General comments:

The authors heated 20 samples of minerals (K-feldspar, plagioclase feldspar, quartz, clay, dust surrogate and carbonate) as well as 4 samples of biological material (Snowmax, lichen, birch pollen washing water and cellulose) using two different heat test procedures. The first was a wet heat test where the samples were submerged in a bath of boiling water and the second was a dry heat test at 250 °C in an oven for 4h. The authors then measured the samples before and after the two types of heat tests and display their results as frozen fractions, as box plots and as n_s plots. The authors then have rather long discussions of speculations (the word assume/assumption is found at least 10 times in the manuscript, at times justified and at times not, when the assumption could be resolved with further experiments). They speculate about what could have driven the differences before and after heat for the different heat tests and for the different types of samples. In general, the authors reference the literature adequately and thoroughly.

The research question is certainly worthwhile, and the authors’ systematic approach is a good idea for evaluating the general applicability and the interpretation of a change in INA after a heat test. I commend the authors for approaching this problem systematically. However, this manuscript is currently too preliminary to be published. This study can be made significantly stronger to make an impact on the community and for the work to be built upon in the future. My key recommendations to improve the study before publication are below:

1. (most important recommendation) The authors are missing key experiments for further conclusions to be drawn. Specifically, the authors should run all 20 mineral and all 4 biological samples in a comparable dry heat test at 95 °C in an oven for 30 mins (or the same amount of time the sample was submerged in the water bath). This test is necessary, since the authors make many assumptions of what can be the cause of inconsistencies between their wet heat test and their dry heat test. Yet, comparisons have 3 variables being changed in both sets of heat tests: the method, the temperature and the time of heating. I would also encourage the authors to consider re-runing their dry heat test at 30 mins (or running all their heat tests at 4h), which would add additional columns in Table 3. These additional experiments would really strengthen the systematic approach that the authors are attempting to present in this work. Right now I am left wondering what is the effect of wet vs dry and what is the effect of temperature and what is the effect of heating time?

2. Furthermore, there are important background water tests missing in this manuscript. The authors should address these details thoroughly before publication. In general, daily blank tests discussed in lines 261-262 are not experiment controls, and do not represent adequately the experimental procedure each sample is submitted to. The authors use 0.1 μm pre-filtered, cell culture-grade deionised water, and could the authors show the following background water data:

1. A sample of background water that was heated in the same type of vial as with the wet heat test (line 208).
2. A sample of background water that was heated in the oven at 95 °C in an oven for 30 mins.
3. A sample of background water that was passed through the same experimental procedure following the sample after heating at 250 °C in an oven for 4h.
4. A sample of background water that passed through the nylon net filter and the cellulose acetate filters (referred to in line 192). I highly suspect that cellulose acetate filters leach material. These control frozen fractions must be shown.
5. Show the data discussed in lines 221-224.
6. What is the role of the pre-sterilized dry heating at a different temperature? Shouldn’t the procedure also involve the same 250 °C temperature as the experiment?

3. The wet heat test will certainly have the water evaporate and therefore change the concentration of the material within the solution. How are the authors accounting for changed in concentration of the ice active material? relevant to the discussion in lines 145-147.

4. The authors should make every effort to compliment the study with alternative measurements. I can appreciate that substantially more work would be required, but it would allow the manuscript to be much more concise rather than listing a list of speculations (for example, the K-fledpsar discussion spans pages 11-14 of speculations). For example, ideas presented in lines 365-377 could be address with elemental analysis and presence of N. Or with a protein test such as the Lowry method. Ideas in lines 368-370 could be tested with a heat test at the same temperature as the wet test (see my point number 1). In addition, total mass of the material after both heat tests can be weighed and measured (assuming the wet heat test and be dried out). Have the authors attempted to dry their material and repeat the heat tests multiple times? Does a wet heat test followed by a dry heat test and vice versa have any effect? Evidence of chemical composition would also be particularly helpful, for example total organic carbon analysis, ion chromatography, elemental analysis, etc. I’ll add here that my criticism is also a general one to our community where we tend to only show INA of material when these results cannot simply be compared without other measurements (such as surface area and/or composition). Finally, point d) at lines 719-725, I would recommend that the authors either don’t discuss it, or do the experiments.

5. The authors should further describe their detailed storage protocols. These protocols come up a few times as excuses for differences but should be detailed to teach the community exactly what was done. (Examples include Line 166, 195 and 201). I’ll also add that the authors’ justification on lines 234-235 is very good.

6. The authors use a high concentration of material (stated as 20 mg/mL on line 190). Are the authors working with suspensions or homogeneous solutions (line 230)? This fact is important since after heating, material’s solubility can substantially be affected. How have the authors addressed a possible change in solubility before and after their heat tests? What is the effect of concentration on the heat test? I think a series with one type of mineral sample with different concentrations for both heat tests would be an interesting series to present.

7. Can the authors show what the role of the time during the heat test can have? This information would be particularly helpful to determine and optimal temperature and time of heating for subsequent experiments by the community (and will be better cited).

8. Have the authors attempted to combine one of their mineral samples with one of their biological samples? This test would better represent an ambient measurement and see if the effect is cumulative or not (see (Steinke et al., 2020)).

9. References: In general, Table S1 could be included in the main test as a reader-friendly reference guide for future work to compare and built upon. Good job to the authors for this compilation - although mentioned in the text, did the authors want to also include (Bogler and Borduas-Dedekind, 2020) in their table S1?

10. Title: Seems to me that the second part of the title is most relevant to the content of the work. I can encourage the authors to consider a title along the lines: Testing (or systematic evaluation) of the heat test for ice-nucleating ability of minerals and biological materials.

11. The introduction can be substantially shorted to focus only on the heat tests experiments listed in Table S1.

12. Following all these comments and suggestions, can the authors create a recommendation rubric for heat test measurements: type (wet vs dry), temperature, length of time, with the ultimate goal to streamline how our community runs these heat tests in the future (including with and without hydrogen peroxide as some groups have done.)

I’ll just add a comment here to the authors, that I am very conscious of the additional efforts being requested for the revisions of this paper. Nonetheless, I think the authors and readers (including myself) would greatly benefit from the study being expanded in its conclusions and implications of the heat tests. I hope the authors will be encouraged to improve their work and go those extra steps further for the benefit of our community.

Refs in this review:

Bogler, S. and Borduas-Dedekind, N.: Lignin’s ability to nucleate ice via immersion freezing and its stability towards physicochemical treatments and atmospheric processing, Atmospheric Chem. Phys., 20, 14509–14522, https://doi.org/10.5194/acp-20-14509-2020, 2020.

Steinke, I., Hiranuma, N., Funk, R., Höhler, K., Tüllmann, N., Umo, N. S., Weidler, P. G., Möhler, O., and Leisner, T.: Complex plant-derived organic aerosol as ice-nucleating particles – more than the sums of their parts?, Atmospheric Chem. Phys., 20, 11387–11397, https://doi.org/10.5194/acp-20-11387-2020, 2020.

The authors investigated the responses of heat treatments (namely dry- and wet-) on different types of atmospheric ice-nucleating particle (INP) proxies using their offline cold stage instrument. Based on their findings, they made some technical recommendations regarding the offline heat treatment study of INPs (L695-725). The study objective and hypotheses are valid.  The reviewer generally agrees that different ice-nucleating materials respond to heating in various ways (e.g., L576 etc.). The authors’ messages are clear (L639-640; L643-645) while some explanations sound speculative. The reviewer has some major and minor comments. Some re-organizations of sections seem necessary to improve the readability.

Major comments

Proteinaceous structures can be destroyed below boiling temperature (Steinke et al., 2016). For example, Szyrmer and Zawadzki (1997) found some known cell-free IN-active microbes (e.g., Fusarium nuclei) are stable only up to 60 °C. Other studies of IN active bacteria, fungi, and lichens have shown heat sensitivity at lower than 100 ^oC. The reviewer is missing the detailed discussion of what protein is (and what is not) denatured in different temperature ranges. It is somewhat temperature-dependent and perhaps employing ~ 80 °C for 10-30 min (i.e., Fig. A2) may be comparable to using truly boiling temperature for heat treatment? What is the minimum time for proteins to be denatured?

Fig. 1 and all associated discussions fit better in the results & discussion section rather than the materials & method section.

L338-358 & L466-467 & L478-479: Hydrolysis and dry-heating likely alter SSA and other physical properties of materials, which impact their ice nucleation abilities. Reporting SSAs of a subset of materials after wet- and dry-heating would clarify the authors’ hypothesis given in these parts and strengthen the paper. Unless the authors can directly quantify the loss of active sites and/or the number of denatured proteins by a set of heat treatments, some arguments seemingly remain speculative.  

Sect. 2.3.2: The choice of 250 dC for dry-heating seems appropriate, but if the authors wish to do the apples-to-apples comparison of wet-heating vs. dry-heating, wouldn't it make more sense to use the same heating temperature and period for both heating methods? The authors state that “The dry heat test is a harsher treatment than wet heating…” in L369-370. Do the authors think the measurements with multi-temperatures could be a better procedure in dry heat tests (e.g., 100 dC vs. 250 dC etc.)? Perhaps, Amazonite microcline may have a different response to dry heat at 100 dC? SSA may be changing depending on the employed heat temperature?

The snapshot example of quartz in Fig. A1 is very nice. The reviewer wishes to see a similar dataset for wet-heat stable compounds (e.g., kaolinite and MCC). Does a similar trend hold for non-quartz samples?

Sect. 2.2.: The used suspension concentration of 1% w/v for MCC etc. seems to exceed what is recommended in previous literature (e.g., Sect. 3.1. in Hiranuma et al., 2019). What is the rationale behind such a high concentration? Wouldn’t such a high concentration cause some issues (e.g., flocculation of suspended particles)? How do these high concentration n_s spectra compare to previous studies? The reviewer sees the K-feldspar reference spectrum in Fig. 2 but not for other materials the authors examined for this study.

L648-670: Indistinguishable by the heat reaction itself but complementary mineralogy and composition analyses can distinguish these two populations. Do the authors intend to argue the applicability of heating on environmental samples (i.e., the mixture of different compositions)?

L755-756: The reviewer thinks that online heating (i.e., INP measurement with a heating inlet etc.) could be a good alternative approach for the quantitative test. Perhaps, the offline heating tests can be done with a set of different temperatures? Include these points in P25 (a), (b), and (d)?

Minor comments

What is the minimum detection limit of evaluation ice nucleation ability and/or efficiency of the cold stage for this study?

L25-28: This sentence makes sense without the last few words (“, so long as … K-feldspar”). This part sounds speculative. The reviewer suggests removing this part from the abstract. The importance of K-feldspar as an INP seems not the main focus of this study.

L57-59: Adding a discussion of the emission rates and atmospheric abundances of mineral dust and biogenic INPs might make this paragraph even more meaningful. Please consider providing some information to the reader. 

L67-70: Tobo et al. (2019) shows soil dust has some contributions to it, too. This can be briefly discussed here?

L287-293: Repetitive, and this part does not fit in the results and discussion section.

L295-303: Better fits in the materials & method section.

L307-307 & L316-318: The authors can introduce a brief statement to guide the reader where the explanation of the observed results is given later in this section (L349-).

L326-336: Fits better in the intro section.

L399-403: Fits better in the materials and methods section.

L405: Quartz presented before feldspar in Fig. 3a. Fig. 3b is not discussed until Page 17. The arrangement of Fig. and sub-sections seems a bit odd.

L430-431: Sounds speculative.

L433-455: Fits better in the materials and methods.

L504-521: Fits better in the materials and method section or SI.

L549-558: Fits better in the materials and method section or SI.

L596-598: Fits better in the materials and method section or SI.

L684-691: Sounds speculative

L739-741: Showing the altered specific surface after wet heating can be more direct evidence. Accounting a different SSA may explain the alternation in IN ability of the material?

Fig. S1: The axis text/numbers and legends are too small to see.

Fig. S3: Is this ns plot generated using the FF spectra data in Fig. S1(u)? It seems that Fig. S3 is missing the point above -12 dC for a non-treated sample. Or the authors did another set of measurements for generating Fig. S3? Please clarify.

Technical comments

L3: Murray1¹

L30: à the absence of ice nucleation active sites,

L39 our models à atmospheric models

L56: 2015b comes before 2015a

L63: ice active à ice nucleation active

L63-66: How small & how great? The reviewer suggests that the authors provide some quantitative information to the reader in this paragraph.

L82: à characterize the ice-nucleating activity of

L84: à known bacterial, fungal, and archaeal

L250-274: “A” should be defined in L251, or the authors can introduce Eqn. 2 in L273.

L306: after a closing-parenthesis change “,” to “.”.

L409: ))

L770: 1 mL or 1.5 mL? One figure says 1.5. What is the vendor and model number of the tube?

References

Steinke, I. et al.: J. Geophys. Res.-Atmos., 121, 13559–13576, 2016.

Szyrmer, W. and Zawadzki, I.: A review. Bull. Am. Meteorol. Soc. 78, 209–228, 1997.

Hiranuma, N., et al.: Atmos. Chem. Phys., 19, 4823–4849, 2019.

Tobo, Y. et al.: Nature Geoscience, 12, 253–258, 2019.