Dear Authors, Dear Editor,

The manuscript presents a valuable dataset on triple stable isotope composition of precipitation from an East Asian locality, namely from the capital of South Korea. The manuscript is principally well-written, however there are some points in the methodology which require more details and it seems that a key reference avoided Authors’ attention which definitely deserves consideration during the revision stage.

Anyway, I think that this dataset deserves publication, and I encourage the Authors to revise their study which can provide a valuable reference dataset for isotope hydro logical research of the Korean Peninsula.

I note that I cannot provide a detailed linguistic revision since I’m not a native English speaker.

General comments:

-I suggest Authors considering the following paper in the revision: Terzer-Wassmuth, S., Araguás-Araguás, L.J., Wassenaar, L.I. et al. Global and local meteoric water lines for δ17O/δ18O and the spatiotemporal distribution of Δ′17O in Earth’s precipitation. Sci Rep 13, 19056 (2023). https://doi.org/10.1038/s41598-023-45920-8

This global review presents comparable data from Cheongju locating from ~100 km south from Seoul from a partially overlapping period (2015-2018) compared to the Seoul record. So comparing the main features must be included in this study. For instance, the δ¹⁷O/δ¹⁸O regression reported for Cheongju (δ′¹⁷O =  0.5283 × δ′¹⁸O +  0.0216  ) definitely can be compared to the equation derived from the Seoul dataset. In addition, the seasonal variation for the overlapping period should be compared in a plot to confirm the spatial consistency. This might bring some major change in section 4.2.

- I missed very much a brief methodological description on the derivation of the local meteoric water line (LMWL). There are a set of methods which can be applied to approximate the linear covariance between δ¹⁸O and δ²H (see Crawford et al., 2014 https://doi.org/10.1016/j.jhydrol.2014.10.033 ). Ordinary least square (OLS) regression is more sensitive to the evaporatively enriched compositions typically accompanied with small precip amount, while reduced major axis (RMA) is theoretically more suited to development of a MWL than OLS because they consider errors in both  δ¹⁸O and δ²H. Precipitation-weighted least squared regression can be the most suitable to derive a LMWL for reference in isotope hydrological comparisons. So, it would be necessary to describe how the LMWL was calculated in this study.

Specific comments:

line 13: I suggest rephrasing in this way “The oxygen isotope composition (δ¹⁸O) ranged widely from 1.15 to –18.21‰, hydrogen isotope composition (δ²H) varied from…”

lines 56-57: I suggest citing the study of Terzer-Wassmuth et al., 2023 mentioned in the general comment section.

line 104: Have you applied oil to prevent evaporation? If not please report it in the appropriate paragraph describing methodology, if yes, please report if you experienced any complication during analysis.

lines 106-107: To verify the evaporation proof storage in HDPE bottle Authors might consider citing the following study: Spangenberg, J.E. (2012). Caution on the storage of waters and aqueous solutions in plastic containers for hydrogen and oxygen stable isotope analysis. – Rapid Communications in Mass Spectrometry, 26, 2627–2636.

lines 120-123: I'm confused. I think that the long-term analytical precision should be estimated based on the repeated measurement results of your laboratory standards rather than based on the calibration standards. see e.g https://doi.org/10.1002/rcm.5037 and https://doi.org/10.1556/24.2023.00134

line 133: Have you experienced a threshold regarding precipitation amount? I mean a minimum amount of precipitation below which the collected water was insufficient for the analysis. For instance, this study reported a ≥0.56 mm/day during the rainy season, and 0.5 mm/day during the snowy season: https://doi.org/10.1038/s41597-022-01148-1

lines 136-137: The sentence sounds like figure caption. I suggest omitting this sentence and referring to Fig 3 at the end of the next sentence (in line 139)

line 159: I suggest writing „The linear relationship...” instead of „The relationship...” at the beginning of this sentence.

lines 161 & 185: I think that double brackets are not needed when referring to panels of certain figures.

line 206: I think that “lower humidity” instead of “humidity”

lines 209&213: I suggest writing “δ¹⁸O values” instead of simply the delta notation

lines 225-235: Please add relevant citations in this paragraph.

lines 269-271: This sounds like figure caption. I suggest removing this sentence and simply referring to Fig7 after the relevant statements.

In this paper, the authors presented precipitation hydrogen and triple oxygen isotope data of precipitation from South Korea and made some exploratory analysis on these data. I recognize that the authors have made great efforts to collect samples and data and put together a manuscript. However, I feel that it does fit with the scope of journal. The ESSD is a high-impact journal publishing flagship datasets for various applications with broad interest. Although it is indeed contributing to the emerging triple oxygen isotope study, this dataset does not make a significant contribution to the progress of this field. I suggest publishing the data in a substantially revised manuscript on a more specialized journal.

1. L49: it is more common for using the prime symbol for ln(δ18O+1) as δ′18O. Also, most people (including IAEA authors) using “Δ′17O” notation (see Aron et al., 2021). The prime symbol is missing.
2. L100: confusing… are you collecting event samples or biweekly samples?
3. L106: is storing samples in freezing conditions problematic? I think most people store samples in liquid at 4 degree C.
4. L122: what is the uncertainty in Δ′17O?
5. Results section: some sentences are not results but are discussion. I suggest authors to have a better separation of results and discussion. For example, L146-153 and L169-196 are mostly interpretations of results, and better put into the discussion.
6. L161: It’s inaccurate. A slope of 8 does not mean a governance of equilibrium fractionation. From the highly seasonal d-excess data, it is obvious that there is a large change in kinetic fractionation from winter to summer. A slope of 8 occurs in your dataset is because the low d18O data can have either high d-excess (winter) and low d-excess (summer). So in d2H-d18O space, the effect of d-excess variation on LMWL cancels out.
7. Section 4.1: although a lot of people were doing this, but I am not advocate of correlation analysis of isotope data with environmental variables. It is reasonable to do this in 1960s… correlation analysis provides little insight into the process and mechanism and correlation is not causation. There have been many papers publishing new precipitation isotope data and analyzing their correlations with various variables, so here there is little novelty except the analysis of Δ′17O data.
8. L200-205: low RH and high SST caused high d-excess data, according to MJ1979. Also, the RH here should be the “RH” referenced to ocean skin temperature, not atmospheric RH. Dry air may cause high d-excess in vapor due to kinetic fractionation but may also cause low d-excess in precipitation due to droplet re-evaporation.
9. L243-L257: one mechanism not considered is the ice formation in winter snow. Ice-vapor fractionation may have very different impacts on d-excess and Δ′17O in winter precipitation, owing to equilibrium fractionation involved in this process.
10. L258-259: this is a repeat of L243-L244.
11. Section 4.3: This section is for comparing measured data with GCM simulations. However, this was not mentioned in the Introduction and Methods sections. There is little novelty of comparing d18O and d-excess outputs from GCMs with observations, as original authors have done this already. D-excess data are often use to “tune” the model. It’s great to mention the contribution of triple oxygen isotope data to benchmark GCM. I suggest authors to collaborate with GCM researchers who already have GCM outputs with triple oxygen isotope components.

General comments:

Kim et al. present a unique data set of stable isotopes (δ²H, δ¹⁷O, δ¹⁸O, d-excess and Δ¹⁷O) of precipitation sampled bi-weekly between February 2016 and December 2020 in Seoul, South Korea. Such data sets can help to better constrain the drivers of isotope variability in precipitation, improve the interpretation of paleoclimate records, and tune isotope-enabled global climate models. In particular, data sets combining d-excess and ¹⁷O-excess remain scarce so far. Therefore, the data set is new and will be useful for future studies. The data set is accessible, however, does not contain uncertainties for each variable. Also, no meteorological data is given in the file, where especially precipitation amounts, but also T and RH data would be useful for the interpretation of the data set and have been used in the manuscript. If these data were derived from a different data base, this should be mentioned in the data availability section.

Overall, the manuscript is clearly structured and well written. However, the methodological section needs more detail, some discussion points appear already in the results and interpretations are often not justified by data. The manuscript is worth publication in ESSD, but needs major revision as outlined below.

Specific comments:

Methodology:

• Missing description of the meteorological data.
• Missing description of how secondary order parameters (d-excess and 17O-excess) are calculated.
• Give analytical precision for d-excess and 17O-excess.
• Details on the comparison of the GSM with observational data presented in the discussion section are missing in the methods. For example, model input parameters, but also more details about the model simulations should be given. I think that this model-data comparison could be a bit over the scope of this journal. Instead of adding mor details to the model, the authors may consider removing this part from the manuscript.
• In line 99 the authors state that precipitation has been collected from January 2016 to December 2020. However, the data set starts in February 2016. This should be corrected.
• Also, they state that sampling was performed bi-weekly. They should make clear that their interpretation is based on amount-weighted monthly values as bi-weekly data is not presented.

Results:

The results are mixed up with discussion points. A better separation of both is needed. Discussion parts that should be shifted to the discussion section: Line 163-164, Line 169-171, Line 173-174, Line 178-179, Line 189-196

Discussion:

Interpretations in the discussion section are often not justified by the presented data. For example, in the first discussion section, correlation between isotope data and local meteorological parameters are investigated. For example, line 204-206 that “lower relative humidity and temperature at the moisture source enhance kinetic fractionation during evaporation, thereby increasing d-excess” However, no information on relative humidity and temperature at the moisture source region is provided nor differences between different moisture source regions are discussed. –Further, more explanation is need in Line 211-212. Here, the authors state that the negative correlation between d-excess and local temperature is controlled by the moisture sources and isotope fractionation during precipitation. This is very general too. Can you explain how this correlation relates to these factors? Also more explanation and justification is needed in line 215-217 and line 222-224.

Line-by-Line comments:

Line 45-47: δ18O and δ2H are influenced by both equilibrium and kinetic fractionation and thus it is difficult to disentangle these two. The secondary parameters, d-excess and 17O-excess are primarily sensitive to kinetic fractionations and thus help to disentangle them. Clarify this in the text.

Line 47-49: δ17O has not been introduced yet. Consider adding a sentence on the value of additional analysis of the 17O isotope before.

Line 79: Be more specific: 5-year record of monthly triple oxygen and hydrogen precipitation isotope data.

Section 2: There is no reference to Figure 2 in the main text. This could be added to a sentence describing the meteorological data.

Line 97-98: I don’t expect this phrase at the end of the paragraph. It should be introduced more at the beginning of the paragraph and then all four seasons need to be described. For now, only summer and winter are described, but which conditions persist in spring and autumn?

Line 137: Why a sine function has been fitted to the data? This should be explained in the text.

Line 147: Which other moisture sources than the ocean are important. Specify this.

Line 149-151: I was first confused by the “unlike” but looking at the figure I understood that the difference between 17O-excess and d-excess is that 17O-excess is highest in spring, while d-excess is highest in winter. Can you make this clearer in the text. Also, Quantify give values for 17O-excess’ seasonal variability (highest value, lowest value).

Line 153-155: During which process kinetic fractionation is more pronounced? As I understood from the previous, this is due to evaporation from the ocean. Is this correct? Be more specific here.

Line 161: Can you add uncertainties for the slope and the intercept of the GMWL?

Line 167-168: Winter precipitation is mainly in the form of snow? Do you see differences between snow and rain samples?

Line 180: the 17O-excess is defined based on the prime values of δ17O and δ18O. This should be defined in the methods and clarified in the main text and the figures.

Line 187: You should refer here to Figure 4.

Figure 4: What is shown in B? It does not make any sense to me. Suggestion to illustrate 17O-excess vs d'18O as no difference will be visible in d'17O vs d'18O, when plotted to scale. The purple line is not the GMWL, should be dashed line, I guess.

Line 206: “mixing” of what? Air masses?

Line 208: This is very general. Can you name the multiple meteorological factors that are interacting?

Line 215: lower δ18O values compared to what? Compared to other months of the year? Is this a rainout effect or an amount effect?

Line 244-246: This is referring to evaporation from the ocean or re-evaporation of precipitation? Specify!

Line 249: evaporation of what? Precipitation?

Technical comments:

• Throughout the manuscript. The unit of ¹⁷O-excess is per meg not per mil. Please correct in text and in figures.
• Line 37-38: repetition of the previous sentence. Consider removing it.
• Line 95: Korean Peninsula
• Line 177: Repetition of slope and intercept not necessary here. Remove.
• Line 258-264: Repetition of previous paragraph. Remove.
• The Summary should be stated before the data availability statement, isn’t it?

Dear authors; dear editor,

Thank you for inviting me to review the manuscript ESSD-2025-374 and for the interesting read. My apologies for being the one reviewer who’s near-deadline to submit a response. I must admit, I dissent in part with the other reviewers.

General comments:

The manuscript presents a new precipitation isotope record for δ²H, δ¹⁸O, d-excess and ¹⁷O-excess for Seoul spanning four years and discusses the seasonality in the context of the regional-scale circulation. It further investigates the asynchronous seasonality of d-excess and ¹⁷O-excess and discusses possible causes.

As for the discussions that emerged regarding the dataset’s/manuscript’s fit into the scope of ESSD, I must admit it’s a delicate trade-off between the novelty and rarity of precipitation ¹⁷O/¹⁸O LMWL datasets, and the limited spatiotemporal coverage of the dataset (4 years, and applicability of an LMWL at best regional).

I am sorry to say that the structure of the manuscript merits improvement. The description of the analytical method is unclear to me (see detailed comments), and results and conclusions are a bit too tightly intertwined. The chapter 4.3 reads like an “encapsulated mini manuscript”; to me it is not adequately introduced at the beginning and includes methods and results which should be in chapters 2 and 3, respectively. A fair bit of the text unfortunately reads very generic or top-level but this is not supported by the granularity and/or spatiotemporal resolution of the data.

My recommendation is, and I am writing this before the background of my own struggles with getting datasets of a similar kind published, that the authors take a step back, review the hypotheses that can be addressed with the already-existing dataset, and then make a renewed attempt to publish an upgraded version of the manuscript.

Specific comments:

As for the annotation of ¹⁷O-excess, please unify your annotation. Commonly, ¹⁷O-excess is expressed as Δ′¹⁷O = δ′¹⁷O - 0.528 δ′¹⁸O, with δ′ = ln (δ+1), an equation which traces back to Angert et al. 2004. The usage of the Δ′ is very much encouraged to distinguish the Δ′¹⁷O from other excess calculations in isotope geochemistry that do not log-normalize the deltas (e.g. Aron et al. 2021 or other reviews on the topic). The annotation should be either in per meg, or in ‰ with three decimal places. It is not correct to use ‰ but express in per meg, as it is often done throughout the manuscript. The authors may also consider to consolidate the “equations” part into a “definitions” section either in the methods or in the introduction. Right now, the ¹⁷O-excess equation is not numbered and in line with introduction text, while the isotope ratio equation is numbered, in the methods, and after the ¹⁷O-excess equation. 

Concerning the listing of isotope effects (line 40), please take into consideration that the “amount effect” is one of the most debated empirical relationships in isotope hydrology, and that the modern-day discourse is cautious of a unanimous endorsement of it. While the cited Conroy et al. (2016) detected it, later publications (e.g. Konecky et al. 2019) have a much more differentiated approach. I acknowledge that the “amount effect” is still widely taught, but the data reality is often much more complicated than the initial concept. Please also note that your manuscript claims to “analyse […] in mid-latitude precipitation”, which I think is a bit of an overstatement since it would suggest a global analysis.

Kindly also work on your definitions of “long-term” and “high resolution” (line 69, 79, 85 etc.). For much of the triple O isotope work, the “long-term” discussion is complicated by absence of records as long as are available for “dual isotopes”. (Leuenberger & Ranjan 2021 and Terzer-Wassmuth et al. 2023 have the longest records reaching back furthest in time, to my knowledge). What is your definition of “high resolution”? To me, it would imply any sampling that is at minimum daily if not sub-daily (like the typhoon records of Munksgaard et al. [2014], the hurricane studies of Sun et al. [2024] and similar). Also, hinting at extreme weather events (e.g. line 96) deems far-fetched in the context of a biweekly sampling.

The sample collection is described as relating to the GNIP manual, but this is neither cited and, in several aspects, does not follow the manual. First, authors should consider referring to one of the 5 methods mentioned in the manual (additional sampler designs are in Michelsen et al. 2018). Furthermore, the GNIP manual nowhere recommends biweekly sampling (presumably because if its inherent difficulties to match the intervals with established monthly records). Also, freezing samples is not described in the GNIP manual. The authors should provide a sketch drawing of the sampler, or some detailed photos (all relevant aspects of sampler design are hidden behind bricks), plus a photo that shows the greater context of the sampling location in the SM for clarity.

The sample analysis largely relies on a previously published methods paper and there are a couple of things that read inconsistent to me. First, you describe that the method determined the injection numbers, but then it’s a fixed number of 20 injections of which the last five are accepted. Second, the method claims to use VSMOW (exhausted – do you mean VSMOW2?), SLAP2 and GISP (also exhausted) for normalization of the data to the VSMOW-SLAP scale, which is acceptable in a methods testing setting but normally discouraged for routine analysis. If in-house standards are used, then their value should be provided and an eventual traceback to the primary reference materials should be given in the SM. Is this the ”laboratory standard” mentioned in line 122? What is the typical uncertainty of the method under routine analysis (e.g. expressed as a 1-sigma SD of the Δ′¹⁷O of a control sample)? It’s been three years since the original method by Kim et al. (2022) was published, hence a review of the method’s benchmark data deems merited.

In the “methods” chapter, the authors may also consider adding a paragraph “data treatment methods”, i.e. not only about the weighted means but also how their LMWLs were calculated. (unweighted? Weighted? The ¹⁷O/¹⁸O one on the δ or δ′? With intercept, or 0-forced?).

In the variations chapter (3.1), I found the description of 130 samples (which I translate as data points) a bit in contrast to the supplementary data file on Pangaea, which is roughly monthly and has less data points than described here. Without extensive calculations, some of the sine functions in Fig. 3 do seem bimodal while others don’t. Whilst I agree with the comparison of the regional patterns with Jeju and mainland China, I miss a comparison with the data from GNIP/Cheongju (IAEA, 2025; admittedly a continental mountain station), as also highlighted by one of the other reviewers. The array of LMWL combinations (Seoul/Cheongju/Hongseung vs. weighted/unweighted) is huge and, to me, poses more questions than “similarities” as described in lines 174-179. It is commonly known that, due to the complex interplay between the Siberian High and the summer monsoon as drivers, the LMWL interpretation is complex, and the data is highly scattered, often causing unusually low R². Note that the slope/intercept reported here are different to those reported in the summary (intercept of 10 here, 11.2 in the summary).

For the LMWL results, I agree that “seasonal disentangling” improves the LMWLs in this context. The R²=1 for the ¹⁷O/¹⁸O MWL is not surprising; similar has been observed by Terzer-Wassmuth et al. (2023) and many others. The authors should, ideally already in the “data treatment” section of the methods’ chapter, outline how the ¹⁷O/¹⁸O MWL was calculated. The slope is very similar to that reported for Cheongju by Terzer-Wassmuth et al. (2023), but the intercept isn’t (0.0105 vs. 0.0216). A comparison of a weighted LMWL intercept with the mean Δ′¹⁷O for Seoul would be helpful (they should be similar for a weighted MWL). I recommend removing Figure 4B; without scale it adds very limited value to the presentation of results. A table of MWLs would be more representative. Much of this section however overlaps with the discussion.

The correlation analysis (I am torn about it) should be introduced in the results section, not in the discussion. The font colour of the correlation plot should be white where the background is dark; the numbers are hard to read in black against dark blue. The pattern observed certainly corroborate the observation that the biggest changes in the seasonality happen in spring and fall, when the two modes switch over. Note that few of them are truly significant (if that is what the asterisk indicates). Note that the correlations are expressed as R (not R²), and an R~0.5 (equivalent to R²~0.25) is not what would generally be considered a “strong correlation” (which I would see as R²>0.5 and significant p-value).

The interpretation of the seasonal decoupling of the two excesses is an important point (I would not call them indices, as such would indicate they are scale-normalized to something, line 239). I agree with the general line of argumentation. Yet, the correlation between Δ′¹⁷O and δ¹⁸O, or between Δ′¹⁷O and d-excess is a complicated matter and existing literature (Terzer-Wassmuth et al. 2023) has demonstrated that either there are few correlations indeed, or the higher uncertainty of CRDS-based measurements blurs eventual patterns. Knowing the routine uncertainty of the measurement process would be helpful. And to be frank, the discussion does not address that only 4 in 10 correlations are significant at p<0.001 and only two have an R²~0.4. Again, I think that the overall line of argumentation makes sense, but the statistics do not provide the robustness of foundation desired.

The chapter on the Iso-GSM analysis (4.3) seems, sorry to say so, misplaced. Although vaguely introduced in the abstract/introduction, it is hardly to any other part of the manuscript. I recommend the authors to correctly bind it into the main text body, including changes in introduction, abstract, possibly even title, or leave it aside completely, or put into the SM as supplementary data analysis. Nothing that’s said in this chapter is wrong, but in my opinion, it does not fit (and it’s not very novel either, to be honest).

If you allow, I’d give two suggestions how to improve: One regards the data analysis: Use daily rainfall data and backtrajectory modelling to determine the source region of the precipitation. This could, as far as I can see, help to refine the conceptual model from Winter=Siberian High / Summer=Monsoon / Spring, Fall=somehow in between to a spatial/seasonal explanation model, and could also help to disentangle the Siberian High fraction in winter. With the existing bi-weekly sampling structures, that could be expressed as “fractions of source region” to match with the isotope dataset. And the second one is forward-looking; I think to make an even greater contribution to modelling improvement, daily samples are, and I am well aware of the collection effort, more poised to address phenomena occurring on a daily/synoptic weather timescale.

References:

• Angert, A., Cappa, C. D., & DePaolo, D. J. (2004). Kinetic ¹⁷O effects in the hydrologic cycle: Indirect evidence and implications. Geochimica et Cosmochimica Acta, 68(17), 3487-3495.
• Aron, P. G., Levin, N. E., Beverly, E. J., Huth, T. E., Passey, B. H., Pelletier, E. M., ... & Yarian, D. A. (2021). Triple oxygen isotopes in the water cycle. Chemical Geology, 565, 120026.
• Conroy, J. L., Noone, D., Cobb, K. M., Moerman, J. W., & Konecky, B. L. (2016). Paired stable isotopologues in precipitation and vapor: A case study of the amount effect within western tropical Pacific storms. Journal of Geophysical Research: Atmospheres, 121(7), 3290-3303.
• Konecky, B. L., Noone, D. C., & Cobb, K. M. (2019). The influence of competing hydroclimate processes on stable isotope ratios in tropical rainfall. Geophysical Research Letters, 46(3), 1622-1633.
• Leuenberger, M. C., & Ranjan, S. (2021). Disentangle kinetic from equilibrium fractionation using primary (δ¹⁷O, δ¹⁸O, δD) and secondary (Δ¹⁷O, dex) stable isotope parameters on samples from the Swiss precipitation network. Frontiers in Earth Science, 9, 598061.
• Munksgaard, N. C., Zwart, C., Kurita, N., Bass, A., Nott, J., & Bird, M. I. (2015). Stable isotope anatomy of tropical cyclone Ita, north-eastern Australia, April 2014. PloS one, 10(3), e0119728.
• Sun, C., Shanahan, T., He, S., Bailey, A., Nusbaumer, J., Hu, J., ... & DeLong, K. (2024). ¹⁷O‐excess in tropical cyclones reflects local rain re‐evaporation more than moisture source conditions. Journal of Geophysical Research: Atmospheres, 129(6), e2023JD039361.
• Michelsen, N., van Geldern, R., Roßmann, Y., Bauer, I., Schulz, S., Barth, J. A., & Schüth, C. (2018). Comparison of precipitation collectors used in isotope hydrology. Chemical Geology, 488, 171-179.
• Kim, S., Han, C., Moon, J., Han, Y., Hur, S. D., & Lee, J. (2022). An optimal strategy for determining triple oxygen isotope ratios in natural water using a commercial cavity ring-down spectrometer. Geosciences Journal, 26(5), 637-647.
• IAEA (2025). Global Network of Isotopes in Precipitation. The GNIP Database. https://nucleus.iaea.org/wiser
• Terzer-Wassmuth, S., Araguás-Araguás, L. J., Wassenaar, L. I., & Stumpp, C. (2023). Global and local meteoric water lines for δ¹⁷O/δ¹⁸O and the spatiotemporal distribution of Δ′¹⁷O in Earth’s precipitation. Scientific Reports, 13(1), 19056.