Peer review of: Landscape of somatic single nucleotide variants and indels in colorectal cancer and impact (2021)


Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

In their revised manuscript, Zaidi et al. have now provided the underlying mutational and clinical 
data and have clarified some aspects of their analysis. 

The main concern of this reviewer remains: In their cohort, they find that about 5% of tumors are 
hypermutated but are neither MSI-H nor affected by driver mutations in POLE or POLD1. If real, 
this would be an important novel subtype of colorectal cancer that has not been identified or 
described in other cohorts before (TCGA, Yaeger et al. Giannakis et al., and others) and the 
description of which would require particular attention in this study. An alternative explanation is 
that this subtype can, at least in part, be explained by artifacts in the mutation calling pipeline. 
The authors should first demonstrate that they have ruled out any artifacts and then describe this 
novel subtype in greater detail. 

While the patterns of non-synonymous mutations in genes known to be mutated in colorectal 
cancer look as expected, the following findings, based on a quick and superficial analysis of the 
newly provided supplemental data, hint at possible issues with the mutation calling pipeline: 1) 
Many of these hypermutated / MSS / non-POLE tumors have an unusually high intronic / non-
coding mutation burden (which of course could be interesting biology as well). 2) The gene RYR1 
contains a suspicious mutational hotspot at amino acid 4469 (E4469A). Is this a real mutation or 
an artifact? 3) 10 samples have a novel, recurrent frameshift mutation in BRAF, although that 
could be a previously undetected passenger mutation in MSI-H tumors. But these are just a few 
small suggestions, and there are many other ways to explore the data. 

In summary: In this reviewer’s opinion, the authors need to further explore the interesting 
subtype that is characterized by an increased mutation burden but an absence of the MSI-H 
phenotype and exonuclease mutations in POLE. This subtype is either biologically novel and 
interesting or can be explained by issues with the variant data. 

Reviewer #2 (Remarks to the Author): 

Strengths are as before - Good mutation detection strategy e.g. validation of reads 

Some ongoing issues 

HM/NHM status as a confounding factor - it is unclear whether the authors have adjusted this 
analysis to minimise the possibility that hypermutated/non-hypermutated status acts as a 
confounding factor, as the other reviewer has pointed out this may explain the full extent of the 
survival association with P53. Presumably this analysis should be performed as a multivariate 
analysis incorporating mutation status + NHM/HM status + stage + grade + age + sex to look for 
independent predictors of survival. I believe the authors analysis currently only incorporates age + 
sex + study. 
This issue has been raised by reviewer 1 and I do not feel that the manuscript has been 
appropriately updated to reflect how tentative these findings of survival benefits are 

There is a discrepancy between “in NHM tumours, 77% of tumours have mutations in the 
Wnt/beta-catenin pathway” (line 140) and “99% of NHM tumours harboured truncating mutations” 
in APC, please can the authors explain this discrepancy as I believe the first version sent to review 
referred to a frequency of 62.7% in NHM tumours 

Minor issues 

Line 32 “comprehensive profiling” - in 2019 a truly 'comprehensive profiling' should include CNAs 
+/- epigenetic changes 

Line 70 - “NHM” has not been defined as non-hypermutated at this point in the manuscript 

“As our study includes almost 10 times the sample size of the first TCGA paper (Nature 2012), our 
study can provide further insights given improved statistical power.” This is misleading as the 
TCGA have published results of their complete cohort (around 600 patients) in Cancer Discovery 
last year (Grasso et al., 2018). 

“We also like to note that we have information on CRC-specific survival, while TCGA has only data 
on overall survival, which tends to weaken associations between mutated genes and survival” + 
“As overall survival is a combined measure of many causes using this would attenuate or obscure 
any association of a gene with CRC-specific survival.” 
What is the evidence for this (no reference given)? 

“We like to point out that no publication using the TCGA data (including the Nature 2012 
publication) reported on survival.” This is slightly misleading - 
https://www.ncbi.nlm.nih.gov/pubmed/29625055.