mTOR activation induces endolysosomal remodeling and unconventional secretion of IL-32 via exosomes in inflammatory reactive astrocytes

This article has been Reviewed by the following groups

Read the full article See related articles

Listed in

Log in to save this article


Astrocytes respond and contribute to neuroinflammation by adopting inflammatory reactive states. Although recent efforts have characterized the gene expression signatures associated with these reactive states, the cell biology underlying inflammatory reactive astrocyte phenotypes remains under-explored. Here, we used CRISPR-based screening in human iPSC-derived astrocytes to identify mTOR activation a driver of cytokine-induced endolysosomal system remodeling, manifesting as alkalinization of endolysosomal compartments, decreased autophagic flux, and increased exocytosis of certain endolysosomal cargos. Through endolysosomal proteomics, we identified and focused on one such cargo – IL-32, a disease-associated pro-inflammatory cytokine not present in rodents, whose secretion mechanism is not well understood. We found that IL-32 was partially secreted in extracellular vesicles likely to be exosomes. Furthermore, we found that IL-32 was involved in the polarization of inflammatory reactive astrocyte states and was upregulated in astrocytes in multiple sclerosis lesions. We believe that our results advance our understanding of cell biological pathways underlying inflammatory reactive astrocyte phenotypes and identify potential therapeutic targets.

Article activity feed

  1. This review reflects comments and contributions by Pablo Ranea-Robles, Gregory Redpath, Venkat Krishnan Sundaram, Rajan Thakur.

    Determining the neurotoxic factors secreted by astrocytes has been an important area of study in the glial research community. In this study, Rooney et al. describe a mechanism to explain how inflammatory reactive astrocytes drive neurotoxicity. This scientific question is relevant as this mechanism is not well known but has a major contribution to neuroinflammatory and neurodegenerative diseases.

    The preprint reports that upon induction of inflammatory response in hiPSC derived astrocytes there is significant lysosomal remodeling. Inflammatory reactive astrocytes have decreased lysosome acidification and degradative capacity with increased lysosomal exocytosis. Via pharmacological and genetic approaches it is shown that the neurotoxic effects of inflammatory reactive astrocytes could be mediated by increased exocytosis in these cells. This is demonstrated in vitro using Caspase 3/7 as a marker for neurotoxicity in neurons cultured with astrocytes conditioned media. The CRISPRi screen is an excellent tool that is smartly used in this study, and the finding of a strong inverse correlation between the pH and exocytosis phenotypes for many hit genes sustains the conclusions. The paper reports a number of hits in the mTOR pathway including mTOR itself, with very remarkable effects of mTOR KO in iAstrocytes on lysosome exocytosis in astrocytes and neurotoxicity.

    The paper is interesting, the experiments sound and the findings are supported by the data. The manuscript is very well written and the findings clearly explained. The inclusion of all the uncropped blots and the corresponding replicates for the immunoblots is a great addition.

    Some comments as well as suggestions for polishing the manuscript are offered below.

    • It is recommended to provide further data to show clear evidence that basal level of autophagy is unaltered upon ITC treatment.
    • There are certain discrepancies on LAMP1 expression on the cell surface post exocytosis. LAMP1 blot data should be correlated with log2FC value of LAMP1 in the proteome dataset.
    • For most of the repetition experiments the paper reports ‘X’ independent wells for each condition. Are these wells (representing independent experiments) done from the same activated astrocytes which were split into ‘X’ wells or these were totally independent experiments? Please clarify if these are technical replicates or biological replicates.
    • Images of cells with Hoescht staining could be provided, as it was used for normalization. It would be great to know how many images/ wells or cells/wells were used for this analysis.
    • There could be further discussion about the results of the study. For example, the fact that OXPHOS genes were the top pathway among the hits of the CRISPRi screen, and how this relates to lysosomal exocytosis.
    • Knocking out genes involved in exocytosis in iAstrocytes leads to a partial reduction in neurotoxicity. It may be worth showing some data to prove that the sgRNA targeted those genes and there is no functional protein. The manuscript could discuss in more detail what may be responsible for the remaining neurotoxicity.
    • Readers may appreciate some further explanation for the selection of Caspase3/7 as the marker for neurotoxicity. Can this be complemented with other markers to strengthen the message?
    • There is inconsistency around the presentation of statistical tests - some figures have them, some don't. Recommend that all graphs include relevant statistical tests. The bar graphs could be presented as just dot-plots.
    • The vehicle is always presented beside the treatment condition. This makes sense, but in some figures the comparison of interest is between the other intervention (e.g., sgRNA target), in which case the graph may be easier to interpret with the vehicle +/- intervention and ITC +/- intervention beside each other.
    • It is unclear how the TIRF images of lysosomal exocytosis add to the study, as they do not show clear exocytosis events that are consistent with published literature. Different videos displaying the distinct exocytic burst could be presented, the images retaken, or this data removed. The flow cytometry data on exocytosis is convincing enough as it is. If the authors desired another visual demonstration of lysosomal exocytosis, cells could be treated +/- ITC, cooled on ice, cell surface LAMP1 detected with their antibody to the luminal epitope and these cells fixed and imaged.

    Figure 1

    • Figure 1D - Is it confirmed that GAPDH is not differentially expressed in RNAseq and proteomics upon ITC treatment? The Log2FC value of GAPDH should be noted (as done for ACTB) in the proteomic plots. This would support the use of the protein as a loading control. This comment is made in light of the implication of GAPDH in autophagy. Furthermore, subtle changes in expression levels picked up by proteomics are not necessarily recapitulated in western blots.
    • Figure 1D - Please mention under the Methods section how background correction, band definition, detection linearity was performed and verified using the LICOR software.
    • Figure 1G - Recommend adding a statistical analysis to this figure. The graph of the autophagic flux with LC3B construct would be more complete with corresponding representative pictures.
    • Figure 1I - To allow the reader to ascertain the extent of differential expression in the volcano plot, please mention the log2FC & P values for the proteins taken into consideration from the proteomics data. This could either be incorporated into the legend or presented as a separate table in the supplementary data.

    ‘lysosomes of ITC-treated iAstrocytes were indeed less acidic than those of control iAstrocytes'- As this was measured by flow cytometry, the standard flow dotplots or histograms could be presented as well.

    ‘Furthermore, ITC-treated iAstrocytes accumulated puncta of LC3B, an autophagosome marker degraded in the lysosome by acid-activated hydrolases (Fig. 1e)’- Recommend providing Western blot data of LC3I and LC3II in addition to the LC3 ICC. This is because important conclusions are derived on steady state autophagy levels and lysosomal degradation of LC3 in the autolysosomes.

    ‘Using a GFP-LC3-RFP-LC3ΔG reporter’- A brief description of the reporter and how this measures autophagic flux would be helpful - the color that is quenched when the autophagosome fuses with the lysosome should be mentioned.

    ‘reflected an impairment in degradative autophagic flux rather than an increase in the steady-state level of autophagic components’ - The data on lysosome acidification and impaired lysosomal degradation of LC3 is convincing. However, the expression levels of autophagic components upon ITC treatment is not mentioned. Recommend presenting the following data with Figure 1:

    1. Log2FC values of Atg genes and LC3 from the RNAseq data along with other genes that pop up in autophagy related GO terms, if any.
    2. The log2FC values of autophagy related genes from the total proteomics data. Also please indicate where LAMP1 is situated in the Lyso-IP proteome volcano plot (Fig 1I).
    3. Western blot data on LC3I and LC3II as mentioned earlier would also add to points 1 and 2 above.

    ‘To test this hypothesis, we used TIRF microscopy to visualize lysosomes in iAstrocytes loaded with LysoTracker Green and expressing a lysosome membrane-targeted mCherry construct (Fig. 2a)’ - Are these control or ITC-treated astrocytes? In Fig 1E, it was shown that lysotracker could not permeate lysosomes as much as the control condition owing to a change in pH. However, it has been used in TIRF microscopy. Would it be possible to clarify how lysotracker signal is detected in this method but not in ICC. Is it simply a question of resolution?

    ‘Supplemental Movies 1,2’ - At the framerate the movies are presented, the exocytic events are not clear. Signal disappears, but the characteristic burst of intensity that accompanies an exocytic event was not observed. I realise kiss-and-run exocytosis would not involve this full fusion, and has been reported not to occur in lysosomal exocytosis ( Different videos displaying these classical fusion events may be used, or the authors could rely on their luminal epitope exposure assay to demonstrate this point.

    Figure 2

    • Figures 2A&B - Images for vehicle-treated astrocytes could be provided. It would be also interesting to know if the rate of lysosomal exocytosis is different or similar in control and activated astrocytes.
    • Figure 2D ‘Total LAMP1 protein in ITC and vehicle-treated iAstrocyte’ - From the immunoblots and the source data, it looks like the membrane was stripped between LAMP2 and LAMP1. However, GAPDH blots seem to be used from the membrane before stripping. If that is the case, GAPDH should be reprobed after stripping for robust normalization. LAMP1 immunoblot data could be verified with the proteomic data to check that it is not differentially expressed between conditions.
    • Figure 2G,H - Recommend a statistical comparison between vehicle and ITC-treated cells.
    • Figure 2K - When comparing Fig 2C right panel and Fig 2K DMSO, the effect of ITC on LAMP1 MIF seems to be lost upon DMSO addition. Interestingly there is significant neurotoxicity. Could some clarification be added for this discrepancy, along with the P value.
    • Figure 2I - SYT11 knockdown leads to significant increase in surface levels of LAMP1 in control treated cells while there is slight decrease in the surface levels of LAMP1 in activated astrocytes. Could these differences be discussed in the text? Does this mean that SYT11 differentially regulates surface LAMP1 levels in control vs activated astrocytes?
    • The 50% decrease in neurotoxicity is not easy to see by looking at the bars in Fig 2J. Some numbers will help visualize the exact effect on neurotoxicity measured by the apoptotic marker.

    ‘no substantial effect of vacuolin-1 on cell-surface TFRC levels’- There is a substantial increase in TFRC at the cell surface when comparing vehicle and ITC treated, with around a 4x increase in MFI. This is an important point, because independent of the effect of vacuolin-1, it strongly implies that general, non-lysosome related trafficking (specifically Rab11-related recycling) is massively upregulated. This is a good demonstration of the specificity of vacuolin-1, but the apparent effect of ITC on increasing exocytosis (or cell surface expression) of other cargoes could be mentioned.

    ‘While SYT11 and VAMP7 knockdown resulted in only a small decrease in cell-surface LAMP1, this was sufficient to reduce ITC-induced neurotoxicity by ∼50% relative to control iAstrocytes’ - The text could acknowledge that the reduction in LAMP1 is not statistically significant for a couple of these knockdowns, and also mention that this may imply the reduction in toxicity could be due to either a non-exocytic mechanism, or lysosomal exocytosis mediated by non-conventional pathways.

    Figure 3

    • Figure 3M,N&O - Multiple pairwise comparison should be done to see if the inhibitor treatment is any different in control vs activated astrocytes.
    • Figure 3N - The effect of TOR inhibitor PP242 on the surface levels of LAMP1 seems to be alike in control and activated astrocytes. This appears contradictory with the findings from the genetic knockdown of TOR.
    • Figure 3P - The model predicts the lysosomal content to be different in control vs activated astrocytes. The secretome of control vs activated astrocytes could be compared to check if there are any significant differences.

    ‘Mechanistically, we have not yet resolved if the relationship between lysosome exocytosis and astrocyte-mediated neurotoxicity stems from direct toxicity of astrocyte lysosome contents, or whether these contents contribute to autocrine-paracrine signaling in astrocytes to induce neurotoxicity through an indirect mechanism’ - More data on astrocyte-mediated neurotoxicity appeared in a recent publication, it may be interesting to compare these data.