Peer review of: Dissecting the cellular specificity of smoking effects and reconstructing lineages in the (2019)



REVIEWERS' COMMENTS: 
 
Reviewer #1 (Remarks to the Author): 
 
In their revised manuscript, authors have adequately addressed most of my concerns raised with the 
original submission. They added CRISPR-Cas9 knockout studies to validate the single cell prediction 
that tuft-like cells are the likely progenitor of both pulmonary neuroendocrine cells and CFTR-rich 
ionocytes. They have improved the cell classification and presentation by including the global umap 
and keep cell group names and colors consistent throughout the manuscript. Overall, the manuscript 
is much improved. Several remaining questions are listed below: 
1. In multiple places, authors assessed smoking effects on cell populations via cell proportional 

changes (Fig2, Fig3, FigS5,). We know that estimating compositional changes in single‐cell data 

requires sufficient cell numbers to robustly assess proportions changes, and sufficient sample numbers 
to evaluate expected background variation. The estimation of rare cell type proportion is even more 
difficult (Fig7), usually requires specific statistical models. While these results can be informative of 
changes in compositions between non-smokers and heavy smokers, however, should be interpreted 
with caution. 
2. Line 243-244: “In all, these data support a single developmental lineage of human secretory cells, 
driven by sequentially activated TFs, which transitions through functional intermediates (club cells) to 
culminate in a multi-functional mucus secretory cell,” The statement is too strong without lineage 
tracing or evidence of the TF driving this process. 
 
 
Reviewer #2 (Remarks to the Author): 
 
The revised manuscript by Goldfarbmuren et al., has nicely addressed many of the points raised after 
the initial submission. Specifically, the authors have: 1) added additional donors and increased the 
number of cells analyzed from their single-cell RNA-seq studies of in vivo samples; 2) more 
extensively validated the scRNA-seq results; 3) performed additional experiments to follow-up some of 
the findings from their in vivo and in vitro scRNA-seq profiling studies. This work, particularly the data 
defining smoke-induced transcriptional changes, will be a valuable resource for the broader respiratory 
community. 
 
Specific comments: 
 
1) While there are certainly novel aspects of this work – e.g., transcriptional changes induced by 
smoke, some that span cell states and others that are state-specific, evidence of a lineage heierarchy 
among tuft cells, PNECs, and ionocytes – some of the other follow-up work presented are validation 
and/or extensions of previously reported work. As such, the authors should cite the relevant 
previously studies to contextualize their findings for the reader. 
a. The relationship between club cells and mucus-producing goblet cells. While the authors raise a 
good point about the findings from mice that suggest that club cells can differentiate into goblet cells 
in response to IL-13, the Okuda paper (Okuda et al., AJRCCM 199: 715-727. 2019) quantifies the 
number of cells that express one or more of SCGB1A1, MUC5AC, and MUC5B in different regions of 
the airway (i.e., the ‘propensity’ of co-expression), and in the discussion, cite work from the Crystal 
lab (Zuo et al., AJRCCM 198: 1375 – 1388. 2018) that, together with their data lead them to propose 
a ‘possible lineage relationship between CCSP+ secretory cells and mucin-secreting cells in human 
airways’. In addition, since the initial submission of this manuscript, the Teichmann lab (Braga et al., 
Nature Medicine 25: 1153-1563. 2019) and the Barbry/Zaragosi labs (Garcia et al., Development 
(2019) 146, dev177428. doi:10.1242/dev.177428) have published complementary data that also 
identified a similar lineage relationship between club and goblet cells from scRNA-seq data from in 

vivo and in vitro (ALI cultures), respectively. These papers should be cited. 
b. The secretory/ciliated hybrid population. Braga et al., and Garcia et al., each describe a 
goblet/ciliated population, similar to the one defined in this work. Zuo et al., also proposed an 
‘ontologic link between club cells and ciliated cells’ based on a small number of SCGB1A1+ DNAI1+ 
cells in their single cell data. Each of these papers should be cited in this context as well. 
c. FOXN4+ population. While the characterization of the FOXN4+ population is certainly more 
extensive in this manuscript, the fact that it was described in Plasschaert et al., (albeit briefly, and in 
the supplement) should be acknowledged by referencing the work. The authors say that they cite the 
paper in the revised manuscript, but I don’t see the citation in the body of the results section. 
Moreover, the FOXN4+ population is described quite extensively as the ‘deuterosomal cell’ by Garcia 
et al., which should be cited as well. 
d. Rare cell populations. The authors are correct that the majority of the work in Montoro et al., was in 
mice, but the manuscript does include scRNA-seq data from primary human samples, which they use 
to identify human pulmonary ionocytes (see Fig. 5 of Montoro et al.). Moreover, Goldfarbmuren et al., 
state that ‘these three rare populations tended to cluster together when the entire epithelium was 
analyzed (in vitro and in vivo, and by others) potentially indicates a shared origin as well as function’ 
citing Plasschaert et al. However, in both Montoro et al., and Plasschaert et al., all three rare 
populations clustered separately in the mouse data, and the ionocytes formed a unique cluster in the 
primary human data (Montoro et al.) and ALI data (Plasschaert et al.) so referencing Plasschaert et al., 
in this in this instance is not correct and potentially misleading for the reader. It should be removed 
from this particular sentence in the manuscript. 
e. ALI timecourse. The authors have done an excellent job collecting data from the in vitro ALI model 
of airway epithelial differentiation at a very high temporal resolution, and the additional follow-up 
presented in the revised manuscript makes this section feel a bit like a paper within the paper. 
However, the number of cells collected per timepoint/donor leaves a bit to be desired. Based on the 
author’s response (‘each single cell time point (n=20) included cells from 3 donors with the cells from 
those 60 donor/time points harvested from 2-3 replicate inserts’), 5,976 total cells would mean that 
~100 cells were analyzed from each donor/timepoint. By comparison, although there was only a single 
timepoint analyzed in Plasschaert et al., that study analyzed 10x the number of cells per 
donor/timepoint. In addition, the recent work from Garcia et al., analyzed 9 timepoints during ALI 
differentiation, each with at least 10x the number of cells per timepoint. While the number of cells 
analyzed by Goldfarbmuren et al., was ‘sufficient to derive both ciliated and secretory cell lineages’, I 
wonder if they would have identified additional trajectories or substates if they had analyzed more 
cells/timepoint. 
2) For the UMAP projections presented in Fig. 1 and Supplementary Fig. 1 it would be interesting to 
know whether different groups (smokers, non-smokers) contribute differently to the cell states. The 
authors should split the data out into different panels by groups in the supplement (perhaps after 
Supplementary Figure 1b, which is very difficult to look at because of the density of the plot). 
3) For the rare states, which the authors define as 0.8% of the total population, it would be 
informative to report the percentage of each rare cell type for each donor to indicate the donor to 
donor variability (Figure 1). Note that in 1g there aren’t any CHGA+ cells, and without a control for 
the antibody there’s no reason to show the channel (i.e., it’s impossible to know whether there aren’t 
any cells in the field or the antibody simply didn’t work). 
4) The x-axis in Supplementary Figure 11b seems to be mis-labelled. Should the 0.25 and 0.5 labels 
be reversed? 
 
 
 
Reviewer #3 (Remarks to the Author): 
 
The authors have responded appropriately to my prior critiques. This revised version of the manuscript 

represents an important contribution to the field. 
 
 
Reviewer #5 (Remarks to the Author): 
 
This manuscript has a wealth of useful information on cellular phenotypes in the airway and their 
responses to smoking. I was asked to just review the electrophysiology in the manuscript regarding 
POU2F3 and FOXI1 KO human airway cultures. It is my understanding reviewers requested this new 
data and while I can appreciate the reviewer’s request and the importance of defining functions of the 
ionocyte, it really is a minor part of this massive and well-executed study. I also appreciate the 
author’s perspective on how detailed they should dig into the ionocyte functional studies in an already 
very lengthy and detailed manuscript. Nonetheless, I have some concerns about making the wrong 
conclusion that would set back the field in an area that is strongly debated. Here are my concerns, but 
I would like to go on record that even without the electrophysiologic functional data, I would say this 
is an outstanding manuscript and should be published. 
 
1) The approach to knockout POU2F3 and FOXI1 assumes that biallelic indels at the target occurs at a 
very high frequency. I would imagine that one would need at least 95% biallelic targeting to classify 
these are true knockout cultures. But the efficiency of gene targeting at the DNA level in these 
cultures is not given and this makes it difficult to conclude they are truly knockout for each gene 
based solely on protein or mRNA FISH expression profile of the gene target. I will simply use FOXI1 
KO as an example here. Fig. 6g shows a 2-fold decline in FOXI1 mRNA expression relative to control 
and no change in CFTR expression. The conclusion being that ionocytes don’t contribute to the 
majority of CFTR expression. But what if the indel frequency in these cultures was about 50%, that 
would mean less than 25% of the basal cells used to seed these cultures were actually nulls. I realize 
they also stain for FOXI1 protein in KO cultures (Fig. 6h) and the decline is larger than in the RNAseq, 
but in this scenario the sensitivity for detecting expression in cells with a single allele indel will also 
decline and could give a false impression of the KO efficiency. Without knowing the actual indel 
frequency in the genomic DNA of these populations it is hard to clearly interpret the functional data. 
How is the indel frequency best demonstrated? The information on the crRNAs used is unclear, but 
they stated they used two crRNAs to each gene, so TIDE analysis may not work if the indels are large. 
The target efficiency would need to be done by DNAseq of the locus or some PCR standard cloning of 
the target and Sanger sequencing. I really don’t mean to be nitpicking, but if the indel frequency in 
the populations is say 50%, I would find the electrophysiology hard to interpret from a CFTR cell 
biology standpoint. If the target indel efficiency is lower than they Fig. 6h might suggest, I think these 
limitations need to be pointed out in the text and conclusions toned down. I would also include the 
crRNA target sites, I may have missed them in the on line supplemental information. 
 
2)My major concern about the electrophysiology data is the manner in which almost all the data is 
presented as normalized to WT controls. This is also a concern for morphometry and cell counts for 
expression of the KO targets. How data is normalized can also affect the statistics (i.e., differences 
with normalization might be significant between groups, where as the raw delta data is not). I would 
much prefer to see the average raw delta data for all groups (including WT controls) with errors and 
some example timed traces that are representative the average deltas for each condition. This would 
provide unit measurements on the y-axis (i.e., uA/cm2) rather than a delta from WT controls. They 
two keep what is in the figures now, and put the additional data in a supplement. Why do I think this 
important? Ionocyte abundance, and maybe tuft cells as well, can vary greatly in human cultures. 
What is the cause of this variability, likely regional differences from where cells were collected in the 
airways (proximal to distal). Time in culture also impact whether CFTR current persist following 
differentiation and this could be related to ionocyte precursors in the cultures. This variability in 
ionocyte abundance also has a relationship to the amount of CFTR-mediated current in ALI cultures 

under stimulatory (forskolin) and inhibitor (CFTRinh172) conditions. In my opinion it important to 
know what the absolute current is under various stimulatory and inhibited conditions. An example of 
how this could affect the data is as follows. If you have a culture that makes few ionocytes and you 
knockout FOXI1, you would expect very little electrophysiologic difference from the WT control, but 
the absolute CFTR-dependent current (forskolin inducible or CFTRinh172 inhibited) in the WT cultures 
could be very low. This variability could be used as a strength, if the correlations between current 
changes were linked to both indel frequency and abundance of ionocytes in each donor culture. Right 
now, my sense is, without seeing the actually values for electrophysiology data rather than reference 
to WT controls, that there likely is this variability between donors and this could be misinterpreted if 
the data is only reported as normalized to WT controls. Well-differentiated human ALI cultures 
typically give CFTR-mediated currents in the range of 20-25 uA/cm2, but there is a very high range 
between donors. Poor human ALI currents can be in the range of 5uA/cm2, but can still have high 
resistances. All of this variability is lost when data is reported as normalized to WT controls. 
 
3)CFTR antibodies have fooled the field for decades, having demonstrated very high levels at the 
apical membrane of ciliated cells, so be careful about interpretation (Fig. 7d). As this group and others 
have shows, ciliated cells have near the lowest levels of mRNA by scRNAseq despite the apical CFTR 
staining with highly sited antibodies. mRNA FISH is the gold standard for CFTR detection. While this is 
not an electrophysiologic concern, the CFTR protein localization is used to make the case around the 
electrophysiology story.