Mitochondrial dysfunction heightens the integrated stress response to drive ALS pathogenesis

  1. Curran Landry
  2. James Costanzo
  3. Miguel Mitne-Neto
  4. Mayana Zatz
  5. Ashleigh Schaffer
  6. Maria Hatzoglou
  7. Alysson Muotri
  8. Helen Cristina Miranda

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Abstract

Vesicle-associated membrane protein-associated protein-B (VAPB) is an ER membrane bound protein. VAPB P56S causes a dominant, familial form of amyotrophic lateral sclerosis (ALS), however, the mechanism through which this mutation causes motor neuron (MN) disease remains unknown. Using inducible wild type (WT) and VAPB P56S expressing iPSC-derived MNs we show that VAPB P56S, but not WT, protein decreased neuronal firing and mitochondrial-ER contact (MERC) with an associated age-dependent decrease in mitochondrial membrane potential (MMP); all typical characteristics of MN-disease. We further show that VAPB P56S expressing iPSC-derived MNs have enhanced age-dependent sensitivity to ER stress. We identified elevated expression of the master regulator of the Integrated Stress Response (ISR) marker ATF4 and decreased protein synthesis in the VAPB P56S iPSC-derived MNs. Chemical inhibition of ISR with the compound, ISRIB, rescued all MN disease phenotype in VAPB P56S MNs. Thus, our results not only support ISR inhibition as a potential therapeutic target for ALS patients, but also provides evidence to pathogenesis.

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    Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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    Reply to the reviewers

    General Statement:

    We appreciate the reviewers for acknowledging the impact of our work to the field of neurodegeneration and motor neuron diseases as well as for the understanding of the biology and function of VAPB itself; “the idea of assaying the function of ALS-causing VAPB mutants in iPSC-derived neurons is great and would be a great asset to the field” (Reviewer 1) “The new iPSC-derived system to study VAPB mutations in human motor neurons is significant and has led the authors to discover new functions for VAPB (i.e., mitochondria-ER contacts).” (Reviewer 2). The main concern raised by both reviewers is that the doxycycline inducible VAPB iPSC lines may not fully recapitulate the physiological environment found in patients, as patients are heterozygous for the VAPB P56S mutation, and our lines had VAPB under the control of an exogenous doxycycline inducible promoter. While we maintain that the doxycycline inducible lines do provide their own substantial benefits to the interrogation of the ALS pathogenesis, namely the opportunity to identify mutant VAPB interactors compared to wild type VAPB interactors through proteomics, as well as to identify pathogenesis associated to mutant VAPB without the confounding effects of wild type VAPB, we do agree with both reviewers that the inclusion of heterozygous patient iPSC lines would increase the significance of our study. Thus, in this revised manuscript we have included iPSC patient lines harboring the VAPB P56S mutation which we reprogrammed in our lab and to uphold the highest standards in the stem cell field we also performed CRISPR mediated genomic editing to generate the isogenic corrected pair. In our assessment of the ALS patient iPSC-derived motor neurons, we have already observed the same mitochondria and translation dysfunction previously described in our work with the doxycycline-inducible VAPB P56S mutant iPSC lines. Most importantly, these phenotypes were also similarly rescued by the integrated stress response inhibitor (ISRIB). Collectively, these findings suggest that the proposed mechanism initially identified in doxycycline-inducible iPSC-derived motor neurons is preserved in ALS patient iPSC-derived motor neurons.

    Reviewer #1 Major Point 1. The method of knocking out and selecting an inducible line in problematic. VAPB is an essential gene-patients with P56S are always heterozygotes, since nonfunctional VAPB is embryonic lethal. Selecting a knockout cell line is already choosing a parent that is very far from physiological, and the reexpression of P56S VAPB as the sole form also is not a good a model for understanding the contributions of P56S to disease. This approach is unusual, as it seems to overlook the advantages of working with iPSCs and patient-derived neurons. Unfortunately, the value of this amazing and rare system is diminished by the design of the selection method.

    *Reviewer #2 Major Point 1. Why did the authors decide to make VAPB knockouts and then introduce the WT or P56S VAPB constructs on a lentivirus instead of generating the point mutations (or correcting them) directly in the endogenous locus? Data in Extended Fig. 1c and Extended Fig. 2a indicate significant differences in either the kinetics of WT vs. P56S VAPB expression (1c) or levels (2a). It seems important to be able to compare comparable levels of WT and mutant proteins, especially for the interpretation of the subsequent IP-MS experiments to identify PTP151. The authors may wish to consider generating (or obtaining) isogenic lines harboring the mutations at the endogenous locus so that equal levels of expression of WT and mutant VAPB can be assessed. *

    Carried Out Revisions

    The development of the inducible system for VAPB was specifically designed to enable a systematic investigation of the effects of mutant VAPB (VAPB P56S) on cellular homeostasis while minimizing confounding influences from the wild-type (WT) protein. Additionally, this system allowed us to assess VAPB P56S binding partners and compare them to those of VAPB WT, which would not have been feasible in the context of heterozygous ALS8 patient cells.

    In response to Reviewer 2’s concern regarding differences in VAPB WT and VAPB P56S expression levels, we utilized ALS8 patient cells and familial controls to calibrate the doxycycline dose response. This approach allowed us to precisely adjust VAPB protein levels in the inducible system to match those observed in ALS8 patient and familial control iPSCs. As a result, the inducible VAPB P56S iPSCs recapitulate the VAPB expression levels found in ALS8 patient iPSCs, whereas the inducible VAPB WT iPSCs mimic the levels present in familial control iPSCs. Furthermore, the differential expression of VAPB between ALS8 patient and control cells is well documented in the literature (Mitne-Neto, et al., 2011)

    Nonetheless, we acknowledge the significance of studying ALS patient-derived iPSCs. To address this, we obtained fibroblasts from an ALS8 patient carrying the heterozygous VAPB P56S mutation, originating from a genetic background distinct from the cells used in our inducible system. These fibroblasts were reprogrammed into iPSCs in our laboratory, followed by CRISPR/Cas9-mediated genome editing to generate isogenic corrected iPSCs as controls.

    The resulting iPSC isogenic pair was differentiated into motor neurons following the protocol described in our manuscript. Notably, ALS8 patient iPSC-derived motor neurons exhibited reduced mRNA translation, as assessed by the SUnSET assay (Fig. 6A), along with a decrease in mitochondrial membrane potential, as determined using the JC-1 assay (Fig. 6B). These findings confirm that the hypotranslation and mitochondrial dysfunction initially identified in VAPB P56S doxycycline-inducible iPSC-derived motor neurons were successfully recapitulated in ALS8 patient iPSC-derived motor neurons. Furthermore, ISRIB treatment effectively rescued these phenotypic defects.

    Overall, these results demonstrate that the molecular and cellular abnormalities identified in the original inducible system can be reliably reproduced in an ALS patient-derived model with a different genetic background, thereby reinforcing the significance and broader applicability of our findings.

    Currently, we are investigating the electrophysiological properties of ALS8 patient iPSC-derived motor neurons compared to the isogenic control using the multi-electrode array (MEA) system. If a reduction in electrophysiological activity is observed, consistent with our initial findings in doxycycline-inducible VAPB P56S iPSC-derived motor neurons, we plan to treat the heterozygous patient-derived cultures with ISRIB on day 45 of differentiation. This will allow us to determine whether neuronal firing deficits in the heterozygous patient-derived motor neurons can be rescued.

    All other concerns have been addressed in this revision.

    Citation:

    1. Mitne-Neto M, Machado-Costa M, Marchetto MC, Bengtson MH, Joazeiro CA, Tsuda H, Bellen HJ, Silva HC, Oliveira AS, Lazar M et al (2011) Downregulation of VAPB expression in motor neurons derived from induced pluripotent stem cells of ALS8 patients. Hum Mol Genet 20: 3642-3652 Reviewer #1 Major Point 2. The interactome analysis is not controlled properly to interpret. It is not the total amount of VAPB that needs to be used as the normalization control, since it is already known 90+% of the P56S VAPB is in cytoplasmic aggregates. The authors need to normalize to the amount of VAPB that made it to the contact sites-a much smaller amount in the cells expressing the diseased form. For example, the fact that the authors can still pull down detectable PTPIP51 in Fig. 2e actually argues for the opposite conclusion than what the authors have stated-if the authors have actually expressed just P56S in a true knock out condition, this means that P56S CAN still bind to PTPIP51 (and possibly even better than WT, as several previous papers have suggested-since there is ~100-fold less available for binding). Without an appropriate normalization, the authors cannot make any conclusion about how to interpret the results of this part of the paper.

    Carried Out Revisions

    We sincerely thank Reviewer 1 for highlighting this critical point. Previous studies have demonstrated that the VAPB P56S mutation increases its binding affinity for PTPIP51; however, it has been proposed that the overall reduction in VAPB levels in cells harboring the P56S mutation leads to a decrease in ER-mitochondrial contacts despite the enhanced affinity (De Vos et al., 2012).

    To address this, we have repeated the co-immunoprecipitation experiment and normalized the data to VAPB levels. Consistent with Reviewer 1’s hypothesis, when normalized to soluble VAPB, we observe an increased affinity of VAPB P56S for PTPIP51. However, the total amount of PTPIP51 co-immunoprecipitated with VAPB remains significantly lower in the mutant compared to WT, likely due to the overall reduced levels of soluble VAPB P56S. This finding aligns with both Reviewer 1’s comment and the previous observations reported by De Vos et al. (2012).

    Figure 2E has been updated to reflect the normalized co-immunoprecipitation data.

    Citation:

    1. De Vos, K. J.* et al.* VAPB interacts with the mitochondrial protein PTPIP51 to regulate calcium homeostasis. Hum Mol Genet 21, 1299-1311, doi:10.1093/hmg/ddr559 (2012). *Reviewer #1 Major Point 3. The electron microscopy data is not interpretable in this form. The authors have provided no data at all on how analysis was performed, how contact sites were defined, how samples were collected and ensured to be representative, blinding that was performed, how sources of bias were accounted for, etc. It is clear even from what little is shown that the authors are not focused on what matters to address their own questions. For example, apart from the P56S Day 35 example, none of the "contact sites" selected for the figure are even possible to be mediated by VAPB, since the distance between the ER and the mitochondria is too far for the maximum tethering distance of VAPB-PTPIP51. Since the authors have neglected to include scale bars in their zooms, the reader cannot be sure of the distance, but it is clearly in excess of 50 nm since there are obviously visible ribosomes between the two organelles. Additionally, the authors provide no information on what "% mitochondria in contact with ER" means (By organelle? By unit surface area? Is the data grouped by cell or all comes from a single cell? How do you account for contact sites vs. proximity by crowding? Etc.). *

    Carried Out Revisions

    We thank Reviewer 1 for their insightful comments on the analysis of the electron microscopy (EM) data and recognize the need for greater clarity in describing our quantification approach. To address this, we have revised the Electron Microscopy section of the Methods to explicitly detail our methodology for quantifying ER-mitochondria-associated membranes (ER-MAMs), as follows:

    "A series of images at various magnifications were provided, and data were collected from unique images at the highest magnification for each condition: D35 WT (13 unique images), D35 P56S (21 unique images), D60 WT (13 unique images), and D60 P56S (18 unique images). All images for a given condition originated from a single well of a 12 mm Snapwell™ Insert with 0.4 µm Pore Polyester Membranes (Corning). No information on cell grouping or sampling strategy was supplied with the images; therefore, we treated the dataset as a random sampling of the culture. Images were blinded, and quantification was performed using FIJI. Mitochondria were identified based on the presence of cristae and a double membrane. The mitochondrial perimeter was traced using the free-draw tool, and the length of ER membranes within 50 nm of this perimeter was quantified. The final measurement represents the percentage of each mitochondrion’s perimeter in contact with the ER, aggregating all visually distinct ER-MAMs, as continuity beyond the imaging plane cannot be determined (Cosson et al., 2012; Csordás et al., 2010; Stoica et al., 2014). Each data point on the graph corresponds to a single mitochondrion, with data collected from multiple cells across the unique images provided by the Core, originating from a single biological replicate."

    Regarding the quantification of ER-MAM distances, VAPB has not been definitively localized exclusively to either the rough or smooth ER. To ensure comprehensive analysis, we quantified ER-MAMs without restricting our assessment to a specific ER subdomain. We adopted a 50 nm threshold as the maximum distance for defining ER-MAMs, a well-established criterion that Reviewer 1 also referenced.

    Furthermore, we disagree with Reviewer 1’s assertion that the presence of ribosomes should justify extending the ER-MAM threshold beyond 50 nm. Ribosomes in human cells have a well-documented diameter of 20–30 nm (Anger et al., 2013), which does not support the claim that an observed ribosome within the contact site necessitates a redefinition of the ER-MAM boundary.

    We stand by our methodological approach and have updated the manuscript to ensure precision and clarity in our EM data analysis.

    Citations:

    1. Cosson, P., Marchetti, A., Ravazzola, M. & Orci, L. Mitofusin-2 independent juxtaposition of endoplasmic reticulum and mitochondria: an ultrastructural study. PLoS One 7, e46293 (2012).
    2. Csordás, G.* et al.* Imaging interorganelle contacts and local calcium dynamics at the ER-mitochondrial interface. Mol Cell 39, 121-132 (2010).
    3. Stoica, R.* et al.* ER–mitochondria associations are regulated by the VAPB–PTPIP51 interaction and are disrupted by ALS/FTD-associated TDP-43. Nat Commun 5, 3996 (2014).
    4. Anger AM, Armache JP, Berninghausen O, Habeck M, Subklewe M, Wilson DN, Beckmann R. Structures of the human and Drosophila 80S ribosome. Nature. 2013 May 2;497(7447):80-5. doi: 10.1038/nature12104. PMID: 23636399. We would like to thank the Editor of Review Commons for clarifying Reviewer #1’s Major Point 4 and will be responding to the Editor’s interpretations as detailed in the Editorial Note.

    Reviewer #1 Major Point 4. The strange pooling of data without explanation, unusual sample sizes, and lack of clarity about statistical testing, false hypothesis testing, and really any clear rigor in statistics of any kind make it impossible for a reader to have any confidence in the results presented here. The fact that every experiment in the paper has just enough n to trigger statistical significance as determined by the authors raises some concerns, suggesting potential biases. The reliability of these conclusions is questionable, especially if the authors were blinded to the identity of their own samples. This is particularly relevant for the EM data, where the determination of contact sites appears to have been made subjectively.

    Reviewer #1: "The strange pooling of data without explanation"

    - When looking into the figures and their captions in more detail, we could also not understand the nature of the replicates and how the data was aggregated or “pooled”. In Figure 1, the stated number of replicates is "N=8 separate wells”. It is unclear whether these are 8 wells from a single dissociation/replating procedure (the procedure is described in Materials & Methods as follows: "Motor neurons were dissociated on day 25 of differentiation and re-plated onto 48-well MEA plate") or whether the eight are sampled across multiple plates across cultures obtained from independent dissociations procedures.

    • We apologize for the lack of clarity and specificity. We have updated the Multi-Electrode Array Recordings portion of the Methods Section with the following: “iPSC-derived MNs from a single well of a 6-well plate thawed as day 15 MNP were dissociated and plated across 8 wells of the MEA plate. Each point on the graph is an average of the weighted mean firing rate of those 8 wells, normalized for cell count across genotypes, obtained after all firings were recorded by dissociating 2 wells per line, counting and averaging the cell numbers, and then normalizing all firings by the ratio of cell number between WT and P56S. Wells with no firing detected were excluded from quantification.”

    - In Figure 3, the number of replicates is "N=13-21 images”. Here, it is unclear whether these images come from the same or independent samples, how many quantifications were performed per image, and how many images per sample were used.

    • We have updated the Electron Microscopy Methods Section with the following: “We were provided with a series of images and magnifications and were able to gather data from unique images at the highest magnification level for each of the following categories: D35 WT: 13 unique images, D35 P56S: 21 unique images, D60 WT 13 unique images, D60 P56S: 18 unique images. All images for a given line come from a single well of a 12 mm Snapwell™ Insert with 0.4 µm Pore Polyester Membranes (Corning). No indication of cell grouping or sampling techniques was provided with the images, therefore the images were quantified as a random sampling of the culture. *Images were then blinded, and FIJI was used to quantify.” *

    We are happy to make all images publicly available.

    *- We also note that replicates are not mentioned in the proteomics analysis. *

    • We apologize for missing this and thank the editor for mentioning it. The Proteomics portion of the methods section has been updated with the following: “The identification of VAPB binding partners via mass spectrometry was performed with one biological sample, while the validation of VAPB-PTPIP51 binding via co-immunoprecipitation and Western Blot was performed with three separate biological replicates.”

    Reviewer #1: “unusual sample sizes”:

    - The wording is indeed not very explicit, but we believe it is reasonable to assume that this point refers to "N=13-21 images” and that it is not clear how the data were pooled. The reviewer makes the related point: "Is the data grouped by cell or all comes from a single cell?", which provides further context to this point.

    • We thank the editor for this clarification, our response to Reviewer #1 Major Point 3 details the updates to Electron Microscopy section of the Methods and covers this. All images were provided to us by the Case Western Reserve University Electron Microscopy Core based on the number of quality images their team were able to obtain from our samples. Reviewer #1: “lack of clarity about statistical testing”:

    - We agree that without a clear description of the nature of the replicates, the statistical analysis is unclear.

    • We hope with the updated clarity on the description of the nature of the replicates as detailed above, the nature of the statistical analysis is clearer. In addition, we have added a Statistical Analysis subsection in the Methods Section. Reviewer #1: "The reliability of these conclusions is questionable, especially if the authors were blinded to the identity of their own samples.”:

    - This is a typo; the word “not” is missing. It should read: "if the authors were NOT blinded to the identity…” and refers to concerns raised by the reviewers about evaluating the EM images.

    • We apologize for this omission, each unique image was blinded after we received them from the core, and then quantification was performed on the blinded images. The Electron Microscopy portion of the methods section has been updated to include: “We were provided with a series of images and magnifications and were able to gather data from unique images at the highest magnification level for each of the following categories: D35 WT: 13 unique images, D35 P56S: 21 unique images, D60 WT 13 unique images, D60 P56S: 18 unique images. All images for a given line come from a single well of a 12 mm Snapwell™ Insert with 0.4 µm Pore Polyester Membranes (Corning). No indication of cell grouping or sampling techniques was provided with the images, therefore the images were quantified as a random sampling of the culture. Images were then blinded, and FIJI was used to quantify.”

    Reviewer #1: “The figures suggest a lack of appropriate blinding, with cherry-picking evident even in the ‘representative’ images'”

    - We agree the wording is somewhat problematic. However, we also feel that there is a discrepancy between the differences highlighted between the EM images shown in Fig 3A and a rather modest change of the median by only a few percent, as shown in the respective violin plots. We agree with the reviewer that the images of Fig 3A might, therefore, not be “representative” of the quantified changes.

    • We appreciate the editor's clarification and have selected images that more accurately represent the subtle changes in ER-MAMs observed in our quantification. These images have been included in Figure EV6 and referenced accordingly in the manuscript to ensure a balanced depiction of our findings. Additionally, we are prepared to make all images publicly available. We would like to again thank the editor for their clarification on Reviewer #1’s Major Point 4 as well as their agreement on the inappropriate nature of some of Reviewer #1’s comments.

    *Reviewer#1 Minor points:

    1. It is not accurate to describe Day 60 neurons as "aged" in the context of P56S-induced disease or imply they are a model for human aging. I could be mistaking, as I am not an iPSC expert, but I believe the field uses these terms in the context of iPSC-derived neurons to mean something more akin to "mature". The authors try to invoke this to argue for the relevance of their results to patient disease, unless the authors know this is somehow actually representative of neurons from older patients, I think this is misleading. *

    Carried Out Revisions

    We apologize for any confusion. Our use of the term "aged" was intended solely as a relative descriptor, indicating that day 60 motor neurons had been maintained in culture for a longer duration than day 35 motor neurons. It was not meant to suggest that these neurons represent a specific age or disease state, but rather that they had been cultured for an extended period.

    Furthermore, we use the term "mature" specifically in the context of motor neuron differentiation to indicate the expression of motor neuron-specific markers, which occurs by day 25 of differentiation. To avoid ambiguity, we have revised the manuscript to use the term "culture time" instead, ensuring clarity in our terminology.

    *Reviewer #1 Minor Point 2. The JC-1 experiment is not being appropriately controlled. These results are predicted by increased cell or mitochondrial death even if the membrane potentials are identical. The authors need to control for apoptotic signaling if they want to make this conclusion. There is an accepted standard in the mitochondrial field for assaying mitochondrial membrane potential (generally using TMRE or TMRM, but JC-1 can be used with proper controls), but it requires lots of careful controls not performed here (normalization to oligomycin- and FCCP-treated cells as a bare minimum. *

    Carried Out Revisions

    We would like to thank Reviewer 1 for this comment. We apologize for the omission, and we did treat the cells with CCCP provided in the JC-1 kit as a positive control. The JC-1 subsection of the methods has been updated to reflect this with the following: “A separate aliquot of cell suspension was also incubated with 1 uL of the supplied 50mM CCCP for 15 min prior to JC-1 dye addition, to act as a positive control and ensure the JC-1 dye was correctly detecting low MMP populations.”

    • The flow cytometry experiments are problematic in general since the authors state that part of their incentive for studying mitochondria in this model is due to effects at synapses, and the sample preparation for the cytometer involved dissociating the cells (i.e.-removing all of the processes where synapses mostly reside). *

    Carried Out Revisions

    We thank Reviewer #1 for this comment. Our citation of the study by Gómez-Suaga et al. (2019) was not intended to suggest that our investigation focuses exclusively on mitochondria at synapses but rather to provide context on the current understanding of the field. To clarify this point, we have revised the manuscript to include the following statement: "It has also been shown that this interaction can occur at synapses, and disruptions to it may impact synaptic activity (Gómez-Suaga et al., 2019)."

    Citation:

    Gómez-Suaga, P.* et al.* The VAPB-PTPIP51 endoplasmic reticulum-mitochondria tethering proteins are present in neuronal synapses and regulate synaptic activity. Acta Neuropathologica Communications 7, 35, doi:10.1186/s40478-019-0688-4 (2019).

    • The normalization for VAPB in the inducible lines is unclear-how is normalization performed simultaneously to two genes at once? The authors do not provide enough information for us to understand what they have actually done, and I wonder if the data presented in the supplement on this is actually sufficiently different from random noise to be interpretable, since no statistics of any kind are given.*

    In response, we have added a qPCR section to the Methods, detailing our experimental approach as follows:

    "Quantitative PCR: RNA was extracted using TRIzol Reagent (Thermo Fisher), and the procedure was performed according to their provided protocol. cDNA was generated using SuperScript™ IV VILO™ Master Mix (Thermo Fisher), following the manufacturer’s instructions. qPCR was conducted using PowerTrack™ SYBR Green Master Mix for qPCR (Thermo Fisher), following the provided protocol, on a BioRad CFX96 thermocycler. Samples were run in triplicate. Quantification was performed using CFX Maestro software (BioRad). VAPB expression was normalized to Neomycin and RPL3 using the software, and the resultant expression values were graphed along with the provided SEM, per standards in the field (Livak & Schmittgen, 2001; Wong & Medrano, 2005)."

    Additionally, we have modified the graph to more clearly illustrate the comparison between VAPB WT and P56S, emphasizing that there is no significant difference in mRNA expression.

    Citations

    1. Wong, M. L. & Medrano, J. F. Real-time PCR for mRNA quantitation. Biotechniques 39, 75-85 (2005).
    2. Livak, K. J. & Schmittgen, T. D. Analysis of relative gene expression data using real-time quantitative PCR and the 2(-Delta Delta C(T)) Method. Methods 25, 402-408 (2001).
    • I don't think the tunicamycin experiments make sense in this context. The authors start with premise that I do not understand: "if the decrease in MERC was underlying the decrease in MMP seen later in differentiation, inducing cell stress early in differentiation could mimic the decreased MMP." Most cell stress pathways enhance ER-mito contact, not decrease it, so I am not sure why they expected this to work this way. They then continue: "We selected tunicamycin, an ER stressor, as VAPB is an ER protein, and if the decreased MMP could be caused, at least partially, by loss of MERCs, ER stress would likely exacerbate it." I don't understand this either- Tunicamycin is not a general ER-stressing agent-it is a specific inhibitor of some N-linked glycosylation-maturation pathways in the ER lumen, which causes ER stress by dysregulation of misfolded protein pathways. Since VAPB has no luminal domains to speak of, is not known to interact with the protein folding and maturation machinery at all, and Tunicamycin has no obvious connection I'm aware of to MERCs, I am not able to follow the authors' intentions or conclusions here. I suspect this needs a major rewrite to explain what the goals were and how the authors controlled for their findings. *

    Carried Out Revisions

    We thank Reviewer 1 for this insightful comment. To provide greater clarity on this point, we have revised the manuscript to include the following statement:

    "MAMs are known to be a hot spot for the transfer of stress signals from the ER to mitochondria (van Vliet & Agostinis, 2018). Consequently, to test whether we could induce mitochondrial dysfunction by exposing iPSC-derived motor neurons to stressors, we selected tunicamycin (TM), an ER stressor, as VAPB is an ER protein, and if the decreased MMP could be caused, at least partially, by loss of ER-MAM, ER stress would likely exacerbate it."

    This revision aims to more clearly articulate the rationale behind our approach and the selection of tunicamycin as an ER stressor.

    Citations

    1. van Vliet AR, Agostinis P (2018) Mitochondria-Associated Membranes and ER Stress. Curr Top Microbiol Immunol 414: 73-102 Minor Adjustments Not in Response to Reviewer Comments

    Several minor adjustments have been made in response to internal reviews and feedback, independent of any specific Reviewer comment. The only modification affecting the presented data resulted from a comment noting a minor discrepancy in the gating of green-fluorescing cells between VAPB WT and VAPB P56S on Day 30 (Figure 3C). To ensure consistency, the gating was redrawn and applied uniformly to both plots, leading to a slight change in values. However, the overall difference remains non-significant, and our interpretation of the data remains unchanged. Additionally, to facilitate visual comparison, the Y-axes of the quantification graphs in Figures 3C and 3D have been standardized, though the data in Figure 3D itself was not modified—only the Y-axis scaling was adjusted.

    Description of analyses that authors prefer not to carry out

    Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

    We have responded to both of Reviewer #2’s Major Points 2 and 3 together, as the answer applies to both questions and the points raised in each idea.

    *Reviewer #2 Major Point 2. The authors highlight PTP151 binding to VAPB as a way to promote mitochondria ER contacts (MERC). They provide evidence that this association is diminished by the P56S VAPB mutation. This raises an important question. How does PTPIP51 binding connect with other phenotypes, such as the neuronal firing and ER stress sensitivity? Can the authors consider experiments to test this directly? For example, is there a way to drive PTP151 : VAPB interactions even in the face of mutant VAPB and see if this rescues the MERC defects and other phenotypes? *

    Reviewer #2 Major Point 3. The authors propose that the detachment of the mitochondria from the ER most likely be the cause for why their mutant motor neurons are more sensitive to ER stressors. Along the lines of the above, is there a way to test this hypothesis directly? Can they use other means to promote ER mitochondria association even in the face of VAPB mutation and test if this rescues phenotypes?

    Analyses We Prefer Not or Are Unable to Carry Out

    We thank Reviewer 2 for these insightful suggestions and fully agree that enhancing PTPIP51:VAPB interactions in the presence of mutant VAPB would be an effective approach to directly demonstrate that the loss of this interaction is the causative event underlying the observed phenotypes or to drive increased ER-mitochondria attachment.

    However, we have not identified a method to achieve this without introducing substantial alterations to the model system, which would likely compromise the interpretability of the results. The most promising approach we considered was the use of rapamycin-inducible linkers, as described by Csordás et al. (2010), which facilitate ER-mitochondria tethering upon rapamycin addition. Unfortunately, rapamycin directly affects translational regulation via mTOR (mammalian target of rapamycin) and given that translation dysregulation is a key phenotype in our study, its addition could influence multiple pathways, making it difficult to attribute any observed effects specifically to the intended manipulation.

    If the reviewers or editors have suggestions for alternative approaches, we would greatly appreciate their input. However, based on the current state of the field, we do not believe there is a method to selectively drive ER-mitochondria attachment or specifically enhance VAPB-PTPIP51 interactions without introducing confounding factors that would obscure whether the resulting effects are due to VAPB P56S pathophysiology or the intervention itself.

    Citation:

    1. Csordás G, Várnai P, Golenár T, Roy S, Purkins G, Schneider TG, Balla T, Hajnóczky G. Imaging interorganelle contacts and local calcium dynamics at the ER-mitochondrial interface. Mol Cell. 2010 Jul 9;39(1):121-32. doi: 10.1016/j.molcel.2010.06.029. PMID: 20603080; PMCID: PMC3178184.
  2. Review Commons

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    Referee #2

    Evidence, reproducibility and clarity

    Mutations in the VAPB gene are a cause of amyotrophic lateral sclerosis (ALS), a human motor neuron disease. To define the mechanisms by which mutations in VAPB cause motor neuron degeneration, the authors establish a new human iPSC-derived motor neuron model. They start by using CRISPR to knockout the VAPB gene and then introduce a lentivirus encoding a doxycycline-inducible construct to express WT or mutant VAPB. They then phenotypically characterize these WT and mutant motor neurons including using multi-electrode array (MEA), which revealed neuronal firing deficits in mutant motor neurons. They performed protein interaction studies WT vs mutant VAPB motor neuron and identified decreased binding to PTPIP51 in the mutant VAPB motor neurons.

    Phenotypically, the authors report that the VAPB mutant motor neurons exhibit decreased mitochondria / ER contacts (MERC) in mutant motor neurons compared to WT as well as decreased mitochondrial membrane potential. They report that these mitochondrial defects lead to heightened sensitivity to ER stress and activation of the integrated stress response, which could be rescued by treatment with ISRIB. Importantly, the neuronal firing defects are also rescued by ISRIB, providing compelling evidence that these defects are tied to activation of ER stress. Overall, this paper presents novel functional analyses of an important ALS gene, VAPB in disease-relevant cell types (human motor neurons). I have the following comments and suggestions for the authors to consider.

    1. Why did the authors decide to make VAPB knockouts and then introduce the WT or P56S VAPB constructs on a lentivirus instead of generating the point mutations (or correcting them) directly in the endogenous locus? Data in Extended Fig. 1c and Extended Fig. 2a indicate significant differences in either the kinetics of WT vs. P56S VAPB expression (1c) or levels (2a). It seems important to be able to compare comparable levels of WT and mutant proteins, especially for the interpretation of the subsequent IP-MS experiments to identify PTP151. The authors may wish to consider generating (or obtaining) isogenic lines harboring the mutations at the endogenous locus so that equal levels of expression of WT and mutant VAPB can be assessed.

    2. The authors highlight PTP151 binding to VAPB as a way to promote mitochondria ER contacts (MERC). They provide evidence that this association is diminished by the P56S VAPB mutation. This raises an important question. How does PTPIP51 binding connect with other phenotypes, such as the neuronal firing and ER stress sensitivity? Can the authors consider experiments to test this directly? For example, is there a way to drive PTP151 : VAPB interactions even in the face of mutant VAPB and see if this rescues the MERC defects and other phenotypes?

    3. The authors propose that the detachment of the mitochondria from the ER most likely be the cause for why their mutant motor neurons are more sensitive to ER stressors. Along the lines of the above, is there a way to test this hypothesis directly? Can they use other means to promote ER mitochondria association even in the face of VAPB mutation and test if this rescues phenotypes?

    Referee Cross-commenting

    There seems to be concurrence between Reviewer 1 and 2 about the interest in the VAPB gene but that the specific approaches and analyses methods used to study mutations in this gene (knockout and then over expression of WT and mutant version) are not a faithful representation of the in vivo situation (heterozygous mutations) and both provide suggestions for improvement of the study design.

    Editorial Note

    This Editorial Note by the Review Commons editorial team was communicated to the author in response to their request for clarification and contextualization of the referee report of reviewer #1.

    Since reviewer #1 did not clarify what was requested by the editorial office, we included the present Editorial Note in the review process after re-analyzing the manuscript in detail again and the referee report of reviewer #1.

    We agree with the authors that the wording used by reviewer #1 is problematic. However, we also see that the substance of the points raised by this reviewer is relevant and affects the study's conclusions. Below, we have included our comments on the individual points and quotes highlighted in your letter.

    Reviewer #1: "The strange pooling of data without explanation"

    • When looking into the figures and their captions in more detail, we could also not understand the nature of the replicates and how the data was aggregated or "pooled". In Figure 1, the stated number of replicates is "N=8 separate wells". It is unclear whether these are 8 wells from a single dissociation/replating procedure (the procedure is described in Materials & Methods as follows: "Motor neurons were dissociated on day 25 of differentiation and re-plated onto 48-well MEA plate") or whether the eight are sampled across multiple plates across cultures obtained from independent dissociations procedures.

    • In Figure 3, the number of replicates is "N=13-21 images". Here, it is unclear whether these images come from the same or independent samples, how many quantifications were performed per image, and how many images per sample were used.

    • We also note that replicates are not mentioned in the proteomics analysis.

    Reviewer #1: "unusual sample sizes":

    • The wording is indeed not very explicit, but we believe it is reasonable to assume that this point refers to "N=13-21 images" and that it is not clear how the data were pooled. The reviewer makes the related point: "Is the data grouped by cell or all comes from a single cell?", which provides further context to this point.

    "lack of clarity about statistical testing":

    • We agree that without a clear description of the nature of the replicates, the statistical analysis is unclear.

    "false hypothesis testing":

    • We agree with the authors that the reviewer is unclear.

    "The fact that every experiment in the paper has just enough n to trigger statistical significance as determined by the authors raises some concerns, suggesting potential biases."

    • We agree that this is an inappropriate statement in absence of evidence or detailed argumentation; we very much regret not having caught this statement up front.

    "The reliability of these conclusions is questionable, especially if the authors were blinded to the identity of their own samples.":

    • This is a typo; the word "not" is missing. It should read: "if the authors were NOT blinded to the identity..." and refers to concerns raised by the reviewers about evaluating the EM images.

    "The figures suggest a lack of appropriate blinding, with cherry-picking evident even in the 'representative' images'"

    • We agree the wording is somewhat problematic. However, we also feel that there is a discrepancy between the differences highlighted between the EM images shown in Fig 3A and a rather modest change of the median by only a few percent, as shown in the respective violin plots. We agree with the reviewer that the images of Fig 3A might, therefore, not be "representative" of the quantified changes.

    We agree that there are statements in this review that are written in a style and tone that is not appropriate. We greatly apologize for this and, we should have caught these issues beforehand.

    At the same time, this reviewer raises significant issues about the study. In this case, we cannot eliminate the entire review since the points raised are relevant to the conclusiveness of the study.

    Significance

    The new iPSC-derived system to study VAPB mutations in human motor neurons is significant and has led the authors to discover new functions for VAPB (i.e., mitochondria-ER contacts). The significance and impact of the study, in my opinion, would be increased if the authors considered using motor neuron lines expressing comparable levels of WT and mutant VAPB, preferably from the endogenous location under physiological conditions. Their discovery of a role of defective mitochondria-ER contact as making VAPB mutant motor neurons more sensitive to ER stress would be bolstered by experiments to directly test this hypothesis by rescuing the contact defects.

  3. Review Commons

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    Referee #1

    Evidence, reproducibility and clarity

    Landry et al. present characterization of iPSC-derived neurons that inducibly express either WT VAPB or P56S VAPB in the context of a VAPB knockout. They do this by first generating a novel iPSC line with a frameshift knockout in a VAPB, and then selecting lentiviral-transduced clones that express either WT or P56S VAPB from an inducible promoter. The resulting lines are then differentiated using conventional protocols, VAPB expression is induced, and the cells are subjected to a battery of cell biological tests to examine mitochondrial function.

    Major Points:

    1. The method of knocking out and selecting an inducible line in problematic. VAPB is an essential gene-patients with P56S are always heterozygotes, since nonfunctional VAPB is embryonic lethal. Selecting a knockout cell line is already choosing a parent that is very far from physiological, and the reexpression of P56S VAPB as the sole form also is not a good a model for understanding the contributions of P56S to disease. This approach is unusual, as it seems to overlook the advantages of working with iPSCs and patient-derived neurons. Unfortunately, the value of this amazing and rare system is diminished by the design of the selection method.
    2. The interactome analysis is not controlled properly to interpret. It is not the total amount of VAPB that needs to be used as the normalization control, since it is already known 90+% of the P56S VAPB is in cytoplasmic aggregates. The authors need to normalize to the amount of VAPB that made it to the contact sites-a much smaller amount in the cells expressing the diseased form. For example, the fact that the authors can still pull down detectable PTPIP51 in Fig. 2e actually argues for the opposite conclusion than what the authors have stated-if the authors have actually expressed just P56S in a true knock out condition, this means that P56S CAN still bind to PTPIP51 (and possibly even better than WT, as several previous papers have suggested-since there is ~100-fold less available for binding). Without an appropriate normalization, the authors cannot make any conclusion about how to interpret the results of this part of the paper.
    3. The electron microscopy data is not interpretable in this form. The authors have provided no data at all on how analysis was performed, how contact sites were defined, how samples were collected and ensured to be representative, blinding that was performed, how sources of bias were accounted for, etc. It is clear even from what little is shown that the authors are not focused on what matters to address their own questions. For example, apart from the P56S Day 35 example, none of the "contact sites" selected for the figure are even possible to be mediated by VAPB, since the distance between the ER and the mitochondria is too far for the maximum tethering distance of VAPB-PTPIP51. Since the authors have neglected to include scale bars in their zooms, the reader cannot be sure of the distance, but it is clearly in excess of 50 nm since there are obviously visible ribosomes between the two organelles. Additionally, the authors provide no information on what "% mitochondria in contact with ER" means (By organelle? By unit surface area? Is the data grouped by cell or all comes from a single cell? How do you account for contact sites vs. proximity by crowding? Etc.).
    4. The strange pooling of data without explanation, unusual sample sizes, and lack of clarity about statistical testing, false hypothesis testing, and really any clear rigor in statistics of any kind make it impossible for a reader to have any confidence in the results presented here. The fact that every experiment in the paper has just enough n to trigger statistical significance as determined by the authors raises some concerns, suggesting potential biases. The reliability of these conclusions is questionable, especially if the authors were blinded to the identity of their own samples. This is particularly relevant for the EM data, where the determination of contact sites appears to have been made subjectively.

    Minor points:

    1. It is not accurate to describe Day 60 neurons as "aged" in the context of P56S-induced disease or imply they are a model for human aging. I could be mistaking, as I am not an iPSC expert, but I believe the field uses these terms in the context of iPSC-derived neurons to mean something more akin to "mature". The authors try to invoke this to argue for the relevance of their results to patient disease, unless the authors know this is somehow actually representative of neurons from older patients, I think this is misleading.
    2. The JC-1 experiment is not being appropriately controlled. These results are predicted by increased cell or mitochondrial death even if the membrane potentials are identical. The authors need to control for apoptotic signaling if they want to make this conclusion. There is an accepted standard in the mitochondrial field for assaying mitochondrial membrane potential (generally using TMRE or TMRM, but JC-1 can be used with proper controls), but it requires lots of careful controls not performed here (normalization to oligomycin- and FCCP-treated cells as a bare minimum.
    3. The flow cytometry experiments are problematic in general since the authors state that part of their incentive for studying mitochondria in this model is due to effects at synapses, and the sample preparation for the cytometer involved dissociating the cells (i.e.-removing all of the processes where synapses mostly reside).
    4. The normalization for VAPB in the inducible lines is unclear-how is normalization performed simultaneously to two genes at once? The authors do not provide enough information for us to understand what they have actually done, and I wonder if the data presented in the supplement on this is actually sufficiently different from random noise to be interpretable, since no statistics of any kind are given.
    5. I don't think the tunicamycin experiments make sense in this context. The authors start with premise that I do not understand: "if the decrease in MERC was underlying the decrease in MMP seen later in differentiation, inducing cell stress early in differentiation could mimic the decreased MMP." Most cell stress pathways enhance ER-mito contact, not decrease it, so I am not sure why they expected this to work this way. They then continue: "We selected tunicamycin, an ER stressor, as VAPB is an ER protein, and if the decreased MMP could be caused, at least partially, by loss of MERCs, ER stress would likely exacerbate it." I don't understand this either- Tunicamycin is not a general ER-stressing agent-it is a specific inhibitor of some N-linked glycosylation-maturation pathways in the ER lumen, which causes ER stress by dysregulation of misfolded protein pathways. Since VAPB has no luminal domains to speak of, is not known to interact with the protein folding and maturation machinery at all, and Tunicamycin has no obvious connection I'm aware of to MERCs, I am not able to follow the authors' intentions or conclusions here. I suspect this needs a major rewrite to explain what the goals were and how the authors controlled for their findings.

    Significance

    While the idea of assaying the function of ALS-causing VAPB mutants in iPSC-derived neurons is great and would be a great asset to the field, the execution here raises significant concerns. It is difficult to draw clear conclusions from the presented data. Necessary controls are either incorrectly applied or missing, the methods section lacks crucial details for reproducibility, and the figures suggest a lack of appropriate blinding, with cherry-picking evident even in the "representative" images. There are also major issues with the entire premise of how the lines were generated, since VAPB knockout cells are highly aberrant lines, the authors have likely selected for all sorts of mitochondrial pathways that would not be operating in an actual patient neuron.

    Claims about mitochondrial dysfunction could potentially mislead the field, as such conclusions do not seem to be supported by the actual data. To be suitable for publication, the study needs substantial revisions, including proper controls, blinding, and detailed methodological information for reproducibility. I understand the challenges and costs associated with using iPSC-derived neurons, but focusing on a few well-controlled experiments would be far more beneficial than presenting numerous, less interpretable findings.

  4. Version published to 10.1101/2024.05.13.594000v1 on bioRxiv