The manuscript explores nitrogen cycling by natural airborne microbial communities using a combination of genetic and biogeochemical tools. Based on their data, the authors conclude that a significant fraction of the airborne microbial community has the potential to process organic and inorganic nitrogen compounds while airborne. Through rainwater incubations, they estimate the contribution of the community in processing these compounds, particularly for bio-assimilatory purposes. They conclude that while the contribution of the airborne microbial community to nitrogen cycling is insignificant on a global scale, it may be relevant for the survival of microbial cells while airborne.

Overall, I find the manuscript innovative and relevant to the field and recommend it for publication. However, I kindly ask the authors to address the following issues prior to publication:

1. Equation 4: I had difficulty understanding this equation and was unable to reconcile the units. I would appreciate it if the authors could explain the equation in more detail and provide an example in the text showing how they performed the calculations.
2. It is fascinating that the authors were able to determine transcripts in the clear sky samples. What was the relative humidity and how does that fit with what has been reported in the literature for microbical acitivity in relation to RH? I wonder if these transcripts could have been produced prior to aerosolization and preserved in the airborne state due to cell inactivity, which would include the turnover of the transcripts. Could the authors exclude this possibility and discuss the consequences for their interpretation?
3. Denitrification is a process that occurs under oxygen-limited or anoxic conditions, where it replaces aerobic respiration. Do the authors have any indications that oxygen is limited for the cells while they are airborne? If so, why would the cells denitrify instead of using oxygen?
4. Nitrogen fixation is an energetically costly process that microbes typically use only when other nitrogen sources are unavailable. This does not seem to be the case in the samples analyzed by the authors. Why would the cells rely on N2 fixation when other nitrogen sources are plentiful?
5. The authors suggest anoxygenic phototrophs as possible candidates for N2 fixation. What would these microbes use as electron donors for N2 fixation while airborne? Many of them depend on reduced sulfur compounds or hydrogen. Are these valid sources in this context?
6. The rainwater incubations lasted for several days. However, in the atmosphere, the retention time of microbes in rain droplets is much shorter. I would appreciate it if the authors could discuss the relevance of their estimates based on these long-term incubations.
7. Lastly, I would appreciate a detailed discussion of Figure 5 (PCA plot) that summarizes the results.

I hope these comments and questions help strengthen the manuscript further. I look forward to your revisions.

In the manuscript by Mathonat et al., the authors describe the potential contribution of airborne microorganisms to nitrogen cycling by combining reanalysis of meta-G and meta-T datasets with laboratory exploration of bacterial isolates and rainwater incubation experiments. Overall, this provides valuable and interesting insights into the potential activity of these microbes under humid conditions. However, several concerns regarding the experimental design, data integration, and interpretation of results arise and should be addressed before the manuscript is accepted, as detailed below.

• The study showed that cloud water samples did not demonstrate enhanced gene abundance (Fig. 1A) or expression levels (Fig. 1B) compared to clear atmosphere samples. The data also show that nitrogen processing genes are less abundant in clouds than in clear atmosphere, and RNA:DNA ratios are also lower in clouds. What does it means? This should be addressed in the discussion of why cloud environments were not enriched in the expected microbial activity. In line 422 the author argue that it is due to higher N2 abundance in open atmosphere. But other factors may also lead to these results, and should be acknowledged/discussed, such as methodological difference in sampling approach, the volume of air sampled for open air and for possible scavenged ones due to rain washdown. 
• The reported RNA:DNA ratios for genes with abundances close to zero in the Meta-G and Meta-T (Fig. 1C) are problematic and may represent mathematical artifacts rather than biologically meaningful expression levels. When the DNA abundance approaches zero, even minimal RNA detection yields inflated ratios that are statistically unstable and probably lack biological relevance. For example, genes with <0.1 ppm bp in the metagenome could show high RNA:DNA ratios purely due to noise in the measurements, not genuine transcriptional activity. therefore, it is recommended to establish a minimum abundance threshold below which RNA:DNA ratios should not be calculated or interpreted.
• On the same line- I have doubts regarding the nitrification taxa presented in Fig. 2. These genes show extremely low values in both MG and MT in Fig. 1 (<1% of nitrogen-related reads), yet Fig. 2 presents detailed phylum and order-level taxonomic breakdowns for these barely detectable genes. And it is most noted for the cloud water MT samples, presenting 100% abundance of Acidobacteriota at the phylum level, and 100% Cytophagales at the order level (which belongs to the Bacteroidota phylum). Can the author explain this discrepancy? My suspected idea is that it results from the low gene abundance and thus outliers may dominant your data.
• The detection of anammox-related genes and transcripts is surprising, as anammox bacteria are obligate anaerobes. Could the authors discuss potential explanations for this observation? Clarification on whether the RNA:DNA ratios for anammox genes suggest active expression or baseline transcription would help interpret whether these organisms are potentially active in atmospheric conditions or simply represent transported but inactive populations.
• The bacterial strains screened for the nifH gene were pre-selected to include 34 known nitrogen-fixing taxa (e.g., Pseudomonadales, Sphingomonadales). This targeted selection can introduce positive bias, making the finding that 15% of tested strains were nifH-positive potentially unrepresentative of the broader rainwater bacterial population. What is the total number of rain-borne isolated bacteria? The authors should clarify whether this 15% reflects the prevalence among all culturable cloud bacteria or only among pre-selected candidate taxa, and be careful about extrapolating this percentage to the entire atmospheric microbial community without appropriate caveats (see e.g., line 434 in the discussion).
• In Table 3 it is shown that the amoA gene remained below the detection limit even after incubation, including in samples showing the highest ammonium reduction in Fig 4 (20230922-RAIN-TF). If ammonium oxidation (nitrification) were responsible for the observed ammonium loss, it would be expected that amoA gene abundance would increase during incubation as ammonia-oxidizing bacteria proliferated. This absence of amoA suggests that ammonium depletion may have occurred through alternative pathways rather than nitrification? A direct examination of the expressed genes through RNA analysis (either RT-PCR to measure selected expressed genes, or RNA-seq to directly explore the activity of nitrification genes during ammonium removal) would dramatically enhance your findings. The presented results provide weak support for the proposed nitrification activity.
• While the authors rightly use broader terminology such as "atmospheric microorganisms" and "airborne microbial communities" in the discussion and acknowledge that nitrogen transformations can occur in clear atmosphere conditions, they do not adequately address this fundamental distinction throughout the manuscript. They extrapolate results "to cloud environments based on rainwater data" and make claims about processes occurring "in clouds" without clarifying whether they are studying indigenous cloud-resident microbes or rain-scavenged airborne populations. The terminology and interpretations throughout the manuscript should be revised to consistently refer to "airborne scavenged microbes," "rain-deposited atmospheric microbes," or "atmospherically transported microbes" rather than implying a distinct "cloud-borne community," as the experimental design does not adequately distinguish between these fundamentally different microbial sources.
• The rainwater incubation conditions are acknowledged as a limitation (particularly the relatively high temperature compared to actual cloud conditions). This also affects the implications, which are at present understated. Incubation at 17°C would likely accelerate microbial growth and metabolism above natural rates, and continuous shaking, and 5-day duration do not reflect the transient, episodic nature of cloud events (range of hours). These conditions may fundamentally alter community dynamics, succession, and biogeochemical rates, making the measured bioassimilation rates weak proxies for actual atmospheric processes. Authors may explore the option of the cloud transition zone: the between cloud and open atmosphere region, which studies imply is at near saturated humidity, and with a wide atmospheric coverage than previously estimated. The present study may indicate this region might be optimal to bacterial activity, as it should be with longer atmospheric duration, and higher temperatures than in the clouds. 
• In line 393, the global estimates for ammonium processing (5.5×10⁷ kg year⁻¹) and in line 412, nitrate transformation (2×10⁷ kg year⁻¹) are derived by extrapolating the average bioassimilation rates measured in the 17 °C rainwater incubations to the total estimated airborne biomass and assuming a 15% cloud fraction. This calculation chain seems to contain multiple uncertainties: (a) laboratory rates that likely overestimate natural rates (difference in incubation and ambient temp, and thus growth rate, incubation time, etc.), (b) extrapolation from a single location to the entire atmosphere, (c) uncertain estimates of global airborne biomass, and (d) the assumption that all cloud-associated bacteria exhibit similar metabolic activity regardless of cloud type (or open atmosphere), altitude, RH, temp, or geographic location. A supported/convincing estimate should include sensitivity analyses to provide uncertainty ranges for these global estimates. In addition, a comparison with other independent estimates (from e.g., atmospheric chemistry models) would strengthen yours.
•  The statistical description in the methodology section is lacking. Authors should expand and describe all tests selected in the analysis of the data. 
• In Figure 5, authors should clarify the significance of the impacting vectors. Significant ones can be marked with asterisks next to them, and please note the statistical tests used in the caption (as well as in the methodology...)
• Did the author conduct rRNA depletion prior to meta-T sequencing? I couldn't find this information in the methodology, nor in the referenced paper by Péguilhan et al. (2025). Since ribosomal RNA typically comprises the majority of total RNA in microbial samples, information on rRNA removal would be helpful for understanding the meta-T data processing workflow.
• The manuscript discusses Fig. 1A and 1C but doesn't mention Fig. 1B. Please check and correct.
• In Figure 1 the nitrogen processing genes are not presented in the same order across panels A, B, and C. This can confuse and possibly mislead readers, making it harder to compare panels and understand the relationships between gene abundance, expression, and activity.
• In addition, the presentation of panel C as bar charts can be improved, as the ratios are not cumulative based on 0, but rather based on 1. Consider changing to a box plot or dots, and keeping open atmosphere and cloud samples in the same direction (upwards) to make comparison easier.