Harmful Effects of Ambient Nitrogen Dioxide on Atopic Dermatitis: Comparison of Exposure Assessment Based on Monitored Concentrations and Modeled Estimates

Round 1

Reviewer 1 Report

The table presented in the reviews absolutely need to be in the paper (why is it not?).  The table is by far the data that someone interested in eczema would be most interested in.

 

Table. Effects of NO₂ on each AD symptom

Symptom	% change (95% CI) per 10 ppb of NO2
Itching	2.53 (0.50, 4.60)
Sleep disturbance	3.62 (1.05, 6.26)
Erythema	0.45 (-1.62, 2.56)
Dryness	1.84 (-0.37, 4.09)
Edema	1.96 (-1.67, 5.72)
Oozing	-9.11 (-15.29, -2.47)

Author Response

Thank you for taking your time and the comments. 

As the reviewer indicated, we have added the results and the Table in Methods (Line 196-197) and Results (Line 320-325).

Reviewer 2 Report

I have no further comments. Thank you.

Author Response

Thank you for taking your time.

Reviewer 3 Report

Thanks again for the opportunity to review this manuscript. The manuscript has been reviewed by three individuals and I think the authors have successfully addressed each of our comments and suggestions. I would, therefore, recommend the publication of this manuscript. I do not have any additional comments or questions at this stage.

Author Response

Thank you for taking your time and the comments.

Reviewer 4 Report

No further comments

Author Response

Thank you for taking your time.

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

Please specify the meaning of the abbreviation AQMS- on line 28

Reviewer 2 Report

Thank you very much for the opportunity to review this manuscript from South Korea which establishes an association between ambient Nitrogen Dioxide (NO2) and atopic dermatitis in a panel of young children. The authors have employed the NO2 concentrations from ambient monitoring sites for their analyses. This paper is generally wel-written and I would recommend the acceptance and subsequent publication of this manuscript. The English language used is without any flaws and the grammar and syntax are all taken care of. I just have some questions overall and I have mentioned these in my comments below:

Line 68: Change associated to 'association'

Line 320: The authors take into consideration only the ambient levels of NO2 for their analyses. They mention that this is one of the limitation of their paper because indoor NO2 measurements were not available/measured. Given the fact that we almost spend 80 to 90% of our time indoors, how accurate the outdoor concentrations of NO2 are? There can be may indoor sources of NO2 such as kerosene heaters, kerosene stoves. Also, tobacco smoke !I am not sure what the source of cooking or heating was at all the places of residence. But did the authors ask these questions to the guardians of the study subject. 

The authors do indicate in lines 82 and 83 about the study subjects being from Seoul Metropolitan Area and the study subjects were monitored from April to July 2014. I understand that this would be the peak summer season in the Korean peninsula. Did the authors record the parental activities of the participants as some of those activities like smoking etc. may be contributing to the indoor exposure of NO2? Any thoughts....?

Lines 326-328: The authors discuss about PM10 and O3 in the overall analyses and how their results are not changed significantly when these are included as covariates in the models. But what about PM2.5? Was no PM2.5 data available? Innumerable studies have shown very robust correlations, both temporal and spatial, between NO2 and PM2.5....the common source being road traffic emissions. PM10 is more of the coarse component of PM but PM2.5 is more attributed to traffic. As such, PM2.5 as well as NO2 are surrogates of traffic emissions. Was any data available for Black Carbon (BC)? I would like to learn the authors reply to this important point. 

On a side note, the study was undertaken in 2014 and we are in the middle of 2020. What took the authors so long to report and publish their results? 

Reviewer 3 Report

This is a longitudinal study that quantifies the short-term association of ambient nitrogen dioxide (NO2) with atopic dermatitis in young children living in Seoul metropolitan area. The method is appropriate and well-described. However, there are a few concerns related to how the study interpreted results obtained from the CMAQ model simulation and AQM ground stations.

1. The results of risk estimates obtained from AQM and CMAQ do not provide any information on misclassification bias. Instead, to check for this, the study should carefully evaluate the simulated NO2 from CMAQ that provides exposure information. In the Discussion (lines 313-316), the authors acknowledged the underestimation of their CMAQ model. This is supported by Table 2 which shows a consistent underestimation at all distance, including at the 60 grid points where the AQM stations were located. The study reported a sizable downward normalized mean bias at -20.1% at these 60 locations, suggesting that the NO2 simulated by CMAQ was lower on average, as seen in Figure 2 particularly in the first two months of study, April and May. The authors should maintain consistency by toning down all interpretations related to NO2 obtained from the CMAQ model, which could also potentially result in some misclassification bias because of underestimation. For example, in the first sentence of the first paragraph in the Discussion section, the authors argued that the measurements from AQM resulted in a misclassification of exposure, but failed to highlight the poor performance of the CMAQ which could similarly result in misclassification (including the first sentence of the Conclusion). In lines 287-288, the authors argued that the concentrations of NO2 by CMAQ matched with those from AQM within 3km but this was not supported by the results in Table 2 (in Discussion, see lines 312-313 for “good agreement”). A remedy is to tone down the interpretations and acknowledge the underestimations.
2. The negative association observed for AQM at >3km is not a strong or valid justification to favor CMAQ over AQM (lines 281-286), because the study did not compare both estimates to the truth (true association/known effect) in a controlled environment (using simulated data for example). Since the study did not know the truth at >3km, it might be premature to assume that the effect estimate based on CMAQ was correct.  
3. The authors should discuss a potential benefit, which is the narrow confidence interval estimate obtained from the CMAQ for distance ≤1km as shown in Table 3, suggesting a higher precision of risk estimation at 46.8%. This should also be mentioned in the abstract, in place of the statement on the negative association beyond 3km.
4. The CMAQ model tended to underestimate in the month of April and May. Would there be any reason worthy of further discussion?

Below are some minor comments.

• In equation (1), the symbol “E” might not be necessary if you wish to retain the error term. Would it be better to write Y_ij, γ_j, and ε_ij to indicate a random intercept model for i measurements in j subject.
• Table 3, what does the asterisk represent?
• Line 249, “…negative trend for boys…” But the 95% confidence interval is very wide, so it may not necessarily be a negative trend. It merely suggests a non-linear association.

Reviewer 4 Report

So my expertise is in AD and not the atmospheric focus of the paper.  So please have the other reviewer comment on some of those specifics but my two big questions/concerns are:

1) The paper is arguing that CMAQ is superior to AQM because AQM shows a negative association at high NO2 levels while CMAQ does not.  But why are the authors certain this should be a linear relationship?  It seems within reason that specific concentrations of NO2 could be damaging, but too high, or too low concentrations could have differing effects.  Biology is filled with examples of "hormesis".  Alternatively, the very high values in AQM might indicate that some other compound is taking over impacting the disease.  For example, very high NO2 could be a marker of some other "protective" pollutant reaching levels of therapy - or very high levels could prompt the kids to go indoors and thus self-regulate their symptoms.  So please explain why CMAQ's linear relationship assures it is indeed superior.

2) Why are the two so different at all?  Figure 2 shows a pretty close overlap in the two metrics, so why do the author's think that the two metrics differ in impact on AD if they don't markedly differ in NO2 prediction levels?  If they are significantly different, please calculate and display that somehow.

3) I'm not understanding the metric of disease therapy indicated in figure 4.  The Y axis only says Log OR but what is this and what does this mean?  The paper would be MUCH stronger if the authors showed ppb versus the actual clinical metrics collected such as total SCORAD, the 0-4 metrics for each indicator (ie erythema, dryness, etc) and the separate sleep and itch complaints.  IE the authors need to make a figure for all the clinical scores versus the ppb calculations to make a comment on the association.  If you want to split into boys and girls, that makes sense, but if the conclusions are that higher ambient NO2 worsens AD symptoms than I would like to see AD symptoms contrasted against ambient NO2 for the entire study population.