General comment

This paper presents original data on the isotope composition of event-based precipitation in different areas of Central Asia. The manuscript covers a necessary topic and is of interest to be published in this journal. I would highlight the presentation of a very large isotopic dataset of single precipitation events, which is important to fully investigate the main factors of variability and to evaluate the relationship between the source areas of precipitation and their isotopic composition. The authors provided a good introduction of the context, and they clearly indicated their own original contribution. However, I feel the manuscript is too immature at this stage for publication because of a series of methodological imprecisions (see comments 8-9 below) and it needs to be revised significantly. Results and discussion should be presented in a clearer and well-structured way taking care to accurately separate the presentation of data from the interpretation provided by these authors. I am not a English native speaker, but the text also includes some typos and grammatical errors. Some sentences are too long (including titles of sections), and some parts are repeated and redundant, so the paper can be shortened. The manuscript would benefit from careful proofreading by a native speaker. Then, considering these limitations, but aware of the effort made by the authors in collecting such a large number of precipitation events and certain of the importance of the data presented here, I suggest reconsidering this manuscript after major revisions. I would be delighted to revise the manuscript again after a general reorganization, a clearer presentation of the methodology, and a more concise discussion of the results. Authors can follow some suggestions below and minor revisions are in the attached file.

Specific comments

Please check the isotopic terminology through the manuscript and see USGS recommendations (https://wwwrcamnl.wr.usgs.gov/isoig/res/funda.html). Generally, the isotopic community use the expressions as follows:

• higher vs. lower values or more/less positive vs. more/less negative when isotopic measurements are compared.
• heavier vs. lighter or enriched vs. depleted when the isotopic composition of a material/substance is defined relative to a reference.

Introduction

Comment 1: The authors reported the name of D-excess through the manuscript. I think the “d-excess” is the correct abbreviation for the deuterium excess. Dansgaard (1964) defined this parameter as d-index. Then Rozanski et al. (1993) called the parameter d cited in Dansgaard (1964) as d-excess. Many articles used d-excess or more easily d. 

Comment 2: I suggest changing lines 78-80 because they are not clear. It seems that a shorter distance between the cloud base and the ground is known to increase the d-excess, but this is not correct. The d-excess tends to decrease as raindrops go through the air column because of sub-cloud evaporation.

Comment 3: Researchers usually use past tenses when describing the research activities they performed. I suggest changing the verbs from the present to the past when describing the objectives (lines 105-106) and presenting the data (e.g., line 292 and forward). 

Data and Methods

Comment 4: At the beginning of subsection 2.1 authors should better describe the study area and provide further details about the sampling sites. How many catchments? How many sampling sites? In which basins are they located? What is the climate for each region/site during different seasons? It could be useful to describe the climate according to Köppen’s classification system.

Comment 5: The reader may get a little confused with the acronyms. Authors could code each sampling site with the acronym of catchment followed by a progressive number (e.g., UA1, AA1, CKS1, CKS2, CKS3, etc.) in order to immediately understand in which area a site is placed. Then, authors could label the sites in Fig. 1a, and report the same codes in Fig. 1c.

Comment 6: At line 136 the authors cited the PALMEX collector model RS1 to collect monthly precipitation, but they did not provide any details about the collectors used for event-based precipitation. Which collector did you use? You should mention that any anti-evaporative system was not used because samples were collected immediately after the events. Are you confident with the reliability of collecting precipitation with no anti-evaporative system?

Comment 7: At line 148 authors should also report the error propagation associated with the d-excess. According to the formula proposed by Natali et al. (2022), the d-excess error was about ±2.5‰, by using the total errors of ±0.2‰ for δ¹⁸O and ±0.6‰ for δ²H. Hence, some differences between sampling sites or seasons may not be significant. Please, check it through the manuscript. Pay also attention to significant digits for d-excess. 

Comment 8: At lines 163-169 authors were confusing when describing regression techniques. The sentence “This approach potentially increases uncertainty in the interpretation of results…” is misleading because different regression methods are useful for different applications. Precipitation-weighted regressions are useful to minimize the impact of possible evaporation processes when dealing with small precipitation amounts (Hughes and Crawford, 2012). So, these lines are more appropriate to represent hydrologically significant precipitation, which is important for local hydrological applications, especially when investigating stable isotopes of groundwater in relation to precipitation recharge. Conversely, unweighted regressions are advisable when researchers aim to evaluate the atmospheric and hydrometeorological processes that govern the isotopic composition of precipitation. Moreover, theoretically, the RMA and MA regressions are more suitable than OLSR because they consider errors in both correlated variables (δ¹⁸O and δ²H). I suggest computing only the OLSR and RMA regressions, and the corresponding weighted models, and comparing these lines in relation to different aims.

Comment 9: The Hysplit analysis described in subsection 2.4 has some methodological issues. Firstly, the authors ran the Hysplit model for four sites, but CKS and CHK catchments include three sites each, so we cannot know at which site trajectories were calculated.

Site elevations were used as starting altitudes for the model, but it is wrong because the starting altitude should ideally correspond to cloud elevation during precipitation. Did the authors have some radiosonde ascent measurements? If not, they may select an altitude that can be representative of the air column where most of the moisture is contained (please see Bershaw et al. 2012, Wallance and Hobbs, 2006, Krklec et al. 2018).

Authors should also consider the duration of each precipitation event. They ran a single trajectory at the beginning of each event, but one single trajectory could not be representative of the mean direction of air masses for longer events. Are these authors confident with the reliability of a single trajectory?

Did authors establish the number of clusters based on the TSV criterion (e.g., see Kostrova et al. 2020)? The authors should provide more details on this.

The expressions “source regions of moisture” or “moisture transport” are frequent in the manuscript, but the results here presented are merely based on trajectory directions and distances. This analysis is correct to determine the origin and mean provenance of air masses producing precipitation, but any evidence of moisture uptake and transport may be found. I suggest using a specific humidity-based model (e.g., Oza et al. 2022, Natali et al. 2023), to account for the history of moisture dynamics along the trajectories, or merely to discuss the mean provenance of precipitation.

Subsections 2.4 and 2.5 can be merged.

Results

Comment 10: “Results” and “Discussion” should be correctly separated into two sections that enable a clearer distinction to be made between the obtained results and the data interpretation provided by these authors. They included part of data interpretation in the “Results” section (see lines 229-231, 252-258, 295-297, 300, 303, 321-323, 419-421, etc.), but these parts should be moved to the “Discussion”. The regression analysis between isotopes and geographical and meteorological variables (lines 259-290) could be moved to the “Discussion” and merged with considerations already done. In the presentation of results, authors could follow this scheme:

• Total isotopic means for all events
• Isotopic means for solid, liquid and mixed precipitation
• Spatial isotope variability
• Seasonal isotope variability
• Results of the Hysplit analysis and air masses origin

Then, the interpretation of these results by authors can be presented in the section “Discussion” along with the evaluation of relationships between the isotopic composition of precipitation and air masses trajectories.

Comment 11: In Fig. 2 the authors reported annual mean values for δ¹⁸O, δD and d-excess (line 237), but they collected precipitation events in the period between 2019 and 2021 (line 135). To which year did the mean values refer? I think it is better to calculate the mean values over the entire period.

Comment 12: The authors collected event-based precipitation samples at 8 sites, but then they discussed data for 4 catchments (e.g., line 241). Were the same events collected for different sites of each basin? If not, I don't understand how the authors can discuss the data by catchment and not by site. If yes, did the authors average the isotopic values of the same events between different sites of each basin? It's really difficult to follow what these authors did. I suggest presenting data for 8 sites first, in order to evaluate the spatial and temporal variability, and then focusing on trajectory analysis performed at selected sites.

Comment 13: The “stepwise regression” method (line 259) and the method of Dansgaard (lines 275-278) should be cited and/or briefly described in the “Data and methods” section. However, the authors had enough data to perform Spearman’s correlation analysis between isotopes and climatic variables.  

Comment 14: Coefficients at line 282 are different from those in the equation 8-9. Please check. 

Comment 15: In the LMWL equations, the authors reported the standard errors associated with slope and intercept. I would suggest providing confidence intervals of the regression models, which is important for comparison purposes.

Comment 16: Lines 403-411 and 437 should be moved to the “Data and Methods” section. As indicated in comment 9, it is not clear how the authors defined the number of clusters (lines 403-404).

Comment 17: I suggest moving the parts dealing with the evaluation of relationships between isotope values and trajectory groups (lines 435-470 + subsection 3.5) to the “Discussion” section.

Comment 18: I am not sure that the high d-excess values (line 467) indicated the contribution of the re-evaporated moisture. It could be due to the atmospheric conditions at the moisture source or to both factors, especially in winter and autumn.   

Comment 19: I have doubts about merging groups 1, 2 and 3 (lines 481-484). Trajectories of Group 1 came from a different area compared to the other groups, so precipitation associated with air masses coming from the north could have a different isotopic signature.

Comment 20: Lines 487-489. Once the authors have established a good correlation between δ¹⁸O and δD, what is the point of repeating the calculations for both variables? I suggest using only δ¹⁸O.

Discussion

Comment 21: lines 517-527 are not very useful in this section. Some sentences are repeated in the “Introduction”, whereas others should be moved to the “Conclusions” as main outcomes from this article. Please, move lines 527-529 to the “Data and Methods”.

Comment 22: lines 530-534. It could be due to the altitude effect. I note that UA is placed at a higher altitude than sites in the CHK catchment, so this trend could be determined by altitude and not by latitude. Please check the elevation of collecting sites in articles for the Chinese Tien Shan.

Comment 23: At lines 551-552 the authors indicated “a strong positive correlation”, but they did not perform any correlation analysis. Please, pay attention to the difference between a correlation analysis (correlation coefficients, r) and linear regression models (coefficients of determination, r²). More caution should be observed by the authors when they proposed using temperature data as a proxy of isotopic values for isoscapes reconstruction. The r² is around 0.5, so the uncertainties would be too large.

Comment 24: The subsection 4.2 should be revised after modifications suggested in the comment 8. 

Comment 25: lines 628-632 may be omitted or moved to the “Introduction”. Lines 634-637 and 644-648 are redundant and should not be repeated in this section.

Figures

The figure numbers are wrong. At line 227 the authors cited Fig. 4, but Fig. 3 had not yet been presented. Please check through the manuscript.

Fig. 1: please use the same codes in Fig. 1a and 1c (see comment 5).

Fig. 7: move the labels to avoid overlapping with boxplots.