|I wish to point out that I was not a reviewer of this manuscript in the first round of review. Therefore, I have not read the original version of the paper. In an attempt to remain unbiased, I read the updated manuscript without consideration of previous review comments or the authors’ response. My review comments are based on the updated version only, with small additions after consideration of the review comments and authors’ response.|
This paper addresses a topic of general interest to the atmospheric chemistry/aerosol community – the contribution of biogenic VOCs to secondary organic aerosol formation in the atmosphere. In that regard, it is timely (especially given other recent publications) and well suited for ACP. It extensively cites previous literature. In general, the text itself is well written (though with some obvious typographical/syntax errors – please edit carefully). I’m not sure that the title is appropriate for what is currently contained in the manuscript, but the abstract certainly covers the wide array of topics included.
This last point about the abstract is one of my main concerns about the paper. The paper seems to jump all over the place – which may be due to trying to incorporate reviewer responses from the previous round. I actually would humbly suggest to the authors breaking up the paper into multiple papers. For example, one paper could focus exclusively on the technique associated with the lab-in-the-field – including discussion of the approach, statistical evaluations associated with before and after perturbations (appendix A), and the limitations associated with the mass spectral comparison technique. This paper could also include the limitations of this approach – unknown mixing, not applicable for certain VOCs, etc. This would be appropriate for submission to Atmospheric Measurement Techniques, for example. A second paper could then focus on use of a-pinene and b-caryophyllene experiments to support their main conclusion and the modeling (assuming all other issues are addressed). I actually think that Appendix B is too short to justify inclusion. Too few experiments are performed – and including this section only increases its length and makes this reader feel like we are going off on a tangent. Assuming the authors are not amenable to splitting this paper, they must at least somehow improve the links between the various sections.
Again, assuming that the authors wish to pursue publication of this manuscript in its current form, the following issues should be addressed prior to resubmission:
Page 5, line 124. If the fans are shut off and the intake into the chamber is determined only by the instrumental pull, how do the authors ensure that the contents of the chamber are in fact well mixed? This subject comes up again in the box modeling section in which a dead volume (never actually defined) of 1.75 m3 (which is over 85% of the total chamber volume) is required to even come close to simulation of measured data? This to me implies that the chamber is not adequately characterized (such a characterization could appear in the suggested AMT paper).
Page 7, line 161. Introduction of the VOCs will naturally influence the levels of the oxidants, however (through consumption of O3 and subsequent formation of OH). The authors only present the average O3 levels in experiments and assume OH levels for modeling. Were time series of O3 within experiments investigated to see any influence of the VOC perturbation on O3?
Page 7, line 178. I am somewhat troubled by the lack of VOC measurements in the experiments. How do the authors know that there were not issues with injection? Thus, the variations in amount of OA formed upon perturbation between experiments might not be due to changes in the ambient air into which the VOC is mixed but due to a change in the amount of VOC in the system.
Page 12, line 310. The authors specify that they perform perturbation experiments at various conditions. Did the responses to these conditions make sense? T? RH? Other factors?
Page 12, paragraph on line 319; page 13, entire page, page 1, line 366. This section deals with changes in MO-OOA, IEPOX-OA, COA, and HOA when the VOC is perturbed by a-pinene or b-caryophyllene. I find this to be a significant weakness of the paper – and along with the broad array of topics covered, is the main basis for my recommendation. Why would MO-OOA only change once? And why is IEPOX-OA only impacted when IEPOX-OA is non-zero in the ambient? And why an entire paragraph about MO-OOA but only one sentence about HOA and COA? Upon reading the other reviewer comments, it seems I am not alone in being troubled by this. Perhaps this could be the subject of another paper – the weaknesses associated with the PMF technique? I find in general that folks put a lot of faith in PMF results without often considering the fact that it is a statistical technique whose goal is to minimize the residuals. I do not wish to belabor this point, as Reviewer #3 from the previous review outlined reasons for this concern.
Page 13, line 337, why is 4 ug/m3 insignificant with respect to g/p partitioning? If the total OA is on the order of 10 ug/m3, this is 40% - and would likely be in the “steep” part of the Y-Mo curve.
Page 18, line 487. The description of model results indicates “it is not necessary to invoke any unexplored mechanisms.” This is potentially a dangerous statement, as it implies that they are getting perfect modeling results of the exact same quantity – where in fact here they are supposing that MT and SQT-based SOA = LO-OOA, and they are not getting perfect results!
Page 18, line 516. One point beyond 0.3 ppb does not signify a ‘plateau.’ The authors have no idea (based on Figure 7) what is occurring between 0.3 ppb and 1.6 ppb. Also, the authors should specify that the NO-free subscript refers to the H2O2 and the high-NOx subscript refers to NO2 and HONO. These are not labeled as such on the Figure.
Figure 2, the time series is unnecessary and adds nothing to the paper since it includes both the ambient and chamber data. This is also true in Figure B1 (if appendix B is retained).
Appendix A, page 42, line 1208. The authors state that the chamber aerosol is lower than ambient due to wall loss. How do they know this? Later, they indicate that wall loss plays a very minor role in the change in LO-OOA. If the wall loss causes a significant change in the ambient vs. chamber, why would it not cause just as significant a loss in the LO-OOA formed. As mentioned above (page 5), is this a mixing issue (dead volume)?
Appendix A, page 43, line 1229. Why select the 8th point? Why not select the point where the perturbation has a peak? How sensitive are the results to this?
Appendix A, page 44, paragraph starting on line 1247. I think it important that the descriptor ‘pseudo’ be used much more frequently to emphasize what is a ‘pseudo’ perturbation.
Appendix A, page 45, line 1287. What happened in the 5 cases when LO-OOA did not form? Are these below some critical oxidant threshold? Or are you certain that the VOCs were actually injected (see my previous point about the lack of VOC measurements)?
Supplement, page 12, line 323. I do not think it is appropriate for the authors to scale their fresh SOA by 0.84 based on the regression shown in Figure S5. This ignores several points where there was no increase in IEPOXOA – which would change the slope (and its associated R value) considerably.
Supplement, page 14, lines 380-400. Please see my earlier comment about wall loss and about what a dead zone means (and how large it is relative to the total volume). In addition, how valid is assuming that there is no inflow of a-pinene or OA in the model?
Supplement, page 18, line 488. This observation of lower NO2 causing more LO-OOA is based only on a small number of data points (3 at higher, 3 at lower). While the authors state that this warrants further study, I’m not sure tossing in something with so few data points is appropriate.
Figure S12. The y-axis label should say ‘chamber’ not ‘bag’ for consistency with the text.
Figure S14. The authors state that the consistent fractional contributions of the various OA factors remains relatively constant. Without error bars, it is hard to say whether this is statistically accurate. For example, it looks as if the HOA fraction is decreasing with respect to time. Is this because HOA emissions have decreased while other OA has increased/stayed constant? What is the overall OA level in each year?
Figure S15. Is the use of yields at a loading of 445 ug/m3 appropriate? This seems rather large.