This work details an interesting pathway for HOM formation and involves robust theory and experiment working in tandem which is nice to see. The work is well presented and of good scientific quality. I am not sufficiently qualified to comment any further on the experimental techniques used however broadly speaking the theoretical methods seem approariate given the moderately large number of heavy atoms.

My only queries and comments regard the way the multiconformer approach is presented. I know that in some formulations of multiconformer approaches, corrections are applied to ensure the correct hindered rotor limit but I do not see such corrections in expression 1. Are these included or are the conformer partition functions calculated entirely within the harmonic oscilator aproximation? If the conformer hindered rotors are not accounted for then expression 1 could be achieved simply by putting the seperate conformers into MESMER. Additionally if every conformer is treated as harmonic then you also have the potential issue of overcounting of states when you reach the hindered rotor regime.

It would also be nice to see some consideration of the hindered rotation potentials? do you have these? I do appreaciate that this is quite a large system and since this paper has a large experimental part I do not consider hindered rotors crucial to publication, however if you have not done a hindered rotor treatement then the comparison between a single well model and a multiconformer model is a little missleading since strictly speaking the conformers are equilibrated and the multiconformer model is simply a way of approximating the fully coupled configuration space of each species. Related to this a brief look at your MESMER input shows each species has a symmetry number of 1? By not including hindered rotors im slightly concerned you are not accounting for the three fold periodicity in any methyl rotations for example although correct me if these all cancel out between reactants and TS? In summary the lack of consideration of hindered rotors while potentially pragmatic in this case leads to potential pitfalls. At the least I would ask the authors to clarify some of these points and make minor adjustments to the text acknowledging some of these issues. Otherwise I am very happy to reccomend publication of this manuscript. 

Overall comment:

This work studied the autoxidation kinetics and mechanism of hexanal+OH oxidation through quantum chemical calculation and flowtube oxidation experiments. The calculation results suggest that the major RO2s from hexanal + OH could autoxidize at 0.17 and 0.86 s-1 and are estimated to be rapid enough to compete with bimolecular reactions under typical atmospheric conditions. Thus, the authors suggested that hexanal oxidation may be a rapid source of atmospheric SOA. In general, this manuscript is well-written and presents new and interesting results. But I have a few questions and comments and think they should be addressed before this manuscript can be published at ACP.

Detailed comments:

1. Experimental design. The experiments used ozonolysis of TME (C6H12) to generate OH to react with hexanal (C6H12O) and to study the hexanal oxidation products. Using TME ozonolysis to generate OH is a common approach, but here, it might not be a good idea, considering that both TME and hexanal are C6 compounds. Some TME oxidation products might be misidentified as hexanal products (see a later comment). I believe that the authors need to provide more thorough experimental evidence that the products identified as hexanal + OH products are not from TME.

1. Calculation uncertainties. At Page 10, Line 204-209, the authors compared the calculated hexanal + OH rate constant with prior experimental measurements and suggested a factor of >10 lower in the calculation. But by reducing the barrier height by 1 kcal mol-1, a more consistent result was obtained. This 1 kcal mol-1 was suggested to be the error margin of the calculation method. I wonder if considering this “error margin” in the H-shift process, how much of uncertainty will be estimated for the autoxidation rate constants (i.e., 0.17 and 0.86 s-1)?

1. Interpretations of some mass spectral peaks and formation mechanisms should be revised or discussed.

(i) As discussed in section 3.3, a C6H11O6 peak was observed as the dominant product in just 1.4 sec of hexanal oxidation. The author proposed a mechanism of C6H11O5-RO2 + RO2, followed by the formed C6H11O4-RO undergoing autoxidation to produce C6H11O6. If this is really the case, then how can the authors argue that autoxidation outcompetes bimolecular RO2 reactions at short time? It sounded like the short-flowtube method was to make autoxidation chemistry more prominent than bimolecular chemistry. Seeing a bimolecular reaction product in the shortest time seems contradicting. Could this C6H11O6 be from TME + O3? Is it present without hexanal?

(ii) Page 17, line 318. The authors proposed that C6H10O5 can be formed from C6H11O7 + RO2 à C6H11O6 + H-shift à C6H10O5 + OH. Why not directly forming C6H10O5 via the classic Russell mechanism: C6H11O6-RO2 + RO2 à ketone + alcohol. It appears that some C6H12O5 is also formed, possibly as the pairing alcohol. This reaction (RO2 + RO2 à ketone + alcohol) appeared to be neglected throughout the entire study (i.e., supporting information S2).

(iii) The closed-shell products, C6H10,12O7 are much smaller than C6H10,12O5,6. How can this be explained?

(iv) The authors suggested that NO3- are more sensitive for species with more hydrogen bonding functional groups (-OH and -OOH). How come in the mass spectra, each pairing ketone has higher response than alcohol (e.g., C6H10Ox vs. C6H12Ox, x=5-7)?

1. The H2O/D2O exchange experiment (Figure 6d) showed some remaining fractions of the peaks at the original masses (no shift). Does this mean that the exchange did not take place for all isomers? Or is this an H2O/D2O exchange efficiency problem. Can you test it using chemical standards?

1. Kinetic modeling results. For the section 3.4, I feel a figure that summarizes the results of the various modeling scenarios would make it more clear. In addition, how about RO2 + HO2? Is it considered at all? What is the aldehyde photolysis rate constant used in the kinetic model? How does photolysis affect the autoxidation pathway and RO2 fates?

1. Lastly, I think extending the autoxidation mechanistic study into SOA formation in the title and as a main conclusion is going too far. This work only showed that autoxidation happens during hexanal oxidation, but did not perform any measurements for SOA formation. It could be mentioned as an implication or suggested as future work, but should not be highlighted in the title and first sentence in the Conclusion. If the authors really want to discuss more on SOA formation, I suggest at least make some estimates of the volatilities of the autoxidation products. And more discussion in that regard is needed.

This work investigated the autoxidation kinetics and mechanism of hexanal+OH oxidation through state-of-the-art quantum chemical methods and flow reactor experiments. It suggests that hexanal (as a case study for aliphatic aldehydes with more than 5 carbon atoms) could be a source of atmospheric secondary organic aerosol. I find the paper very well written and clear, fitting the scope of ACP and overall employing the correct scientific approaches necessary to perform such a study. However, I should state that I cannot comment on the experimental part of the work, as my field of expertise is theoretical and computational chemistry. And in this respect, my attention was drawn precisely to the kinetic details of the hexanal+OH bimolecular reaction. My comments and questions are the following:

1) The authors use robust MC-TST calculations to treat the unimolecular H-shift reactions, but then use a much simpler approach (Eq. (2)) to calculate the rate coefficient for the hexanal+OH reaction. Why is that? And why is there no tunneling correction in Eq. (2)? Simple and cost-effective bimolecular MC-TST protocols that account for these issues have been recently proposed, for example A. S. Petit and J. N. Harvey, PCCP, vol 14, 184-191 (2012) and L. P. Viegas, Environ. Sci.: Atmos. DOI: 10.1039/D2EA00164K [and references therein]. 

2) Between lines 100-115 the authors talk about the calculation of TS conformers for this reaction. The authors write "(...)except for the aldehydic H-abstraction, in which case, the initial TS optimization is carried out using the MN15/def2-tzvp level of theory instead of B3LYP/6-31+G* since the latter method failed to find the TS structure. The conformer sampling step on the OH aldehydic H-abstraction TS structures did not lead to additional conformers." I am a bit confused on how many aldehydic H-abstraction TS structures were found. Could the authors clarify this and the total number of TSs for the hexanal+OH reaction? Also, how many conformers for the hexanal reactant were found?

3) Reactions between the OH radical and volatile organic compounds are well known to often proceed via the formation of a pre-reactive complex that precedes the hydrogen abstraction step. The literature is incredibly vast on this. However, Figure 3 does not show the formation of these complexes. Could the authors explain why?

4) Between lines 200-210 the authors discuss the quality of their obtained bimolecular rate coefficient, which is lower than the experimental and SAR rate coefficients by approximately one order of magnitude. The authors then state that "Reducing the barrier height by 1 kcal mol -1 (within the error margin of the method used), we obtain the overall rate coefficient 1.3x10(-11) cm3 s-1 that is compatible with the reported experimental results.", based on (and please correct me if I misunderstood this) the fact that their barrier heights are higher than the ones obtained by Castañeda et al. (2012) at the CCSD(T)/6-311++G**//BHandHLYP/6-311++G** level. First of all, I think that barrier heights calculated at the RHF-RCCSD(T)-F12a/VDZ-F12 level over wB97X-D/aug-cc-pVTZ or MN15/def2-tzvp geometries are of better quality than CCSD(T)/6-311++G**//BHandHLYP/6-311++G** calculated barriers. So, in my opinion, the problem with the underestimated rate constant does not come from the barrier heights. Secondly, I do think that this underestimation is being caused by the lack of an MC-TST treatment to this reaction, as well as the lack of a tunneling coefficient in Eq. (2). Also, by showing Eq. (2) in that form, it makes the reader think that the authors only used one reactant and TS conformer for the calculation. However, small aldehydes such as CF3CH2CHO and CF3CF2CHO have at least 7 low energy aldehydic transition states (L. P. Viegas, DOI: 10.1039/D2EA00164K) which strongly contribute to the final rate constant value. Table 1 of the same paper also shows the underestimation effect on the final rate constant by considering only the lowest energy reactant and TS conformer, k_OH^LC-TST(calc), compared to a more complete MC-TST value, k_OH(calc). So, this multiconformational effect added to a tunneling factor could place the calculated hexanal+OH rate coefficient much closer to the experimental result. 

In light of these comments, I ask the authors if they could please clarify these issues and make the necessary adjustments to the manuscript before it can be accepted to be published in ACP.