Pyruvate Supports RET-Dependent Mitochondrial ROS Production to Control Mycobacterium avium Infection in Human Primary Macrophages

  1. Lisa Marie Røst
  2. Claire Louet
  3. Per Bruheim
  4. Trude Helen Flo
  5. Alexandre Gidon

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Abstract

Macrophages deploy a variety of antimicrobial programs to contain mycobacterial infection. Upon activation, they undergo extensive metabolic reprogramming to meet an increase in energy demand, but also to support immune effector functions such as secretion of cytokines and antimicrobial activities. Here, we report that mitochondrial import of pyruvate is linked to production of mitochondrial ROS and control of Mycobacterium avium ( M. avium ) infection in human primary macrophages. Using chemical inhibition, targeted mass spectrometry and single cell image analysis, we showed that macrophages infected with M. avium switch to aerobic glycolysis without any major imbalances in the tricarboxylic acid cycle volume or changes in the energy charge. Instead, we found that pyruvate import contributes to hyperpolarization of mitochondria in infected cells and increases production of mitochondrial reactive oxygen species by the complex I via reverse electron transport, which reduces the macrophage burden of M. avium . While mycobacterial infections are extremely difficult to treat and notoriously resistant to antibiotics, this work stresses out that compounds specifically inducing mitochondrial reactive oxygen species could present themself as valuable adjunct treatments.

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  1. Version published to 10.3389/fimmu.2022.891475
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    Reply to the reviewers

    Reviewer #1 (Evidence, reproducibility and clarity (Required)):

    Here, authors confirm that glycolysis is important macrophage defense against mycobacterial infection and describe a central role of pyruvate in linking glycolysis and antimycobacterial mtROS production to control the intracellular burden. Alike previous authors who have demonstrated that the non-pathogenic Bacillus Calmette-Guerin and heat-killed M. tb increase glycolysis, they show that human primary macrophages infected with M. avium increase glycolysis to facilitate mycobacterial control. Rost and coll. show evidence that the killing mechanism act through the production of mtROS by the complex I of the electron transport chain via the engagement of RET. This mechanism acts in parallel to other immunometabolic defense pathways activated in M. avium infected macrophages, such as the production/induction of itaconate via the IRF-IRG1 pathways (Alexandre Gidon 2021). * * They give evidence that IL-6 and TNFa are not involved in regulating the pyruvate-mtROS and show chemical evidence that mitochondrial import of pyruvate through MPC activity is necessary to generate a high membrane potential and the subsequent production mtROS. However, the data presented here don’t explain how pyruvate is driving RET and mtROS; if pyruvate targets the electron transport chain directly or is converted (via TCA) to another metabolite that initiates RET and mtROS. Above all, this work brings attention to the possibility of using compounds that specifically engage mtROS production for therapeutic perspectives

    Reviewer #1 (Significance (Required)):

    While the data presented here don t explain how pyruvate is driving RET and mtROS; if pyruvate targets the electron transport chain directly or is converted (via TCA) to another metabolite that initiates RET and mtROS, this work merits to be deeply evaluated for potential publication in a RC journal. However, the language must be improved and polished before submission.

    We thank the reviewer for appreciating the importance of our findings. We are sorry for any inconveniences the language may have caused and have carefully revised the manuscript with the intention of improving it.

    Reviewer #2 (Evidence, reproducibility and clarity (Required)):

    Overall evaluation

    This study addresses an interesting aspect of host-pathogen relationship, namely how the metabolism of the host impacts directly or indirectly on the metabolism and/or fitness of the pathogen. For example, the generation of ROS in a way independent of NADPH-oxidases has been suggested to play a role in a number of infections. In particular, whether and how such ROS might be part of the cell-autonomous defence against an intracellular bacterial pathogen, in the present case M. avium, is of relevance. Despite these positive points, the study and manuscript suffer from a high number of serious problems both in form and content. The authors are strongly advised to revise the experimental evidence presented, including by performing additional experiments and re-interpreting some of the ones documented, as well as extensively rewrite/reformat the manuscript.

    Major comments:

    1- Normally, I would list the following criticisms in minor comments, but their accumulation makes them a major point:

      • The reference style is cumbersome, because they are listed in alphabetical order of the FIRST NAMES of the first authors, which renders it difficult to identify what is cited and when *
      • Similarly, the citations in the text include the author first names, whoch is unusual and heavy. * We thank the reviewer for bringing this to our attention. It was a mistake and we have now changed the reference style accordingly by replacing first names with initials and listing citations alphabetically from the first author’s last name.

    In addition, the authors almost systematically introduce each of the articles cited with a sentence such as "Mills and colleagues did this and that ...". This is sometimes used in articles, but should not be the norm. Usually, this is used to emphasise that a given group has contributed not only substantially, but also on a regular basis to a field for years. One would write Palade and colleagues ..., or Rothman and colleagues ... . But in the present manuscript, this is mentioning first authors and their colleagues. Mills et al is a contribution from the O'Neils laboratory, which speaks to me.

    We see the point and have changed some of these sentences accordingly to either write “O’Neill and colleagues …(ref)”, “First-author et al. showed that…. (ref)”, or “Others have shown …(ref)”. Editing was made page 3, lines 49, 51 and 54-56; page 4, lines 74; page 6, line 111; page 9, lines 178, 182, 193 and 197.

    2- Page 4, the authors report that the positive control used to shift macrophage metabolism towards glycolysis did not work. This places doubt on the other experiments and conditions.

    We thank the reviewer for bringing this point of confusion to our attention. In an Agilent Seahorse assay, which is commonly used to report glycolytic flux in scientific publications, the extracellular acidification rate (ECAR) is used as an indicator of glycolysis. Extracellular acidification occurs as protons are exported from the cell alongside lactate. In figure 1B we show quantitatively (ng/cell/24h) that lactate export is significantly increased in MDMs after LPS challenge, which translates to an increased ECAR on the traditional Seahorse assay. We also show further evidence that LPS treatment does switch the metabolism to glycolysis: the two first intermediates of glycolysis, G6P and F6P, are consumed (Fig. 1D), though between-donor variation leaves the LPS-induced increase in glucose consumption not significant. Overall, we are confident that our NMR and mass spectrometric metabolic profilings, which have been tested in several publications listed in the methods section are reliable and recapitulate previous knowledge. We have rephrased the paragraph on page 4 line 76 to clarify this point.

    *3- Page 5. I am not sure to really understand the reasoning behind : "Quantification by targeted mass spectrometry did not reveal a significant accumulation in the intracellular level of pyruvate in macrophages infected with M. avium or treated with LPS when compared to untreated controls (Fig. 2A), suggesting that pyruvate is rapidly metabolized." *

    The rationale for performing mass spectrometric quantification of pyruvate was to confirm experimentally that pyruvate is consumed - which we already know indirectly as its reduced product, lactate, is produced and excreted by the infected cells (Figure 1B). The hypothesis is that a proportion of the pyruvate could also enter the mitochondria and TCA cycle as shown by Mills et al.

    We have tried clarifying this in the revised manuscript by replacing the original text by “Quantification by targeted mass spectrometry did not reveal a significant accumulation in the intracellular level of pyruvate in macrophages infected with M. avium or treated with LPS when compared to untreated controls (Fig. 2A), confirming that pyruvate is metabolized. Mills et al have demonstrated that during LPS activation, mouse macrophages switch to aerobic glycolysis while repurposing the TCA cycle activity to generate specific immunomodulatory metabolites (Mills EL 2016), which implies that a fraction of the pyruvate formed by glycolysis enters mitochondria.”(page 5 line 90).

    4- The metabolomics experiments seem to be performed on a global population of infected and uninfected cells, without any clear mention of the fraction of infected cells, which is potentially low (Fig 1 appears to indicate less than 50%), and very likely variable between experiments. This is a serious confounding factor and likely precludes interpretation of the results?! The percentage of infected cells, at time "zero" and at each time point post-infection has to be quantified in each experiment.

    The reviewer is right that the analysis was carried out on a mixed population. However, even with an infection level of 50% this should be sufficient to pick up significant changes in metabolite levels resulting from infection, which is also not seen with LPS treatment that you would assume activates all cells. We have tested another protocol of infection (MOI 10 for 120 min) that yields almost 100% infection with similar results. These data are included as supplementary figure 1 in the revised manuscript (page 6, line 124).

    It would also be useful to analyse and graph the total fluorescence (coming from M. avium) per cell and the average fluorescence per cell.

    Intracellular growth was quantified by measuring M. avium fluorescence intensity per cell (n>500 cells per donor and per condition) as mentioned in the figure legends. The bar charts represent the average intensity obtained from at least 500 cells per donor and conditions, each point representing an individual donor. We have successfully used this method to analyze and quantify M. avium growth in human primary macrophages (Gidon et al, PLoS Pathogens, 2017; Gidon et al, mBio 2021).

    5- Page 6. How can the authors conclude "Overall, this set of data reveals that no major perturbations of the TCA cycle are induced by the infection, excluding a potential antimicrobial property of these TCA intermediates" from their data? Their experiment do not test the potential antimicrobial activity of the metabolites!

    We agree with the reviewer that our data cannot preclude any anti-microbial effects of TCA intermediates. We agree that the phrasing is confusing and not as intended and have replaced it with the following sentence “Since we and others have previously found that altered intracellular levels of the TCA cycle-derived metabolite itaconate following an infection was indicative of an anti-microbial function (Gidon et al, mBio 2021; Chen et al, Science, 2020), we conclude that none of the TCA cycle intermediates warranted further investigation to explain the anti-microbial effect of glycolysis.”. (page 6, line 115).

    *6- The effect of the chemical inhibitors used has to be evaluated on the growth of bacteria in broth to exclude the possibility that they directly impact them. *

    We agree with the reviewer that this is important to control for. We have performed the suggested experiments and the results, showing that none of the different drugs influence M. avium in vitro growth, are included in a supplementary figure 2 in the revised manuscript (page 8, line 158).

    *7- Figures. None of the graphs present error bars. In addition, for example for Fig 1A, the number of points correspond each to one donor. But there is mention neither of the number of biological replicates nor of technical replicates. This is absolutely required. *

    The number of donors used for each experiment are included in the figure legend. All the experiments were done independently and are therefore biological replicates. Each point represents the value obtained for one independent donor with no technical replicates. Since we show all individual measurements (donors) an error-bar, to our opinion, is not needed. We have now changed the text in the legend to better reflect this information (page 17, lines 353, 357; page 18, line 361; page 20, lines 371, 375, 378, 383, 383; page 23, lines 410, 413, 417, 422).

    8- It is unclear whether the effects documented have been measured in the whole population or only in the infected cells. And when they are measured in infected cells and uninfected cells, are these cells from a population in the same well, or from a well containing only uninfected cells?

    By nature, antimicrobial effects can only be detected in infected cells therefore all the experiments measuring the effect on intracellular growth, the mitochondrial potential and the production of mitochondrial ROS were measured on infected cells. Control refers to a well containing only uninfected cells.

    *9- In Figure 3A, the localisation of M. avium has to be shown. *

    We have edited the Figure 3 that now includes images from the M. avium-CFP channel to help identify the infected cells.

    *10- The mechanism proposed at the end of the abstract "...this work stresses out that compounds specifically inducing mitochondrial reactive oxygen species could present themself as valuable adjunct treatments." should be tested to close the loop and validate the data and hypothesis. *

    We agree with the reviewer, and we are currently finalizing another manuscript on metformin, which is known to induce mitoROS, as a possible Host Directed Therapeutic agent in a mouse model of M. avium infection.

    Minor comments:

    1- The manuscript does not show any numbering, neither of pages nor of lines, which renders the writing of the review difficult.

    We are sorry for the inconvenience. This is now included in the revised manuscript.

    *2- The authors write "undirect" instead of indirect. *

    We have corrected the mistake in the revised manuscript.

    *3- They also use "if" instead of whether quite frequently. *

    We thank the reviewer for bringing that detail to our attention. We have changed the manuscript according to the comment.

    *4- Page 5, second line "... a 40% increase in cells treated ..." An increase of what? *

    Treatment of infected cells with 2-DG increases the fluorescence coming from M. avium, reflecting the increase of the intracellular burden. We have changed the manuscript to make this point clearer (page 4, line 82).

    *5- Page 5. The second paragraph belongs to the introduction or the discussion. *

    We don’t agree on this point. We feel that it is important to inform the reader on how pyruvate can be used within the cell before showing the results, but we feel it does not fit with the broader introduction on glycolysis. However, if the editor/reviewers disagree with us, we will move this paragraph in introduction.

    *6- Page 6. The authors mention that AMP, ADP etc... are nucleosides. But they are nucleotides. *

    We changed the manuscript according to the suggestion (page 6, line 120; page 13, line 279; page 20 line 381).

    __Reviewer #2 (Significance (Required)): __

    The study explores an interesting question, but in its present state, the conclusions are not sustained by the evidence.

    We thank the reviewer for acknowledging the importance of our work. We believe that we have addressed the concerns expressed in the comments.

    Reviewer #3 (Evidence, reproducibility and clarity (Required)):

    *This manuscript reported that macrophages rely on glycolysis and RET to control M. avium infection and provide molecular evidence linking pyruvate, the end-product of glycolysis, to anti-mycobacterial mtROS production. The advantages of this paper are the clear thinking, from phenomenon to molecular mechanism, strong logic. However, there are also many shortcomings: *

    Major comments:

    *1.The main shortcoming of this paper is that authors only found macrophages control M. avium infection through glycolysis and RET in vitro. Although they use primary macrophages from healthy donners, not the cells lines, is it consistent in vivo? Authors should use mouse model that challenged with M. avium. Moreover, authors can isolate primary macrophages from patients that infected with M. avium, and compared it with primary macrophages from healthy donners. *

    We agree with the reviewer opinion, and we are finalizing another manuscript using Metformin, a drug known to induce mitochondrial ROS, as a Host Directed Therapy in a mouse model. However, dissection of mechanisms involved such as pyruvate import to mitochondria and RET is not possible in vivo. We are not sure of the meaning of the suggested experiment: comparing primary macrophages from mav-infected patients vs healthy donors.

    *2.This paper found that macrophages control M. avium infection by producing mitochondrial reactive oxygen species. This is a very interesting observation. How does mitochondrial reactive oxygen species resist mycobacterial infection? *

    We thank the reviewer for appreciating our work. Yet, we are not sure what does the reviewer mean by “*How does mitochondrial reactive oxygen species resist mycobacterial infection?”. *It has been shown in many studies that cellular ROS causes oxidative damage and can be toxic to pathogens (and cells), including mycobacteria (Fang FC, Nature Reviews in Microbiology, 2004; Dryden M, Int. J. Antimicrob. Agents, 2018; Kim et al, J. Microbiology, 2019; Herb and Schramm, Antioxidants, 2021). However, the role of RET-induced mitochondrial ROS is a relatively new concept, that, to the best of our knowledge, has never been demonstrated to be involved in the control of mycobacterial infection nor in human primary macrophages. Conversely, bacteria have evolved defense mechanisms to protect and counteract the production of antimicrobial ROS (Kim et al, J. Microbiology, 2019).

    *3.To make this data solid, whether giving pyruvate supplements to patients with mycobacterium infection can alleviate their disease? or it can be tested in mouse model. *

    Initiating a clinical study is beyond the scope of this study. Furthermore, even if we could supplement infected mice with pyruvate, there is no guarantee it will get into the cells and further imported into mitochondria to induce the anti-mycobacterial effects shown in the present study. We rather believe that the key for future treatment would be to induce mitochondrial ROS through the use of other, known agonists to strengthen this cell-intrinsic defense mechanism. As stated above, we are finalizing another manuscript using a compound known to induce mitochondrial ROS as Host Directed Therapy in a mouse model.

    *4.This work demonstrated that IL-6 and TNF-α could control the intracellular burden of M. avium. Many cytokines are produced by macrophage during infection. Are there other pro-inflammatory cytokines that play a role? *

    We agree with the reviewer view that many cytokines influence host defenses to mycobacterial infections in addition to TNF-a and IL-6, e.g., IL-1, IL-10 and interferons. However, some of these are not induced in Mav infected macrophages (IL-1, interferons), and our previous works have shown that TNF-a and IL-6 are consistently induced by the infection (Gidon et al, PLoS Pathogens, 2017) and that they are involved in the control of the intracellular burden (Gidon et al, mBio, 2021). We therefore chose to focus on these.

    *5.In Figure 1C, authors did not observe an increase of glutamine consumption in LPS-activated human macrophage which is in contrary to previous published study. How author explain this contrary result? *

    We thank the reviewer for bringing this point to our attention. We have previously published the glutamine consumption of multiple myeloma cell lines quantified by the NMR based method described herein, proving it is sensitive enough to detect differences between cell lines at cell densities comparable to those of the seeded MDMs (Abdollahi et al, The FASEB journal, 2021). Hence, we are confident that the applied methodology would detect significant differences in glutamine consumption, given that the cells in question rely on glutamine. Previous observations of glutamine uptake were made using mouse macrophages and it is referenced that human and mouse macrophages do not share the exact same metabolism (Thomas et al, Frontiers in Immunology, 2014; Vijayan et al, Redox Biology, 2019). It’s worth noting that the species-specificity also extend to how macrophages respond to TLRs ligands (Sun et al, Science Signaling, 2016). As this result does not contribute significantly to the mechanism described in our paper, we do not feel the need to discuss it extensively.

    Minor comment:

    The authors do not provide sufficient information in the Materials and Methods, and figure legends, such as how many times the experiments were repeated? How to measure the concentration of citrate, isocitrate, succinate......

    The number of donors used for each experiment are included in the figure legends. All the experiments were done independently and are therefore biological replicates. Each point represents the value obtained for one independent donor with no technical replicates. The concentrations of citrate, isocitrate, succinate and the other TCA cycle intermediates were measured by capillary ion chromatography tandem mass spectrometry, as described in the legend of Figure 2 and in detail in the Materials and Methods section on page 13-14. All metabolite measurements by targeted mass spectrometry are based on validated and published methods from our laboratory (Kvitvang et al, 2014; Stafnes et al, 2018; Røst et al, 2020). We have included more details to the methods section describing mass spectrometric metabolic profiling (page 13-14).

    Reviewer #3 (Significance (Required)):

    Mycobacteria avium infection is a common and serious kind of inflammation, in which macrophages has been reported to play an important role. Recently metabolic reprogramming of macrophages is proved in many diseases. By using LPS stimulation, the metabolic reprogramming of macrophages has been reported and have been confirmed to play a role during infection. Therefore, it is not so exciting to see this role of metabolic reprogramming in controlling M. avium infection.

    We are sorry that our findings did not excite the reviewer, but we strongly disagree that our study does not report any novel findings. Both the significance of mitochondrial ROS in mycobacterial defense and the discovery that pyruvate can induce mitochondrial ROS via RET, are novel findings not shown before to our knowledge. And – as a note – a phenomenon described for LPS and/or in mouse macrophages does not necessarily reflect what happens during any bacterial or viral infections, nor in humans.

  3. Review Commons

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    Referee #3

    Evidence, reproducibility and clarity

    This manuscript reported that macrophages rely on glycolysis and RET to control M. avium infection and provide molecular evidence linking pyruvate, the end-product of glycolysis, to anti-mycobacterial mtROS production. The advantages of this paper are the clear thinking, from phenomenon to molecular mechanism, strong logic. However, there are also many shortcomings:

    Major comments:

    1. The main shortcoming of this paper is that authors only found macrophages control M. avium infection through glycolysis and RET in vitro. Although they use primary macrophages from healthy donners, not the cells lines, is it consistent in vivo? Authors should use mouse model that challenged with M. avium. Moreover, authors can isolate primary macrophages from patients that infected with M. avium, and compared it with primary macrophages from healthy donners.
    2. This paper found that macrophages control M. avium infection by producing mitochondrial reactive oxygen species. This is a very interesting observation. How does mitochondrial reactive oxygen species resist mycobacterial infection?
    3. To make this data solid, whether giving pyruvate supplements to patients with mycobacterium infection can alleviate their disease? or it can be tested in mouse model.
    4. This work demonstrated that IL-6 and TNF-α could control the intracellular burden of M. avium. Many cytokines are produced by macrophage during infection. Are there other pro-inflammatory cytokines that play a role?
    5. In Figure 1C, authors did not observe an increase of glutamine consumption in LPS-activated human macrophage which is in contrary to previous published study. How author explain this contrary result?

    Minor comment:

    The authors do not provide sufficient information in the Materials and Methods, and figure legends, such as how many times the experiments were repeated? How to measure the concentration of citrate, isocitrate, succinate......

    Significance

    Mycobacteria avium infection is a common and serious kind of inflammation, in which macrophages has been reported to play an important role. Recently metabolic reprogramming of macrophages is proved in many diseases. By using LPS stimulation, the metabolic reprogramming of macrophages has been reported and have been confirmed to play a role during infection. Therefore, it is not so exciting to see this role of metabolic reprogramming in controlling M. avium infection.

  4. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

    Learn more at Review Commons

    Referee #2

    Evidence, reproducibility and clarity

    Overall evaluation

    This study addresses an interesting aspect of host-pathogen relationship, namely how the metabolism of the host impacts directly or indirectly on the metabolism and/or fitness of the pathogen. For example, the generation of ROS in a way independent of NADPH-oxidases has been suggested to play a role in a number of infections. In particular, whether and how such ROS might be part of the cell-autonomous defence against an intracellular bacterial pathogen, in the present case M. avium, is of relevance. Despite these positive points, the study and manuscript suffer from a high number of serious problems both in form and content. The authors are strongly advised to revise the experimental evidence presented, including by performing additional experiments and re-interpreting some of the ones documented, as well as extensively rewrite/reformat the manuscript.

    Major comments:

    1. Normally, I would list the following criticisms in minor comments, but their accumulation makes them a major point:
      • a. The reference style is cumbersome, because they are listed in alphabetical order of the FIRST NAMES of the first authors, which renders it difficult to identify what is cited and when
      • b. Similarly, the citations in the text include the author first names, whoch is unusual and heavy.
      • c. In addition, the authors almost systematically introduce each of the articles cited with a sentence such as "Mills and colleagues did this and that ...". This is sometimes used in articles, but should not be the norm. Usually, this is used to emphasise that a given group has contributed not only substantially, but also on a regular basis to a field for years. One would write Palade and colleagues ..., or Rothman and colleagues ... . But in the present manuscript, this is mentioning first authors and their colleagues. Mills et al is a contribution from the O'Neils laboratory, which speaks to me.
    2. Page 4, the authors report that the positive control used to shift macrophage metabolism towards glycolysis did not work. This places doubt on the other experiments and conditions.
    3. Page 5. I am not sure to really understand the reasoning behind : "Quantification by targeted mass spectrometry did not reveal a significant accumulation in the intracellular level of pyruvate in macrophages infected with M. avium or treated with LPS when compared to untreated controls (Fig. 2A), suggesting that pyruvate is rapidly metabolized."
    4. The metabolomics experiments seem to be performed on a global population of infected and uninfected cells, without any clear mention of the fraction of infected cells, which is potentially low (Fig 1 appears to indicate less than 50%), and very likely variable between experiments. This is a serious confounding factor and likely precludes interpretation of the results?! The percentage of infected cells, at time "zero" and at each time point post-infection has to be quantified in each experiment. It would also be useful to analyse and graph the total fluorescence (coming from M. avium) per cell and the average fluorescence per cell.
    5. Page 6. How can the authors conclude "Overall, this set of data reveals that no major perturbations of the TCA cycle are induced by the infection, excluding a potential antimicrobial property of these TCA intermediates" from their data? Their experiment do not test the potential antimicrobial activity of the metabolites!
    6. The effect of the chemical inhibitors used has to be evaluated on the growth of bacteria in broth to exclude the possibility that they directly impact them.
    7. Figures. None of the graphs present error bars. In addition, for example for Fig 1A, the number of points correspond each to one donor. But there is mention neither of the number of biological replicates nor of technical replicates. This is absolutely required.
    8. It is unclear whether the effects documented have been measured in the whole population or only in the infected cells. And when they are measured in infected cells and uninfected cells, are these cells from a population in the same well, or from a well containing only uninfected cells?
    9. In Figure 3A, the localisation of M. avium has to be shown.
    10. The mechanism proposed at the end of the abstract "...this work stresses out that compounds specifically inducing mitochondrial reactive oxygen species could present themself as valuable adjunct treatments." should be tested to close the loop and validate the data and hypothesis.

    Minor comments:

    1. The manuscript does not show any numbering, neither of pages nor of lines, which renders the writing of the review difficult.
    2. The authors write "undirect" instead of indirect.
    3. They also use "if" instead of whether quite frequently.
    4. Page 5, second line "... a 40% increase in cells treated ..." An increase of what?
    5. Page 5. The second paragraph belongs to the introduction or the discussion.
    6. Page 6. The authors mention that AMP, ADP etc... are nucleosides. But they are nucleotides.

    Significance

    The study explores an interesting question, but in its present state, the conclusions are not sustained by the evidence.

  5. Review Commons

    Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

    Learn more at Review Commons

    Referee #1

    Evidence, reproducibility and clarity

    Here, authors confirm that glycolysis is important macrophage defense against mycobacterial infection and describe a central role of pyruvate in linking glycolysis and antimycobacterial mtROS production to control the intracellular burden. Alike previous authors who have demonstrated that the non-pathogenic Bacillus Calmette-Guerin and heat-killed M. tb increase glycolysis, they show that human primary macrophages infected with M. avium increase glycolysis to facilitate mycobacterial control. Rost and coll. show evidence that the killing mechanism act through the production of mtROS by the complex I of the electron transport chain via the engagement of RET. This mechanism acts in parallel to other immunometabolic defense pathways activated in M. avium infected macrophages, such as the production/induction of itaconate via the IRF-IRG1 pathways (Alexandre Gidon 2021).

    They give evidence that IL-6 and TNFa are not involved in regulating the pyruvate-mtROS and show chemical evidence that mitochondrial import of pyruvate through MPC activity is necessary to generate a high membrane potential and the subsequent production mtROS.

    However, the data presented here don t explain how pyruvate is driving RET and mtROS; if pyruvate targets the electron transport chain directly or is converted (via TCA) to another metabolite that initiates RET and mtROS. Above all, this work brings attention to the possibility of using compounds that specifically engage mtROS production for therapeutic perspectives

    Significance

    While the data presented here don t explain how pyruvate is driving RET and mtROS; if pyruvate targets the electron transport chain directly or is converted (via TCA) to another metabolite that initiates RET and mtROS, this work merits to be deeply evaluated for potential publication in a RC journal. However, the language must be improved and polished before submission.

  6. Version published to 10.1101/2022.02.01.478654v1 on bioRxiv