The Reviewers agree this manuscript is much improved. Two Reviewers suggest minor changes. I request the Authors please consider these changes, adapt the manuscript as necessary, and offer a short point by point response. The final acceptance will be by the Editor with no further review required.

Reviewer 2:
Suggestions for revision or reasons for rejection (will be published if the paper is accepted for final publication)
I would like to thank the authors for improving the quality of their manuscript and for clarifying many important points listed by all 4 reviewers. Although most on the points highlighted in my original review were addressed (mainly the specific comments), there are key points that need to be clarified before the manuscript can be accepted. The main points are listed below:

1. The addition of Table 1 with the fraction of doubly charged particles is very valuable. However, I am surprised there are not triply charged particles in the studied ash samples. Note that you provided the triply charged particle fraction in the answer to point #4 but they are not given in the Table 1. The authors did not provide the particle size distribution (PSD) of the 300 nm size selected particles as requested. I think this needs to be part of the main text. Note that the PSD should be in log scale to better identify the doubly and possibly triply charged particles.

2. It is really sad that the authors were not able to conduct the missing experiments. I think an effort in this direction could have been made by requesting an extension to submit the revised manuscript. “We decided to include the data, even without the chemical analysis, because we wanted to show that beech ash is comparable to the other wood bottom ashes.” Although it is true that it is nice to show that the ice nucleating abilities of beech ash and the wood bottom ashes are comparable, the reviewer does not see the point to add this data if the reasons of why beech ash particles behave similarly to the wood bottom ashes are not provided. I mean, is this observation simply a coincidence, or is it because the chemical composition, soluble material, and/or particle’s surface properties of both samples are really comparable?

3. The reviewer is not really satisfied with the answer given to this point: “Possibly, CaCO3 is the dominant phase of the water soluble fraction. During the combustion process, CaO is produced (present in the initial sample, see Fig. 1 and Table 3) which may react with H2O to form Ca(OH)2. CaCO3 may form from Ca(OH)2 upon reaction with CO2 from the air (Steenari et al., 1999). That we do not see any needles on the SEM image of spruce ash suspension particles (Fig. 2 (c)), even though this sample contains 11 % more CaO than the fly ash sample, is possibly due to the variety of different crystal shapes which CaCO3 is known to occur in and which include needles, hexagonal plates, and others (Kim et al., 2009). Particularly hexagonal plates might not be as easily distinguishable from the insoluble particles as the prominent needles and might be seen, at least to some extent, in Fig. 2 (c), where the resolution of the pictures unfortunately does not allow a better analysis.” The presence or absence of this large needle particles or small hexagonal plates after passing through the dryer needs to be better quantified given that they significantly change the size distribution of the particles entering the LACIS and hence the concentration and potentially the size of the cloud droplets. I think this points deserves a solid and clear explanation.

4. A good way to support the conclusion that the particles produced via the wet system are less efficient that those produced via the dry system will be adding the size distributions of the 300 nm (wet system) together with the size distribution of the dry system. In this figure readers will see how comparable the PSD are and what is the effect of multiple charges in the particles. The authors mentioned that the fraction of multiple charge particles is around 20% for the dry system and very low for the wet system. 20% is a large fraction and this can be the reason of why the dry particles showed a better ice nucleating efficiency. Is this 20% from the PSD obtained at the beginning of the experiment or at the end? The authors showed that the fraction of multiple charged particles increases with time.

5. Given that lack of data I think the following statement should be softened or the lack of data acknowledged: “There is a trend of beech bottom ash being the most effective”

6. “We revised this section in terms of citing more field observations of fly ash particles and calculating the in-stack concentration especially for the power-plant Lippendorf. Even though the section contains a lot of speculation, we would like to keep it in the manuscript. Firstly, we clearly state when we make a certain assumption and secondly we think that this estimate supports the relevance of the topic”. The reviewer considers that there is no need to keep this in the manuscript. It does not add anything valuable to the paper and it will confuse readers which are not very familiar with this topic/calculation.

Reviewer 3:
Suggestions for revision or reasons for rejection (will be published if the paper is accepted for final publication)
General comments:
I have two more comments regarding the BET calculations:
- First, the new left y-axis in Fig. 4 is dispensable from my point of view as it is the same as the right y-axis. The concern to compare the same metrics to each other is not addressed with this second y-axis. I agree that it might be too much to get the BET surface for your samples, however, since you did already an estimate of the conversion factor between your ns and the ns,BET provided by Umo et al. (2015), why don’t you use it in the plot? You could provide an uncertainty area around the curve. This would be more valuable than duplicating the y-axis.
- Second, for the calculation on P17,L24 the volume of the particles needs to be calculated, therefore the volume equivalent diameter needs to be used instead of the mobility diameter (Kulkarni 2011). You assumed a spherical shape and a mobility diameter of 300nm for your particles. The validy of using the mobility diameter depends on the shape factor of the ash particles. This is not considered in the calculations. From your manuscript I understand that for fly ash particles the assumption of sphericity seems to be valid. However, the SEM images do not support this assumption for the bottom ash particles. Please re-consider your calculations. This should be included in an uncertainty band around the curve in Fig.4

Technical comments:
- Delete “(a)” on p.13, first line of Figure 3 caption. The full circles are shown in all other subplots as well, not only in (a).

The authors have not made any changes to the manuscript, they have only answered the reviewers.

These points were returned in the second review as changes that were ignored in the first ; the reviewers specifically requested changes in the manuscript.

The manuscript will be reconsidered when the reviewer changes are addressed in the paper.

The authors have made the reviewer suggested changes or explained why they could not. As such this manuscript is now publishable at ACP.