Dear Authors,

Thank you for addressing the original reviewer concerns. I sent back to the original reviewers based on their initial comments. I have now heard back from the two reviewers. Both agree that this paper should be accepted with minor revisions remaining. I ask that you please address these last requested revisions and resubmit so I can make a final review. I agree with the latest assessment made by the reviewers on the last draft so this is why I'm accepting with minor revisions remaining.

I hope you all are doing well. Most sincerely, Jason Surratt

Final Comments to Address:

Reviewer 1:

After carefully reviewing the revised version of the manuscript, it is apparent that the
author spent a decent amount of effort to improve the clarity and readability of the manuscript, as
well as discussing the assumptions and limitations of the method in greater detail.
Even though this manuscript is a continuation of the previously published work of the
author, there are several parts of the manuscript that are innovative and contain enough scientific
significance to be published on ACP, including (1) using a new (and improved) formula to
estimate the viscosity; (2) a comparison of the estimated viscosity with measurements from
laboratory generated SOAs; (3) an estimation of the viscosity with different mass loadings; and
(4) an estimation of the viscosity of the organic component of the biomass burning aerosols
based on molecular composition. Just like any other models, this model has to make certain
assumptions and is not perfect (also as reviewer 1 mentioned), but it is still important because it
is one of the few so far that can estimate the viscosity of small organic mixtures (such as SOA),
which will benefit the atmospheric community. Readers will be able to use the model from this
manuscript to estimate viscosity of SOA-like mixtures, and some readers may even be able to
further improve the model in the future. This paper certainly meets the publication standard for
ACP.

After reviewing the manuscript, there are a few parts that should be modified to be
clearer to readers.

Line 87-88. The author mentioned a piece of negative experimental evidence:
“Gorkowski et al. (2017) did not observe significant diffusion limitations for glycerol and
squalene in α-pinene SOA. Quasi-equilibrium versus kinetically-limited or non-equilibrium SOA
growth remains an open issue and warrants further investigations.” However, in a few other
papers that the author mentioned (such as Abramson et al. PCCP, 2013, Zhang et al. ES&T
Letters, 2018), there is positive experimental evidence showing that there are kinetic limitations
regarding SOA evaporation, diffusion, and formation from multiphase reactions. It is better to
mention these positive findings together with the Gorkowski et al. results to provide a more
balanced viewpoint.

Line 318, 523. As previously discussed, the author agrees that the isoprene SOA
generated from the PAM might be different from the ambient isoprene-derived SOA due to
different reaction mechanisms. So I would recommend to change “isoprene SOA” to “PAMgenerated
isoprene SOA” in line 318, 523, and other parts of the manuscript, so as to avoid
generalization of the isoprene SOA.

The Batemen et al. results in Figure 4 and Figure 6 are not consistent with the same result
in Figure 7. As review #1 mentioned, bounce results are not accurate in measuring viscosity, but
the transition from bounce to non-bounce can provide a small viscosity range where a particle
changes its phase state from semi-solid to liquid. If a particle does not bounce, it should be
liquid. But if a particle does bounce, it may still have a relative low viscosity that will not cause
diffusion limitation. According to Bateman et al. (JPC A, 2015) and Reid et al. (Nature
Communication, 2018), the bounce results shown in Bateman et al. (Nature Geoscience, 2015)
should be in the range of 100-102 Pa s, corresponding to RH 60-80%. In Figure 4 an 6, the author
assigned the RH to be 40-60%, which is different from Figure 7, where the RH range was 60-
80%. Please make the RH in all Figures to 60-80%. The text that contains 40-60% needs to be
changed to 60-80%, too.

Line 444-446: the author says the O:C ratios based on nano-DESI-HERM was lower than
the O:C reported by Song et al. (2016). So why a lower O:C ratio results in higher viscosity
estimation then? In line 493-494, the author states that higher O:C ratio will result in a higher
viscosity estimation, which is contrary to how the author explained the data in line 444-446. The
part may need to be revised to proper explain the difference between the model and the
measurement.

Line 500-501: the author should add “providing the upper limit of the viscosity of the
organic component, while APPI MS gives the lower limit”, to make it more clear that the
predictions are only applicable to organic component rather than the whole biomass burning
aerosols.

Line 908, the table and the text overlap with each other. Please fix that.
One general suggestion I have is about the figures. Figure 1 looks very much like the
author’s other paper on Nature Communications. It could give people the wrong impression that
this was a similar paper compared with the old one, but actually this paper contains a decent
amount of new information. In this future it is probably better to modify the figures not to be so
similar to previous published ones when the author writes a follow up paper, so as to avoid
confusion for the readers. But I understand why the author uses this style this time and no
changes are needed from me for this draft.

One last comment I have is the using of the fragility parameter D. I think the current
model is fine using different D values to predict the viscosity. But more recent physical
chemistry theory about liquid/glass relaxation has been improved so that all D values could
collapse into one single uniformed equation Elmatad et al. (JPC B, 2009). All the experimental
data agree nicely with the new theory without introducing the D value. Maybe the author can
consider that applying this theory to the viscosity estimation in the future.
Overall, this article provides an improved model of estimating glass transition
temperature and viscosity of organic components that can extend to molar mass of up to 1100 g
mol-1. The study cross compares with literature data and molecular measurement of the biomass
burning aerosols to show the validity of the model. The manuscript reads well especially after the
second revision, and is suitable to be published on ACP.


References
Bateman, A. P., et al. (2015). "Sub-Micrometre Particulate Matter Is Primarily in Liquid Form
over Amazon Rainforest." Nature Geoscience 9: 34.
Elmatad, Y. S., et al. (2009). "Corresponding States of Structural Glass Formers." J. Phys. Chem.
B. 113(16): 5563-5567.
Abramson, E., et al. (2013). "Experimental Determination of Chemical Diffusion within
Secondary Organic Aerosol Particles." Phys. Chem. Chem. Phys. 15(8): 2983-2991.
Reid, J. P., et al. (2018). "The Viscosity of Atmospherically Relevant Organic Particles." Nat.
Commun. 9(1): 956.
Song, M., et al. (2015). "Relative Humidity-Dependent Viscosities of Isoprene-Derived
Secondary Organic Material and Atmospheric Implications for Isoprene-Dominant
Forests." Atmos. Chem. Phys. 15(9): 5145-5159.
Zhang, Y., et al. (2018). "Effect of Aerosol-Phase State on Secondary Organic Aerosol
Formation from the Reactive Uptake of Isoprene-Derived Epoxydiols (Iepox)." Environ.
Sci. Technol. Lett. 5(3): 167-174.


Reviewer 2:

The authors have done a reasonably satisfactory job of addressing most of the questions and concerns raised during peer-review. With its focus on estimating only the glass transition temperature and viscosity, and not the actual diffusivity and equilibration timescales, I still do not find much scientific value to this approach. All that has really been accomplished is to extend their previous model to include larger MW organics. However, the manuscript has improved during review and is now of an acceptable quality to recommend publication, after they address the major criticism in my original review that they have tried to side-step in their rebuttal (please see below). Although I rate the significance and originality of this manuscript to be rather low for ACP standards, we can let the community decide over time if this is a useful advance in our understanding of organic aerosol particles.

Their rebuttal that the (superior, in my opinion) functional group-based method for estimating viscosity by Rothuff and Petters cannot account for mixed organic aerosol systems is well taken. The ability of these author’s approach (extended here to higher molecular weights) to model mixtures is a positive attribute.

The critical issue which the authors tried to avoid directly addressing in their rebuttal and revisions concerns the real need for a better understanding of diffusivity and equilibration timescales in atmospheric particles. Viscosity and Tg, which is all this paper focuses on, is indirectly related to diffusivity, but does not provide the information required to understand equilibration timescales, or any of the other important processes the authors lay out in the paper’s introduction to motivate their work. Throughout their rebuttal in response to my questions regarding the importance of diffusivity they just state “estimations of bulk diffusivity and mixing timescales are beyond the scope of this study”. And this is why I do not find much merit to what is being reported in this manuscript. It is fine if the authors wish to restrict this paper to only consider Tg and viscosity, but then the authors MUST significantly modify their introduction and conclusions to make it clear to readers what exactly can and can NOT be learned from viscosity in relation to all the critical processes they outline in the introduction. Without making these necessary revisions, the authors are frankly being somewhat deceptive by presenting their viscosity-limited work as though it can directly advance our understanding of critical atmospheric physics and chemistry. To borrow from their introduction (from their revised manuscript), here are some of the processes they outline in such a way that the reader is led to believe their viscosity estimates will advance our understanding of these same processes (_my emphasis_):

Line 64: “The particle phase state has been shown to affect gas uptake and chemical transformation of organic compounds due to _kinetic limitations of bulk diffusion_”

Line 70: “_Water diffusion can be still fast_ even in an amorphous solid matrix under room temperature, but it can be hindered significantly under low temperatures (Mikhailov et al., 2009; Zobrist et al., 2011; Bones et al., 2012; Berkemeier et al., 2014; Price et al., 2014), _affecting homogeneous vs. heterogeneous ice nucleation pathways_”

Line 79: “Partitioning of semi-volatile compounds into viscous particles may result in _kinetically-
limited growth_ in contrast to _quasi-equilibrium growth_ (Perraud et al., 2012; Shiraiwa and
81 Seinfeld, 2012; Booth et al., 2014; Zaveri et al., 2014; Mai et al., 2015; Liu et al., 2016), which
also affects the _evolution of particle size distribution upon SOA growth_ (Shiraiwa et al., 2013; Zaveri et al., 2018). Chamber experiments probing _mixing timescales_ of SOA particles derived by oxidation of various precursors such as isoprene, terpene, and toluene have observed _strong kinetic limitations_ at low RH, but not at moderate and high RH (Loza et al., 2013; Ye et al., 2016; Ye et al., 2018). Gorkowski et al. (2017) did not observe significant _diffusion limitations_ for glycerol and squalene in α-pinene SOA. _Quasi-equilibrium versus kinetically-limited or non-equilibrium SOA growth_ remains an open issue and warrants further investigations.”


This is certainly a nice introduction that discusses many of these important and uncertain processes, with good references to recent findings. Unfortunately, estimating only the glass transition temperature (and thus phase state and viscosity) tells us very little about diffusivity, equilibrium timescales, heterogeneous ice nucleation, kinetic-limitations to particle growth, etc. Yet the introduction gives the reader the strong impression that the new results presented in this paper will in fact advance our understanding of these critical processes. To summarize, the authors need to be much more upfront regarding what can and what cannot be learned just from their estimates of the glass transition temperature, and the phase state and viscosity they estimate from Tg.

Dear Authors,

Thank you so much for your detailed revision and reply to the second round of reviewer comments. Based on your replies and edits to the text, I have now agreed to accept this for publication in ACP. Congratulations!

We look forward to receiving more work from you in the future!

Most sincerely, Jason Surratt