This manuscript is based on a wealth of data obtained with a range of scientifically sound methods. It shows how meltwater from terrestrial surfaces increases the abundance and modifies the composition of INPs in a Greenlandic fjord at a particular time of the year. The evidence leading to this insight convincingly unfolds throughout the manuscript. There is little I can suggest to further improve this well written manuscript.

Figure 1: Perhaps add photographs of the sites, so the reader gets an impression of the surroundings in which the samples were collected.

Section 3.2 discusses differences between SML and SBW in terms of INPs. Lines 276-279 state: "In addition, our study revealed enhanced INP-10 concentrations in the SML compared to the corresponding SBW samples (Fig. 3b). This finding aligns with observations by Wilson et al. (2015) and Hartmann et al. (2021), whereas Irish et al. (2017) observed no significant upconcentration of INPs in the SML." Yet, a closer look at Figure 3b reveals that one third of the samples does not show an upconcentration. So, better qualify the cited statement.

Can you extrapolate the trendlines in Figure 7b to get a rough estimate of what INP concentration might be in pure meteoric water (fMW = 1.0)? This number would allow for a more quantitative comparisons with INP concentration in other freshwaters discussed in lines 480-487.

General Comments:

Wieber et al. highlight a possible importance of terrestrial runoff as a source of biological ice nucleating particles (INPs) based on the measurements in two southwest Greenlandic fjords for the period between June and September 2018. Although the INP data are limited to a narrow temperature regime above about -14 degree C, it seems that the samples in June contained highly active INPs compared with those in July and September, and this result is potentially unique. For example, the results of freezing experiments before and after filtration (Fig. 4) and heat treatments (Fig. 5) indicate that the INP properties for the samples in June 2018 were somewhat different from those in July and September 2018. However, I would have to say that explanations related to the main conclusions of this work have several fatal flaws (see the following specific comments). Thus, I cannot recommend the publication in Atmospheric Chemistry and Physics.

Specific Comments:

1)    The authors propose two alternate explanations for the seasonal variations in INP properties proposed by the authors (Lines 382-393). The first explanation is that INPs in June may have been released by pollen, fungal spores, or lichen in terrestrial environments and transported into the seawater by streams. On the other hand, based on the analysis of the eukaryotic community derived from 18S rRNA data (Figs. S4, S5, and S8-S11, and Table S1), the authors suggest that fewer organisms exhibit correlations with INPs active at -10 degree C, and these correlations are weak (Lines 407-408). I think that there is a discrepancy between the first explanation and the 18S rRNA data. Why did the authors lead to the above first explanation?

2)    The authors propose two alternate explanations for the seasonal variations in INP properties proposed by the authors (Lines 382-393). On the other hand, according to explanations related to the analysis of the bacterial community derived from 16S rRNA data (Figs. S6, S7, S12, and S13, and Table S2), it seems that certain mechanisms related to the bacterial community are more important than those related to the eukaryotic community for the seasonal variations in INP properties. Why did the authors exclude the possible contribution of the mechanisms related to the bacterial community from the two explanations?

3)    I strongly suggest that the authors perform additional analyses and discuss the possible relationship between the variation of the bacterial communities derived from 16S rRNA data and terrestrial runoff. In particular, the authors should compare the bacterial communities found in the sea water samples with those in terrestrial and marine sources, and then evaluate whether the bacterial communities found in the June sea water  samples were indeed characterized by terrestrial runoff. In addition, the authors should give more detailed explanations for the reason why the authors focused on the relation between only three taxa (Aquaspirillum arcticum, Colwellia sp., and SUP05) and a high concentration of INPs active at -10 degree C (Lines 431-446) and ignored other taxa.

4)    Although the authors explain that “we found a strong negative correlation between salinity and the concentration of INPs active at -10 degree C with significantly lower salinity but higher concentration of INPs observed in June (Fig. 7a) and these correlations suggest a strong impact of salinity within the observed fjords, pointing towards terrestrial runoff or melting sea ice as input of freshwater and potentially INPs (Lines 427-430)”, I doubt if there is a possibility that this is a result from the depression of the freezing point caused by salinity. If the authors believe that a negative correlation between salinity and INP abundance suggests freshwater input as sources of INPs (Line 25-26), they should provide evidence that this negative correlation was not caused by the depression of the freezing point.