Isotopic insights into the dynamics of soil water pools along an elevation gradient

Kocum, Jiri; Falatkova, Kristyna; Sipek, Vaclav; Patek, Karel; Hnilica, Jan; Jenicek, Michal; Sanda, Martin; Trakal, Lukas; Vlcek, Lukas

doi:10.5194/egusphere-2025-3922

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https://doi.org/10.5194/egusphere-2025-3922

Preprints

21 Oct 2025

| 21 Oct 2025

Isotopic insights into the dynamics of soil water pools along an elevation gradient

Jiri Kocum, Kristyna Falatkova, Vaclav Sipek, Karel Patek, Jan Hnilica, Michal Jenicek, Martin Sanda, Lukas Trakal, and Lukas Vlcek

Abstract. Recent intensive research on the soil–plant–atmosphere continuum has introduced novel methodological approaches. These include new in-situ extraction techniques and the application of stable hydrogen and oxygen isotopes in water, which enable tracing of water movement and plant responses at much finer spatial and temporal scales. Such approaches provide detailed insights into soil water dynamics and plant adaptation to changing environmental conditions under climate change. This study aims at an intimate description of dynamics of distinct soil water pools—mobile versus tightly bound water—along an elevation gradient, together with the impact of the absence of snow accumulation in lowland areas on water distribution within the soil profile compared to higher elevations. In contrast to conventional bulk water sampling, the key innovation of this research lies in the novel extraction method that selectively isolates tightly bound soil water for isotopic analysis, combined with a unique experimental design encompassing sites across the elevation gradient. Our results indicate a prolonged residence time of winter-derived soil water in lowland sites, despite limited snow cover, contrasting to a rapid turnover at the highest elevation, where the winter water signal dissipated shortly after snowmelt. Simultaneously, distinct isotopic compositions among water pools—mobile versus tightly bound water—were also found, especially in lowland areas at the edges of the growing season (up to 3 ‰ and 21 ‰ for δ¹⁸O and δ²H, respectively), while tightly bound and bulk soil water exhibited—on average—only minor or no isotopic differences. Facing the projected continued decline in snow cover at higher elevations in Central Europe, these findings are critical for improving predictions of soil water storage and, consequently, plant water availability under ongoing climate change.

Received: 11 Aug 2025 – Discussion started: 21 Oct 2025

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Jiri Kocum, Kristyna Falatkova, Vaclav Sipek, Karel Patek, Jan Hnilica, Michal Jenicek, Martin Sanda, Lukas Trakal, and Lukas Vlcek

Status: final response (author comments only)

RC1:
'Comment on egusphere-2025-3922', Anonymous Referee #1, 03 Dec 2025
General comments
In this work, the authors compared isotopic dynamics and seasonal origins of different soil water pools at four study areas at various elevations. The novelty of this study lies in the use of a new extraction method to determine tightly bound soil water. This new technique appears promising, but no spike-experiment results and no comparisons with other soil-water-extraction methods are presented. Furthermore, the uncertainty associated with the mass-balance mixing model was not estimated. A detailed description of the technique and its critical evaluation is necessary to assess the quality of the results. In addition to this major comment, other descriptions of the methods should be improved (e.g., the determination of soil water content) and/or moved to other sections (e.g., the use of RMA-based regression).

Specific comments
Line 65: Maybe I missed that information, but I do not see a definitive protocol proposed in Ceperley et al. (2024).

Table 2: Please group soil cores and mobile soil water by sampling depth, and please indicate the number of locations used for each water source in each study area.

Section 3.2: The main findings of this research depend on the application of this method to extract tightly bound soil water (TBW). Conventional spike experiments were performed (lines 156-157), but the manuscript does not present evidence of these results or a critical evaluation of the method (including comparisons with other approaches). The use of glass balls for air removal (are they effective?), and the choice of the labelled water seem fundamental for the method and to determine the isotopic composition of TBW based on a mass balance mixing model (and to minimize the uncertainty in the estimations of TBW). Uncertainties arising from the application of the mixing model (e.g., calculations can be based on the error propagation method) should also be presented and discussed. Finally, it would have been helpful to compare the obtained results with those derived from soil water extracted by other methods (e.g., by cryogenic vacuum distillation).

Line 147: Please provide the isotopic composition of the traced water. I also suggest using ‘isotopically labelled water’ instead of ‘traced water’ to improve the clarity. Furthermore, I expect that the isotopic signature of the traced water is significantly different from that of the samples. Otherwise, it would be challenging to discriminate between TBW and the traced water.

Line 158: Do the values between parentheses represent isotopic shifts or isotopic compositions?

Lines 195-196: Besides a better visual representation, is there a more quantitative purpose for the application of a 3^rd-degree polynomial fit? Given that you cannot use it to obtain an amplitude for the specific water sources, I would suggest removing such analysis based on polynomial fits.

Lines 197-206: The description of RMA-based regression lines should be moved to section 3.3, before Equation 3. Please clarify whether RMA was applied to determine the δ²H-δ¹⁸O regressions of all water sources.

Section 3.5: Did you apply any isotopic correction for samples with an evaporative signature? If so, please describe it. If not, you should consider it for samples with a negative lc-excess.

Section 3.6: I do not understand very well the aim of this statistical analysis, and particularly of the ‘differences in the annual courses of isotopic composition of individual waters’. Are you comparing δ²H-δ¹⁸O regression lines or time series of different water sources? The current text is unclear.

Section 4.1 and Figure 3: Are the regression slopes significantly different or not? Many TBW samples fall on the left side of the LMWL; do they lie within the 95% prediction interval for precipitation? If not, why do they plot there? Were there any issues (e.g., organic contamination) observed during the isotopic analysis?

Figure 4: I recommend showing the sample size associated with each boxplot, as well as which water sources are significantly different.

Line 274: Please provide the name of the statistical test when you state that there are (or there are not) significant differences among samples.

Section 4.3: Soil water content is mentioned many times here, but details about the measurements (sensors, locations, spatial and temporal resolution) were not reported in earlier sections of the manuscript.

Figure 5: In this figure, there are too many dots, lines, and vertical bars that make the interpretation very difficult. For instance, vertical bars for precipitation amount are not very visible, and symbols or lines for soil water content are not clearly represented. If soil water content is indicated by the vertical bars for TBW and MW, I do not think these values are representative of soil water content at the monthly scale (or of the temporal variability of wetness conditions) in the study areas. Moreover, it seems that the fitted lines do not capture well the temporal dynamics of the various water sources, but their efficiency needs to be quantified and deserves an explanation.

Lines 317-320 and Table 3: The comparison between the fitted lines does not make much sense if the sine function can model a small fraction of the total variability. I also do not think this analysis is particularly informative in supporting the key messages of this work; therefore, this method and these results can be removed.

Figure 6: How many SOI values are there for each month? Please report the sample size inside each cell.

Lines 351-355: This text belongs to the discussion. Please move it.

Line 397: The previous text and the figures do not present the estimation of the transit times. Please revise the text and refer only to the phase shift.

Technical corrections
Line 18: Please replace ‘intimate’ with another term (e.g., ‘comprehensive’, ‘detailed’).

Line 115: ‘lower sampled soil layer’ instead of ‘lower soil layer samples’.

Line 142: ‘and’ instead of ‘with’.

Equations 1 and 2: Please use ‘TBW’ instead of ‘S’.

Line 189: Zuecco et al. (2024) is not present in the list of references.

Line 274: The term ‘absolute quantities’ is unclear (not very precise); please replace it with another term.
Citation: https://doi.org/10.5194/egusphere-2025-3922-RC1
RC2:
'Comment on egusphere-2025-3922', Anonymous Referee #2, 18 Dec 2025
The manuscript on “Isotopic insights into the dynamics of soil water pools along an elevation gradient” provides an interesting data set along an elevation gradient. The manuscript is mostly well structured, but has several weaknesses that need to be addressed. I am not sure if these can be addressed in a revision, but hope the authors can address the issues raised below:
No hypotheses provided, but a list of objectives, of which the last one is unclear to me what it could mean

The authors used a little (or not) known method for their isotope analysis and did not provide any evaluation of the method nor do they refer to a test presented in a previous manuscript. This is a major issue that will be difficult to address.

It is unclear why the authors did not target to sample at least one entire year. I understand the logistical challenges for the mountainous snowy study site, but it seems all sites had only 10 months covered.

No snow sampling is a problem, because this is likely to impact the delta_WinterP in the calculations of SOI

Why is the “historical” data shown in Figure 8 ignored in this study? It appears that with Figure 8 results are introduced in the discussion section.

It seems that a correction of evaporation fractionation prior to SOI calculations is missing. This will affect the interpretation of the data.

Figures have little information content and questionable choice of visualization

The reviewed literature is limited in the current manuscript. There have been several studies looking into mobile and bulk soil water isotope composition, while the authors discuss their results basically with two studies.

The visualization (e.g., monthly bar plots) loses too much information

These major aspects are more outlined in the detailed comments below.
Line by line comments:
18: I don’t think “intimate” is the right word here.
72: I suggest framing this as a definition. It seems that your definition of TBW is the water that remains in the pore space and cannot be extracted via suction lysimeter. I suggest rephrasing accordingly
76-86: This reads like a summary of methods. I don’t think this is helpful or necessary in the introduction. I’d suggest to focus on research gaps, hypotheses, and objectives at the end of the introduction
91: unclear what this means.
143: How was evaporative fractionation prevented over the 2 week period?
3.2: this seems to be a rather new or little used method. I think that a method evaluation is missing in this manuscript or there should be a reference to a study where it was done.
128: it's a weakness that there was not even one full year of precipitation sampling for the isotope data. I hope the sampling continued and this manuscript can be updated with that data prior to publication.132: please do not call these depth shallow and deep. 40 cm is arguably not deep. In times of LLMs scraping manuscripts such definitions will give a wrong assessment of "deep" processes. I ask you to simply use the depth and talk about "20 cm and 40 cm depth samples".
180: what was the cut off in lc-excess?
189: Citation should be the manuscript that defined equation 4, which is Kirchner
204: I think you should provide the standard deviation here
3.5: I believe that Allen et al. calculated for the SOI the “non-fractionated” water isotope ratio by back calculating where on the LMWL the water sample is located using Benettin et al. (2018). This would need to be done in this study here as well, because the soil water samples have been partly evaporated.
219: unclear what Y, A, and B represent. The "i" likely represents the bootstrap models, but I think its definition is missing
Figure 4: it's unclear why you would show your data as boxplots. You sample every two weeks to then bulk all the results into seasons? You lose so much information this way and I would highly recommend to show the data as time series.
269: you are describing temporal dynamics between precipitation input and soil water isotopes. I think that a revised figrue 4 should show these temporal dynamics. Please add precipitation isotope time series to the new figure 4.
272: what does "stabilized" mean in this context? From figure 5, I would think that you mean that the values became all the same across 20 and 40 cm and for BW and TBW. If so, I don't think that stabilized is the right word.
277: due to the know density of water, you should provide the water content as volume percentage. Grams per 100 cm3 is an uncommon unit.
Figure 5: this is a very busy figure and I do not know the benefit of the trend lines. Why are these amplitudes and sinusoidal fits done? I understand that these are usually used to infer Kirchner's young water fraction. However this is not done here and I do not see a benefit of these fitted lines. Again, unit of water content should be adjusted.
Figure 6: again, there is quite a loss of information when the data gets grouped to monthly averages. I further think that a time series with SOI on the y-axis is a more informative visualization than using a heatmap.
346: I do not think that the isotope values were corrected for evaporative fractionation, which is why I don’t think these interpretation necessarily hold in this paragraph.
Figure 7: What is the difference between this graph and Figure 6?
388: I do not think that comparing the TBW with any of the xylem data from the referenced studies across the world in entirely different climates is meaningful at all.
397: I have not seen any transit times reported in the results
522: Why “despite”?
525: “meteoric origin” sounds awkward. Is not all water that you sampled of meteoric origin? What else would potentially be another origin?
526: A bias could be that the evaporative signal is being diluted in the equilibration method, right?

Benettin, P., Volkmann, T. H. M., von Freyberg, J., Frentress, J., Penna, D., Dawson, T. E., and Kirchner, J. W.: Effects of climatic seasonality on the isotopic composition of evaporating soil waters, Hydrol. Earth Syst. Sci., 22, 2881–2890, https://doi.org/10.5194/hess-22-2881-2018, 2018.
Citation: https://doi.org/10.5194/egusphere-2025-3922-RC2

Jiri Kocum, Kristyna Falatkova, Vaclav Sipek, Karel Patek, Jan Hnilica, Michal Jenicek, Martin Sanda, Lukas Trakal, and Lukas Vlcek

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Short summary

The study employed a uniquely designed experimental setup to investigate how the dynamics of distinct soil water pools vary along an elevational gradient and how reduced snow accumulation at lower elevations influences soil water distribution compared to higher-altitude sites. A novel methodological approach was used to separate individual soil water pools, enabling a more precise characterization of the seasonal origin of soil water, potentially benefiting future research on plant water uptake.


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