Review of Spreading of a virulence lipid into host membranes promotes mycobacterial pathogenesis

This Zenodo record is a permanently preserved version of a PREreview. You can view the complete PREreview at https://prereview.org/reviews/3718438. We, the students of MICI5029/5049, a Graduate Level Molecular Pathogenesis Journal Club at Dalhousie University in Halifax, NS, Canada, hereby submit a review of the following BioRxiv preprint: Spreading of a virulence lipid into host membranes promotes mycobacterial pathogenesis CJ Cambier, Steven Banik, Joseph A. Buonomo, Carolyn Bertozzi bioRxiv 845081; doi: https://doi.org/10.1101/845081 We adhered to the Universal Principled (UP) Review guidelines proposed in: Universal Principled Review: A Community-Driven Method to Improve Peer Review. Krummel M, Blish C, Kuhns M, Cadwell K, Oberst A, Goldrath A, Ansel KM, Chi H, O'Connell R, Wherry EJ, Pepper M; Future Immunology Consortium. Cell. 2019 Dec 12;179(7):1441-1445. https://doi.org/10.1016/j.cell.2019.11.029 SUMMARY: Cambier CJ, et al. investigated the mechanism by which a virulence lipid on the outer mycomembrane (OM) of Mycobacterium marinum prevents host immune activation. They report on a system for extracting lipids from the OM, and also for reconstitution of OM lipids. Using this technique, the authors confirmed that the virulence lipid, phthiocerol dimycocerosate (PDIM), is required for avoiding host toll-like-receptor (TLR)-dependent immune responses to aid bacterial infection. The authors describe a novel method for labelling specific lipids on the OM. Using this approach, the authors demonstrated that PDIM spreads away from the M. marinum OM and into the membranes of nearby zebrafish host cells. By fixing PDIM to the OM to prevent spreading, they demonstrate that this spreading phenotype is required to avoid the host TLR-dependent immune response. Overall, we thought this was an excellent paper. Although we were confused about several findings, we believe the authors could likely address our main concerns by including clarifying statements in the text. OVERALL ASSESSMENT: STRENGTHS: Overall, we thought that a clear rationale was provided for each experiment. The manuscript introduced interesting new techniques like lipid reconstitution and labelling. New insights into PDIM spreading into host membranes could be valuable for better understanding Mycobacterium pathogenesis in humans and warrants further research. WEAKNESSES: Several results were difficult to interpret and could be misleading without further clarification. In particular, distinguishing between levels of TLR-independent and TLR-dependent macrophage activation was confusing. In at least one instance, a control experiment that would greatly aid interpretation is missing. DETAILED U.P. ASSESSMENT: OBJECTIVE CRITERIA (QUALITY): 1. Quality: Experiments (1-3 scale) SCORE = 1.5 Figure by Figure, do experiments, as performed, have the proper controls? · In general, we thought the authors did an excellent job of including appropriate controls. For instance, we were convinced by their hydroxylamine control experiments in Figure 4E that the fluorescent modifications themselves were unrelated to the in vivo spreading of PDIM that they report. · However, in Figure 2C the bacterial volumes for both M. marinum strains should also be reported in MyD88-deficient zebrafish. This would allow us to make clearer comparisons to the findings in Figure 2D. Are specific analyses performed using methods that are consistent with answering the specific question? Is there the appropriate technical expertise in the collection and analysis of data presented? · Overall the authors used the appropriate methods for answering their specific questions (although we lack some relevant expertise, as noted below). Our issues are not with these methods, but instead with interpretation of results. However, we did have issues with several analyses, which may be resolved by adding clarification in the main text. · We were confused about the results reported in Figure 2D regarding macrophage recruitment by bacteria. If WT lipids are required to circumvent the TLR response, we believe that the expected result would be low macrophage recruitment for the WT lipid treatment regardless of whether the zebrafish are MyD88-deficient. Instead, the recruitment levels seem similar to the result with mmpL7 knockout lipids when MyD88 is present. At the very least, this finding requires more explanation in the text. · Most of the in vivo spreading experiments are focused on spreading specifically to macrophages. However, azido-DIM spreading to epithelial cells occurs in the absence of macrophages (Figure 4F and G). Although the authors do point this out, it remains unclear whether there is a difference in affinity between macrophages and epithelial cells. · For Figure 6E, we were also confused why the WT Live samples had such high macrophage recruitment. Again, this result seems at odds with the conclusion that WT lipids enable the bacterium to down-regulate TLR-dependent activation of macrophages. The confusion here may arise due to the difficulty in distinguishing macrophages recruited from TLR-dependent and TLR-independent signaling. Again, at the very least this distinction should be clarified in the main text. In particular, the authors should emphasize that the data in Figure 6E (and Figure 2D) is consistent only with PDIM-deficient bacteria or bacteria unable to spread PDIM onto host membranes to require TLR signaling to recruit macrophages. Based on the macrophage recruitment findings alone it is not convincing that these cells are detrimental. Also, the authors should emphasize that macrophage recruitment is high irrespective of lipid composition. Is there the appropriate technical expertise in the collection and analysis of data presented? · To the best of our knowledge the authors have the appropriate expertise. However, we should note that many of the techniques in this study, and particularly the chemistry work, is outside our own expertise. Do analyses use the best possible (most unambiguous) available methods, quantified via appropriate statistical comparisons? · We did find certain approaches ambiguous (see above points), which should be clarified. · Many of the comparisons from Figure 2 onwards did not include any statistical tests. We do not anticipate that the key findings of this paper will change after including statistical tests, but nonetheless these should be included to make the results more convincing. In addition, significance stars should be indicated on the figures and the authors should describe all statistical tests they perform. · Several times in the text the authors mention their result is representative of three separate experiments. Based on this wording, it is unclear whether all reported differences were reproducible across separate biological replicates. If there were no differences in interpretations across different experiments this should be clearly stated. Alternatively, if there was a lot of variation across experiments, then this additional data should be included in the manuscript (perhaps as supplementary figures depending on the extent of disagreement). Are controls or experimental foundations consistent with established findings in the field? A review that raises concerns regarding inconsistency with widely reproduced observations should list at least 2 examples in the literature of such results. To address this question may occasionally require a supplemental figure that, for example, re-graphs multi-axis data from the primary figure using established axes or gating strategies to demonstrate how results in this paper line up with established understandings. It should not be necessary to defend exactly why these may be different from established truths, although doing so may increase the impact of the study. · The key findings of this paper are consistent with other work in this area. 2. Quality: Completeness (1-3 scale) SCORE = 1 Does the collection of experiments and associated analysis of data support the proposed title/abstract-level conclusions? Typically, the major (title or abstract level) conclusions are expected to be supported by at least two experimental systems. · The authors' fluorescent labelling approach convincingly showed that PDIM spreads into host membranes. · PDIM spreading was shown to be required for the TLR-dependent activation of macrophages (Figure 6E), although we are unclear why the numbers of macrophages would be so similar when recruited through a TLR-independent route (i.e. for the Live samples). · They also convincingly show that PDIM spreading into host membranes promotes pathogenesis, based on the observed increases in bacterial volume (especially in Figure 6F). Are there experiments or analyses that have not been performed, but if "true" would disprove the conclusion (sometimes considered a fatal flaw in the study)? In some cases, a reviewer may propose an alternative conclusion/abstract that is clearly defensible with the experiments as presented, and one solution to 'completeness' here should always be to temper an abstract or remove a conclusion and to discuss this alternative in the discussion section. · Again, we believe further clarification is needed to discuss the high levels of macrophage recruitment due to a TLR-independent process. If a clear explanation cannot be given, then there could be issues with how some of the results in this paper are interpreted. However, we think the main conclusions of the article are robust. 3. Quality: Reproducibility (1-3 scale) SCORE = 1 Figure by Figure, were experiments repeated per a standard of 3x repeats or 5 mice/cohort etc.? · The sample sizes of all experiments presented were sufficient. Is there suffic

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