Interactive comment on “ Using critical area analysis to deconvolute internal and external particle variability in heterogeneous ice nucleation

This manuscript presents a new mathematical approach to describe laboratory immersion freezing data based on the concept of ice active surface sites in combination with a stochastic model of heterogeneous freezing. The unique feature of this approach is that it assumes a continuous distribution of the ice nucleating activity, expressed as a function of contact angle, θ, of a particle’s surface without defining the size or number of active sites. This yields a function, g(θ), to determine the freezing probability for an ice nucleating particle. This approach is applied to examine the internal and external variability in immersion freezing experiments which, in part, may be due to different particle concentrations among droplets. The authors derive a critical surface

which it does not in absence of a physical model.More careful language would be more appropriate.
As for the mathematical concept: A distribution referred to as a "g-distribution" is introduced.It is not clear of which kind, but always seems to be a normal distribution function.In principle, this concept is very much the same as the α-PDF, the updated soccer ball model (SBM) or other distribution based fits.The emphasis on continuous distribution values is not clear to me as both α-PDF and the SBM are continuous in a mathematically sense.
As the frozen fractions curves shift to lower temperatures due to a decrease in surface area and below the critical threshold area as stated here, g cannot reproduce the data.However, freezing data can be described when choosing contact angles and calculating g values as many times as necessary.The authors are correct that a new distribution for below threshold surface areas is not necessary.(If it were, would it imply that the fit is truly unphysical, i.e. not representing particle properties?)But obviously, drawing as many times as necessary from g (which contains all possible contact angle values) to represent the freezing curve does not mean anything physically.One could argue that the number of draws represent just another free "fit parameter".In general, I am not surprised that data can be fitted with this mathematical construct, but the manuscript must include, state, discuss properly its assumptions.The emphasis to have discovered something "real" in view of these assumptions is incorrect.The effects may all be a result of an assumption that is not known to be true or even applicable.More studies and experiments are necessary.
I remain confused about the details of the method.It would also be beneficial to show g and the numbers of draws for different experimental data sets to establish this method.Many other questions remain and I mention a few here.It is stated that θ is randomly chosen but does this mean that θ is first sampled from a uniform probability density function, and then g(θ) is calculated?Does this method of draws also work equally well for above the surface area threshold?Is it correct to say that the g-distribution is not C3 a probability density function from which θ is derived and used in the J_het equation, but is it a scaling function or a change from a surface to line integral as stated in the manuscript?
The manuscript does not sufficiently discuss previous work on immersion freezing.On the model side, the authors could test if "subsampling" of an α-PDF or other distributions (deterministic etc., see e.g.Marcolli or Lohmann group) will result also in a better representation when surface area is changing -likely yes, if sufficient draws are allowed.The water activity based immersion freezing model by the Knopf group also can describe immersion freezing for illite.As far as I recall they do not need to invoke external or internal mixtures to consolidate freezing data obtained from differently sized particles.
Regarding experimental studies.Somehow it feels irritating that the authors, claiming to have a new parameterization model, just discuss one study by Broadley et al. and do not test their model with other studies.Also, some statements in this regard are not entirely correct.There are cold stage experiments that apply micrometer-sized droplets with rather uniform INP immersed within those droplets like the studies by the Koop and Knopf groups that include surface area and time variance.There is also CFDC data covering size and time dependence that could be tested by this new model.A "negative experiment" would also be beneficial, e.g.testing if frozen fraction curves from experiments employing smaller surface area result in a g distribution that cannot describe smaller or larger surface area freezing data.I believe the Pinti et al. freezing data would represent an ideal test case for this model and in fact, may be in contrast to the results here.Pinti et al. found that at large surface areas for a variety of dust particles, a unique freezing temperature of some droplets was observed warmer than the freezing temperature of the rest of the droplet population.
The authors use the Broadley et al. data as an "absolute data set" meaning the uncertainty of the data and its implication for the application of this model is not considered.In this study it is emphasized that the nucleation process is stochastic in nature C4 whereas Broadley et al. do not assume this.The Broadley et al. data likely possesses a large statistical uncertainty when stochastic processes are implied.Furthermore, the ice nucleating surface area in each droplet will be uncertain.As stated in figure caption 5, droplets with diameters 10-20 µm were applied.This results in about one order of magnitude uncertainty in surface area.This uncertainty alone would consolidate all curves shown in Fig. 5.In other word, this uncertainty nullifies attempted analysis and proof of the validity of the assumption of internal and external variability and suitability of this parameterization.Again, the presented approach may have some validity but it is very poorly executed by just looking at one data set and not discussing the uncertainties of the data set.Furthermore, the authors mention that they performed cold stage freezing experiments but these data are not shown.Why not making a stronger case, if there is the data?
In summary, the manuscript should clearly communicate the assumptions and caveats of the model and the data investigated.No molecular processes are directly observed or measured.Any interpretation in this regard should be suggestive, speculative, hypothetical in wording reflecting the nature of this mathematical exercise.There is no loss by doing this.Time will tell if this was the correct way for yet unknown reasons.The manuscript about a new model would be much stronger when tested using different experimental data.
p.1, l. 13-19: The 2nd sentence of the abstract lacks carefulness.Other researchers would claim their parameterizations are consistent with their experimental studies since they describe frozen fraction curves for changes in area, time, etc.There is no clear definition for "consistent" or "comprehensive", and "freezing properties"?The following sentence then introduces the model with the statement that it uses a continuous function of contact angle and no restrictions on actives sites.These statements are somehow misleading.Fact is, the model can reproduce experimental data.
p.1, l. 26-27: The authors write "the two-dimensional nature of the ice nucleation ability of aerosol particles".What is the meaning of this?The only way I can make sense of C5 this, is assuming that external and internal particle mixtures are meant by this? p. 2, l. 2-5: This sentence has to be reworded.A distribution cannot be statistically significant.
p.2, l. 6: "will not" This exemplifies a claim of certainty, when in fact this is based entirely on a model assumption of some active site surfaces.As mentioned above there is no direct experimental evidence for an internal/external active sites.p. 3, l.13-14: The results of Vali (2008) do not show there is a strong spatial preference because this could not be directly measured.Vali (2008) might have claimed his experimental results suggest there are active sites in preferential locations (based on mathematical analysis).
p. 3, l.16-19: The role of time for what?This is very sloppy discussion and does not reflect the community's concern on this issue besides lacking important laboratory work from Koop, Knopf, Lohmann, and others and field work indicating the important role of time to explain observations.This section has to significantly improve if time dependence is addressed in this manuscript.As it is, the reader is left pretty clueless and cannot do more than accept written statements.p. 3, l.20: "completely"?What is meant by this? p. 3, l. 29 -p.4, l. 2: This is in principle the repetition of previous sentence describing the findings by Ervens and Feingold.However, here it is somehow generalized: What models?What results?Why are their more drastic variations?p. 4, l. 3: "First principles of classical nucleation theory".This is a strong claim.I would much doubt that the authors show any derivation from first principles in this manuscript.There is no discussion or derivation of clustering, free energy changes or chemical potentials, capillary approximation, etc. p. 4, l. 5-8: "accounts for the variable nature of an ice nucleant's surface and the distribution of ice active surface site ability across a particle's surface (internal vari-C6 ability), and between individual particles of the same type (external variability)."This must be much more careful formulated.There is no direct evidence for the variable ice nucleating nature of a particle surface or the surface of different particles.This is an assumption the authors make based on previous work that predisposed this assumption into a mathematical fit.Also, on l. 5, ice embryo growth and dissolution is part of classical nucleation theory.This is part of a testable physical theory, but not "proven" to occur.The authors need to recognize that even an ice embryo is theoretical.The existence of a g-distribution is even less so as it serves a mathematical scaling or integrating fitting function, not something physical.
p. 4, l. 10: "and interpret".This model cannot interpret the freezing data since it is not based on a testable theory.Its assumptions cannot be proven and a g-distribution cannot be measured.The authors want to interpret freezing as the result of active sites, when in fact they already assume that the presence of active sites result in freezing.This indicates circular reasoning.Although, it is sufficient to say that this approach can successfully describe the freezing data -a valuable result.
p. 5, l. 17-19: Reflects a misunderstanding of the authors about CNT. 1. "pure" makes no sense here.2. CNT does not assume/indicate that ice nucleation occurs uniformly across a particles surface.This formulation considers only an embryo on a surface.3. A particle surface area is not included in Eq. 2, this is because there is no dependence on particle surface area.Maybe the authors assume that the contact angle is uniform over the entire surface and from this, when applying Eq. 2 over the whole particle surface, infer that ice nucleation ability is uniform across the entire surface.In other words, CNT has never made any assumption of uniformity of particle surface areas, but a single contact angle is only conceptualized by previous studies in the literature.It is not a facet or constrain of CNT.This should also be changed on p. 8, l.12-14.
p. 5, l. 22: Equation 3 can only be formulated assuming that every particle has the same surface area.The authors define A as the surface area of a single particle.Then this A must have an index for each particle?The assumptions for this equation are not C7 clear and are misleading.
p. 6, l. 3-6: "A more realistic approach is to recognize" is a very bold statement.How about "We assume. .."? p. 7, l. 1-8: Maybe make clear that these are the authors' definition of internal and external variability.This does not represent text book knowledge and agreed-uponfacts.
p. 7, l. 9-11: This is a misleading statement and should be discarded.There is no proof that this approach provides direct insight.The authors are assuming variability without showing that particle surfaces are considerably variable in terms of their ice nucleation ability.Again this is a mathematical construct.
p. 8, Eq.8: J, per definition, is not a function of time but of temperature.Here, this is only the case because via the cooling rate it gives temperature.This is confusing when coming from CNT and not necessary.One could start with Eq. 9.
p. 8, l.16-21: This is an example, where the authors show no sensitivity that their approach is mathematical only, but use the good fit to make firm statements about the underlying process for which there is no proof/direct observation.In fact, other fitbased studies could claim the same.For now, these are non-testable statements and should be avoided.
p. 8, l.22 to p. 9, l.6: This section has to be improved.This is too difficult to understand in terms of what has been done mathematically to derive the freezing probabilities.I am left with several assumptions how to proceed.
p. 9, l.17-22: Again, strong statements for an effect that cannot be fundamentally proven as of yet and that can also be described by other mathematical/physical means.
Why not frankly state something like: "These results suggest that . ..may. ..may. . .though previous parametrizations have also been able to describe. ..".I assume the authors want to put out this new idea, something to further investigate in the future...

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p. 9, l.27-p.10, l. 1: This text section states that a g distribution is just a probability density function that indicates the numbers of sites with a certain θ.But the text starting on p. 15, l. 8 states that the authors draw θ from a uniform distribution and then calculate g(θ)?So g is not a probability that particles have a certain θ value?Does this mean every θ from 0 to 180 • has an equal chance to be present on the surface of particles, but freezing probabilities are scaled by the integrating factor g(θ)?
p. 10, l. 4-8: This is very confusing.First somehow one large active site is assumed (summing up surface area) but then it is stated that this active site (which by definition has one nucleation probability) has a continuum of ice nucleation activities.
p. 10, section 3.2: Why not plot the continuous distributions used in this work including the approximated one and full one (g and g_bar)?Could be added as a supplement.
p. 11, l. 12-21 and following: Again, very firm statements on the underlying molecular processes not treated by the mathematical formalism.Statement of active site size is incorrect.CNT does not give size of active site but gives size of a critical ice embryo for given supersaturation.That this somehow, potentially reflects the size of an active site is very speculative and questioned by most recent findings using molecular dynamics simulations (e.g.Cox et al., 2013, Zielke et al., 2015).The fact is that a number can be calculated by integrating Eq. 11, but this is only a result of your assumption of a g distribution.It does not give significant insight.
p. 12, l. 25 -p.12, l. 2: These general statements are incorrect.See general comments above.There are other types of cold stage experiments that apply micrometersized droplets and INPs with surface areas that are atmospherically relevant.Also, this manuscript does not give a fundamental proof that studies using large particles result in erroneous nucleation descriptions.If so, this would have ramifications far beyond the area of atmospheric sciences.
p. 12, l. 7-9: This is confusing, also due to above issues of definition of variability.The frozen fraction curve resembles freezing of droplets not considering the INPs inside C9 it.The Murray group observes a subset of droplets freezing differently than others, suggesting external mixtures.A few lines above, one large particle in one large droplet is described and here one large droplet with many small particles is considered, but still within one droplet.In fact many small particles should express a larger surface area.The effect of many small cannot be resolved since only freezing of that one entire droplet is observed.
p. 12, l. 16-18: Poor wording: "threshold of statistical significance".Of a distribution?p. 12, Eq. 12: Until now the word 'system' has been something general, but here is there a specific definition to this?What is one system?What is the ith system?Is a single droplet a system, is a single particle a system with active sites, etc.? Be consistent throughout the document.
p. 14, l. 1: What are high particle concentrations?Whose data are you using here?Should be stated in the beginning of this section.What is a retrieved averaged g distribution?
p. 14, l. 7-31: It seems discussion starts with the right panel of Fig. 4. Why not plotting this one in the left panel?Please add experimental data as well to show model representativeness.
p. 14, l. 22-24 and l. 27-30: Your approach is successful, but only due to the assumptions used in simulating the freezing.This does not mean that it actually happens in your sets or Broadley et al., 2012. p. 15, l. 1-5: This is important.When introducing a new model, it has to be evaluated by different data sets.Why are these results not shown?
p. 15, l.6-11: Isn't a running index for g(theta_r) missing to indicate that the calculation