The manuscript by Brasseur et al focusses on the vertical distribution of INP over boreal forest in Finland and has been carried out by aircraft measurements during spring 2018 above Hyytiälä. The manuscript is well-written and includes new and important data. The topic is important for atmospheric scientists and might be published in ACP after some minor corrections.

Comments:

Introduction: The topic has been well introduced and the relevant new literature has been cited. However, the authors might mention their own paper Vogel et al. which is under discussion as well. Also, the older literature at similar locations deserves attention (e.g. Prenni 2013). The authors mention the ice nucleation temperature of desert dust being below -15°C but I miss a statement regarding the biological INPs and INMs which are below -2°C depending on the origin. In this regards the authors might also mention that dust could be a carrier, coated with bio INMs, which turns them into bio INPs.

Methods: The description is very detailed. However, I have remarks regarding the figures:

Figure 1a: The map is very pale and the scripts are small. I would recommend to add a general map where the location on the European continent is documented.

Figure 2: The color code is missing. The x-axis might be labeled “day time” or “position of the sun”

Results: Figure 3: Please explain the calculation of the TKE dissipation rate from the Doppler lidar in more detail.

Figure 5a: add ticks on the y-axis for every order of magnitude.

Figure 6a: add a size bar, explain the color code in more detail

Figure 7: add ticks on the x- and y-axes for every order of magnitude

Figure 11a and b: add size bar. Better explain PES.

Conclusion: The conclusion reads more like a summary. I miss a real discussion and conclusion from the results along these questions: What do we learn regarding the emission of INP and their transport from the forest ecosystem, above canopy, into the free troposphere? Can you speculate about the transport mechanisms? How do wind and humidity influence these potential processes?

References

Prenni, A. J., Tobo, Y., Garcia, E., DeMott, P. J., Huffman, J. A., McCluskey, C. S., ... & Pöschl, U. (2013). The impact of rain on ice nuclei populations at a forested site in Colorado. Geophysical Research Letters, 40(1), 227-231.

The “Vertical distribution of ice nucleating particles over the boreal forest of Hyytiälä, Finland” by Brasseur et al. is an interesting study investigating how INPs vary with height in a region that could release a lot of INPs and is understudied. Aircraft measurements of INPs are particularly useful, because the majority of studies are ground-based and thus cannot usually provide measurements at the heights where clouds can form. The authors present both INP and aerosol data from several flights, which they use to normalize the spectra for insight into vertical efficiency. I especially thought the case study section was strong and gave convincing evidence for the possibility of periodic transport from the surface to the free troposphere but that most of the time it is different. It would be most interesting to investigate further (in the future) the potential mechanisms for the transport.

Despite the positives of this work, there are several things I believe can be improved upon, both in the figures and text. The main things I note are being clearer about the blank corrections, as they matter significantly for the free tropospheric samples; being extremely careful about not overstating claims: I don’t think some of the conclusions are supported by the data presented (as worded). This happens throughout the manuscript. I also thought the number of studies for comparing to previous work could be improved. In general, I think the manuscript reads too long, and could be tightened to improve its readability. I fully intend and hope my comments are helpful for the coauthors and offer a useful perspective. I would recommend it for publication, but only after these comments are given consideration and the claims in the text are represented better.

Specific comments:

Introduction: Should add Levin et al. (2019) as they made vertical measurements of INPs from the surface to free troposphere over California, for comparison. They found increased concentration with height.

Levin, E. J. T., DeMott, P. J., Suski, K. J., Boose, Y., Hill, T. C. J., McCluskey, C. S., Schill, G. P., Rocci, K., AlMashat, H., Kristensen, L. J., Cornwell, G. C., Prather, K. A., Tomlinson, J. M., Mei, F., Hubbe, J., Pekour, M. S., Sullivan, R. J., Leung, L. R., and Kreidenweis, S. M.: Characteristics of ice nucleating particles in and around California winter storms, J. Geophys. Res.-Atmos., 124, 11530–11551, https://doi.org/10.1029/2019JD030831, 2019.

Lines 103-112: Much of this should go in the methods and is distracting from the main message of the introduction.

Figure 1a: Map is hard to read, but I like the colored flight track. Can you improve the resolution (and maybe spatial extent)?

Line 160: A place with the basics of filter collection is needed: how many of each locational type were collected?

Line 162: Please specify the length of soaking in 10% H₂O₂ and number of water rinses

Line 193/Figure A1: Were the blank samples corrected in INPs/mL suspension space? I don’t think that is the unit you want to correct in if your ground samples were resuspended in 8 mL and boundary layer/free troposphere samples were resuspended in 5 mL, as that number is a function of resuspension volume. I think it is necessary to correct in total INPs/filter (multiply by resuspension volume), unless some blanks were resuspended in 8 mL to correct for the ground samples, and other blanks were resuspended in 5 mL. However, if everything was resuspended in 5 mL for your data, it would be ok and please make that clearer.

It would be helpful to indicate on Figure A1 which samples you ignored from being within your threshold, and you could also indicate in the text the percentage of filters you were able to keep. In the text, I would suggest providing more detail about the background corrections, and not only refer to previous literature (even though I know it is a related study). The reason is that often free troposphere/boundary layer airborne filters as you know are very close to the limit of detection, and so blanks can play a very big role in the answers and thus the conclusions that are drawn. Additional questions that I have, for example, are did you average the blanks and create a regression to subtract? For the samples that you adjusted because they were within a factor of two of the blanks, were you able to keep some points or did you remove the entire spectra? It would be great to indicate the points on a plot (Figure A1 for example) that were measured on the INSEKT but did not pass your criteria. I think it would be worthwhile to spend time to make this clearer. I think the criteria is acceptable, but at this point it is not repeatable.

Figure 2: This is a very nice figure and is helpful to a general audience.

Paragraph beginning with Line 302: The ice onset is not helpful here because as you state, the volumes are very different. I would remove it, or if you keep it in, also qualify the free troposphere portion at the end as the volumes were the shortest (I understood 7 LPM for 1 hour average).

Figure 4: I would suggest you have a criteria for plotting/not plotting the histograms (at the cold end) based on the number of observations (e.g. >50%). I understand and appreciate you including the number of observations, but as most apparent in the ground histograms, the colder observations will be biased low based upon the more concentrated samples needing more dilution.

Lines 334-337: The fact that the activated fraction brings the free troposphere closer to the rest of the observations than INP concentrations alone, would there be an argument for that making them more efficient (relatively speaking: still “less efficient” overall) as now some of the histograms overlap (especially with the previous study) over the range with many observations? It is unexpected to me that they are closer, and is an important finding to highlight more, even if it is not within the main message of the paper.

Line 376-379: How do you reconcile the similarity of the activated fractions of the free troposphere to the Schneider et al. study (especially below -20) with this statement? INP concentration speaking, I agree with your statement. Lines 382-383 are affected as well.

Paragraph starting with Line 417: This paragraph is wordy and doesn’t really present anything new. A point of needing more samples would be sufficient in the conclusions. I would suggest to trim/remove this. I do like the HYSPLIT analysis in this general section.

Line 444: Define CFDC at first use

Lines 447-450: There is not a sufficient explanation on why the aircraft OPS data was not used for all aircraft samples, even if you are assuming the air is similar enough. I would at least include that representation in the supplemental information for transparency, maybe as an additional figure or column. Were the percentages any different?

Line 476: I think successfully is too strong of a word here. I agree that it performs the best out of all tested parameterizations (which is a nice finding of your study), but you need to take care to qualify and not overstate your conclusion. It’s possible that another parameterization out there may fit your data better. The fit line shows the limitations.

Line 482: This is another sentence that needs qualifying. Yes, strictly speaking, based upon the factor of 5 and 2 percentage of points (which come with uncertainty as INP measurements have large error bars), the parameterization works better for the boundary layer. But visually, comparing Figure 7a and 7b, they look similar. Your statement “Thus the Schneider et al. (2021) parameterization can successfully represent the well-mixed boundary layer, but not the more remote free troposphere where INPs can be more scarce and originate from distant sources,” is not convincing to me as the percentages and fit slopes are too similar to warrant a statement this strong. The word “successfully” appears again in the conclusions and abstract.

Line 526: The onset difference here mostly looks related to limit of detection.

Figure 8: I think it would be helpful to indicate which studies are from what zone: ground, boundary layer, or free troposphere. This could either be accomplished in the legend with text or by grouping markers in the figure. It is confusing the way it is presented both in the figure and in the text right now. You could also trim the cold end to make the measurements easier to read, as few of yours go much colder than -25 °C. Adding an additional or two free troposphere study would also add value, as it seems that portion is lacking. This would help strengthen or potentially modify your statement in Line 541 saying the free tropospheric measurements fall within the same range as previous measurements. It would be insightful to compare how the free troposphere stacks against other free troposphere studies. Some that may be of use (both ground/airborne studies) would be Conen et al. (2022: https://acp.copernicus.org/articles/22/3433/2022/acp-22-3433-2022.html) Lacher et al. (2018: https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2018JD028338) Barry et al. (2021: https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2020JD033752), in addition to the Levin et al. (2019) study I mentioned previously. You don’t need to add all of these studies, I just think that it would bolster your figure/argument.

Lines 557-559: Is it possible the water negatives were high in this particular sample, thus causing the gap between sample and negative to be too low, causing this junction? Sometimes you can just get unlucky and could also be physical if certain INPs are being inactivated in large volumes of dilution water. The shorter sampling time reason doesn’t make a lot of sense, and you should be able to limit particle settling by resuspending the sample before dispensing. Ideally, I would suggest to rerun this sample because it is a part of your case study (maybe pick a lower level of dilution). If there isn’t much sample left, you could just run the dilution. However, maybe there isn’t any sample left in which case there’s nothing you can do. In any case, I would remove the bit about shorter sampling time, because clearly you are still able to get detection to almost -15 °C.

Section 3.7 General: Overall, I think the case study portion is well done and provides evidence at different angles. I really like the potential cloud processing depletion signal. The only caveat to this section I would mention is that just because the aerosol responds in a certain way doesn’t mean the INP, a very small fraction of the total, will respond the same.­

Lines 628-629 and Figure 11c: I am not familiar with FLEXPART, but how certain can you be that there was little time below 200 m if the vertical resolution is 250 m? I say this because the lowest level seems to have an unexpected stripe with little variation. Could this be an artifact? It seems odd to me that there would be little surface influence the whole way. Again, I am no expert here, just pointing out an observation.

Line 630: The way it is written is confusing, I think it would be more correct to say that the air spent time in a particular layer.

Conclusions: I think this section can be trimmed down and focused: it is lengthy and carries over some of the issues I noted in the main text.

Lines 669-672: I don’t agree that you would need longer sampling times in order to do treatments on the suspensions: even 5 mL should give enough leftover volume to do one treatment and could be informative especially on some of your higher signal samples here. Definitely it would not be worthwhile for all of them, since some of them are near the negatives. It would be a good way to confirm the particles are similar with previous work. If you want to leave it for future work, that is fine, but I would suggest to remove/revise the explanation given.