|While this manuscript fits the scope of the journal, there are a number of major comments that the authors need to address before this manuscript can be accepted:|
1. There are a number of papers with high res seasonal OA data from Atlanta, in multiple sites at multiple seasons. In fact, the same JST site as discussed in this paper. (Xu et al PNAS 2015, ACP 2015). Given the large number of papers published about the OA in the SE US (including Budisulistiorini et al. EST 2013, Xu et al. PNAS 2015, Xu et al. ACP 2015), this manuscript fails to situate their results in the context of what we currently know about organic aerosol in the SE US. Specifically, Xu et al. (PNAS 2015 and ACP 2015) presented high res data from multiple seasons from Jefferson Street already. What is new in this work in terms of OA characterization at JST in Atlanta? If their results are all consistent with Xu et al., please say so. If not, please discuss the differences.
2. Published high res data suggest that the m/z 91 is C7H7, not C3H7O3 as proposed by the authors. The authors acknowledged that ACSM cannot differentiate between these two, but HR-ToF-AMS can. Therefore, if the authors believe that their so called 91Fac is different from the LO-OOA factor (high in m/z 91, C7H7) proposed by Xu et al. (PNAS 2015), they need to justify this better. After all, their data and Xu et al are from the same site (JST) obtained around the same time period. Their revised manuscript has not done this sufficiently.
3. I am not convinced that the 91Fac is related to isoprene SOA. I think that the 91Fac is probably just the SVOOA factor with some interference from m/z 44. The reason why I think that is the case is that in Xu et al. (PNAS 2015 and ACP 2015), the authors resolved SVOOA all the year round using a HR-Tof-AMS at the JST site. However, the authors only resolved SVOOA in winter and fall in JST in this manuscript. I strongly urge the authors to go over their PMF analysis again.
4. I see a number of other problematic details in their PMF analysis. For example, in Fig. 6, the time series of 91Fac drops suddenly from summer to fall. This suggests that their season dividing is problematic, and this will affect the conclusions drawn in this manuscript. It is possible that if the authors include the first day in fall to the summer period, the 91Fac concentration will change a lot. The authors need to discuss how the seasonal dividing will affect their conclusions. Also, the HOA diurnal trend at the JST site shown in Fig. 8b seems unlike what has been published before. Specifically, I find that steep and huge drop between 0800 and 2000 pretty unbelievable even though the authors have attributed the diurnal trend to urban OA associated with morning traffic. Yes, a drop would be expected but not something this steep. The diurnal trend of the HOA factor at the JST has been published previously (Xu et al. ACP 2015), and such a steep drop was not observed. This is another sign that the PMF analysis in this manuscript may be problematic. Again, I strongly urge the authors to go over their PMF analysis again.
5. I strongly suggest that the authors specifically discuss what new insights this manuscript can provide to the scientific community. As it currently stands, I fail to see any new scientific insights, whether it is from biogenic-anthropogenic interactions in SE USA or seasonal OA trends, provided by this manuscript that has not already been discussed in published literature.
Other more detailed comments:
6. Page 5, lines 8-12: “Studies in Atlanta, Georgia have characterized the chemical components of ambient aerosol collected during different seasons (Lee et al., 2002, Kim et al., 2003, Butler et al., 2003); however, they were limited by low-time or -mass resolution.” This does not accurately reflect the state of the current literature. Xu et al. (ACP 2015) has comprehensively characterized the OA in multiple seasons at multiple sites in Atlanta using high resolution mass spectrometry.
7. Page 5, line 15: “Additionally, isoprene-derived SOA has been recently observed to contribute substantially to SOA in downtown Atlanta during summer (Budisulistiorini et al., 2013, Xu et al., 2015)” Xu et al. (ACP 2015) needs to be cited here as well.
8. Page 6, line 5-6: “Because previous studies on detailed OA composition in the southeastern U.S. are limited by low-time resolution…” This does not accurately reflect the state of the current literature, please revise. See comments 1 and 6.
9. Page 12, lines 8-9: “The lack of correlations between OA and pH as well as LWC indicate that pH and LWC might not limiting factors in OA production in this region.” Xu et al. (ACP 2015) first demonstrated that pH and LWC are not limiting factors for OA production in the SE US. It would be appropriate to cite it here.
10. Page 14, lines 12-14: “Variability in organic-to-sulfate ratio could indicate different photochemical conditions that could affect concentrations of OA and sulfate (Hildebrandt et al., 2010)” Do the authors mean aging? If that is the case, the authors should explicitly state this, instead of making the readers infer this.
11. Page 16, lines 9-10: “Diurnal patterns of IEPOX-OA are different at JST and LRK.” Why are the diurnal trends different? This needs to be addressed.
12. Page 16, lines 12-14: “At JST, the diurnal pattern of IEPOX-OA followed that of total OA, where it slightly decreased during the day before it increased again in the evening, which is different from previous observations at JST during summer 2011 (Budisulistiorini et al., 2013).” Why are these observations different from the previous study given that the same sampling time period and site?
13. Page 17 lines 7-8: “Ratios of LV-OOA:sulfate at both sites were on average >1, suggesting the LV-OOA was aged.” How did the authors come to this conclusion? If there is a previous study discussing this, the authors need to cite it to support their conclusions.
14. Page 17 lines 13-14: “average ratio of 91Fac:sulfate of <1 (Fig. S25) suggest that 91Fac was a less oxidized factor.” Similar comment as comment 13.
15. Section 3.3: “Seasonal changes and contributions of OA sources” The authors should discuss their results in the context of those published by Xu et al. (ACP 2015) given the similarities of the work.
16. Page 21, lines 7-8: “However, during the fall the LV-OOA factor becomes a significant contributor at LRK.” Why is this the case? Some explanations should be provided.
17. Page 22, lines 16-19: “On the other hand, a weak correlation (r2 = 0.2) between m/z 91 ion of 91Fac and m/z 82 ion of IEPOX-OA factor might indicate that biogenic source(s) contributed to 91Fac formation in densely forested area like LRK site.” I find this sentence confusing. Is the author saying that the observed weak correlation indicates biogenic sources?
18. Page 23, lines 2-3: “ SOA tracers of isoprene ozonolysis were weakly to fairly correlated (r2 = 0.2–0.5) with both IEPOX-OA and 91Fac” What is the correlation between the 91Fac and other tracers they detect?
19. Page 23, lines 19-23: “However at LRK, isoprene was more abundant (~2 ppb) than monoterpenes (<1 ppb) during the 2013 SOAS campaign as measured by online high-resolution proton transfer reaction time-of-flight mass spectrometry (HR-PTR-TOFMS) (Budisulistiorini et al., 2015). Thus, isoprene chemistry could be more influential in formation of 91Fac at LRK.” I don’t agree with this conclusion. Higher isoprene concentrations does not mean higher influence on SOA. After all, monoterpenes have higher SOA yields than isoprene.