Dear Authors,
Given the strongly diverging reviews in this round, I proceeded with a personal review of the manuscript - and have concluded that there is value in the work being published, but requires considerable work before this is possible. I agree with the concerns raised by reviewer #1. Both also note that considerable effort needs to be placed in improving the language. Please follow the recommendations of the reviewers to the extent possible before resubmitting your revision.
We are looking forward to your response!
Best regards,
A.Nenes

Dear authors,

Thank you for your patience in waiting for the decision. I have went through the manuscript carefully. The calculations are sound, the figures are nice and the language has improved – but I feel that the interpretation of the results are often not supported by data or even incorrect, and that is where the bulk of my comments originate from. Much of the discussion tends to decouple LWC from the soluble ions that drive pH calculation – although appropriate for clouds, this cannot be said for aerosol. I am providing a list below with what I feel are the main issues.

Also, the size-resolved calculations of pH could be supported by gas-phase measurements that were taken by the MARGA. Even if the periods are not perfectly aligned, you still know the order of magnitude of e.g., NH3 that is around during a certain period. This can be used to confirm the thermodynamic calculations. Even if you have some error in NH3, pH is less sensitive to it (e.g., Guo et al. 2017 found that a factor of 10 chance in NH3 is required to change pH by one unit).

Note that all the references below are already in the References list.

Once these concerns are addressed, the manuscript should be ready for publication in ACP. I am looking forward to your revised manuscript.

All the best,
A.Nenes



Comments
Page 1, line 19: “due to the stronger ability…ions”. Affinity with the H+ is not the underlying reason (otherwise, increasing HNO3 would also drive acidity up, and it doesn’t really). The very low volatility of SO4 compared to the neutralizing cations (mainly NH4) is the reason for the strong acidity associated with SO4 in aerosol. NH4 evaporates to NH3 in achieving equilibrium, and that by nature creates an ion imbalance that leads to H+ production through dissociation of H2O. The appropriate reference for this is Weber et al., 2016.

Page 1, line 24: “hydrolysis of … and ALWC”. The authors mention hydrolysis of ammonium salts throughout the manuscript, but do not provide any calculations to support this. Even a pure ammonium sulfate particle, when deliquesced, will evaporate some NH4 to the gas phase to produce NH3 – this is the reason for acidity, as mentioned above. LWC variability does lead to a pH unit change for typical variations throughout the day (and this has also been shown before by the Guo et al. studies and others).

Page 3, line 40. “In addition…acid rain”. Incorrect statement. Aerosol acidity is decoupled from acid rain pH. The reason being that the water per kg of aerosol “mass” is fixed by the RH – so pH changes are relatively insensitive to changes in absolute aerosol mass, while rain water is decoupled from the aerosol mass – so rainwater pH changes considerably with different aerosol loading. Otherwise the acid rain program would have failed in the US – because aerosol acidity has not gone down over time (e.g., Weber et al., 2016).

Page 3, line 44. “A net … alkalinity”. Hennigan et al., and others have shown that the ion balance derived from observations works when all the ions (even trace ones) are well constrained and the dissociation state of multivalent ions are known. This of course cannot be satisfied for aerosol, so the statement must be erased. The studies quoted (especially Wang et al.) based most of their discussion on ion balances, and therefore are not well-supported.

Page 3, line 66. “NCP showed”. These studies have showed to contain important issues (e.g., Song et al., ACP, 2018; Guo et al., 2017) that does not make the neutral pH inferences likely. I agree that the mildly acidic pH are quite likely, and that it is higher than the pH levels found in other locations, so please modify the sentence accordingly, perhaps removing the references to neutral pH levels.

Page 4, line 66. “particulate matter concentration is very low”. pH variations from diurnal variability in RH is always occurring, because the LWC per kg aerosol mass changes drastically with RH. Therefore please remove the “In some countries…very low”.

Page 4, line 79. “size-resolved pH are still rare”. That is true, but some studies should be cited here that have done this work.

Page 5, line 128. You do not have NH3, HNO3 and HCl concentrations. How do you address this when calculating the pH? It is good to make sure people understand this issue.

Page 6, line 161-163. Seinfeld and Pandis is a good reference, but it is not clear from there why the DRH is low enough in the NCP to assume metastability. Metastability is supported by the RH history of the particles, and their composition (the likelihood of being in the efflorescence or deliquescence branch of the water uptake curves). I defer to the Song et al., 2018 manuscript and all the discussion in the ACPD form of the manuscript, to see what are the arguments that supports metastability.

Page 6, line 177-182. I’m quite surprised that the partitioning is sensitive to the phase state. What version of ISORROPIA do you use? Are you sure you use the latest version of the code (2.3) with the latest bug fixes? If not, I can provide a copy of the code upon request. The conclusion that pH inferences when the RH is low is also supported by other studies – so it would be good to cite those. Guo et al. JGR (2017) suggest that the lower limit is about 40%, why do you think it’s different from the 30% cited in this study?

Page 7, line 189-191. But you have gas-phase concentration of semi-volatile species with the MARGA. Why not use those? It is much better than the unconstrained iterative procedure of Guo et al. which really works when you have an “idea” of the expected NH3 (or other) levels. This is a major issue of the paper – that it doesn’t seem to constrain the size-resolved pH well because the gas-phase is not constrained well enough.

Page 7, line 208-209. Gas-particle disequilibrium does not assume that you can neglect the gas-phase! Either remove this section, or justify why you can assume this. If you cannot, then you have to revise the section (and related calculations) to accommodate for this.

Page 7, line 215. “Nh4 and Ca2”. True, but Ca also associated with SO4 and makes insoluble CaSO4 which can strongly depress the amount of soluble materials (hence LWC). You really need to include the hygroscopic ions too (K, Na, Mg).

Page 8, line 252. ISORROPIA issues an error message whenever there is “too much” Ca, Na, etc. If this is the case, then you need to say this – and basically say there is unneutralized carbonates in the aerosol. In general, these cases are characterized by external mixing – so the bulk pH may be affected. This needs to be considered in the discussion. If there is unneutralized carbonates, then the pH calculation may need to be revisited.

Page 9, line 287. “indicating that … particle water”. You contradict the statement above, that says composition is the only thing that matters.

Page 9, line 290-293. “Specifically … in winter”. This discussion is not correct. The liquid water content scales with the aerosol mass when RH < 100% (it’s in thermodynamic equilibrium), so LWC does not vary independently from aerosol mass. Therefore, you cannot talk about “more” or “less” seeds that dissolves in liquid water. This discussion is, of course, relevant for clouds – but here you talk about aerosol. So please remove this sentence overall.

Page 10, line 302. “Theoretically, … release H+”. Although highly soluble, HNO3 does not deliquesce to form aqueous aerosol in the troposphere, therefore it cannot by itself “generate” H+. If there is already some aerosol present, the additional HNO3 is too small to cause H+ to form (unless if you are talking about clouds, where the water is orders of magnitude higher than aerosol). What happens with HNO3 is that it needs to co-condense with NH3 or “bind” with Na, K, Ca to form salts that generally are “neutral”, so do not generate H+. Given that with the formation of the salt also generates LWC, this leads to the generally observed increase of pH that you see when NO3 increases. This has been extensively discussed in Guo et al., (2018), Shi et al. (2019) and others. Please revise this section accordingly.

Page 10, line 307. NH3 “binding H+” doesn’t really describe the situation, as the NO3 co-condenses with NH3 to form NH4NO3, either if it is in aqueous or solid phase (in the latter, there is no H+ at all).

Page 10, line 315. “which might be attributed to limited ALWC”. The aerosol has to be acidic for LWC changes to affect pH. So, in this sense, this segment is incorrect and should be deleted.

Page 10, line 315-318. “Compared … ions”. Comparing the aerosol and cloud pH can be discussed in terms of the large difference in LWC. Because of that, ions (like HSO4) tend to become SO4-, but to talk about “hydrolysis” of ammonium salts is, in itself, not relevant here. Unless of course if I misunderstood the authors – in which case they should actually clarify (with calculations and an explanation) about what they mean and support these statements with numbers.

Page 10, line 320. “has a role … conversion process”. There are very few locations in the lower troposphere where you have free H2SO4 in the air, most of the forms found are either HSO4 or SO4 salts. Therefore, one can claim that HNO3 and sulfates have comparable “H+ generation capacity” at best. However, the main issue is the relative volatility of the species. HNO3 does not by itself form aerosol (at lower tropospheric conditions), while H2SO4, HSO4 and SO4 salts always are in aerosol form. That, together with the large hygroscopicity of SO4 salts (with the exception of CaSO4) is the reason why sulfate-rich aerosol can be much more acidic than nitrate-dominated aerosol. This is discussed in numerous references (e.g., Guo et al., 2018).

Page 10, line 330-331. This is an established fact, please cite the appropriate references here.

Page 10, line 332-334. Although the statement is correct, it does not really describe the situation in the US. In the SE US, for example, the composition of the aerosol is much more like NH4HSO4 than (NH4)2SO4 (e.g., Weber et al., 2016) – especially in current years where SO4 levels are relatively low. Given this, and that the deliquescence humidity of NH4HSO4 is 40%, while for NH4NO3 is 61.8% at 298K (Seinfeld and Pandis, 2016) and the efflorescence point of both salts is very low. Both of these facts suggest that the LWC (per mass of aerosol) in the US should tend to be higher, actually, than for China. Please correct the statement or erase it.

Page 11, line 344-345. This statement goes against all studies to date that I know of. True, RH increases partitioning of species like HNO3, but that is usually with co-condensation of e.g., NH3. If H+ increased in the aerosol phase, that would in itself promote evaporation of HNO3. Given that, and the very large increase of LWC with RH all point to an increase in pH, or decrease in H+.

Page 11, line 345-350. This discussion has, in my opinion, the flawed approach of decoupling LWC from H+. Both do not vary independently, because of thermodynamic equilibrium considerations. You can make such discussions in the cloudwater pH, because indeed water is not bound to the aerosol through a thermodynamic constraint (aw=RH).

Page 12, line 380. “in the fine mode … excessive NH3”. The reason why under 1um size you tend to have small variations in pH is because the aerosol is in thermodynamic equilibrium with the gas phase. The pH would remain the same even if there isn’t any excess NH3 (e.g., Fang et al., 2017). Besides, the authors do not define what “excess NH3” even means.

Page 13, line 422. “In summary…important”. This is not a new finding.

Page 13, line 447. Replace “decreased” with “increased”?

Page 13, line 447-449. “Excess … United States”. This is already known (e.g. Guo et al., 2017), but it is good that the authors also find this.

Page 14, line 454-453. “pH was still … salts”. This is a strongly incorrect statement. The reasons (volatility, and thermodynamic equilibrium considerations) should be stated instead.

Dear Authors,
Thank you for your efforts in revising the manuscript as per the suggestions. This is a welcome and important contribution to the literature. Congratulations and thank you for choosing ACP as your publication outlet!
All the best,
A.Nenes