Peer review of: Fibroblast-enriched endoplasmic reticulum protein TXNDC5 promotes pulmonary fibrosis by (2019)

Reviewers' comments: 

 

Reviewer #1 (Remarks to the Author): 

 

1. Please make sure that the figure legends for animal studies point out clearly that (eg Figure 2) the 
tissue extracts and other histology are from day 21 post bleo animals. 

2. The data in figure 2 show mRNA levels at day 21 of bleo treatment. How does this data compare 
to the several array data sets in the literature already?? (Kaminski et al 2000; Haston et al 2005 or 
Cabrera et al 2013). 

 

3. Supplementary figures appear to be added to previous concerns about localization of TXDNC5 to 
fibroblasts only. Endothelial cells appear positive (Supplementary fig 2c and 2d) so what endothelial 
cell functions or productions are affected in the global KO mice that could affect fibrogenesis?? 

 

4. Figure 3d implicates TXNDC5 in fibroblast accumulation after bleo, but what is the effect of 
TXNDC5 deletion on other fibroblast functions in other tissues?? (tissue repair, normal growth, 
female post menstruation restructuring, etc). 

 

5. Fig 3b what does “white areas” refer to? How is it detected? How does this show lung volume 
reduction? 

 

6. Also for 6e the details refer to “Targeted deletion of Txndc5” when it is a global deletion and this 
same usage is in second to last paragraph of discussion “Using global TXNDC5 knockout mouse line 
we have shown that targeted deletion of TXNDC5 “ can be confusing as to what is the “targeted” 
cell? In my understanding, targeted implies the gene is being deleted in a specific cell. The 
experiment to delete in lung fibroblasts (Fig 5 a and b) specifically uses fibroblast in culture and 
cannot be universally applied or construed to relate to fibroblast specific deletion in vivo. 

Very confused aggregation of data in combining individual cell cultures alongside in vivo Bleomycin 
experiments. 

 

7. Fig 6 TXNDC5 knockdown should be shown to be effective by decrease or absence of TXNDC5 
mRNA. Again, the use of “targeted deletion” (fig 6d) is confusing and missing the day 21 detail that is 
needed to clarify the situation in the bleomycin experiment. It was a global deletion mouse that was 
used. 

 

8. The claim is that TXNDC5 facilitates the folding of TGFbR1, but what is the effect of this chaperone 
on TGFbR2?? Supp figure 7 shows the FRET data for TGFbR1 but what is the data for TGFbR2?? Both 
are required for proper TGFb1 signalling?? 

 

9. Fig 7b: If TXNDC5 acts through TGFbR1 and not 2 there should be R2 dependent genes that are 
regulated through TGFb stimulation. You should show this to certify that R1 is the target even 
though it is recognized that R2 forms a heterodimeric complex with TGF-beta receptor type-1, and 
binds TGF-beta to phosphorylate proteins, which then enter the nucleus and regulate the 
transcription of genes related to cell proliferation, cell cycle arrest, wound healing, 
immunosuppression, and tumorigenesis. Are any or all TGFb responsive genes depleted by KO of R1? 

 

Also co-precipitation is a usual way to show direct protein-protein interaction but Fret analysis 
seems good for conclusion. 

 

10. For a Nature article in 2019, the background references regarding the myofibroblast and 
pulmonary fibrosis seem somewhat dated (ref 2,3 and 7). There has been much written about these 
2 issues since 2003 and 2013. 

 

11. The most crucial question regarding whether fibroblast specific deletion (therefore fibroblast 
targeted deletion) of TXNDC5 leads to inhibition of fibrogenesis is addressed in Fig 10 and suggests 
strongly that this is an important pathway in progressive fibrosis. Critical questions revolve around 
whether this pathway of intervention in TGFb1 mediated fibrosis is any different from those 
examined through the use of other ALK 5 inhibitors, (such as LY 364947 or SD201) and can avoid the 
cardiac toxicity (at least) seen with both of these very powerful TGFb1 inhibitors?? 

 

 

 

Reviewer #2 (Remarks to the Author): 

 

The study by Lee et al seeks to understand the pathogenic mechanisms underlying the progression 
of pulmonary fibrosis. The study’s major focus is on the protein TXNDC5, a disulfide isomerase 
abundantly expressed in the ER of mammalian cells. Interest in this protein relates to a recent report 
by this group showing that deficiency of TXNDC5 exacerbates cardiac fibrosis in rodents. In this 
study, the focus is on TXNDC5 expression in the lung. The major findings are that levels of TXNDC5 

are increased in lungs of IPF patients as well as bleomycin-exposed mouse lungs, and that global or 
fibroblast-specific deficiency of TXNDC5 ameliorates experimentally induced pulmonary fibrosis in 
mice. Mechanistically, investigators also purport that TXNDC5 is critical for regulating myofibroblast 
differentiation by controlling the expression of TGFbeta receptor 1 levels. Overall, findings in this 
publication are likely to be of interest to the wide readership audience of this journal, although 
conclusions are somewhat oversimplified and seem to argue against the current paradigm of ER 
stress playing a pathogenic role in fibrotic lung diseases. To support the conclusions of the 
manuscript the following studies should be considered. 

Major 

1) The mechanistic connection between TXNDC5 and ER stress is rather weak. Please examine more 
than one ER stress pathway, namely PERK and IRE and their downstream effectors as well as 
consider verifying that protein aggregation is increased in cells. 

2) As a control, please knockdown either the PERK or IRE pathways (regardless of whether elevated) 
to confirm that TXNDC5 is not regulated through other arms of the unfolded protein response. 
Otherwise, it is somewhat premature to conclude that everything is regulated through ATF6. 

3) The idea of knocking down TXNDC5 to reduce pulmonary fibrosis is somewhat confusing since one 
would expect that ER stress would be increased in the absence of this proteins expression (cells 
would have a harder time folding proteins). To address this, please examine markers of ER stress in 
lung and fibroblasts of TXNDC5 expressing and non-expressing cells. 

4) Figure 2 B and C do not permit adequate visualization of TXNDC5 expression in type II cells, which 
are also known to upregulate UPR machinery in response to bleomycin. Please provide low power 
images of lung under bleomycin conditions to confirm that TXNDC5 is not expressed in these cells. 

5) Please confirm that TXNDC5 deficiency fibroblast are still viable. Otherwise, it is possible that 
increased cell death explains the reduction in myofibroblast markers after knockdown of this 
protein. 

 

 

 

Reviewer #3 (Remarks to the Author): 

 

The authors have performed a number of assays to report a connection between expression of a 
protein disulfide isomerase and pulmonary fibrosis. There is an interesting story here. However, 
there are some issues with internal consistency and the proposed mechanism. There's clearly an 
effect on lung tissue and cells. Whether it is related to TGFB1R is debatable. 

 

My main concerns are to change the histograms to scatter plots to more accurately present the 
data, provide more details about some of the imaging assays, reconcile differences between 
experiments, and to get rid of the deeply flawed FRET assay. Details are listed below. 

 

Fig. 1. Rather than cover up the noisiness of the data with block histograms, the authors should 
present scatter plots that show the range of the data. Please state whether errors are reported as SD 
or SEM. 

Fig. 1b. I disagree with the conclusion that there is a strong correlation. Collagen levels are highly 
variable relative to TXNDC5 levels. The R value reflects an averaging effect, not a good fit. 

Fig 1e. FN data inclusion is questionable. There does appear to be a difference between low and high 
TXNDC5 expression and FN levels, though the FN level differences are quite modest, maybe 30% at 
best. That seems too low to report as significant. 

 

Fig 2. Please show scatter plots. 

Intensity is misspelled. 

Inadequate immunofluorescence microscopy information is provided. What objective was used? 
what filters? What excitation source? What kind of coverslips? 

This is highly relevant for the colocalization experiments. The red patterns look consistently smaller. 
I'm wondering whether the objective used is corrected for chromatic aberrations. This looks like the 
images are focused to different focal planes. 

 

Fig. 3f I don't understand the figure. Why are there two lines for each condition and why do they 
converge at the same endpoint? 

 

Fig. 4. Field is misspelled. 

4a. It's a little surprising that the large histogram differences only result in p values in the * category. 
The use of scatter plots will help readers better understand the data. 

 

 

Fig 8. The FRET assay is highly problematic. First, the authors claim to have created positive and 
negative controls, but the data from the controls are not shown. The range of possible FRET values is 
unclear. A unimolecular positive control is reasonable, but a bimolecular negative control is not. The 
FRET values are not comparable. Importantly, the reporter construct is in the wrong compartment. 
TXNDC5 is a resident endoplasmic reticulum protein. TGFBR1 is a protein that would interact with 

TXNDC5 in the endoplasmic reticulum. The FRET construct puts fluorescent proteins at each end, 
which would prevent the signal sequence from targeting the construct into the endoplasmic 
reticulum. Thus, it should neither fold correctly nor could it interact with TXNDC5. Furthermore, 
even if the authors created a correctly targeted reporter, they used ECFP and EYFP, which were 
shown by the Tsien lab back in 2003 in Zacharias et al. (Science) to be prone to dimerization unless 
the proteins were monomerized with an A206K mutation. This will lead to aberrant positive FRET 
signals, especially on a bimolecular reporter. Finally, the correct negative control would be an 
unfoldable mutant TGFBR1, preferably due to a single point mutation. Taken together, the FRET 
assay is invalid and is unlikely to be correctable without a massive effort, well beyond the scope of 
this manuscript. 

 

How does TXNDC5 OE influence TGFBR1 levels? In fig 6b, there's nearly a 3 fold increase. In 7b, the 
value drops to only about a 70% increase (even though the representative blot bands look 
dramatically more contrasted than a 70% difference). In Fig 8e, the increase with OE is even lower, 
maybe 40%, and the representative band difference looks more like the presented histograms. This 
extreme variability to a frankly subtle effect raises serious concerns about the reproducibility of the 
effect and the proposed mechanism. 

 

I'm confused by the ATF6 assay. BiP levels clearly increase, but ATF6 p50 levels exhibit an extremely 
modest change in fig 9a. I'm not convinced the antibody actually recognizes the p50 version of the 
protein. There's only one antibody available that recognizes ATF6 was generated by the Mori lab. 
ATF6 degrades rapidly and requires special handling for immunoblot assays. Changes in the reported 
p50 levels are extremely modest. There is also no other standard positive control for ER stress or a 
time course. BiP levels usually increase hours after UPR induction and ATF6 cleavage is an early 
event. 

 

The TXNDC5 OE control is not a great choice. Overexpression of any ER protein induces transient ER 
stress and adaptation. A negative control would either an inactive version of the protein (as used in 
8e, though the effects with wt were much more modest in the assay) or an inert resident ER protein. 

 

The luciferase assay is somewhat surprising. The difference increased luciferase production in 
stressed cells is less than 50%. Luciferase has a tremendous dynamic range of 3 orders of magnitude, 
and yet message levels are similarly modest in increase in response to stress (less than 50%). In most 
assays, a 1.5 fold difference is considered the bare minimum for clear evidence of upregulation of 
message levels. One interpretation is that ATF6 does not directly regulate TXNDC5 levels (a helpful 
control would be to mutate the proposed ATF6 binding site of the luciferase reporter) and instead, 
another downstream TF is responsible. 

 

To robustly nail down a mechanism, the authors would need to do immunoprecipitations of wt vs 
mutant and endogenous TXNDC5 with TGFBR1. As presented, there appears to be something 
happening, but direct evidence of mechanism is missing.