RR:C19 Evidence Scale rating by reviewer:
Potentially informative. The main claims made are not strongly justified by the methods and data, but may yield some insight. The results and conclusions of the study may resemble those from the hypothetical ideal study, but there is substantial room for doubt. Decision-makers should consider this evidence only with a thorough understanding of its weaknesses, alongside other evidence and theory. Decision-makers should not consider this actionable, unless the weaknesses are clearly understood and there is other theory and evidence to further support it.
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Review:
The study investigates the effect of intestinal inflammation in IBD patients on the expression of SARS-CoV-2 entry factors, including entry receptors and host protease, and identifies putative upstream regulators of ACE2 in human ileum and colon. Using a combination of bulk and single cell RNA sequencing authors have convincingly demonstrated that mRNA intestinal expression patterns of ACE2 differs between ileum and colon of healthy and IBD patients as well as between control and inflamed tissues. The core hypothesis put forward is that inflammation occurring in the context of IBD results in dysregulation of ACE2 expression and therefore might lead to an increased susceptibility of IBD patients to SARS-CoV-2 infection. Authors conclude that adequate disease management is important for reducing the risk of COVID-19.
Essential revisions:
In this study authors clearly demonstrate that inflammation can trigger an increased mRNA expression of ACE2 in inflamed colonic tissue of IBD patients. Both, inflamed tissue biopsies isolated from IBD subjects and UC colonoids exposed to inflammatory stimuli in vitro, showed higher ACE2 expression in comparison to tissue isolated from non-IBD individuals and uninflamed controls from IBD patients. Given the crucial role of ACE2 in host cell invasion by SARS-CoV-2 and its known contribution to the rapid spread, severe symptoms and high fatality rates of infected patients, these findings are interesting and could be of relevance for the on-going global health crisis.
However, the current manuscript lacks evidence to support the authors’ conclusions concerning the importance of IBD medication in COVID-19 risk management.
Firstly, as authors clearly indicate (Page 15, Line 378-379), to date there is no direct evidence that could prove the causal link between altered expression of intestinal ACE2 and increased SARS-CoV-2 tropism or entry into intestinal tissue and, therefore increased susceptibility of IBD patients to COVID-19 infection. - Secondly, there is currently no evidence demonstrating the reduced risk of COVID-19 in IBD patients undergoing “adequate” treatment.
Given the above, I would suggest that the authors revise their manuscript to remove the following statements:
• “Our data support the importance of adequate control of IBD in order to reduce the risk of (complicated) COVID-19” (Page 3, Line 47-48) as not supported by the presented data
• “In line with our findings, national and international registries suggest active IBD as a risk factors for (complicated) COVID-19” (page 16, Line 395-396) as misleading – most of the provided references conclude no correlation being demonstrated between disease activity and patient’s susceptibility to COVID-19,“
• “Adequate disease management, by appropriate dampening of intestinal inflammation, therefore, seems key in preventing IBD patients from COVID-19.” (page 16, Line 395-396) as not supported by data,
• “Overall, our translational data provide further evidence for the clinical recommendation to pursue adequate control in patients with IBD to reduce the risk of (complicated) COVID-19” (Page 17, Line: 423-425) as not supported by the presented data, or to clearly indicate that these statements represent author’s opinion or hypothesis and are not undeniably provable with the data or current knowledge.
Alternatively, the above statements could be proven experimentally by providing the evidence for:
a) Increased risk of COVID-19 infection in patients with (active) IBD through evaluation of the number of SARS-CoV-2 particles (or spike-pseudotyped lentiviral particles, as reported by others: https://doi.org/10.1101/2020.04.13.039917) entry into tissue explants or colonoid cultures OR investigation of the binding of spike protein (recombinant version is commercially available) of SARS-CoV-2 to inflamed/uninflamed intestinal tissue of healthy individuals and IBD patients.
b) Decreased risk of COVID-19 infection in patients undergoing immunosuppressive treatment through studies of the effect of the specific IBD therapeutics on the potency and the evasiveness of SARS-CoV-2 in in vitro models or through a comprehensive summary of clinical reports (if available) that confirm this hypothesis. These data could not only strongly increase the impact of this manuscript but also provide evidence-based answers to long debated research questions.
The strength of this manuscript lies within the comparison of intestinal mRNA expression levels of various entry factors of SARS-CoV-2 across various intestinal regions (ileum and colon), healthy and disease states (including CD and UC) and disease activity (uninflamed and inflamed tissues) as well as in the direct demonstration of the in vitro induction of ACE2 expression in inflamed colonoids from UC patient by a mix of pro-inflammatory molecules. Since mRNA levels do not always correlate with functional protein levels, pairing bulk and single-cell RNA sequencing data with protein expression data could significantly strengthened the observations reported by the authors and ensure more accurate and complete conclusions.
Accordingly, I would suggest to validate the most critical data (i.e. ACE2 expression in healthy gut and in active IBD) via proteomic analysis, even a simple Western Blot analysis may be used for that purpose.
Moreover, authors should provide more information on the statistical significance and power of the scRNA-seq analysis.
Minor revisions:
1) It is not clear why tissue samples from uninflamed IBD individuals are grouped differently in bulk and scRNA-seq datasets. In the first case, uninflamed samples from both UC and CD subjects are pulled together into one group (uninflamed IBD ileum, uninflamed IBD colon), while inflamed tissues are grouped individually (inflamed CD ileum, inflamed UC colon and inflamed CD colon). In contrast, in the scRNAseq dataset all samples are grouped individually into: healthy ileum or colon, uninflamed CD ileum or UC colon, inflamed CD ileum or UC colon. - Authors should either describe the rationale behind the strategy used for grouping the data or unify the way that the data is represented across various figures in order to make their interpretation easier and more institutive. This could allow the readers to clearly distinguish the effect of disease activity or the disease subtype on the expression of ACE2/TMPRSS2/DPP4.
2) The authors claim (Page 3: Line 31-32, Page 14: Line 337, Page 16: Line 419) that the current study investigates the effect of inflammation on the “viral entry mechanisms”. - However, they do not provide any evidence to correlate transcriptomic expression of ACE2 with actual internalization of the virus, therefore, the use of the terms “viral entry factors, receptors or features” would be more appropriate.
3) The authors use term “organoids” when referring to tissue-derived cultures originating from colonic crypts. - According to the guidelines proposed by intestinal stem cell consortium (doi:10.1152/ajpgi.00493.2011), I would suggest the use of term: “colonoids” when referring to epithelial only cultures.
4) The title doesn’t seem to reflect the content of the paper well, I would suggest a change that would reflect more accurately the critical findings i.e. the effect of inflammation on the expression of SARS-CoV-2 entry factors.
5) Page 4, line 67 and 69, Page 5: line 84, Page 9: line 193: should be DPP4 not DDP4
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