In this work, Ringsdorf et al. describe atmospheric measurements of carbonyl containing OVOCs in the Amazon Rainforest using PTR-ToF-MS and NO⁺ CIMS. The use of PTR-ToF-MS and reagent switching enables differentiation between ketones and aldehydes which in turn enables the determination of their atmospheric fate, including reactivity and dry deposition. This includes vertically resolved measurements at 80-325 m of multiple species.

The paper exploits reagent ion switching to obtain information about ketones and aldehydes separately which is relatively novel.

The OVOC behavior described in this article is consistent with previous data, so although the measurements are somewhat novel there are no significant new conclusions.

The methods are described thoroughly, including calibrations or sensitivity estimates as well as possible interferences from isomers or decomposition of other species such as peroxides.

The authors do a very good job in contextualizing the measurements of each individual OVOC being reported. They cite the literature extensively and pose multiple hypotheses for observed diurnal and height variations in measurements.

Although reproducibility is impossible with field data, the authors do a great job detailing instrumental parameters such as E/N and sensitivity calculations which will enable future measurements to directly compare their results to the ones herein.

In terms of structure and presentation, the article has a good title and abstract which reflects the contents. The abstract and sections are logical and well organized, and the writing is great. Regarding content, most of the text is dedicated to previous work about the observed OVOCs making it seem more like a merge between a review and a measurement report. This level of background detail makes for a nice introductory read but it is not new science per se.

Regarding the supplementary data, I think the paper would benefit from some time series data. The only measurements presented in the article are averaged diurnal profiles and correlation tables. Presenting some time series data could provide further insight into the sampling height differences, reagent ion switching and differences between seasons which would strengthen the article.  

As of now the article can be published with technical corrections. 

Minor comments:

Line 333: reference to chapter 4 should be removed.

Figures S3-S5 are incorrectly ordered.

Figure S2 text boxes are illegible.

Figure S4 could benefit should be replaced with a higher resolution version.

Figure S5 shows a plot of benzene with no data and non-sensical axes.

Review of “Investigating Carbonyl Compounds above the Amazon Rainforest using PTR-ToF-MS with NO⁺ Chemical Ionization” by Akima Ringsdorf et al. The manuscript analyzes the characteristics of different carbonyl compounds and emphasizes the necessity of supplementing the NO+ CIMS method to measure carbonyl compounds. The authors examine the sources and sinks in the Amazon rainforest of the selected carbonyl species in combination with a sufficient literature review. The article is substantial, with many citations and argumentation work. However, the writing focus of the discussion section of the manuscript is not clear enough, and the data analysis method is relatively simple. I recommend a major revision before its publication. My concerns in the manuscript are mainly listed below:

Specific comments:

1. Line 99-100: What is the temporal variation of humidity during the observation? Even with NO⁺ ionizing chemistry, the reported C₂-C₉ carbonyl compounds are greatly affected by humidity. The author needs to specify whether the signal of these compounds has been calibrated for humidity.
2. Line 101-121: What is the delay time of measured compounds？Does the time resolution of 20 s for NO⁺ PTR-ToF-MS be able to guarantee that the measured signal of speciated compounds was from the actual atmosphere, not the tube residue?
3. Line 141-143: The author needs to specify the parameter setting for NO⁺ mode, including the ion source voltage and drift tube voltage since the difference of parameter setting will affect the abundance of impurity ions (H₃O⁺, O₂⁺, and NO₂⁺). And the author also needs to give the abundance of impurity ions during the campaign, especially for the ratio of O₂⁺/NO⁺, due to O₂⁺will cause interference when using NO⁺ ionization for measurement.
4. Line 187-197: It seems that the parameterized quantitative method proposed by Cappellin et al. is based on the proton transfer reaction between organic compounds and H₃O⁺ I wonder if this method is suitable for NO⁺ chemistry. Because NO⁺ ions can react with organic compounds with multiple ways and occur simultaneously. I think the author needs to reconsider this issue. In addition, it is suggested that the author use a formula to explain how to obtain the sensitivity for those compounds not included in the gas standard based on k-rate.
5. Table 1 and Table S1: According to previous studies for the reaction pathway of NO⁺ to organic compounds, the multiple reactions of NO⁺ to organic compounds (Charge transfer (M⁺), hydride abstraction (M⁺- H), association reaction (MNO⁺) or hydroxide ion transfer (M⁺- OH)) should occur simultaneously. However, the differences in ionization energy (IE) and the chemical bond can cause species to react more easily with NO⁺ in one particularly pathway, associated with the formation of fragments. Therefore, we need to identify the characteristic product ions (which refers to the ion formula the author shown in the table) according to the contribution of each product ion after reaction. The author should show this contribution here, which also be better explain the influence of different E/N conditions to measurements.
6. Line 268-285: What is the contribution of local emissions and long-range transport during the measurement in dry season? As mentioned above that region is affected by long-range transport from African biomass burning pollution. And I prefer to see an overall picture of carbonyl emissions with concentrations and contributions.
7. Line 298-309: Just a suggestion, maybe the author could further quantify the influence of biomass burning from Africa and South America based on PAN, which is basically present in aging plumes.¹
8. Line 334: Short-lived aldehydes do not include isoprene.
9. Line 440-443: The authors believe that ethanol was formed by anaerobic reactions on the surface, but why does the ethanol concentration decrease with increasing altitude during the transition season?
10. Line 498-545: During the daytime, acetone and C5-ketones have stronger vertical gradients than the more reactive isoprene and monoterpenes. This phenomenon is very important for analyzing the sources and sinks of ketones. On a well-mixed daytime, it is difficult to understand the strong vertical gradient of ketones, even though the ketones have a strong source at the surface, as the authors believe.

Technical Corrections:

1. Table 1: The references involved in the table may be annotated separately.
2. The picture can be named (for example, Fig. 1(a)), which can avoid the description of upper, lower, etc.
3. S6 and S7: The naming format used for each species in the figures should be unified, now there are both species names, molecular formulas and ionic formulas
4. S7: Why is the first picture empty?

Reference

1. Liang, Y.; Weber, R. J.; Misztal, P. K.; Jen, C. N.; Goldstein, A. H., Aging of Volatile Organic Compounds in October 2017 Northern California Wildfire Plumes. Environ Sci Technol 2022, 56, (3), 1557-1567.