I appreciate the authors’ efforts in improving the manuscript. But I still show some concerns about the conclusions.
1. The authors use PNA+ (PNA-) to represent the months with top (bottom) 25% PNA values. This is misleading for many readers who don’t read this paper very carefully or just go through the figures very quickly. We usually think PNA+ are those months with positive (above the median value) values. The authors should use a different symbol or specify their definition carefully in the figures and main text.
2. The authors concludes that ‘the PNA-induced variation in planetary boundary layer height was found to be the most dominant meteorological
factor that influenced the concentrations of PM2.5, sulfate, ammonium, organic carbon,
and black carbon, and the PNA-induced variation in temperature was the most
important parameter that influenced nitrate aerosol’. All of these results just come from a CTM study without using the observations. In order to show PBL is the major driving factor, I have suggested that the authors should do a sensitivity test by fixing the PBL, but they think their statistical methods are very robust and don’t do this test. In Figure 7, the PBL height decreases only 5% in the eastern US. I am skeptical if this will still pass the significance test if they use a p-value 0.05 instead of 0.10. Are these results still true using a different PBL scheme or a different reanalysis met field? Also they don’t explain why PBL will decrease under PNA+ months. I think the authors should address the following questions before this paper is accepted.
First, this conclusion is made without using the observations. If we compare the PNA-driven differences in PM2.5 between observation (Figure 3) and GEOS-Chem (Figure 5), we can find many big discrepancies. For example, little effect of PNA on PM2.5 is found in California in GEOS-Chem. As a result, there is no discussion about California, a very important state for the US, in Section 5.2. To our knowledge, present CTMs have many problems in simulating the aerosol variability. As such, the analysis only based on CTM results can hardly contribute to our understanding of the effects of PNA on PM2.5. I think the authors should re-do the analysis in Table 4 using observations. They can use PBL from GEOS4 since there are no PBL observations.
Second, they think the PBL height is very important in explaining the variability in PM2.5, which may not be true in some regions. One issue is that this paper never explains why the PBL will change. Any analysis on this topic will be very useful to this community. Figure 7 shows that the PBL in the Midwest changes fewer than 25 meters (<5%) in the Midwest. However, the PNA-driven changes in PM2.5 are 20%-40% in observations (Figure 3) and 10%-20% in GEOS-Chem in this region. According to these numbers, it seems that the PBL shouldn’t be an important factor in explaining the PNA-driven changes in the Midwest. For the intermountain west, I agree with the authors’ conclusion that PBL should be an important factor according to Figure 7, but this conclusion is subject to large uncertainties due to the complex topography there. The authors should make this clear in the conclusion and discussion.
Third, they think ‘PNA-induced variation in temperature was the most
important parameter that influenced nitrate aerosol’. This conclusion should be correct due to our present knowledge in atmospheric chemistry. But the observed and simulated NO3 changes in Figure 3 and Figure 5 are not quite different in spatial distribution. So the authors need to clarify this.
3. Section 5.1 raises many questions. First, why the box in Figure 6b doesn’t include the whole California? Second, why the mass fluxes are integrated from surface to 100 hPa? The top layer (100 Pas) is already in the stratosphere, which shouldn’t have big influence on the surface. Third, numbers in Table 3 will change a lot if the location of the boundary is shifted. For example, if the west boundary is in the ocean, the transport via west boundary should be close to 0. Fourth, the authors should explain why the underestimate in GEOS-Chem over west US won’t compromise this conclusion in more details. The underestimate should change the transport via west boundary a lot. Please consider if this section is needed for this paper.
Figures. If detrended PM2.5 concentrations are used, please clarify in the captions. Does Figure S4 use the detrended data?
Introduction. Please be more accurate when citing previous results. For example, the exact number of climate-driven PM2.5 changes is ±0.1-1 μgm-3 (P4 L81). Please also check other sentences.
P180. Please clarify the method you used here instead of asking readers to jump over to the later section.
P187. When you fit the regression model, do you use data only in the winter or the whole year? Be more accurate here.
P215. What is the exact height of PBL? The readers don’t know these details of GEOS-Chem vertical resolution.
P229. PNA phases are only part of meteorological parameters here.
P289-290. The numbers here are misleading. Are these numbers the average change of all sites in this region? Seems not.
P309-310. Change ‘were’ to ‘are’. Please fix many other similar problems in the whole text.
P347. It seems the PNA can only explain a very small fraction (<15%) of the variability. Is PNA important for aerosol? Please give some discussion here.
P349. How many sites show high FTVEP values? Please provide the fraction number.
P469-471. Obviously the model doesn’t capture the difference in California. Please be more accurate here.