CNT Parameterization Based on the Observed INP Concentration during Arctic Summer Campaigns in a Marine Environment

Round 1

Reviewer 1 Report

Cirisan and coauthors provide a nice, succinct study using previously published summertime Canadian Arctic coastal and marine INP measurements to develop an improved parameterization for INP concentration simulations. They discovered very good agreement between the observed and predicted concentrations as compared to existing parameterizations. Improved Arctic INP parameterization is crucial, given existing parameterizations are not based on Arctic measurements and, more broadly, Arctic cloud formation processes and climate effects are some of the most poorly quantified compared to lower latitudes. The manuscript is for the most part well written but would require some revision before publication, as detailed below.

Main comments:

Title: Happy to see the authors specified this is the Arctic summer, but marine and terrestrial environments regarding INP concentrations and sources can be very different. The authors should consider changing to something along the lines of “Arctic marine summer campaigns” or “Arctic summer campaigns in a marine environment”

Introduction: There is a quick jump to the Arctic focus on line 54. Any information prior to this part is generally focused, which is fine, but there needs to be some dedication on Arctic INPs and their background, and more broadly, why it is important to improve prediction of INPs in the Arctic (e.g., Arctic mixed-phase clouds are poorly constrained, yet have a large impact on the surface energy budget and thus energy affecting frozen surfaces). I would recommend spending a paragraph focused on the Arctic to emphasize the importance of this work.

Methods: Although I realize the observations are previously published, there should be at least a brief overview of the immersion mode techniques used since those data are central to this work. There is a sentence or two on the technique in the beginning of the results section, but this information belongs in the methods section.

Results (pg 4): SMPS and APS are mentioned, but again, there needs to at least be some brief description of them in the methods (e.g., size ranges, how they were combined into one distribution even though they measure different types of diameters, etc.)

Results (pg 4): So, contact angles were essentially guessed to match the INP concentration observations, correct? How can this be verified to what the actual contact angles of nucleation might have been? Obviously, contact angles were not measured, but some effort should be spent explaining this in more detail and the possible caveats associated with this assumption.

Results (pg 6): The Meyers, DeMott, and Fletcher parameterizations are brought up here but not described. It would be helpful to provide some background on these parameterizations and how they were developed (i.e., the observations used), such that this information provides clear evidence as to why they might not work in an Arctic marine scenario. Also, can the authors comment on if the McCluskey marine INP parameterization was considered? That one would be more closely related given it is a similar regime, albeit it was developed from Southern Ocean observations.

McCluskey, C. S., DeMott, P. J., Ma, P.‐L., & Burrows, S. M.: Numerical representations of marine ice‐nucleating particles in remote marine environments evaluated against observations. Geophysical Research Letters, 46, 7838– 7847, https://doi.org/10.1029/2018GL081861, 2019.

Discussion and summary: The actual “summary” part of this section is nonexistent. The authors should consider providing a brief summary of their findings, reiterate the broader implications for their work, and perhaps provide some recommendations for how this parameterization should be applied to future work or recommendations for future Arctic INP parameterization studies. Specifically, this work was conducted in a specific Arctic location. Can the authors comment on how this parameterization might be useful or suffer from limitations in other Arctic regions or during other Arctic seasons, such as the more polluted haze or oilfield locations? This may be difficult given this is a first, but the authors could at least comment on how this should be tested in a wide range of Arctic regimes in the future.

Minor comments:

There are typos and grammatical issues throughout that need to be rectified. Specifically, INP is defined and used incorrectly (e.g., defined as “ice nucleus particle” when it should be “ice nucleating particle”, should be used as “INPs” when plural, and at times is still defined as “IN”). Please correct these and use the most widely accepted terminology by Vali et al. 2015.

Vali, G., DeMott, P. J., Möhler, O., and Whale, T. F.: Technical Note: A proposal for ice nucleation terminology, Atmos. Chem. Phys., 15, 10263–10270, https://doi.org/10.5194/acp-15-10263-2015, 2015.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

The manuscript presents a new CNT based parameterisation for immersion freezing for the Arctic developed from Arctic field data. It uses a temperature dependent contact angle fit. The parameterisation is compared against the same field data and three widely used mostly temperature dependent parameterisation schemes, which have been derived from worldwide field data. The presented parameterisation aims to improve simulations of mixed-phase clouds in the Artic region, where current parameterisations often fail to estimate the freezing processes happening in these clouds. Allthough the approach for deriving the parameterisation scheme seems to be solid, the interpretation, evaluation, discussion and extrapolation of the results is poor. In addition to that the manuscript is poorly written and some language edition would be needed.

I can only recommend to accept this paper after the language has been edited and the following major revision have been adressed:

1.) It is not clearly motivated why the field data was used to derive a CNT based parameterisation scheme, instead of a (simpler) temperature dependent parameterisation scheme (such as an ice active surface site density ns scheme). This should be explained in more detail and also the implications of this choice should be stressed. For the comparison (see point 3) it would make more sense to add a simplified scheme that has been fitted to the field data and the differences between the different type of schemes should be highlighted.

2.) The motivation for the parameterisation presented here was to improve the representation of mixed-phase clouds in the Arctic in different models. However, neither the implication of the results are discussed in terms of a new parameterisation scheme for models, neither how this scheme should be implemented and used in such models. The CNT parameterisation scheme needs some input on the freezing abilities of the different aerosol species (contact angle). In this case this information is derived from field data, not for a specific aerosol type. In GCMs were aerosols and their chemical composition is explicitly modelled the question would be how to use this scheme. Would it be a region specific parameterisation for all the aerosols within this regions and from where to where would the regional boundaries be? Or is the idea to use the temperature dependent contact angle for all aerosol particles worldwide independet of chemical composition? That would be nearly a contradiction to using a CNT based scheme at the first place? However, it seems to be incomplete to present a parameterisation but not discuss how it should be used.

3.) The resulting parameterisation is compared against the data, which was used to derive the parameterisation with. For a first step that seems to be ok, but the comparison to three other schemes independent of the field data set is missleading here. This can help to show that exisiting parameterisations cannot predict well the field data measured in the Arctic. One can also show that the new parameterisation scheme fits better for this case, but that is not surprising since it was fitted to that data. That should be more critically discussed. Additional the comparison cannot be used to estimate how well a temperature dependend CNT scheme would fit the data in terms of a parameterisation type. To look into that aspect the same field data would needed to be fitted in different (simpler) ways and the corresponding results should be compared. I would advise the authors to do such a comparison as well.

4.) Some details of the field data used for the fitting could be explained better:
- How long was the time interval for each sample?
- Where/around where were the samples distribued (a map could help here)?
- Was the fit in the end based on 25 (days) * 4 (temperature) data points? In the plot legend of Fig. 1 some days have more than one data point - why? Was the interval in between filter samples shorter here? How representative are you assuming the field datapoints to be?
- How was the cooling rate /time step used- did these result in even more data points (FF at a certain temperature and then another one 1 s later)?
It is also nearly impossible to differentiate the data points in Fig. 1, maybe a separate figure of the datapoints would help here and would be appreciated.

5.) Validation of the new parameterisation scheme (Fig. 3):
It is not clearly explained what is plotted here. Does each point reflect one temperature or how is the temperature reflected in these points (and size as well)? Is for each point the temperature and size of the aerosol used to calculate the INP conc. from the parameterization scheme and this then plotted agains the measured INP conc.. How would uncertainties in size/temperature change the plots that one can see here? Why is deviation from the 1:1 line (the slope) so different for all parameterization schemes compared to the field data? Is the INP conc. in the field data less dependent on temperature/size as in the parameterisation schemes or are there other factors leading to this picture? That are all aspects that should be discussed in the paper. As discussed before it would be interesting to see a Fletchers/Meyers similar approach here based on the field data in comparison. A different CNT approach as a comparison could also be interesting (for example the Zobrist parameterisation that you use before as a reference as well).

6.) Revise the text in terms of language and clarity (especially the introduction but also the description of CNT). Many sentences are imprecise and not fully correct, e.g. "In recent years, by increased knowledge of ice nucleation from fiel and laboratory studies, cloud-aerosol interactions are included in models." -> Cloud-aerosol interactions include more process than ice nucleation etc..

 

Small comments:

- The title of the paper is missleading, no modelling is presented.

- The formulas are inconsistent in terms of indices (Jhet should be Jimm, the t in Nxt is confusing because later on t is explained to be time...) and many variables are not clearly explained and or not give which formulas are used to calculate the variables (for example sigma_iw).

- Some expressions are not explained, such as onset temperature, HIN etc. - please check again your text carefully.

- line 15: you write here something about aerosol and gas phase, be more specific/precise in terms of the topic of this paper.

- line 17: more complicated in terms of what?

- line 18: INP = ice nucleating particle

- line 19: body? Better use droplet?

- line 20-21: Sometimes you speak of mechanism, sometimes of mode - be consistent.

- line 24: ... used an empirical...

- line 31: Be specific which uncertainties remain.

- line 32-68: pleace revise the text and explain the differences of different parameterisation schemes better and what the need is of a new scheme, such as yours. What is the motivation of the approach chosen in the paper? In what aspect is it different to existing schemes? Elaborate the differences.

- Table 1: What does mid-sample mean?

- line 107: Why "However"?

- line 121-128: This is not very clearly explained - revise.

- line 123: Space missing in between the number and units for the cooling rate.

- line 126: chapter 2 = section 2.

- line 130-131: What is meant with "results could be different...". If there is some uncertainty in the fit due to some characteristics of the data (comcentration, composition etc.) this should be discussed in more detail. It would be valuable to discuss the uncertainty of the presented parameterisation scheme due to the limitations of the field data used to derive it.

- line 133: Why is the log used - explain.

- Fig. 2: Please use the same unit for the parameterisations of theta(T) - does it make sense to compare exactly these to approaches?

- line 178-179/Fig. 2: The interpretation is going a bit too far here.

- Fig. 3: The colors for year 2014 and 2016 look quite similar.

- The Discussion and summary misses a dicsussion on limitations of the new scheme.

- line 171-173: The surface tension argument is a physical meaning?

- line 184-190: I don't understand the context/connection of this discussion to the content of the paper.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf