Comment on acp-2021-1011

Fouqueau and co-workers present an experimental kinetic, mechanistic, and multiphasic study on the nitrate radical-initiated oxidation of two atmospherically relevant terpenoid hydrocarbons, terpinolene and beta-caryophyllene. Experimental studies of this type are very valuable for furthering our understanding of atmospheric oxidation processes, which the authors tackle using a two chamber systems and a variety of analytical approaches. In general, the work is well-presented and once the authors have addressed the following points, I would be happy to recommend publication of this work in Atmospheric Chemistry and Physics.

the authors tackle using a two chamber systems and a variety of analytical approaches. In general, the work is well-presented and once the authors have addressed the following points, I would be happy to recommend publication of this work in Atmospheric Chemistry and Physics.
General comments: Yields of SOA in chamber experiments such as these are generally challenging, with various complications such as: a dependence on the starting concentration of the alkene reactant; a dependence on the amount of alkene reactant that has been consumed; and a dependence on the aerosol mass loading. Given that chamber experiments tend to be run under higher than ambient concentrations of the alkenes and their oxidation products, it is generally unclear whether the yields that are presented here would actually apply to ambient conditions. Let us assume that if one were to oxidize enough of almost anything in a chamber environment, it would eventually form aerosol as the chamber contents reach supersaturation with respect to a condensable component. For example, some of the estimated vapour pressures that are present in the beta-caryophyllene mechanism are very low (~5 × 10 -11 atmospheres). I think that this would mean that a concentration of such a compound would reach supersaturation in the air at a concentration of approximately 50 ppt. If we took a typical concentration of consumed [BVOC] to be 400 ppb, then we could estimate that if the branching ratio towards this low vapour pressure product was any larger than 1/8000, then such a molecule would overcome its vapour pressure within your chamber conditions, and would therefore begin to condense.
So the question remains, what could we actually expect to be the true SOA yield to be under ambient conditions, considering that BVOCs would be diluting and mixing during oxidation, in contrast to the chamber experiments presented here? Perhaps it is mostly the different concentration regimes that are used in the various literature experiments that lead to the spread of SOA yields?
Added to this, the authors are quite inconsistent in the SOA yields that they mention in the abstract and throughout the text. In the abstract, they list maximum SOA yields of 60% for both compounds. In section 4.1, they suggest that beta-caryophyllene could be as high as 90%. In the conclusions section, the authors seem to favour the 5% and 40% values at 10 micrograms per cubic metre. I am therefore not exactly sure which of these numbers (if any) I should be considering from this work.
Minor comments: Line 13: … to form (a) number of… Line 17: it isn't clear what you are "following up" on, you should either delete this, or provide further details.
Line 20: since there is some previous data, you cannot state that there is a lack of experimental data, since lack denotes an absence.
Line 25: are also, not also are. Precursors, not precursor.
Line 35: Globally, there have been some changes since 1995. Is there a more up-to-date account of VOC emissions from the various sources?
Line 53: For me, "proved" is a rather strong word to use, especially without a citation to back up your assertion. Scientifically, it is generally easier to disprove something, rather than prove it. Please consider a rephrase.
Line 81: requested is not the right word. Required?
Line 120 (whole paragraph): Where are the data for these integrated band intensities?
Line 130: It is potentially confusing to talk about the reactor in the instrument in this sense, since you are dealing with other types of chamber reactors in this study. Would it be better to give it a more specific name such as a drift tube or an ion-molecule region?
Line 136 (whole paragraph): Again, it is nice to be able to point to the actual data for these band intensities that you are referring to.
Line 144: It is not entirely clear, but it seems like what you are describing is not a rate exactly, but the extent to which the chamber contents have been diluted. Rephrase.
Line 146: Please describe how the dilution rate was measured.    : It is apparent that the absolute measurements have a large amount of experimental variability. It would be instructive for the authors to suggests reasons why this may be the case. Is it possible that reaction times are sufficiently rapid that they are affected by mixing times and instrument response time?
Line 298 (whole paragraph): I find this comparative discussion of reactivity to be more confusing than it is educational. You mention the enhanced stability of the exocyclic double bond as evidence for the increased reactivity of terpinolene (which seems to be strange and unexpected). You also mention that the conjugated system of alpha-terpinene leads to a stabler alkyl radical. If I am understanding this correctly (and there is a good chance that I am not), you are arguing that if the reactant or product is stabler, then k is bigger. So, I must insist that you state this argument more thoroughly. Are you trying to justify this on thermodynamic grounds? Something else? Let the readers know. Table 3: You acknowledge that there are potentially large uncertainties in these estimates. Do you expect that there errors that you are providing here would be symmetrical in each case. I think this would be surprising. Please can you explain how these errors were calculated? Table 3: Similar to Table 1: I don't like the formatting of BVOC name. Perhaps you can rotate the names by 90 degrees, which will allow you to avoid these inconsistent abbreviations.
Lines 406 -409: I agree with the authors about the sensitivity of SOA yields to various experimental parameters. Is it possible that [NO2] and radical concentration in general could also play an important role in SOA formation? It is important to note for example that although you have made specific efforts to reduce N2O5, you will inevitably have higher [NO2] than in a normal environment. Can the authors suggest a route towards understanding this SOA yield of these terpenoid compounds in a more fundamental way?
Line 413 -414: Although I just-about understand what you mean to say by this statement, I don't think this is a good way of saying it. Whether the slope was zero for a secondary product would very much depend on delta[alkene] over which the slope was calculated. Please consider a more robust rephrase of this statement (or delete it). Line 454: In a region that was impacted by NO3 radical at night, one would expect elevated NOx concentrations. This would enhance nitrate yields in chemistries that were initiated by other oxidants such as OH, so I am not sure that this comparison with the field is very insightful.
Line 456: I don't think it really confirms anything. At best, I would suppose that it suggests that NO3 chemistry may contribute towards SOA production.
Line 460 -461: Is this really true? Do you know that all classes of compounds are detected in an accurate and sufficiently sensitive way using this approach? Please justify this statement.