Stress-primed secretory autophagy promotes extracellular BDNF maturation by enhancing MMP9 secretion

The stress response is an essential mechanism for maintaining homeostasis, and its disruption is implicated in several psychiatric disorders. On the cellular level, stress activates, among other mechanisms, autophagy that regulates homeostasis through protein degradation and recycling. Secretory autophagy is a recently described pathway in which autophagosomes fuse with the plasma membrane rather than with lysosomes. Here, we demonstrate that glucocorticoid-mediated stress enhances secretory autophagy via the stress-responsive co-chaperone FK506-binding protein 51. We identify the matrix metalloproteinase 9 (MMP9) as one of the proteins secreted in response to stress. Using cellular assays and in vivo microdialysis, we further find that stress-enhanced MMP9 secretion increases the cleavage of pro-brain-derived neurotrophic factor (proBDNF) to its mature form (mBDNF). BDNF is essential for adult synaptic plasticity and its pathway is associated with major depression and posttraumatic stress disorder. These findings unravel a cellular stress adaptation mechanism that bears the potential of opening avenues for the understanding of the pathophysiology of stress-related disorders.

5) line 239. This is an aspect of discussion and as a comment not easy to follow.
6) The use of the term stress is often misleading and there is a certain tendency to overinterprete the data. The authors are not clearly separating between cellular stress or stress as an adaptive in vivo response. For instance in the abstract, line 48: These findings unravel a novel mechanistic link between stress, stress adaptation and the development of psychiatric disorders. This is not true. The authors don't show a mechanistic link between stress and the development of psychiatric disorders.
Or line 85ff: We explored a possible role for secretory autophagy as a mechanism linking GC-mediated stress to the development of psychiatric disorders. 7) Figure 7b is not covered by data.

Robert Blum
Reviewer #2 (Remarks to the Author): In this manuscript, Martinelli and Anderzhanova et al describe the involvement of stress response in relationship to FKBP51 on secretory autophagy. Autophagy and stress response are central homeostatic regulators. Glucocorticoids are central players in stress response. Here, the authors use a number of different cell lines and manipulations to investigate the role of FKBP51 in secretory autophagy and find that FKBP51 forms complexes with some key players involved in this pathway. In addition, FKBP51 levels and/or GR activity through Dex treatment regulate secretory autophagyrelated proteins. They complement these findings using microdialysis in wt and FKBP5 knockout mice exposed to stress, which revealed impaired release of CTSD, MMP9 and mBDNF into the interstitial fluid, similar to what was found following treatment with an autophagy inhibitor (ULK1i). Finally, they showed that increased FKBP51 elevates release of these same factor from microglial cells and that SAFit1 treatment reduces this. Overall, it is an interesting story, but there are major issues with the writing and data interpretation that weaken enthusiasm for the work. In addition, the overall novelty is considered moderate. Specific comments can be found below, which would strengthen the paper: • The overall writing is not cohesive. The title does not well represent the paper, the introduction does not flow into the results, the results and discussion both have information that should be in the introduction, and the discussion has information that is more results and does not summarize the whole story well. Major revisions are needed. • Conclusions are drawn from the co-IP data that cannot be made. Co-IPs will reveal complexes and are not quantitative. Other direct methods of binding need to be used to make statements about direct interactions between proteins. In addition, it does not appear that the lysates were precleared with beads to ensure only specific complex interactions are measured, as many proteins can stick to the beads directly.
• Do other GR-regulated proteins cause the same increase in secretory autophagy? • Why were microglial cells selected? • A known positive regulator of secretory autophagy should be used to compare to the results found in this paper for FKBP51 and Dex treatment • Readouts of Dex treatments need to be shown throughout. Charcoal stripped media should also be used to remove the effects of FBS hormones. • Confirmation of FKBP51 levels and GR activity should be confirmed in each cell line being used. • Reviews are referenced, where original manuscripts should be referenced instead. The introduction would benefit from additional references. Some references are misleading, for example Ref 1, which does not mention bipolar or schizophrenia, and Ref 8, which is not the first time secretory autophagy is described.
• Baf should be defined in the results section. • Line 395: Secretory pathway is activated only after prolonged or excessive stress? This does not support their stress paradigm since the authors describe footshock as an acute stressor. • Line 404-408, 412-414: missing references • Line 428-429: It mentions NMDAR without explaining it relation to BDNF or synaptic plasticity. • Line 448: Indicate type of stress (GC-induced, acute or both) • Line 443: Need to discuss the "contrasting" findings-"However, despite some consistent findings, other studies report incongruent or contrasting results". • Methods are missing for some technical aspects, including descriptions of the experiments for Figure  6 and Baf treatments.
• Authors must include exact number of n values for in vitro and in vivo experiments. Also, report the number of times the experiment was repeated, or replicates included in the final analysis.
• Mention if all animal procedures followed standard policies animal care. Include age, sex and number of animals used for each experiment. Overall, the Ns are very low for these studies and should be increased. Sex of the mice should also be considered as an independent variable. Time of day for the experiments should be carefully described in the methods • Explain the rationale for choosing one-tailed over two-tailed unpaired t tests. Reviewer #3 (Remarks to the Author): FKBP51 (gene name: FKBP5) is a glucocorticoid (GC) receptor binding protein, which acts as a cochaperone of heat shock protein 90 (HSP90) and regulates GC-mediated stress. This protein is also known to be associated with mental disorders.
The authors of this study showed previously that GC-mediated stress leads to the activation of macroautophagy, which is regulated by FKBP51 (Gassen etal., pLos Med., 2014). In the present study, they show that GC induces another type of autophagy called secretory autophagy and that FKBP51 plays an important role in this secretory autophagy by interacting with specific SNARE proteins ( Fig.  1). They further show that MM9 is a novel cargo molecule of GC-mediated secretory authophagy (Fig.  3), that FKB51 is critical for secretion of MMP9 (Fig. 4), and that the MMP secretion plays an important role in BDNF maturation (Fig. 4, 5).
1. The authors provide strong cellular evidence that FKBP51 is critical for secretory authophagy of MMP9 leading to BDNF maturation. However, I feel that the biological significance for this role of FKB51 in living mice is missing or obscure.
As the authors stated in Abstract, BDNF is essential for synaptic plasticity. Thus, I would imagine that the reduced BDNF maturation in the stress response by FKBP5 KO has strong a strong behavioral phenotype in the BDNF-related behavior, such as learning and memory. However, previous study seems to fail to show such phenotype in the FKBP5 KO mice. For instance, O'Leary et al. (2011, pLos One) described that FKBP51 KO mice showed antidepressant behavior without affecting cognition and other basic motor functions. This previous result does not seem to be consistent with the proposed function of FKBP51 in stress-induced BDNF maturation. The authors of the present study should show some sort of behavioral or neurological phenotype associated with the reduced BDNF maturation by FKBP5 KO mice. Without such evidence, the readers of Nature Communications remain puzzled about the role of FKBP5 in stress-induced synaptic plasticity and BDNF maturation.
2. Co-IP data in Fig. 1J is NOT described correctly. Fig. 1J is labeled as "GFP-IP", which I believe is correct. Based on the figure, I believed that the authors overexpressed SEC22B as GFP-fusion protein and IPed using GFP-Ab. However, the used antibody was labeled as "FLAG-Ab". This should be "GFP-Ab". The Figure legend to Fig. 1J described this experiment as "FLAG-tagged FKBP51 co-IP (FLAG-IP). I believe that the legend should be "GFP-tagged SEC22B co-IP (GFP-IP).
Reviewer #4 (Remarks to the Author): In this manuscript by Martinelli et al., termed " Stress-primed secretory autophagy drives extracellular BDNF maturation" the authors identify the matrix metalloproteinase 9 (MMP9) as a stress-induced secreted protein involved in the cleavage of pro-brain derived neurotrophic factor (proBDNF) to its mature form (mBDNF). The authors demonstrate the involvement of the co-chaperone FK506-binding protein 51 (FKBP51) in stress-elevated secretion of MMP9 in the mouse brain, exploiting in vivo microdialysis in WT and Fkbp5 KO mice. The importance of the autophagy machinery for the stress elevated secretion is assessed in WT mice by including a ULK1 inhibitor. The authors claim that stressinduced secretion of MMP9 is through secretory authophagy, facilitated by FKBP51.
The novel finding in this manuscript is the involvement of FKBP51 in stress-elevated secretion of MMP9 in the mouse brain, resulting in maturation of BDNF. BDNF is essential for synaptic plasticity and altered BDNF signaling is associated with stress-related psychopathology. Hence, this finding is of general interest and contributes to the understanding of MMP9 secretion in the CNS. Overall, the biochemical data are well performed and the use of proteomic methods, data mining and in vivo microdialysis reflect an extensive amount of work. Nevertheless, the manuscript has some critical shortcomings that have to be addressed before publication.  (Fig. 1e). However, that does not necessarily mean that TRIM16 binds to CTSD since IP-based interaction detection can reflect indirect binding of the proteins in question. Secondly, FKBP51 is a known co-chaperone of heat shock protein 90 (HSP90) and HSP90 has been assigned a key role in secretory autophagy of IL-1β, mediating import of IL-1β into the autophagsomal intermembrane space (Zhang et al., 2015; doi: 10.7554/eLife.11205). The authors do not address this point at all other than showing that mutating the HSP90 binding site of FKBP51 reduces a potential interaction between FKBPB51 and galectin 8 (Fig. 2b). Finally, the authors show that FKBP51 is essential for the association of SEC22B with its Q-SNARE partners in SH-SY5Y cells (Fig. 1j). However, there are no data presented that demonstrate the importance of the formation of this SNARE complex for stress-induced MMP9 secretion in SIM-A9 (microglia) cells or mice. Detailed comments and suggestions are included below.
Major comments: 1) Figure 1b,c,d and e and figure S1 a and b: Interaction between FKBP51 and SEC22B or TRIM16 is implicated from reciprocal co-IPs. To demonstrate a direct binding between FKBP51 and SEC22B or TRIM16 the authors could use a GST-pulldown assay with labeled in vitro translated proteins. Furthermore, co-localization images in cells to visualize FKBP51 together with SEC22B or TRIM16 would be helpful. The same applies for the implied interaction between TRIM16 and CTSD.
2) For the blots in figure 1d, e and g, which form of CTSD is shown/recognized by the antibody? CTSD exists in different forms with the inactive precursor of the enzyme, procathepsin D, being cleaved, resulting in different forms of mature/active cathepsin D. 3) Figure 1l-"Schematic overview of the interactions of FKBP51 in the secretory autophagy pathway": Here FKBP51 is shown to interact with GAL8 but no data have yet been presented to show this. TRIM16 binds to GAL8 and the figure should indicate that. Furthermore, HSP90 is shown as a binding partner of FKBP51 but HSP90 is not included in the blots of any of the IPs in figure 1. Furthermore, there are no data presented indicating the importance of FKBP51 for transfer of the TRIM16-cargo (CTSD) to the autophagosome or data indicating that HSP90 is not present. TRIM16 association to SEC22B is independent of FKBP51 according to figure 1e. And there are no comments or experiments addressing how CTSD, that normally resides in lysosomes, is translocated into the lumen of autophagosomes prior to its secretion. Therefore, the claim on page 6 line 148-149. "From these data, FKBP51 results to be involved in several key steps of the secretory autophagy pathway (Fig 1l)", appears as an overstatement. 4) In figure 2c and 2d the authors use a tandem tagged (mRFP-GFP) galectin 3 (tfGal3) in SH-SY5Y cells to monitor lysosomal damage. The reduction of the GFP signal is a result of acidification of tfGal3. Gal3 is recruited to damaged lysosomes and Gal3 becomes acidified trough lysophagy. Lysophagy involves autophagosomal engulfment of damaged lysosomes that subsequently become degraded by fusion with intact lysosomes (Maejima et al., 2013; doi: 10.1038/emboj.2013.171). LLOMe induces lysosomal damage that culminates in lysophagy and Dex appears to be able to do the same. Inhibition of lysosomal acidification with BafA1 abolishes the effect. Therefore these data actually show degradation of Gal3 on damaged lysosomes through autophagy. The authors should comment on how they envision the effect of dex on lysosomes and how this relates to secretory autophagy. 5) In figure 2 e) and 2 f) SIM-A9 secretion of CTSD in response to LLOMe and dex treatment, respectively should also include BafA1 treatment to determine if the secretion is dependent on functional lysosomes or not. 6) In figure 4 the dex induced MMP9 secretion should be shown in FKBP51 KO SIM-A9 cells as well to complement the in vivo results in figure 5. Furthermore, in order to link MMP9 secretion to secretory autophagy the authors could use siRNA knockdown of TRIM16 or SEC22B in these cells. The presence of MMP9 in an IP of TRIM16 or co-localization study of MMP9 with TRIM16 in cells would also be desirable. 7) Figure 7-"Schematic representation of the findings and proposed model": In a, TRIM16 is shown to interact with MMP9. Again, there are no data in the manuscript that demonstrate this interaction and this schematic drawing is thus not accurate.
Minor comments: 1) In Supplementary Table S1 of 29 identified interactors of FKBP51 in HEK293 cells, HSP90 is not listed. The authors should comment on that.
2) Page 5 line 114-115: "…the interaction of FKBP51 with SEC22B (Fig. 1b,c), previously only deduced via differential centrifugation13". Please clarify, since the cited reference ( 9) The discussion section is rather long and should be more focused on the obtained data in this study.
Reviewer #5 (Remarks to the Author): The manuscript by Martinelli et al. "Stress-primed secretory autophagy drives extracellular BDNP maturation" described the mechanism of enhancement of secretory autophagy by glucocorticoidinduced stress. The authors use interactomics and secretome analysis by mass spectrometry to identify proteins involved in the process and propose an elegant step-by-step mechanistic model validated by several other methods. The paper is well written, the findings are novel and this reviewer supports the publication in Nature Communications which will allow these results to reach a broad readership. There are a few minor concerns, mostly technical in nature, that should be addressed before acceptance.
Detailed comments: 1. Since TRIM16 was confirmed to be an interactor of FKBP51 by Western blot, but not originally found in the MS dataset, can the MS data be researched and perhaps TRIM16 peptides can be found (maybe with the help of the inclusion list?) 2. For the interactome analysis, the transfection with a vector containing FLAG only was used. Can the authors include more description of how the control (unspecific) binders were eliminated? The only explanation I could found is in lines 651-651, that the proteins overlapping from all four replicates were counted as interactors. This is not sufficient. 3. For the secretome analysis, the media supplemented with FBS was used throughout the whole experiment. Is that correct? If so, how was the signal suppression by the overwhelming amount of protein handled? Was the albumin removed? This was not an issue for detection because the labeling was used, but signal suppression would be an issue anyway. Can the authors comment on that? 4. Another useful clarification of the secretome analysis would be the comparison of growth rates and cell death between the wild type and the Atg5 KO cells. Are they identical in this respect, and if not, how was the data normalized?

Reviewer #1
We thank Robert Blum (Reviewer #1) for his constructive and insightful comments. We addressed his valid suggestions by performing additional experiments and tried to clarify imprecisions with additional information.
Reviewer #1 (Remarks to the Author): The paper by Martinelli Anderzhanova et al presents new insights in regulation of secretory autophagy, identifies new and important regulatory proteins of secretory autophagy. The study shows for the first time, how one important cargo protein of secretory autophagy, the matrix metalloproteinase 9 (MMP9) can contribute to more behavior-related, extracellular abundance of mature BDNF.
BDNF is one of the most important key proteins in synaptic plasticity, it can be stored in synapses and undergoes activity-dependent secretion. BDNF is involved in diverse synaptic processes, including synapse maturation, synapse refinement, synaptic transmission and even pre-and postsynaptic LTP. Two BDNF isoforms are known to regulate synaptic transmission, the mature BDNF, a homodimeric protein with high affinity to TrkB, and proBDNF, an isoform carrying the so called pro-domain. Even the cleaved pro-domain has been shown to be involved in synaptic processes. proBDNF shows high-affinity to p75, another neurotrophin receptor. There is an ongoing debate about proBDNF secretion and processing.
In this important study, the authors show that FKBP51, a stress responsive cochaperone is critically involved in secretory autophagy. Notably, MMP9 is a cargo of these granules and undergoes regulated secretion, possibly for the local cleavage of proBDNF to mBDNF. The finding that cellular stress-related release from autophagosome-like granules/vesicles is associated with extracellular mBDNF abundance is credible.
The design of the study is straightforward and conceptually strong. The experiments are convincing and there is a lot of important, new and relevant information available. For instance, the interactome of FKBP51 is well worked out and the experiments help better understand how FKBP51-positive autophagosomes behave within the trafficking pathway. Much of the work has been done in cell lines (SH5YSY, neuroblastoma-like cell line; Hek293, SIM-A9, microglia-like), but the detailed information about key proteins in the secretory autophagosome (SEC22B, RACK1, UBC12) pathway will help to find out how secretory autophagy is acting in neurons, at synapses or between cell types (microglia) at synapses.
The in vivo experiments clearly show, with a new approach, direct determination of behavior-related secretion of BDNF isoforms. However, we do not learn from which cells BDNF is secreted, an aspect beyond the scope of this study. Nevertheless, the data convincingly reveal that MMP9 and BDNF appear in the prefrontal cortex in the course of a behavioral test and the data show that MMP9 contributes to more mBDNF.
I'm sure that these proof-of-principle experiments will motivate many researchers in the field to look again at the fundamental biology of synaptic BDNF in 'real' learning and memory paradigms.
The methodology is of highest quality. I think that this paper is of substantial importance. For me, there are some major concerns that have to be addressed before it can be considered for publication in Nature communication.
Major comments: (1) The authors write (line 88): …an increase in cleavage of pro-brain-derived neurotrophic factor (proBDNF) to its mature form (mBDNF) both in vitro and in vivo.
However, the data do not show that proBDNF cleavage leads to less proBDNF and more mBDNF. The data show the same amount of proBDNF (in vitro-ELISA) and in vivo (Immunoblotting; but size is not given). If there is cleavage on cost of proBDNF, Western analysis should show less proBDNF at its full size relative molecular weight and more mBDNF at 13 kDa. The interpretation and discussion of the data should be in line with the data.

Response:
Dexamethasone treatment leads to an increase in BDNF expression, as shown in the supplementary fig. S5, and to a consequential increased proBDNF secretion, resulting from ELISA ( Fig.4b) and microdialysate data ( Fig. 5e and I and supported by the following table showing the additional statistics of the 2-way ANOVA analysis performed in the microdialysates experiment where proBDNF's expression is dependend on the time factor but independent from the genotype or treatment factor). This enhanced expression could explain the almost unchanged levels of proBDNF, as it is more expressed and secreted while it is degraded extracellularly.
Regarding the molecular weight of mBDNF, we observe proBDNF and the physiologically active mBDNF dimer in the microdialysates as 32-kDa-and 26-kDasignals, respectively. We do identify a signal at 13 kDa corresponding to monomers of mBDNF. However, this signal is below the LOD and for this reason not quantifiable (see figure below showing a representative SimpleWestern blot quantified for experiments shown in Fig. 6: secreted proBDNF or BDNF from DMSO-treated mouse organotypic brain slices.) (2) Fig. 3: Secretome. proBDNF and mBDNF should appear in the secretome, but the authors do not show the data and do not discuss it (or I have overseen it). My question is: Is there more or less pro-domain or mBDNF in the secretome of SIM-A9 cells after Atg5KO or is there an explanation why there is not much BDNF in the secretome?
In line with the overall concept of the study, one assumption would be that if BDNF is in a different vesicle and is not co-released with MMP-9, one would expect to see more pro-domain in case of Dex/Atg5KO. Is this really extracellular cleavage on cost of proBDNF or are there other explanations?

Response:
ProBDNF and mBDNF indeed have not been detected in the secretomics experiment. A general drawback of untargeted, discovery-driven MS analysis applied here is the fact that the selection of full peptides on MS1 level for the fragmentation and subsequent identification on MS2 level is intensity-based. This means that only the x most intense peptide ions in a MS1 spectrum are selected for further processing in MS2 (where x might range from 5 to 20 depending on the MS method used). Consequently, low intense peptides (derived from proteins of low intensity) might be missed from mass spectrometric detection although they have been present in the sample. This has most certainly happened to proBDNF and mBDNF, which, however, have been detected in a targeted assay ( fig. 4 and supplementary fig. S4c). Furthermore, the fact that mBDNF levels are significantly reduced upon treatment with MMP9i (which inhibits MMP9's enzymatic activity only in the extracellular space), demonstrates that the proBDNF to mBDNF cleavage occurs extracellularly and at the hand of MMP9.
(3) Fig 4: Important data depend on SIM-A9 cells, a microglia-like cell line. The data suggest that the cells produce BDNF and secrete it. However, western analysis is missing. Western blotting data would help to find out whether proBDNF is intracellular and then secreted as proBDNF. It can well be that this is secretion or abundance of cleaved pro-domain versus mBDNF. In Western blotting after SDS-PAGE, mBDNF should appear at 13 kDa, the cleaved pro-domain should run close to 15 -maybe 20 kDa, the uncleaved pro-domain may be expected, in its glycosylated form at about 32-34 kDa. Immunoblotting from supernatants, maybe after IP or after protein concentration, should answer this important aspect. It may be that the authors find other or new anti-pro/anti-BDNF immunoreactive bands. This experiment can help to better understand the overall data set.

Response:
Regarding the size of proBDNF and mBDNF please refer to our answer to comment 1.
For the purpose of our investigation, we found ELISA assays more sensitive and reliable and therefore favored this method. We used in some cases Western blot analyses (see supplementary Fig. S4 f and g) which confirmed our findings with the additional information of the protein sizes. However, the technical steps necessary to remove the high abundance of serum proteins contained in the culture medium would interfere with a direct comparison between the intracellular and extracellular protein quantifications. Furthermore, the extracellular quantification focuses on exactly our point of interest of whether MMP9 leads to extracellular cleavage of BDNF, since we have two observation time points: before and after treatment. While the detection of further or novel variants of BDNF represents an interesting challenge, it might deviate from the scope of this manuscript.

Response:
We updated the Method section in particular in reference to the recently published paper (Anderzhanova et al., 2020), where a comprehensive validation of the measurements using multiple methods was provided. Furthermore, SimpleWestern blotting is an automated system where capillary-based immunoblotting signals are automatically quantified and normalized by the system. The shown quantifications are, therefore, the original data (outputs) of the assays. Additionally, all original raw data are made available to the editors in the final submission procedure. Regarding the information relative to the Antibodies, they are the same used for PAGE Western blotting.
(5) In Fig. 6, after the in vivo data, the authors present the SAFit1 inhibition of FKBP51 in cell culture. The data fit better to Figure 3. Again, as mentioned above, the data are not supported by Western blotting. Here, it is ELISA detection of proBDNF or mBDNF from supernatants. ProBDNF is unchanged, but there is less mBDNF after SAFit1 inhibition. It can well be that MMP9 is acting at a different place. Or another yet unknown MMP9-associated process leads to more secretion of mBDNF. This might explain that there is almost no change in proBDNF in Fig. 4, 5e and 5i. Fig. 6. Anyhow, in Fig. 5, it is very clear that mBDNF goes up, in vivo, extracellular, regulated and behavior-related. This direct verification of regulated, in vivo BDNF secretion is a very important finding.

Response:
Please refer to our previous responses to comments 1 and 3. The main proof of the extracellular cleavage is the fact that by inhibiting the extracellular enzymatic activity of MMP9 via MMP9i, the mBDNF levels do not increase (Fig. 4f). We do not have any evidence to suppose a novel function of MMP9 that acts on mBDNF secretion, since its extracellular enzymatic activity is well characterized and there is no structural feature of MMP9 that leads to hypothesize such a function.
Regarding Fig. 6, we followed reviewer #1's suggestion and added the FKBP51 overexpression and SAFit1 treatment data to the dataset of Fig. 4, which we think reviewer #1 was referring to and we think would fit best.

Response:
We tried to add this information, but it felt really forced as we address the BDNF cleavage from an unbiased finding of MMP9 secretion. We never exclude the existence of other proteolytic enzymes, nor we claim to be the first to describe BDNF cleavage by MMP9. On the contrary, we focus on the secretion of MMP9, thus the cleavage of BDNF by other enzymes (whether plasmin or other metalloproteases) is out of our focus.
(7) Regarding line 419: The authors do not show a change in the ratio. This would mean that more mBDNF appears on cost of proBDNF, but the authors show an increase in the ratio because they see more mBDNF. That's a difference. This does not mean that this interpretation is wrong, but, as mentioned above, there are plausible other options. Please, re-write accordingly.

Response:
As stated in the responses to comments 1, 3 and 5, even though we acknowledge the reviewer's concern regarding the lack of decrease in extracellular proBDNF, there is indeed proof that the increase in extracellular mBDNF occurs on cost of proBDNF since this process can be impaired via inhibition of MMP9, that is responsible for such conversion. The increase in mBDNF/ proBDNF ration remains therefore valid, as only mBDNF increases and not proBDNF, which is the important aspect here given the opposing roles of the two isoforms in synaptic plasticity.
(8) Line 602: How many animals were excluded? What was the surgery success rate?

Response:
We started our experiments with six mice per experimental group, taking into account a possible loss of 1-2 mice per group. Despite having a surgery success rate of 100% we had to exclude some animals during perfusion. Sometimes microdialysis probes stop working, which is a strong indication to exclude the animals. Most of the microdialysate data derive from four mice per group and from five mice for some groups (individuals indicated by dots in graphs).
(9) The secretome data are not easy to interpret. The authors should briefly discuss the limitation of the data set. In Fig. 3b, it is not clear me whether the volcano plot represents a mean of all samples or one representative sample?

Response:
The major challenge of secretome analyses is the large abundancy of serum proteins in the medium that hide the signal of secreted proteins. To avoid this problem, we used an innovative technique developed by Eichelbaum and colleagues (Eichelbaum et al., 2014) where proteins were labelled with AHA (L-Azidohomoalanin), an amino acid analog of methionine, then purified via click-it reaction and subsequently analyzed via LC-MS/MS. The AHA labelling procedure presents some limitations such as the fact that proteins low in methionine might have been missed from initial enrichment by click chemistry. Similarly, methionine-containing peptides are missing from the dataset. In such way, the chance to detect e.g. small proteins is lower. The coverage of proteins (based on peptides) is lower which can makes quantification and sometimes identification somehow difficult.
Finally, a general MS drawback is that a data-dependent acquisition is used here. This means that only a sampling of the most intense peptides for further fragmentation and identification has happened. Very low intense secreted proteins might have been missed from detection. Overall, however, this method allowed us to have a more accurate sampling of the secretome compared to the traditional, non-labelled analyses.
Regarding the volcano plot data, each dot represents the sample mean. This information was added to the legend.
(10) line 239. This is an aspect of discussion and as a comment not easy to follow.

Response:
We removed that last sentence and integrated it into the discussion.
(11) The use of the term stress is often misleading and there is a certain tendency to over-interpret the data. The authors are not clearly separating between cellular stress or stress as an adaptive in vivo response. For instance in the abstract, line 48: These findings unravel a novel mechanistic link between stress, stress adaptation and the development of psychiatric disorders. This is not true. The authors don't show a mechanistic link between stress and the development of psychiatric disorders.
Or line 85ff: We explored a possible role for secretory autophagy as a mechanism linking GC-mediated stress to the development of psychiatric disorders.

Response:
We acknowledged the overstatement and edited the whole manuscript with this in mind. We better differentiated between evidence-based findings and speculations. We also tried to better define stress, as it is a very broad and variable concept and topic that has different interpretations in the different scientific fields.
(12) Figure 7b is not covered by data.

Response:
That is correct. Figure 7b is a proposed model of the autophagic stress-response dynamics. We took the possible misunderstanding into consideration and added this information to the legend text for clarity.

Reviewer #2
We thank Reviewer #2 for their detailed feedback. We edited the manuscript according to their suggestions in a way that we hope will result more cohesive to the reader. We also addressed technical aspects with additional data and control experiments.
Reviewer #2 (Remarks to the Author): In this manuscript, Martinelli and Anderzhanova et al describe the involvement of stress response in relationship to FKBP51 on secretory autophagy. Autophagy and stress response are central homeostatic regulators. Glucocorticoids are central players in stress response. Here, the authors use a number of different cell lines and manipulations to investigate the role of FKBP51 in secretory autophagy and find that FKBP51 forms complexes with some key players involved in this pathway. In addition, FKBP51 levels and/or GR activity through Dex treatment regulate secretory autophagyrelated proteins. They complement these findings using microdialysis in wt and FKBP5 knockout mice exposed to stress, which revealed impaired release of CTSD, MMP9 and mBDNF into the interstitial fluid, similar to what was found following treatment with an autophagy inhibitor (ULK1i). Finally, they showed that increased FKBP51 elevates release of these same factor from microglial cells and that SAFit1 treatment reduces this. Overall, it is an interesting story, but there are major issues with the writing and data interpretation that weaken enthusiasm for the work. In addition, the overall novelty is considered moderate. Specific comments can be found below, which would strengthen the paper: (1) The overall writing is not cohesive. The title does not well represent the paper, the introduction does not flow into the results, the results and discussion both have information that should be in the introduction, and the discussion has information that is more results and does not summarize the whole story well. Major revisions are needed.

Response:
We thoroughly revised the paper with this comments and the editor's feedback in mind and hope that reviewer #2 will find the new version more coherent and readable.
(2) Conclusions are drawn from the co-IP data that cannot be made. Co-IPs will reveal complexes and are not quantitative. Other direct methods of binding need to be used to make statements about direct interactions between proteins. In addition, it does not appear that the lysates were precleared with beads to ensure only specific complex interactions are measured, as many proteins can stick to the beads directly.

Response:
We acknowledge that co-IP data do not necessarily implicate a direct interaction, therefore we replaced the term "interaction" with "association", meaning the formation of a complex via direct or indirect interaction. In fact, an indirect interaction would not contradict our model and our focus remains to show that FKBP51 is necessary for the complex formation with SEC22B and the SNARE proteins that leads to the secretion of the secretory autophagy cargo. However, to address Reviewer #2's demand, we also performed pull-down experiments that demonstrate that FKBP51 can directly interact with TRIM-16 in vitro ( Supplementary Fig. S1c).
Regarding the technical aspects of the IP's specificity, we precleared the beads with BSA (bovine serum albumin) to omit unspecific binding of proteins. This way of proceeding allows an increased specificity for the target protein (i.e. for the antibody), while reducing unspecific binding to the bead material. In addition, to enhance specificity we performed a selective elution of IP-material from antibody-loaded beads using peptide competition with excessive amounts of FLAG peptide.
(3) Do other GR-regulated proteins cause the same increase in secretory autophagy?

Response:
We have not tested other GR-regulated proteins, since we selected FKBP51 based on the newly found interaction with SEC22B. Although it would certainly be interesting to assess whether stress can affect the secretory pathway via other proteins, the fact that FKBP51's absence (in SH-SY5Y KO) or inhibition (via SAFit1) suffices to impair this pathway, suggests that FKBP51 has a rather unique and specific role that we think is hardly a general feature of other GR-regulated proteins. A possible examination of the role of other GR-regulated proteins in the secretory pathway is a laborious project (or projects) and is out of the scope of this manuscript.

Response:
Our interest focuses on stress-related psychiatric disorders, therefore we wanted to analyze this mechanism in brain cells, and to ensure a proper readout for our experiments we selected microglia cells as they are the main secretory cells in the brain.
(5) A known positive regulator of secretory autophagy should be used to compare to the results found in this paper for FKBP51 and Dex treatment

Response:
We used L-leucyl-Lleucine methyl ester (LLOMe) as a positive regulator of secretory autophagy (Fig. 2 c and e) since it is the best characterized secretory autophagy inductor (Kimura et al., 2016). We added this information to the manuscript for clarity (line 199-201).

Response:
They are now aligned.

Response:
They look indeed similar as they represent the same proteins and same conditions but in two different cell lines. However, a close look reveals several small differences that confirm that they are indeed two different blots. (little cut in the FKBP51 and SNAP29 bands of Fig. 1i, shadows of bands in the FLAG conditions of STX3 and SEC22B in fig.  S2, different shape of all the other bands).

Response:
FKBP51 and SEC22B are indeed the same. We repeated them in the supplements for completion. We realized it can lead to confusion and therefore proceeded to remove SEC22B from the supplementary figure (S1a), but kept FKBP51 since it is the immunoprecipitated protein.
(9) Line 184-185: Seems to be out of place, proteins shown here look to be part of previous set of experiments (first section in results).

Response:
We did not use SIM-A9 cells for the first section of the results. However, we acknowledge that this sentence is not well incorporated in the paragraph and, therefore, rewrote it.

Response:
WT SIM-A9 cells underwent the same transfection procedure as the Atg5 KO cells but without the gRNA targeting Atg5. SEC22B and FKBP5 KO SIM-A9 cells were generated with the Alt-R CRISPR-Cas9 system from Integrated DNA Technologies. WT control cells were identified by WB after single-cell cloning procedures and therefore underwent the same transfection and isolation procedure as the KO cells.
(11) Line 214: Authors did not discuss CTSF despite it represented the biggest fold change in Fig 3c.

Response:
The deeper investigation of the effect of stress on the secretion of cathepsines is out of the scope of our manuscript, but is part of a follow up study (Niemeyer et al., in preparation).
(12) Due to the limit of allowed references in the main manuscript, the references of Table  1 can be found as Supplementary references file. We added the missing link to it in the Table legend (lines 1308-1309). We ask the Editor for suggestions for the best format for this purpose.

Response:
As control, an empty vector was used (same vector as ect. FKBP51).
(14) Fig S4: Describe the vehicle used in the experiment. Indicate meaning of lines (inhibitor)

Response:
We added the information regarding the used vehicle to the method "Treatments" section (line 545). We also indicated the meaning of lines in panel c.
(15) Readouts of Dex treatments need to be shown throughout. Charcoal stripped media should also be used to remove the effects of FBS hormones.

Response:
In our experience, glucocorticoids contained in FBS are in too low concentrations to elicit any GR activation. However, to ensure that this is true for the mechanism analyzed in this manuscript, we performed additional experiments with charcoal stripped medium. We measured secreted CTSD and MMP9 via ELISA. The figure below shows the results from WT and Atg5 KO SIM-A9 cells treated with vehicle or 300 nM of dexamethasone for four hours and cultured in FBS-or charcoaled stripped serum (CSS)-supplemented culture medium for 24 h hours (n=3).
From these results, we can observe a rather diminished response to GR activation in the presence of complete FBS and, as a consequence, the significant results obtained using complete FBS do rather strengthen our output and conclusions.
In the tables below, the complete statistics regarding the multiple comparison are shown, confirming that complete FBS does not affect the outcome of our experiments.
(16) Confirmation of FKBP51 levels and GR activity should be confirmed in each cell line being used.

Response:
Dexamethasone stimulations in SIM-A9 was performed and FKBP51 levels were analyzed via western blot. Dexamethasone treatments led to a significant increase of FKBP51 levels confirming the dexamethasone-induced GR activation and increased expression of FKBP51 in this cell line. These data are shown in Supplementary Fig. S2a.
(17) Reviews are referenced, where original manuscripts should be referenced instead. The introduction would benefit from additional references. Some references are misleading, for example Ref 1, which does not mention bipolar or schizophrenia, and Ref 8, which is not the first time secretory autophagy is described.

Response:
Due to the limit in number of references that are allowed we sometimes preferred to reference the reviews to convey more information especially in reference of a broader topic such as secretory autophagy, for which there is no real first publication, but rather a first publication in which the term was coined (Jiang et al., 2013). However, we now added more direct references in addition to the reviews in order to better specify our sources.
(18) Baf should be defined in the results section.

Response:
It is defined in lines 198-202.
(19) Line 395: Secretory pathway is activated only after prolonged or excessive stress? This does not support their stress paradigm since the authors describe footshock as an acute stressor.

Response:
Footshock is an acute but very strong stress. It, therefore, falls into the category excessive stress.

Response:
References were added.

Response:
The discussion was thoroughly revised and adapted to the new data. In this optics we also incorporated the discussion about NMDAR, BDNF and synaptic plasticity in a more cohesive way.

Response:
We better defined this point both here (line 523). However, we would like to specify that throughout the whole manuscript, when we talk about stress, we always refer to GC-mediated stress, as stated in the introduction (lines 96-97).
(23) Line 443: Need to discuss the "contrasting" findings-"However, despite some consistent findings, other studies report incongruent or contrasting results".

Response:
The discussion was thoroughly revised and adapted to the new data. In this process, this sentence was eliminated.
(24) Methods are missing for some technical aspects, including descriptions of the experiments for Figure 6 and Baf treatments.
SAFit1 and Baf treatments were indeed missing and were added in the section "Treatments" (lines 545-550) (25) Authors must include exact number of n values for in vitro and in vivo experiments. Also, report the number of times the experiment was repeated, or replicates included in the final analysis.

Response:
The exact n values can be found in each figure legend and all information will be reported in detail in the source data table upon acceptance. However, all experiments were performed in at least three technical replicates and at least three biological replicates.
(26) Mention if all animal procedures followed standard policies animal care. Include age, sex and number of animals used for each experiment. Overall, the Ns are very low for these studies and should be increased. Sex of the mice should also be considered as an independent variable. Time of day for the experiments should be carefully described in the methods

Response:
We added the first information in the Methods section "Animal housing conditions" (lines 666-673). We specify here that all procedures were done in accordance with European Communities Council Directive 2010/63/EU and approved by Government of Upper Bavaria. All mice used in in vivo experiments were males. FKBP51-KOs and respective WTs at the age of 14-16 weeks were used in FS experiments ( fig. 5 c-f). C57Bl/6NCrl mice at the age of 13-15 weeks were used in FS/ ULK1 inhibitor experiments ( fig. 5 g-j). Microdialysis experiments were performed during the first half of the day at an inverted day-night light cycle. FS was applied between 11.00, and 12.00 am.
(27) Explain the rationale for choosing one-tailed over two-tailed unpaired t tests.

Response:
We know that Dex treatment, i.e. GR activation, leads to FKBP51 induction and, therefore, we expect a change in only one direction. (29) All references should be in the same format. (Some include web link and DOI, see #26 and 35)

Response:
The bibliography formatting has been revised and modified according to the feedback.
(30) Fig S3: Equal amount of Gapdh protein cannot be appreciated in the figure.

Response:
Quantifications of the blot were added and GAPDH quantifications are indicated in the following graph. Despite being the GAPDH signal slightly lower in the KO compared to the WT line, this difference is negligible compared to the difference in Atg5 signal in WT compared to KO, where in the KO line the signal is not detectable.
We thank Reviewer 3 very much for their positive and constructive feedback. Their interesting observations led us to further investigate and clarify the role of stressprimed secretory autophagy on the neurophysiological level.
Reviewer #3 (Remarks to the Author): FKBP51 (gene name: FKBP5) is a glucocorticoid (GC) receptor binding protein, which acts as a co-chaperone of heat shock protein 90 (HSP90) and regulates GC-mediated stress. This protein is also known to be associated with mental disorders.
The authors of this study showed previously that GC-mediated stress leads to the activation of macroautophagy, which is regulated by FKBP51 (Gassen etal., pLos Med., 2014). In the present study, they show that GC induces another type of autophagy called secretory autophagy and that FKBP51 plays an important role in this secretory autophagy by interacting with specific SNARE proteins (Fig. 1). They further show that MM9 is a novel cargo molecule of GC-mediated secretory authophagy (Fig. 3), that FKB51 is critical for secretion of MMP9 (Fig. 4), and that the MMP secretion plays an important role in BDNF maturation (Fig. 4, 5).
The authors demonstrated these results using FKBP51 overexpressed HEK-293 cells, Atg5 KO and FKBP-5 KO cell lines as well as FKBP5 KO mice. The story is novel, logical and supported by an impressively large amount of data which appear to be sound and quite convincing. I have two concerns however.
(1) The authors provide strong cellular evidence that FKBP51 is critical for secretory authophagy of MMP9 leading to BDNF maturation. However, I feel that the biological significance for this role of FKB51 in living mice is missing or obscure.
As the authors stated in Abstract, BDNF is essential for synaptic plasticity. Thus, I would imagine that the reduced BDNF maturation in the stress response by FKBP5 KO has strong a strong behavioral phenotype in the BDNF-related behavior, such as learning and memory. However, previous study seems to fail to show such phenotype in the FKBP5 KO mice. For instance, O'Leary et al. (2011, pLos One) described that FKBP51 KO mice showed antidepressant behavior without affecting cognition and other basic motor functions. This previous result does not seem to be consistent with the proposed function of FKBP51 in stressinduced BDNF maturation. The authors of the present study should show some sort of behavioral or neurological phenotype associated with the reduced BDNF maturation by FKBP5 KO mice. Without such evidence, the readers of Nature Communications remain puzzled about the role of FKBP5 in stress-induced synaptic plasticity and BDNF maturation.

Response:
We agree with reviewer #3 that further investigation on the learning and memory effect would be of extreme interest. However, we think that acquiring such answers is out of the scope of this manuscript, but would rather represent the subject of an interesting follow-up project. The possible physiological and behavioral downstream effects could be many and variable. However, in order to shed some light on possible effects of increased mBDNF on neuroplasticity, we performed 2-photon experiments. The resulting data (Fig. 6) provide a validation to the physiological effect of stress-induced secretory autophagy not only on BDNF maturation but also on the consequential change of neuroplasticity in ex vivo murine organotypic brain slices. With the obtained results we could confirm our previous hypotheses and corroborate the effect on a neurological phenotype.
Regarding the absence of cognitive effects of the lack of FKBP51 reported by O'Leary et al., an important aspect to consider is that for that paper only old mice (between 17 and 22 months of age) were used. Age is a fundamental component when analyzing cognitive behaviors and the outcome of the same experiment might have been different in younger animals. The same is true for other variables such as type and intensity of stress. With our results we highlight the fact that there is a novel pathway that links excessive stress to neuroplasticity and we hypothesize that this is a mechanism regulating stress adaptation and possibly be correlated to psychiatric disorders when dysregulated. The exact consequences of such pathway need to be analyzed into detail and differentiated from other similar pathways triggered by similar but different stimuli.
(2) Co-IP data in Fig. 1J is NOT described correctly. Fig. 1J is labeled as "GFP-IP", which I believe is correct. Based on the figure, I believed that the authors overexpressed SEC22B as GFP-fusion protein and IPed using GFP-Ab. However, the used antibody was labeled as "FLAG-Ab". This should be "GFP-Ab". The Figure legend to Fig. 1J described this experiment as "FLAG-tagged FKBP51 co-IP (FLAG-IP). I believe that the legend should be "GFP-tagged SEC22B co-IP (GFP-IP).

Response:
Thank you for noticing. It is was indeed a labelling mistake and we corrected it.

Reviewer #4
We thank Reviewer #4 for their insightful feedback and suggestions. We addressed all the raised issues by performing additional experiments and by editing the manuscript in order to answer all the concerns.
Reviewer #4 (Remarks to the Author): In this manuscript by Martinelli et al., termed " Stress-primed secretory autophagy drives extracellular BDNF maturation" the authors identify the matrix metalloproteinase 9 (MMP9) as a stress-induced secreted protein involved in the cleavage of pro-brain derived neurotrophic factor (proBDNF) to its mature form (mBDNF). The authors demonstrate the involvement of the co-chaperone FK506binding protein 51 (FKBP51) in stress-elevated secretion of MMP9 in the mouse brain, exploiting in vivo microdialysis in WT and Fkbp5 KO mice. The importance of the autophagy machinery for the stress elevated secretion is assessed in WT mice by including a ULK1 inhibitor. The authors claim that stress-induced secretion of MMP9 is through secretory authophagy, facilitated by FKBP51.
The novel finding in this manuscript is the involvement of FKBP51 in stresselevated secretion of MMP9 in the mouse brain, resulting in maturation of BDNF. BDNF is essential for synaptic plasticity and altered BDNF signaling is associated with stress-related psychopathology. Hence, this finding is of general interest and contributes to the understanding of MMP9 secretion in the CNS. Overall, the biochemical data are well performed and the use of proteomic methods, data mining and in vivo microdialysis reflect an extensive amount of work. Nevertheless, the manuscript has some critical shortcomings that have to be addressed before publication. The authors do show the presence of CTSD in a co-IP of ectopically expressed FLAG-TRIM16 in SH-SY5Y cells (Fig. 1e). However, that does not necessarily mean that TRIM16 binds to CTSD since IP-based interaction detection can reflect indirect binding of the proteins in question. Secondly, FKBP51 is a known co-chaperone of heat shock protein 90 (HSP90) and HSP90 has been assigned a key role in secretory autophagy of IL-1β, mediating import of IL-1β into the autophagsomal intermembrane space (Zhang et al., 2015; doi: 10.7554/eLife.11205). The authors do not address this point at all other than showing that mutating the HSP90 binding site of FKBP51 reduces a potential interaction between FKBPB51 and galectin 8 (Fig. 2b). Finally, the authors show that FKBP51 is essential for the association of SEC22B with its Q-SNARE partners in SH-SY5Y cells (Fig. 1j). However, there are no data presented that demonstrate the importance of the formation of this SNARE complex for stress-induced MMP9 secretion in SIM-A9 (microglia) cells or mice. Detailed comments and suggestions are included below.

Response:
Concerning the use of CTSD instead of IL-1b as an established cargo, this was done for two reasons: 1) the implication of IL-1b in this pathway is the focus of another study we are currently completing (Hartmann et al., in preparation). We attach here confidential results showing that IL-1b is regulated in the same way as CTSD.
Quantification of IL1b via ELISA assay. IL1b from supernatants was measured via ELISA after SIM-A9 cells were treated as follow a) LLOMe for 4, 8 and 24 hours or vehicle for 24 hours. b) 3nM, 30nM and 300nM Dex or vehicle for 4 hours. c) 300nM Dex or vehicle for 4 hours in WT and Atg5 KO SIM-A9 cells. d) transfected with FKBP51 expressing plasmid or control vector. *P < 0.05; ***P< 0.001; ****P< 0.0001. Tukey's multiple comparison test was used for a, b and c; unpaired t-test was used for d. Significances in c are referred to comparison of Dex 300nM with each of the other conditions. Error bars expressed in SEM.
2) IL1b was not detected as part of the secretome in the MS experiment, probably because below the detection limit. Therefore, to give a complete picture, we decided to opt for CTSD as another well-characterized secretory autophagy cargo.
Finally, regarding the importance of the SNARE complex formation for the stressinduced MMP9 secretion, we generated a SIM-A9 SEC22B KO line with which we demonstrated that the absence of SEC22B impairs not only the secretion of MMP9, but also of CTSD. Detailed results are shown in response to comment 6.
Major comments: (1) Figure 1b,c,d and e and figure S1 a and b: Interaction between FKBP51 and SEC22B or TRIM16 is implicated from reciprocal co-IPs. To demonstrate a direct binding between FKBP51 and SEC22B or TRIM16 the authors could use a GST-pulldown assay with labeled in vitro translated proteins. Furthermore, co-localization images in cells to visualize FKBP51 together with SEC22B or TRIM16 would be helpful. The same applies for the implied interaction between TRIM16 and CTSD.

Response:
To address this point (addressed also by Reviewer #2), we performed the suggested pull-down experiments to verify the direct interaction between FKBP51 and TRIM16 and found that there is indeed a direct interaction in vitro (supplementary Fig. S1c). However, we also rephrased the parts describing these results replacing the term "interaction" with "association", meaning an either direct or indirect interaction. In fact, for the presented mechanism it is irrelevant whether the interaction is direct or not. What we show is that the proteins form a complex for which they are immunoprecipitated together, and, more importantly, this association (whether it is direct or not) affects the pathway.
(2) For the blots in figure 1d, e and g, which form of CTSD is shown/recognized by the antibody? CTSD exists in different forms with the inactive precursor of the enzyme, procathepsin D, being cleaved, resulting in different forms of mature/active cathepsin D.

Response:
As shown in the representative blot below, the predominant and quantified CTSD form is the cleaved/mature one (CTSD heavy chain).
(3) Figure 1l-"Schematic overview of the interactions of FKBP51 in the secretory autophagy pathway": Here FKBP51 is shown to interact with GAL8 but no data have yet been presented to show this. TRIM16 binds to GAL8 and the figure should indicate that. Furthermore, HSP90 is shown as a binding partner of FKBP51 but HSP90 is not included in the blots of any of the IPs in figure 1. Furthermore, there are no data presented indicating the importance of FKBP51 for transfer of the TRIM16-cargo (CTSD) to the autophagosome or data indicating that HSP90 is not present. TRIM16 association to SEC22B is independent of FKBP51 according to figure 1e. And there are no comments or experiments addressing how CTSD, that normally resides in lysosomes, is translocated into the lumen of autophagosomes prior to its secretion. Therefore, the claim on page 6 line 148-149. "From these data, FKBP51 results to be involved in several key steps of the secretory autophagy pathway (Fig 1l)", appears as an overstatement.

Response:
With the FKBP51-IP displayed in Fig 2b, we show that FKBP51 associates with GAL8. Whether this association is direct or indirect is irrelevant for the proposed mechanism.
In fact, we state that this association is, at least partially, indirect and occurs via HSP90. With additional WB analyses we detected HSP90 in the FKBP51 eluate, as further confirmation of our hypothesis (these data have been added to Fig. 2b). The model represented in Fig 1l, takes into account data from Fig. 2 (as stated in the image). Taken together these data we, therefore, do not think that asserting that FKBP51 is involved in several key steps of secretory autophagy is an overstatement because being involved represents a very mild action verb and, for that meaning, we believe to have the adequate supporting data.
(4) In figure 2c and 2d the authors use a tandem tagged (mRFP-GFP) galectin 3 (tfGal3) in SH-SY5Y cells to monitor lysosomal damage. The reduction of the GFP signal is a result of acidification of tfGal3. Gal3 is recruited to damaged lysosomes and Gal3 becomes acidified trough lysophagy. Lysophagy involves autophagosomal engulfment of damaged lysosomes that subsequently become degraded by fusion with intact lysosomes (Maejima et al., 2013; doi: 10.1038/emboj.2013.171). LLOMe induces lysosomal damage that culminates in lysophagy and Dex appears to be able to do the same. Inhibition of lysosomal acidification with BafA1 abolishes the effect. Therefore these data actually show degradation of Gal3 on damaged lysosomes through autophagy. The authors should comment on how they envision the effect of dex on lysosomes and how this relates to secretory autophagy.

Response:
With our study, we do not expect to answer the question of how Dex can lead to lysosomal damage (e.g. lysosomal membrane permeabilization) as it would be a far to complex topic to investigate and is beyond the interest of this manuscript. However, with our data we can confidently affirm that Dex indeed leads to lysosomal damage and activates the repair mechanism involving the recruitment of galectines on the lysosomal membrane. As for the mechanism leading to the lysosomal damage, many could be the hypotheses, but having no data to this regard we are reluctant to postulate any. Here are some articles that describe the mechanisms (and its complexity) that can lead to lysosomal damage and that are still not fully unraveled: Jia et al., Galectins Control mTOR in Response to Endomembrane Damage, Mol. Cell, 2018; Napolitano and Ballabio, TFEB at a glance, J. cell sci., 2016. A hypothesis of a more direct effect of GCs on the biophysical properties of cell membranes, that we can apply to the mechanism leading to lysosomal damage, was described by Van Laethem et al. (J Immunol, 2003). In their study, dexamethasone caused alterations in lipid raft palmitate content inducing a decline in the proportion of saturated fatty acids while increasing unsaturated ones. From a biophysical perspective, the changes in membrane lipid composition increase fluidity and therefore it is tempting to speculate that these changes also affect lysosomal osmotic stability (Yang et al., Cell Biol. Int., 2013).
(5) In figure 2 e) and 2 f) SIM-A9 secretion of CTSD in response to LLOMe and dex treatment, respectively should also include BafA1 treatment to determine if the secretion is dependent on functional lysosomes or not.

Response:
We performed additional experiment that were added to supplementary Fig. S2 as panel c, where we show that Baf has the expected effect on CTSD secretion (i.e. reversion of Dex and LLOMe effects) and confirmed that CTSD secretion correlates indeed with lysosomal damage.
(6) In figure 4 the dex induced MMP9 secretion should be shown in FKBP51 KO SIM-A9 cells as well to complement the in vivo results in figure 5. Furthermore, in order to link MMP9 secretion to secretory autophagy the authors could use siRNA knockdown of TRIM16 or SEC22B in these cells. The presence of MMP9 in an IP of TRIM16 or colocalization study of MMP9 with TRIM16 in cells would also be desirable.

Response:
To answer this question, we generated Fkbp5-KO and Sec22b-KO SIM-A9 cells and analyzed CTSD, MMP9, proBDNF and mBDNF secretion via WB of supernatants. In line with the rest of our data, results of this experiment showed that the secretion of CTSD, MMP9 and mBDNF is both SEC22B and FKBP51 dependent as is significantly impaired in the both KO cell lines compared to WTs, while the secretion of proBDNF is unaffected by FKBP51 or SEC22B (see Fig. S4 f and g).
(7) Figure 7-"Schematic representation of the findings and proposed model": In a, TRIM16 is shown to interact with MMP9. Again, there are no data in the manuscript that demonstrate this interaction and this schematic drawing is thus not accurate.

Response:
We rephrased the figure title as "proposed model based on the findings".
The manuscript by Martinelli et al. "Stress-primed secretory autophagy drives extracellular BDNP maturation" described the mechanism of enhancement of secretory autophagy by glucocorticoid-induced stress. The authors use interactomics and secretome analysis by mass spectrometry to identify proteins involved in the process and propose an elegant step-by-step mechanistic model validated by several other methods. The paper is well written, the findings are novel and this reviewer supports the publication in Nature Communications which will allow these results to reach a broad readership. There are a few minor concerns, mostly technical in nature, that should be addressed before acceptance.

Detailed comments:
(1) Since TRIM16 was confirmed to be an interactor of FKBP51 by Western blot, but not originally found in the MS dataset, can the MS data be researched and perhaps TRIM16 peptides can be found (maybe with the help of the inclusion list?)

Response:
TRIM16 was not found in the FKBP51 interactome list, nor in the control one. We think that this is due to a below the detection level expression of this protein. In fact, we confirmed the interaction of FKBP51 with TRIM16 via a pull down assay ( Supplementary Fig. S1c).
(2) For the interactome analysis, the transfection with a vector containing FLAG only was used. Can the authors include more description of how the control (unspecific) binders were eliminated? The only explanation I could found is in lines 651-651, that the proteins overlapping from all four replicates were counted as interactors. This is not sufficient.

Response:
We considered as interactors of FKBP51 only proteins that fulfilled both of the following criteria: • Bind only to FKBP51-FLAG and not control FLAG • Be found in all four replicates of FKBP51-FLAG transfected cells This selection method is quite stringent as it results in the exclusion of false negatives, but allows us to be confident in the identification of the positive candidates.
(3) For the secretome analysis, the media supplemented with FBS was used throughout the whole experiment. Is that correct? If so, how was the signal suppression by the overwhelming amount of protein handled? Was the albumin removed? This was not an issue for detection because the labeling was used, but signal suppression would be an issue anyway. Can the authors comment on that?
Yes, the secretomics experiment has been carried out in the presence of FBS to avoid any artefacts introduced by serum starvation. In order to study secreted proteins of low intensity irrespective of e.g. high-intense albumin in the background, we performed labeling of newly synthesized proteins and selective enrichment according to a protocol that has been published before (Eichelbaum K, Winter M, Diaz MB, Herzig S, Krijgsveld J: Selective enrichment of newly synthesized proteins for quantitative secretome analysis. Nat Biotech 2012, 30(10):984-990.). In more detail, the cells were labeled with azide-containing azidohomoalanine that is substituting methionine in newly synthesized proteins. In a second step, these proteins were selectively enriched and covalently linked to alkyne beads by click chemistry. Consequently, other non-labeled proteins such as FBS-derived albumin were removed before subsequent LC-MS/MS analysis was performed.
(4) Another useful clarification of the secretome analysis would be the comparison of growth rates and cell death between the wild type and the Atg5 KO cells. Are they identical in this respect, and if not, how was the data normalized?