Review of “Time-dependence of Heterogeneous Ice Nucleation by Ambient Aerosols: Laboratory Observations and a Formulation for Models” by Jakobsson et al.

This study analyses the time-dependence of freezing exhibited by ambient aerosol samples collected in southern Sweden. Constant cooling and isothermal experiments were performed with a recently developed cold-stage. The time dependence was found to be comparable to that seen in previous studies. A representation of time dependence for incorporation into schemes of heterogeneous ice nucleation, which currently omit time dependence, is proposed. The relevance of time-dependence in heterogeneous ice nucleation and its implementation in freezing schemes of cloud models is a timely and important topic. Yet, the study has major weaknesses that need to be addressed before publication. Moreover, the manuscript is not written carefully. The language and formulations are often imprecise and unclear, which hampers the understanding. 

Major comments:

1.    All the samples were collected at the Hyltemossa research station located in southern Sweden. The investigated samples were assigned to the following aerosol classes: marine dominated, mineral dust influenced, continental pristine, continental polluted, combustion dominated, and rural continental based on wind directions. In addition, BC content, PM1 and PM10 were determined. No attempt was made to further characterize the samples to confirm the assignments. The frozen fraction as a function of temperature shown in Fig. 6 and the INP concentration (Fig. 5) are all very similar and do not show the diversity found for INP samples collected at different locations. Also, the IN activity exhibited by the different samples are often opposite to expectations based on the class they were assigned to; e.g. the marine and the mineral dust samples were found to exhibit very similar INP concentrations, yet marine samples typically exhibit much lower INP concentrations than mineral dust samples. Thus, the claim that the collected samples cover the major relevant INP classes needs to be abandoned, unless it were to be supported through chemical characterization (e.g. elemental analysis).

2.    As it seems, the cold stage used in this study has not been described before. Therefore, its performance needs to be characterized properly. What is the precision and accuracy of the temperature measurement? Is there a freezing bias depending on the location of the drop on the substrate? What is the freezing curve of pure water? 

3.    A time dependence is inferred without specifying whether it complies with the assumption of stochastic ice nucleation. The reason of the time dependence should be discussed. It should be analyzed to what degree the time dependence is indeed stochastic, i.e. stemming from identical INPs freezing at a certain rate, or whether distinct nucleation sites exhibit gradual shifts or sudden jumps in freezing temperature as e.g. shown in Vali (2008), Wright and Petters (2013) or Kaufmann et al. (2017).  

4.    The relevant literature is not sufficiently taken into consideration in the introduction and in the discussion of the results (see specific comments). 

Specific comments:

Line 41: the “many possible pathways” should be specified in the text.

Line 44: Field and Heimsfield (2015) is not listed in the reference list. Moreover, more references should be given to support this statement, e.g. DeMott et al. (2010); Mülmenstädt et al. (2015).

Lines 53–58: The discussion of the different types of atmospherically relevant INPs includes only two references. This is not sufficient.

Lines 61–62: this statement is too general.

Line 93: here again, more than just one study should be referenced, e.g. add Vali (2008; 2014). 

Lines 96–105: There have not been many studies on temperature dependence but more than mentioned here. Older studies have been reviewed in Vali (2008) and Westbrook and Illingworth (2013). More recent laboratory studies have been performed by Herbert et al. (2014), Beydoun et al. (2016), Alpert and Knopf (2016), and Kaufmann et al. (2017). Moreover, there have also been recent modeling studies on the time dependence of immersion freezing, namely by Vali and Snider (2019) and Fan et al. (2019). These references should be included and discussed.

Lines 178–179: Do you mean the particle size range between PM1 and PM10?

Line 305: should it be “arise” instead of “rise”?

Lines 314–326: Here, the INP concentrations are just compared with Fletcher (1962), without mentioning where the samples from Fletcher (1962) were collected. Typical INP concentrations of the claimed aerosol classes should be added and used for comparison.

Lines 331–332: statistical tests should be performed to analyze whether the investigated samples are statistically different.

Lines 347–349: do these variations in freezing temperature refer to the instrumental precision or characterize the samples?

Lines 357–360: The values given here should become part of a table, in which also the largest and smallest standard deviations could be listed. 

Line 360: Vali et al. (2008) is not in the reference list. 

Lines 362–369: It should be stated which fraction of the droplets remains unfrozen, e.g. as an additional column in Table 4. The difference for most drops was stated to be “about 1–2 K”. How was this value calculated?

Lines 376–378: The differences between individual isothermal experiments cannot be seen properly in Fig. 8, because all the isothermal experiments are shown as blue data points. Please choose different colors for different isothermal experiments. Moreover, the larger diversity between isothermal compared to constant cooling experiments should be discussed/explained.

Line 381 and throughout the manuscript: There seems to be a confusion between “freezing fraction” and “frozen fraction”, which seem to be used synonymously. Yet, the frozen fraction means the fraction frozen at a given time, while the freezing fraction designates the fraction of drops that froze within a set time interval. As it seems, the authors mean “frozen fraction” most of the time.

Line 381–385, Fig. 9 and Table 4: The information provided in Fig. 9 is given more precisely as part of Table 4. This figure can therefore be removed. Moreover, the formula to calculate the data of Fig. 9 should be explicitly given.

Line 386 and Fig. 10: The analysis is unclear, also because freezing and frozen fraction are mixed up. The quantities in the formula should be properly defined. Did you really take the derivative or not just evaluate time intervals?

Lines 391–392: What is meant in this sentence by more and less active INPs? Typically, the ice nucleation rate of an INP increases with decreasing temperature. Yet, this sentence does not mention any temperature dependence and seems to imply that there are fast and slow nucleating INPs independent of temperature. The concept of slow and fast INPs needs to be clarified.

Lines 394–405: Here, a time dependence of INP activation is proposed without taking the temperature dependence into account. Yet, models need to combine both, and cover also situations of temperature fluctuations: e.g., what would be the time dependence of freezing in an air parcel that was supercooled by 1 K before reaching the isothermal period? Vali (1994) found that this depletes the INPs that are active at the isothermal temperature. The proposed approach should also be discussed in view of the findings of Vali and Snider (2015).

Line 419–421: Again, this argumentation insinuates that less active sites activate more slowly than the more active ones. Yet, the nucleation rates of sites are highly temperature dependent.

Line 440, Eq. 4: How is the time dependence of the INP concentration calculated? How can the temperature shift approach be combined with temperature fluctuations observed in air parcels?

Line 467–468: This listing of temperature information should be put in a table.

Lines 478–480: This sentence needs to be formulated better.

Line 486: Again, a table would be more appropriate.

Lines 488–489: How did you establish the consistency?

Lines 493–495: this sentence should be formulated better.

Lines 499–500: this sentence should be formulated better.

Line 507: it is Budke and Koop, 2015.

Line 524–525: A further explanation of the time dependence would be non-stochastic changes in IN activity that have been found e.g. in refreeze experiments by Vali (2008), Wright and Petters (2013) or Kaufmann et al. (2017). An estimate of the contribution of such changes compared to stochastic freezing would be interesting. 

Lines 532–537: Here, the possibility of several INPs present in the same drop is discussed as a risk. Yet, it is a fact that there are multiple INPs present in microliter drops, albeit with different characteristic freezing temperatures. Also in cooling experiments, several INPs compete in ice nucleation. To judge how many INPs have similar characteristic ice nucleation temperatures and might compete within a drop, samples with different degrees of dilution should be compared. The authors should consider performing experiments with more diluted samples for comparison.

Lines 541–552: Here again the temperature range of activity needs to be specified. This discussion does not make sense without specifying the temperature.

Lines 549–552: CCN are mostly liquid and do not contain any INP. Thus, having several INPs in one cloud droplet is highly unlikely.

Lines 564–644: this needs to be explained better.

Lines 574–590: The use of Q needs to be explained better. 

Line 714: Knopf et al. (2021) has been published in the meantime.

Line 831: do you mean "quartz" instead of "quarts"?

Figure 5: The formula that was used to calculate the INP concentrations should be stated or referenced. The different aerosol classes exhibit quite similar INP concentrations as a function of temperature. Therefore, statistical tests need to be performed to test whether the aerosol classes are statistically different. Moreover, each droplet population could be shown as separate line in Fig. 5, as it is done in the freezing spectra in Fig. 6, to judge visually whether the different aerosol classes are different. Finally, the INP concentrations should be compared with typical INP concentrations of the aerosol classes they should represent.

Figure 6: The differences in frozen fraction between aerosol classes are small and difficult to judge the way the frozen fraction is plotted. The figure could be improved by narrowing the temperature range to -5°C to - 25°C (as it is done in Fig. 13) and by adding gridlines to the panels.

Figure 7: It might be helpful to add dots for the drops that did not freeze during the isothermal experiments. They could be put at the bottom of the panel (at -25°C). 

Line 884: what is meant by “minimum of 4 cooling cycles”?

Figure 8: These plots are again difficult to read. The frozen fraction for each experiment should increase continuously but the blue data points just scatter, most probably because they stem from isothermal experiments performed with different droplet populations. In this case, they should be shown in different colors or symbols so that different experiments can be discriminated. Were the data points taken at defined time intervals? 

Figure 9: the information provided by this figure is also given in Table 4. It can be removed.

Table 1: The line numbers are shifted to the right. 

Line 982: what do you mean by “much more limited”?

References: 

Alpert, P. A. and Knopf, D. A.: Analysis of isothermal and cooling rate-dependent immersion freezing by a unifying stochastic ice nucleation model, Atmos. Chem. Phys., 16, 2083–2107, https://doi.org/10.5194/acp-16-2083-2016, 2016.

Beydoun, H., Polen, M., and Sullivan, R. C.: Effect of particle surface area on ice active site densities retrieved from droplet freezing spectra, Atmos. Chem. Phys., 16, 13359–13378, https://doi.org/10.5194/acp-16-13359-2016, 2016.

DeMott, P. J., Prenni, A. J., Liu, X., Kreidenweis, S. M., Petters, M. D., Twohy, C. H., Richardson, M. S., Eidhammer, T., and Rogers, D. C.: Predicting global atmospheric ice nuclei distributions and their impacts on climate, P. Natl. Acad. Sci. USA, 107, 11217–11222, https://doi.org/10.1073/pnas.0910818107, 2010. 

Fan, S., Ginoux, P., Seman, C. J., Silvers, L. G., and Zhao, M.: Toward improved cloud-phase simulation with a mineral dust and temperature-dependent parameterization for ice nucleation in mixed-phase clouds, J. Atmos. Sci., 76, 3655–3667. https://doi.org/10.1175/JAS-D-18-0287.1, 2019.

Herbert, R. J., Murray, B. J., Whale, T. F., Dobbie, S. J., and Atkinson, J. D.: Representing time-dependent freezing behaviour in immersion mode ice nucleation, Atmos. Chem. Phys., 14, 8501– 8520, https://doi.org/10.5194/acp-14-8501-2014, 2014.

Kaufmann, L., Marcolli, C., Luo, B., and Peter, T.: Refreeze experiments with water droplets containing different types of ice nuclei interpreted by classical nucleation theory, Atmos. Chem. Phys., 17, 3525–3552, https://doi.org/10.5194/acp-17- 3525-2017, 2017.

Mülmenstädt, J., Sourdeval, O., Delanoë, J., and Quaas, J.: Frequency of occurrence of rain from liquid-, mixed-, and ice-phase clouds derived from A-Train satellite retrievals, Geophys. Res. Lett., 42, 6502–6509, https://doi.org/10.1002/2015GL064604, 2015.

Vali, G., 1994: Freezing rate due to heterogeneous nucleation. J. Atmos. Sci., 51, 1843-1856.

Vali, G.: Repeatability and randomness in heterogeneous freezing nucleation, Atmos. Chem. Phys., 8, 5017–5031, doi:10.5194/acp-8-5017-2008, 2008.

Vali, G.: Interpretation of freezing nucleation experiments: singular and stochastic; sites and surfaces, Atmos. Chem. Phys., 14, 5271–5294, https://doi.org/10.5194/acp-14-5271-2014, 2014.

Vali, G. and Snider, J. R.: Time-dependent freezing rate parcel model, Atmos. Chem. Phys., 15, 2071–2079, https://doi.org/10.5194/acp-15-2071-2015, 2015.

Wright, T. P. and Petters, M. D.: The role of time in heterogeneous freezing nucleation, J. Geophys. Res.-Atmos., 118, 3731–3743, doi:10.1002/jgrd.50365, 2013.

General Comments

This is quite a nice study, using a limited number of samples to study the time dependence of ambient ice nucleating particles freezing in the immersion freezing mode. In contrast to what I read in another review, I find the details about the experimental device (LUCS) and methods to be very good (and the authors responsible for it are to be lauded). The writing is also fairly clear, excepting poor introduction/definition of terms used in equations. The results demonstrate a relatively weak time dependence to freezing that is nevertheless consistent with prior studies using soil samples and cloud water. The consequent impact can be described by a temperature adjustment of say 2K in order to describe freezing at longer time scales. One does wonder to what extent temperature control of the drops and where an INP may be floating in individual drops may influence these results. This is not discussed. In any case, the corrections in comparison to very short time scales range up to at most about a factor of 2. It is interesting that this is well within the bounds of the agreement of many immersion freezing methods when compared together. This is not spoken about either, but should be mentioned, the reason being that it emphasizes the utility of such measurements, regardless of whether used in a deterministic manner or with an approach as suggested here to describe the modest time dependence. While much effort is expended on analyzing cooling ramps and isothermal data on six samples, the least convincing aspect of the study is that these six cases can be clearly identified and taken as sufficiently representative and attributable to the types of aerosols identified for comparison. There are reasons that there should be variability amongst those types, and season could matter for different types as well. I recognize that numerous caveats were added in regard to the inability to know INP composition, but they are ultimately ignored in fashioning a parameterization that differs for the different types. Consequently, in suggesting that these results could be used as representative of INP types present in the noted aerosol scenarios (e.g., mineral, or organics) moving forward, when in fact the differences between them are modest (note Fig. 5 and Fig. 10, with insignificant differences apparent), is questionable. In reality, it seems unnecessary, unless one is only intent on using the referenced parameterizations instead of simply pointing out how deeper insights could be gained in the future using these methods in places where certain aerosol scenarios are clearly more dominant. This is not meant as a severe judgment on a study that has been needed for a long time. Needed and useful, especially for pointing out that corrections to INP data for time dependence is small, and results do not change greatly in repeated experiments, challenging some other recent studies (not noted, but oddly referenced at one point for the exponential decay of freezing rates – which those authors seem to attribute to experimental artifacts) that suggest that immersion freezing nucleation is largely purely stochastic for ambient INPs. It should be emphasized more that the present results appear to reject that hypothesis. One other factor that I felt needed to be brought out in discussing Westbrook and Illingworth is the extreme population (extraordinarily high INP concentrations) required by that study to exist for their hypothesis of long freezing time constants to explain ice formation in clouds. Considering all other existing measurements of INP concentrations in the ambient atmosphere, and results such as presented in this paper on time dependence of freezing, the numbers required by that conjecture are not within the realm of possibility. I kept expecting the discussion to come back to this point, but clearly the authors have in mind to do full model simulations to invalidate the earlier hypothesis. That is a bit disappointing, because it leaves the readers hanging. In the end, the study is demonstrative of what could be done, with great effort obviously, if many more cases are identified or if done in environments that are more clearly dominated by certain INP types. I have an assortment of related and other specific comments added to this, which I do below in order of appearance. My recommendation is that this paper needs revision in places before being accepted for publication.

Specific Comments

Abstract

Line 13: It should read “six” ambient samples, to be explicit.

Introduction

Line 53: The first ice in any mixed phase cloud does not have to be from activation of INPs if sedimentation occurs from higher levels that may reflect homogeneous freezing conditions.

Lines 61: Only spot I saw where ice nuclei is used in preference to ice nucleating particles.

Lines 72-73: There is a fine point here that is not stated with regard to Westbrook and Illingworth’s argument. This is that the action of a stochastic process over many hours would require an INP population unlike any ever measured. It already seems a nonstarter, but this study provides insight.

Lines 93-94: A reference seems appropriate to support this point

Line 115: This is a curious reference for a paper that ultimately finds results in complete disagreement with single parameter CNT. Is it meant to point out that this is the case for certain INPs, such as illite?

Line 130: “…here is an inevitable cost from lack of identification of the precise chemical species initiating the ice in observed samples.” I appreciated these caveats, so then I wondered why the selected samples were not treated only as examples, rather than suggesting they are meaningfully representative of specific aerosol types. There are ways to get at INP composition, even via immersion freezing methods, they simply are not used herein (see below). 

Methods

Lines 159-160: I am curious about the selection of filter pore size. I understand that larger pores allow high flow. Was face velocity and collection efficiency considered to estimate if there were undercollection of particles at 0.4 microns and smaller?

Line 161: What does it literally mean that not all filters were able to achieve a full 24-hour sampling? This is an unusual statement. The pump stopped because of overloading of the filter? The flow rate changed and you did not record it over time to get an accurate volume? If flow rates were not recorded, then this should be stated as an uncertainty for INP concentrations.

Line 168: There is a difference between marking the samples to reflect different aerosol types and what will dominate as INPs, right? Sometimes the dominant composition is irrelevant if one particular type acts with higher efficiency. I think you aimed to select episodes that represented potentially different dominant aerosol types, assuming that these might reflect different abundances of INPs of different types. Ideally, you need a single type that is not influenced by trace amounts of another type, but there is literature to show that a little mineral dust sometimes overwhelms a marine INP population. Hence, the approach has a great deal of uncertainty associated with it. This of course is the nature of ambient sampling, and why some attempt to parse out influences of the different aerosol types present through more detailed approaches.

Line 174: You need to say more about how the HYSPLIT model was set up, and it should be referenced appropriately. I especially did not understand why the trajectories were set to end at 500 m, instead of somewhere closer to the surface site. Did you test different levels for this end point location?

Lines 188-189: But can you say that soil dust does not dominate also in the “combustion-dominated” sample, or any particular continental sample for that matter? You are a bit blind without knowing anything about the nature of the INPs contained in the air at any time.

Section 2.2.2 overall: I will say that I otherwise appreciated the honesty and accuracy in statements made in this section about how certain (not very) one could be about the assumed total aerosol composition as representing INPs. Then why title it “Sample classification according to likely dominant composition of INPs”? Again, you are referring to what you think is the dominant aerosol type. There is no guarantee that the total aerosol type abundance will be reflected by a dominant INP of that type. It depends on individual efficiencies and what all types are there, which I think the authors understand. I suggest that in the future it could be beneficial to analyze for general INP types using methods in the literature (e.g., Testa et al., 2021, J. Geophys. Res, doi: 10.1029/2021JD035186). There are ways to get at inorganics that would include minerals and black carbon, for example.

Section 2.2.2 also: Have you considered testing your assumption using aerosol reanalyses, such as MERRA-2?

Section 2.2.3: What is a sterile cryogenic vial? That is, what do you mean by sterile? Was it tested for INPs released by pure water?

Lines 306-308: No freezing, meaning zero wells frozen? In general, I felt that the testing of water, field blank filters rinsed in water, and any other handling protocols need  a little better documentation, especially for temperature ramps. Surely there is a background in the device. There were no frozen wells for DI in similar ramps, nor for the field blanks?

Results

Lines 319-326: These generalizations are fine. At such a sampling site, even these characterized types must have seasonality, no? Perhaps in the conclusions you should note that using these 6 samples to characterize different source types might be a stretch until an annual cycle is explored or means are derived to more carefully distinguish influences and assured impacts on INPs.

Lines 331-332: Given this, I do not think that you can make the statement that it is “highly likely” that these six identified types differ significantly. You have not proven that. They all look quite similar within some bounds (again, differences in both Fig. 5 and Fig. 10 are minimal). Are they representative of INP in general for the region? That seems likely. If you have the aerosol data and can make such calculations, could you not normalize all of these events (except the dust one where there is no data) by total aerosol surface area to see if that separates them at all? I understand that what you would want is speciated surface area, but total could be informative.

Figure 5: Should you not actually show the variability you are referring to in the caption, e.g., with error bars?

Line 340. I became confused already earlier in the paper as to whether or not repeated cycling involving heating and cooling were used. This fact should be moved forward in the methods.

Lines 366-367: “…because the probability of any drop freezing during any isothermal experiment decreases with decreasing normal freezing temperature below the isothermal temperature.” I did not understand this at all. This is not intuitive without some additional explanation.

Figure 8: Question of clarification. The “freezing fraction” here is on the basis of the droplet population, correct? Or on the basis of the final number frozen? This figure is difficult to read due to the use of a logarithmic scale on the x-axis. What do these look like with time on a linear scale of say hours starting from time zero? That would seem to be a starting point, before plotting them this way.

Figure 9: I especially cannot understand this figure. Should not the end total ice fraction be larger than the initial ice fraction in all cases? Why would this ratio be less than 1? Or does 0.5 mean a 50% increase and so on? If so, the y-axis needs redefinition.

Figure 10 and discussion around it: This is an interesting figure that suggests to me that the INPs generally have similar freezing behaviors that are describable in nearly a chemical kinetic fashion (e.g., DeMott et al., 1983, J. Clim. Appl. Meteor., doi:10.1175/1520-0450(1983)022<1190:AAOCKT>2.0.CO;2). I wondered though what N and N_ice exactly are.  They are the same? These are not defined anywhere, either in the manuscript or the caption. Are they the total number of drops? Or the total number frozen after xx hours? If looking at the change in freezing rate, it seems like the reference should be the total INP population, not the drop number that may or may not reflect an INP per drop. I think that the relevant value is N_ice,infinity, in Eq. (1), but it is unclear how this is determined or estimated. I think this is finally stated later, perhaps at line 408. Hence, the introduction of these things is a bit out of order.

Figure 10 caption: “Occasional negative rates are not plotted.” How do you get a fractional freezing rate that is negative?

Line 399: Now N_ice(t) is a frozen fraction? This is very confusing. Frozen fraction or number terms need careful definition before they are used. N normally refers to number, but I sense it is being used for both number and fraction in this paper.

Line 534: That there are multiple INPs in each drop is a risk? This is a fact of the method, at least for cooling ramps that extend over the mixed-phase regime. It is accounted for in most immersion freezing analyses, ala Vali (1971).

Lines 571 to 572: I do not trust that you can make such correspondences at all. The study is not sufficiently detailed to do so. You do not even know if sources are organic or inorganic, for sure.

Line 590: Possibly. It remains to be seen how useful the approach will be. But this is where we are left hanging. If the total INP number is not so much greater than measured deterministically with a small temperature shift, aren’t the conjectures of Wetsbrook and Illingworth invalid already?

Line 644-645: It may enable it, but odd to highlight a single study without proving it. Can we expect that robust simulations will be achieved? I suggest that the emphasis on saying that single events can be used to target certain aerosol types be removed from this paper, and postulated instead in the next one that seems in preparation.

Data availability: No statement was made. Will the data be made available somewhere? This is important.

Editorial notes

Line 24: decline, rather than declines.

Line 124: do you really need the word “Background”, which is not really quantifiable. Just say you collected aerosol data?

Line 137: I would omit “assumed to be likely”. It does not help qualify that there is no way to be certain about influences, considering limited information on aerosol compositions.

Line 616: “for what we have inferred to be representative of mineral…”