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

Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

The authors applied scRNA-seq to identify cell types and states of the tracheal airway epithelium in 
smokers and nonsmokers, infer the lineage relationship among these cells, and determine the 
influence of cigarette smoke on individual airway epithelial cell types. This study provided insights into 
cellular heterogeneity in human airway epithelium, lineage relationships, and cell type specific 
responses to smoking. The dataset and study could be a useful resource in the field. 

Major comments: 

1.The cell names are not clearly and consistently defined. Each figure appears to have different cells
not clear how they defined and how they related (Fig1b, 2a, 3d, 4a, 5a). The authors presented
several clustering analyses using different subsets of cells and summarized the clustering
specifications in Supp Table 5, it is difficult to read the text and figures while map clustering results
back to Supp Table 5. No complete cluster information was shown in the figures; instead, clusters
were replaced with cell types/states in the different figures, some of which do not have the same
number types/states as the number of clusters. It is unclear how clusters were mapped to those cell
types/states and any clusters were merged or removed in different analyses. Providing tSNE/UMAP
visualizations of complete cell clusters and the mapping of clusters to cell types/states in their
corresponding figures will greatly help understand the analysis. The authors should be very clear
about the total number of major cells and associated subtypes (in one t-SNE or several associated t-
SNEs in one figure) and explain the evidence supporting the definition (e.g, early vs later vs
maintenance vs mature ciliated or secretory cells, basal vs basal-like, differentiating and intermediate
basal).

2.While pseudotime lineage predictions and interpretations are interesting, the figure presentation is
not easy to visualize (Fig2b, 3e). It would be nice to see the pseudotemporal ordering of the single
cells along each differentiation lineage as in many of the publications. The authors should provide
further evidence from the literature or their own validation to support the novel predictions (e.g., tuft-
like to ionocytes). Any evidence to support the transdifferentiation of mature mucous cells to mature
ciliated cells? In Fig1, these two populations are not close to each other. Similarly, the rationale for
why they use four gene modules to represent secretory cell lineage instead of the previous defined cell
types and subtypes and how these gene modules in relationship with the cell subtypes is not clearly
explained.

3.The authors stated in abstract and multiple other places in the manuscript that they generated a
first comprehensive atlas of human airway epithelial cell types, states, lineages, and cell-specific
responses to smoking which will be a useful resource to the field. But neither raw nor processed
scRNA-seq data have yet submitted to any public repository (e.g., dbgap or GEO). It is required by the
journal to make the data accessible. A public website to host and query these data will be a nice
addition of the manuscript and useful tool to the field.

Specific comments: 

1. Fig1i presents one of the major results of cell type specific responses to smoking. Nevertheless, the
methods used to reach the conclusions were not clearly presented.
(a) Please describe the analysis. What’s the gene list? How many of the genes from the bulk RNA-seq
analysis were able to be mapped to the single cell data and used in the analysis? Any of those genes

differentially expressed between nonsmokers and heavy smokers in any cell types? 
(b) What does the “mean normalized expression” mean? The variances of individual genes in 
individual cells were not shown. “Mean” operations can be greatly affected by outliers. Fisher-exact 
test can be used to check whether the smoking genes from bulk RNA-seq are enriched in specific 
airway cells. 
 
2. Fig1j showed the common and cell type unique smoking responsive genes from single cell analysis. 
Are any of these genes overlapped with the bulk RNA-seq derived smoking response genes that were 
used in Fig1i? 
 
3.For the lineage reconstruction for KRT8hi and mucous secretory cells, (a) Please show the clustering 
results, such as visualizing the 9 clusters in tSNE or UMAP in FigS2. The visualization of 8 clusters in 
FigS2a is difficult to read the clusters. (b) How were the 9 clusters in FigS2ab mapped to the four 
modules in Fig2a? 
 
 
4. The MUC5AC and MUC5B correlation analysis. 
Fig2c showed 78% of mucous secretory cells co-expressing MUC5AC and MUC5B, “consistent with the 
transcriptome-wide homogeneity observes”. However, Fig2e showed that there is little overlap in 
genes correlated with MUC5AC and MUC5B. Seems to suggest a heterogeneity within this population 
of cells. Are these two results contradicted to each other? Is the difference due to smoking? 
 
5. Fig3c is insufficient to support that “MUC5AC was induced and MUC5B was suppressed by heavy 
smoking”. No statistics were shown to support the change in the expression levels or in the expression 
frequencies, the % change could due to sampling. 
 
 
6. The name and analysis of “proliferating basal cells” in Fig1b, Fig3d and FigS3d/e are confusing. 
In Fig1a and FigS1, authors named the cluster as “proliferating basal”, in Fig3d, there are 
“proliferating basal SMG cells” and “surface proliferating basal”, are those are same cluster or sub-
cluster cells. Why was this original “surface” basal cell population considered in the analysis of SMG 
cells? If “proliferating SMG basal cells” were considered as SMG basal cells, why were these cells not 
involved in the lineage reconstruction analysis? In FigS3d, a subset of “proliferating SMG basal cells” 
are closed to “myoepithelial” cells and away from other cells. Are they in a same cluster in the sub-
clustering analysis? Please show the clusters of sub-clustering analysis. 
 
7. Doublet analysis cannot be purely based on the gene count. Several new doublet detection tools 
can be used to detect potential doublet. E.g., Are the SMG myoepithelial cells (epithelial/mesenchymal) 
doublets? Are the hybrid secretory/ciliated cells doublets? 
 
8. The analyses in Fig3 and FigS3 are insufficient to support the stem function of the “SMG 
myoepithelial cells”. 
(a) The “SMG myoepithelial cells” are not proliferative, no SOX9 expression, the pseudo time analysis 
manually specified myoepithelial cells as the starting point, please provide rationale for doing that. It 
is obvious that the expression of muscle related genes will reduce and basal related genes will 
increase when moving from myoepithelial cells to basal-like cells, as these are the markers that were 
used to define the two cell populations, this is not be enough to support that “SMG myoepithelial cell” 
is the progenitor population. 
(b) For the lineage construction analysis in FigS3h, “myoepithelial cells” appears away from other SMG 
cells and not in the backbone of the inferred lineage. Should the green cells, located around “2.5 of 
component 2” at the end point of the backbone of the inferred lineage, be more appropriate to be the 

start point? 
(c) In addition, there is another end point of the backbone that consists of cells with dark green color 
in the far right of “Component 1” (SMG basal 3?). From FigS3e, dark green cells were close to 
“proliferating SMG basal cells”. Would this point be more appropriate to be the start point? 
(d) Why were the “proliferating SMG basal cells” not considered in the lineage reconstruction analysis? 
I think it will be helpful to include this population, it likely to be the starting point. 
 
 
 
 
Minor 
1. Fig2b and 3e are difficult to read. The variances of individual genes in individual cells were not 
shown in this type of graph presentation. 
2. The network presentations are hard to read and impossible to see the relationships among the 
functional terms. Suggest to move these hairball networks to supplementary figures and summarize 
key model schema of the network in the main figure. 
 
 
 
Reviewer #2 (Remarks to the Author): 
 
The manuscript by Goldfarbmuren et al., describes a series of single-cell RNA seq experiments, 
designed to generate an atlas of tracheal epithelial cell states from smokers and non-smokers, and to 
ultimately define the changes in states and/or lineage trajectories driven by cigarette smoke. The 
authors reach several conclusions based on their data, most of which lack substantial follow-up and 
instead read more as intriguing hypotheses based on bioinformatic analysis of the scRNA-seq data. 
Overall, while the single-cell RNA-seq data presented is interesting, there are several factors that limit 
the impact of the work: 1) the number of samples (3 non-smokers, 2 ‘light’ smokers, and 2 ‘heavy’ 
smokers), as well as the number of cells (13,840 in total, note that it isn’t clear how many cells are 
from each donor) is quite limited, making the claim in the abstract ‘we generated a comprehensive 
atlas’ questionable; 2) many of the observations reported (e.g., FOXN4+ population, a continuum of 
secretory states from club through goblet with markers of both cell types co-expressed) have been 
described elsewhere (see Specific Comments, below); 3) many other observations described 
throughout the manuscript are based solely on the scRNA-seq data and lack proper validation. 
The most interesting, and indeed novel aspect of this study is the overlaying of the smoking data onto 
the non-smoking atlas. If the authors focused more of the study on the changes induced by smoking, 
provide rigorous validation of the sequencing data, and identified new, potential therapeutic strategies 
for restoring airway homeostasis in smokers, this would undoubtedly increase the impact and broad 
interest of the work. 
Specific comments: 
1. Figure 1: While this figure lays the foundation for much of the work in the paper, there are several 
challenges to the experimental design: 1) the number of samples for each ‘condition’ (3 non-smokers, 
2 ‘light’ smokers, and 2 ‘heavy’ smokers), as well as the number of cells in total (13,840), is quite 
modest; 2) the characteristics of each donor group vary broadly, particularly for the ‘heavy’ smokers, 
where one donor has 15 total pack years and the other has 90. Additionally, the heavy smokers were 
in their late 50s, while the light and non-smokers were in their mid-30s or younger; 3) It’s unclear 
exactly how many cells were sequenced for each donor (if it’s an equal number per donor then it 
would be less than 2000 cells for each). This is extremely important, given the small number of 
donors per group, and the fact that the authors only observe transcriptomic differences between the 
heavy smokers and the non-smokers. Altogether this raises questions about the conclusions that the 
authors make about the effects of smoking throughout the manuscript. This study would greatly 

benefit from many more donors (and more cells per donor), particularly for the smoking groups. 
2. The relationship between club cells and mucus-producing goblet cells has not only been described in 
mice (as the authors reference), but the co-expression of club cell markers (SCGB1A1) and mucins 
(MUC5B and MUC5AC) in surface epithelial cells has been recently described in humans (Okada et al., 
AJRCCM 199: 715-727. 2019.). In fact, the staining in Fig. 2D essentially reproduces the staining in 
Fig. 6 of the Okada paper, which the authors do not cite. While the transcriptional data, and the gene 
modules identified from the pseudotime trajectory analysis are interesting, the previously published 
work decreases the novelty of the ‘developmental lineage of human secretory cells’ from intermediate 
basal cells through a club cell state and into a mucus-producing goblet cell the authors report. 
Functional validation of one or more of the genes present in any of the gene modules identified (e.g., 
determining whether any of the transcription factors identified are necessary and/or sufficient for 
secretory cell formation/maturation) would increase the impact of the authors’ findings. 
3. The transcriptional changes induced by smoking are largely not validated by in situ hybridization 
(e.g., RNAscope) or at the protein level by IF (apart from a single panel image in Figure 3g). The 
smoking data is the most novel aspect of this work, and a more thorough, careful validation of the 
changes observed in the scRNA-seq data would increase the impact of the work. 
4. The ALI scRNA-seq timecourse data set has the potential to be quite impactful, but (similar to the 
primary human data) the number of cells analyzed (5,976) is really quite low. It’s unclear how many 
cells were sequenced at each time point, but assuming an equal number per timepoint (20), that 
would mean about 300 cells per timepoint. Moreover, it’s unclear whether all of the timepoints were 
from multiple donors (which would make the number of cells per timepoint per donor extremely small) 
or whether a subset of timepoints were from donor 1, a subset from donor 2, etc., and whether all of 
the cells used in the ALI experiments were from non-smokers (I’m assuming this is the case). Overall, 
the limited number of cells analyzed, and the lack of clarity about the samples used, limit the impact 
of this part of the study, which could be a valuable resource for the community. 
5. Although the ALI data set is limited with respect to the number of cells analyzed, this is the part of 
the paper with the most validation, with the authors focusing on FOXN4 and performing a CRISPR 
experiment in the ALI model to test whether it is required for ciliogenesis. However, there are at least 
two factors that limit the impact of this finding: 1) the observation that FOXN4 is expressed during 
MCC differentiation was described recently (Plasschaert et al., Nature 560: 377-381. 2008). In fact, 
the staining shown in Fig. 4c is very similar to the data shown in Extended Data 4B in Plasschaert et 
al.; 2) the CRISPR experiment lacks sufficient information about controls, e.g., how the percent 
editing was determined, and whether the percent editing (indel) correlates with the effect on 
ciliogenesis. 
6. The secretory/ciliated ‘hybrid’ population described by the authors has been previously observed in 
primary human tissue samples (Tyner et al., JCI 116: 309-321. 2006). 
7. The authors description of the rare cell types (PNEC, tuft, and ionocytes), and in particular the 
markers that are expressed in each one, as well as their originating from basal cells, has been 
described recently (Montoro et al., Nature 560: 319-324. 2018; Plasschaert et al., Nature 560: 377-
381. 2008). While the lineage relationship among the rare populations is potentially intriguing, the 
data supporting this speculation is limited to the RNA-seq analysis without proper validation with 
immunofluorescence, or testing whether depleting tuft cells (for example, by knocking out POU2F3) 
results in fewer ionocytes, which would support the authors statement that ‘tuft-like cells may be a 
precursor to ionocytes, and possibly PNECs’. In addition, using the clustering of the rare populations in 
the tSNE plot in Figure 1 as evidence that they have ‘a shared origin as well as phenotype’ is not a 
particularly strong argument, and could simply be the result of these cells being represented by a 
small fraction of the data. It’s worth noting that in the Plasschaert et al paper that the ionocytes 
clustered separately from the ‘Brush + PNEC’ cluster in the human ALI cultures, and each of the three 
rare populations clustered independently in the in vivo mouse data, although the authors cite the 
Plasschaert paper as having seen the cell types cluster together as they report. Finally, the previously 
published work by Montoro et al., and Plasschaert et al., define ionocytes as FOXI1+; V-ATPase+ 

based on the expression of these factors in ionocytes in other organisms/tissues. The expression of 
CFTR is a feature of pulmonary ionocytes, but should not be used to define whether a cell is an 
ionocyte or not. 
 
 
 
 
Reviewer #3 (Remarks to the Author): 
 
General comments: 
In this study Goldfarbmuren and colleagues performed sc-RNAseq on tracheal epithelial cells isolated 
from 3 lifelong nonsmokers, 2 "light smokers", and 2 "heavy smokers". This work: 1) confirms and 
extends lineage specification trajectories established in mice to human tracheas; and 2) investigates 
how cigarette exposure alters gene expression profiles in a cell-type-specific manner. On the first 
point, the authors validate the existing paradigm that secretory cell arise from basal cells and provide 
evidence that goblet cells pass through a Club-cell-like intermediate stage and importantly they define 
specific transcription factors involved in this progression. The authors also identified a population of 
cells that express markers of mature MCCs and mucus secretory cells, and thus suggest that mucus 
secretory cells may transdifferentiate into MCCs rather than both arising from a shared Club-cell-like 
progenitor. Additionally, the authors: 1) characterized differences between submucosal gland (SMG) 
and superficial secretory cells, suggesting that myoepithelial cells may be an early progenitor for SMG 
basal cells; 2) provide evidence that rare cells such as tuft and ionocytes are phylogenetically related; 
and 3) newly identify FOXN4 as a MCC-specific transcription factor required for proper MCC 
development in vitro. Overall, the data presentation and visualization are excellent, the methods 
described in exacting detail, and many of the individual observations highly novel. 
 
However, data regarding cell-type specific influence of cigarette smoke are hard to interpret due to 
several factors. The sample size is extremely small and not aged matched. The authors acknowledge 
that the 2 samples they termed "light smokers" did not differ from nonsmokers in measured 
parameters, which is not surprising given they had minimal smoking history and were from relatively 
young individuals. Many of the crucial findings of the paper such as the impact of CS on MUC5B and 
MUC5AC are thus generated from three young nonsmokers versus 2 older patients with an extensive 
smoking history. Neither PFT data or imaging data are provided to ensure these patients did not have 
lung disease. In-group, as opposed to between-group comparisons are minimal. These issues 
substantially limitations interpretation of smoking related effects. 
 
Specific comments: 
1. The authors should increase the sample size of nonsmokers and smokers and use more standard 
descriptions (not light and heavy smokers). It would be preferable for the groups to be better age-
matched. Also, it is necessary to know whether the long-term smokers had COPD. Demographic 
characteristics should be included in the body of the manuscript. 
2. While the data supports the conclusion that Club cells serve as a progenitor population for mucus-
expressing cells, care must be taken to not imply that progression through each module is inevitable 
"culminates... in a mucus cell." These data are not incompatible with the hypothesis that only a subset 
of Club cells make the final transition to mucus cells depending on external cues. 
3. While the authors correctly state that smoking-induced alterations in lineage specification are 
associated with diseases such as COPD and asthma, they do not mention that the bulk of pathology in 
these disease arise from small airways. The types and proportions of cells differ along the 
tracheobronchial tree, yet the authors only sampled large airways. This should be acknowledged as a 
limitation of the study. 
4. Please clarify the source of tracheal tissue that was used to identify rare cell types (i.e. Fig. 1g). 

5. Core smoking-related genes were defined as present as in >4 cell types. The authors should 
separately provide information on how this number varies when more stringent criteria are used (i.e. 5, 
6, 7, all cell types). 
6. The authors should provide a second method of pseudotime trajectory analysis to validate findings 
in 2b and 3e. 
7. The authors should provide the EM image currently in the supplement for Figure 4d. 
8. Since protein-level data is not provided, differences in CFTR expression between ionocytes and 
other cell types don't provide much biologically relevant information. It seems very surprising that 
Krt8+ transitional cells would be a major source of CFTR since these may have minimal contact with 
the airway lumen. This should be better explained/discussed in the manuscript. 
9. PNECs are clustered at airway branch points and present sporadically throughout the epithelium. If 
sufficient cells are available, the authors should provide subclustering information on PNECs and 
determine whether different clusters correspond to these 2 groups.