that from a molecular/cell biological point of view, the key issue is whether Sparcl1 is a synaptogenic factor released from astrocytes following CD38/cADPR/calcium signaling (irrespective of whether other factors may be in play); and whether raising Sparcl1 levels is sufficient to recover spine morphology and synapse numbers. Of course, if these experiments were performed in vivo using AAV-mediated overexpression of Sparcl1, it is also reasonable to think that the deficit in social memory may be reversed on testing.

    The issues of whether there is a difference in observable behavioral phenotypes between the astrocyte-specific and constitutive CD38 knock-outs is an interesting one, as is why there is only a deficit in social memory seen following astrocyte-specific CD38 ablation. These issues should at least be discussed.

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    Referee #1

    Evidence, reproducibility and clarity

    Summary

    In their work submitted for review, Hattori et al. identify an astrocyte enriched protein (CD38) as important for social memory tasks in mice. The authors developed a conditional KO model to remove CD38 specifically in astrocytes using the GLAST-CreERT2 line crossed to a CD38 floxed line. The investigators use a three-chamber social approach test to show that loss of CD38 leads to reduced interaction time with a novel social stimulus only when the animal is given a break between test periods. The authors test whether changes in neuronal morphology or synapses in the medial prefrontal cortex (mPFC), a region important for social memory, can account for their behavioral phenotype. The researchers found that mPFC neurons in their conditional CD38 KO (cKO) animals have significantly less mature spines than wild-type (WT) controls. The authors then claim that this reduction in mature spines correlates with a reduction in VGluT1 positive excitatory synapse density in mPFC of cKO vs. WT. Next, the investigators use mass spectrometry of astrocyte conditioned media and neuronal cultures treated with astrocyte conditioned media to test whether a known astrocyte secreted synaptogenic factor, Sparcl1/Hevin, could underlie their reported changes in synapse density in their cKO animals. Finally, the authors use pharmacological inhibitors against different components of the CD38 signaling pathway to test whether CD38 regulates Hevin secretion by astrocytes. While the reported behavioral phenotype is interesting, this reviewer has several major concerns with the data claiming that reduction in Sparcl1/Hevin is underlying synaptic phenotypes in the CD38 cKO. Therefore, the paper is not suitable for publication without addressing the concerns listed below.

    Major Concerns:

    Synapse analysis in vivo: For the analysis of VGluT1 excitatory synapses in mPFC, it is not clear how the statistical analysis was performed. From the plotted error bars, it seems that the investigators used individual z-projections as the n for a t-test. This is inappropriate for this analysis as it would overinflate the N and down the p-value. It would be more appropriate to plot and compare animal averages between conditions or use a test that can account for the fact that there are repeated measures taken from the same animal. Additionally, the authors note a decrease in VGlut1+ puncta in the global CD38 KO but no change in the protein levels in both the global and cKO.

    Synapse analysis in vitro: The authors are missing key experimental controls for their analysis of synapse induction by astrocyte conditioned media. Firstly, the authors do not include a condition of neurons cultured alone without astrocytes or astrocyte conditioned media treatments. This is critical to this experiment because, without this control, it is impossible to assess the effectiveness of the astrocyte conditioned media or any recombinant protein treatments on synapse formation. Secondly, the authors give very few details and no supporting data about the purity of their neuronal cultures. This is critical to this experiment because any contaminating astrocytes in their cultures could severely skew the data for any given condition. Finally, the authors do not specify how they determined the doses for astrocyte conditioned media and Hevin treatments. The researchers give no details on how the astrocyte conditioned media was collected or treated before adding onto neurons. For this experiment to be viable, the researchers must collect the conditioned media in serum-free media, determine the protein concentration of their samples, and the dose-response to the astrocyte conditioned media must be performed to determine the optimal dose for each batch. When comparing between genotypes, this type of quality control is critical to assess whether there is, in fact, a difference in their synaptogenic capacity.

    Western blots: All western blot quantification of astrocyte conditioned media should include total protein normalization. The authors do not describe how they normalize the astrocyte conditioned media blots, but without a total protein stain to normalize, it is impossible to be sure the same amount of protein was loaded into the gel for each lane. In Figure 3L, the western blot data showing the expression of VGluT1 and PSD95 should be improved, and a better representation is recommended. It is also strange that the CD38 cKO has no expression because CD38 is also expressed in endothelial cells. Why not isolate astrocytes from CD38 KO? Also, for VGluT1 and PSD95 western blots, it would be better to test mPFC lysates rather than whole cortical lysates. Astrocyte morphogenesis: Since the astrocyte-specific deletion of CD38 from P10 impairs postnatal development of astrocytes, the authors should investigate if the impaired synaptogenesis seen in later stages is due to impaired astrocyte morphogenesis or the defect in the secretion of synaptogenic proteins like Sparcl1/Hevin or thrombospondins.

    Mass spectrometry: There is no information about how many samples were used for mass spectrometry. This reviewer is concerned that this experiment may be underpowered given that other published datasets have identified significantly more proteins in wild-type ACM (about double than what was identified here). There needs to be a quality assessment of the ACM to help ensure the production protocol can capture the full extent of proteins secreted by cultured astrocytes.

    RNA sequencing: RNA sequencing results seem underpowered, and an accurate description of their collection methods is missing. It also seems to this reviewer that any prolonged culturing of the astrocytes would lead to additional transcriptional changes independent of their genetic manipulation. To avoid confounds due to culture artifacts, it might be cleaner to FACS sort astrocytes using a fluorescent reporter such as the Aldh1l1-eGFP line or RTM in their GLAST-creERT2 model. In the latter case, this could also provide data on the specificity of their recombination, which is lacking elsewhere in the manuscript.

    Comparison between astrocyte-specific cKO and global KO: Considering the abundant expression of CD38 in astrocytes compared to other cell types in the brain, I am wondering whether the comparison between the current astrocyte-specific CD38 cKO and the previous constitutive CD38 KO mice would provide a different phenotype with respect to its importance in synaptic function in neural circuits that mediate social behaviors in various brain regions. The authors note the importance of CA1, CA2, and NAC in social memory, but they only assessed synapses in mPFC. Multiple studies, including one from the authors, have reported that constitutive CD38 KO mice exhibit impaired social behaviors. Expanding beyond what is already known would require better spatial and temporal regulation of CD38 expression than presented here.

    Rescue experiments: The authors claim that reduced levels of Hevin secretion are responsible for reducing intracortical synapses in mPFC and the inability of their CD38 KO ACM to stimulate synapse formation. However, Hevin has primarily been linked to the formation of VGluT2+ synapses with only a transient effect on VGluT1+ synapses. Furthermore, Hevin's synaptogenic effect in astrocyte conditioned media is masked by its homolog Sparc. To claim that Hevin is responsible for reducing VGluT1+ synapses in mPFC the authors need to do a rescue experiment by expressing hevin in CD38 KO through AAVs brains or intracortical injections of recombinant Hevin.

    Other synaptogenic factors: The authors focus on Sparcl1/Hevin; however, other synaptogenic factors have been reported to affect VGluT1+ excitatory synapse formation and development directly. Notably, thrombospondins have been shown to regulate the formation of this specific synapse type through their receptor a2d1. The authors do not report any investigation into this family of factors despite their clear link to VGluT1+ synapse development.

    Effect of CD38 cKO on astrocyte numbers: The authors note that CD38 cKO alters GFAP expression; however, they also report a decrease in the number of GFAP+ and S100ꞵ+ cells without a change in NDRG2+ cells. The authors should address this discrepancy in astrocyte numbers with additional known markers such as Sox9.

    MBP quantification: The authors previously reported changes in MBP expression and oligodendrocyte maturation in the global CD38 KO animals. However, there is no quantification of the MBP staining in the cKO in supplementary figure 1. It would be important to verify that white matter structures developed properly in their cKO model, especially in mPFC.

    Minor Concerns:

    1. SPARCL1 annotation should be Sparcl1.
    2. Avoid repetition of the same sentences in multiple places. E.g., The sentence- "Social behavior is essential for the health, survival, and reproduction of animals" is repeated both in the abstract and introduction.
    3. The introduction needs to be thoroughly revised. In the first paragraph, a description of various studies(Fmr/Mecp2) which indicated the importance of synaptic function in neural circuits that mediate social behaviors in various brain regions could be presented later part of the introduction in a very concise manner since the article doesn't cover anything related to these genes. This part can be presented along with the narration of CD38, where authors described its importance in social behavior. Introduce the importance of social behavior and their behavioral paradigm, especially what social memory is and what brain regions are important for it.
    4. Introduction feels too short and abrupt.
    5. In Figures 2 and 3, Are the spine numbers/density/synapses affected in the p42 ctrl/CD38 AS-cKO group compared to the p10 ctrl/CD38 AS-cKO group?
    6. In Figure 2; The authors should compare both the behavioral phenotype seen in two different tamoxifen injection/time points with the respective constitutive CD38 KO mice data.
    7. In Figures 3 and 4, the authors should analyze the spine numbers/density both in WT or CD38 KO ACM treated experiments and Sparcl1 KD/Sparcl1 treated rescue experiments?
    8. The discussion section needs to be revised to reflect better the conclusions drawn from the data without overstatement.

    Significance

    Understanding the mechanisms underlying control of behaviors is important and linking non-neuronal cell types to behavioral processes is novel and timely. However, the study at its current state lacks important controls, and interpretations are overstated and often too targetted to a favorite mechanism. These concerns limit the impact of the study and reduces its significance.

  5. Version published to 10.1101/2021.12.23.474051 on bioRxiv