Soil Deposition of Atmospheric Hydrogen Constrained using Planetary Scale Observations

Tardito Chaudhri, Alexander Karim; Stevenson, David S.

doi:https://doi.org/10.5194/egusphere-2024-3247

RC1: 'Comment on egusphere-2024-3247', Anonymous Referee #1, 20 Jan 2025

Soil deposition of atmospheric hydrogen constrained using planetary scale observations by Chaudhri and Stevenson

This manuscript uses the recently updated global NOAA H₂ dataset to help constrain the soil sink by latitude and season. The observational data are compared with what would be predicted using a prototype soil deposition scheme that applies current functions of moisture, texture, and temperature. Emissions, atmospheric chemistry, and atmospheric transport of H₂ are included. Discrepancies between predicted and observed atmospheric concentrations then identify shortcomings in our understanding of the budget, especially regarding the magnitude and seasonality of the soil sink. This research extends the Xiao et al (2007) study, both in time and in latitudinal resolution. The approach taken here seeks to take full advantage of the latitudinal distribution of the NOAA data sites, slicing the world into 64 latitudinal bands instead of 2 to 6, while meanwhile keeping computation costs low. The prototype deposition scheme was thoughtfully applied and utilize the most recent published works. There is a lot of information densely packed into this manuscript, providing a wealth of insights. This appears to be a novel approach to addressing the major uncertainties in the global atmospheric budget of H₂.

I only have a few minor recommendations, largely to support the readability of the manuscript.

1) Figure 1 shows the sites with different deposition rates, anomalous means, and late peaks. Can you please identify these stations so the reader can cross-compare with the NOAA dataset? This information can be provided in Supplementary Materials. There may be some local factors that can explain the statistically anomalous sites. For example, there may be local pollution sources, strong local soil sinks, variable sampling times, or potential sampling issues. Sites identified by your work might be tagged for further scrutiny. It would also be helpful to describe what is meant by ‘low’ vs ‘high’ deposition, and how this was assessed for each site.

2) Line 43. The Meredith et al., 2017 paper, appears to be the appropriate reference here, in lieu of their 2014 paper.

3) Line 101: “The seasonal H₂ signal does not depend significantly on zonal variations in local deposition”. Can you please clarify what is meant by this sentence? What does it mean for local deposition to vary across latitudes?

4) Line 153-154: In the model, the “long lifetime of H₂ compared with timescales of horizontal mixing in the atmosphere indicating that H₂ is reasonably well mixed across zonal bands”. Is this true for all latitudes, including the tropics which have a much larger circumference (and hence mixing time)? There can also be large variability within single latitudinal bands even without identified strong local deposition. (e.g., it appears there can be 30 ppb variation in the mean at specific latitudes, even those that have not been identified as anomalous).

5) “Line 224-226: “In particular, the seasonality due to soil temperature captures the strong seasonality of BF1 in the NH mid-latitudes, which has been identified in microbial laboratory studies (Smith-Downey, 2006).” This sentence may need to be reworded. The microbial laboratory studies reveal the temperature sensitivity of H₂ deposition, but do not themselves identify the strong seasonality in NH mid-latitudes.

6) Line 311-313. “Without a seasonally varying soil uptake, zonal mean surface H₂ would peak with a similar amplitude during the late summer to early autumn in both the NH and SH extra-tropical regions”. Is this based primarily on estimated emissions, oxidation and mixing? What are the most important factors strongly influencing the modeled seasonality when soils are not included?

7) [optional] Lines 235-237. It would help the reader if the specific locations discussed are visually identified in figures 8a and 8b, such as with a circle, arrow or by indicating “areas of darker blue shading”.

8) Lines 240-243 “In the NH, better agreement is achieved where this lag and the amplitude of the seasonality of the peaks are decreased with increasing latitude; the peak at 52N (D) agrees well with BF1 for a ~1 week lag and a 60% multiplier”. This statements suggests a steady decrease in the amplitude and lag time as you go towards the poles. Is this true, or does it refer to a specific high latitude band?

9) Lines 264-265: “enhanced deposition with a maximum of around 0.2 Tg yr-1/ lat focused in the NH mid-latitudes, and peaking in both hemispheres between December and February (Fig 9b)”. A Dec-Feb peak in deposition is not obvious in Figure 9b.

10) Lines 322-323. “In the SH the prototype scheme results in too-high surface mixing ratios in the annual mean, and differences in phase and a weak amplitude of the seasonality in the Southern tropics and subtropics”. Are your results consistent with a small but widespread additional sink in the Southern Hemisphere, such as a weak ocean sink? This may be too speculative for the manuscript, but it may be helpful to question the role of the oceans in the H₂ budget.

Citation: https://doi.org/10.5194/egusphere-2024-3247-RC1

RC2: 'Comment on egusphere-2024-3247', Anonymous Referee #2, 28 Jan 2025

Tardito Chaudhri and Stevenson present a study to better constrain the soil sink of atmospheric H₂, a critical yet highly uncertain component of the global H₂ budget. The authors employ a relatively simplified 2D (latitude-height) model and leverage NOAA observations of atmospheric H₂ to test existing modeling schemes and identify numerical modifications that improve the model-observation agreement. Overall, I am very supportive of the goal of the work: utilizing observational data and the latitudinal/seasonal variation of H₂ to evaluate soil uptake schemes, extending the analysis of Paulot et al. (2024, ACP) with a simpler and more flexible model. (I suggest the authors better articulate this work's distinctions and advancements compared to Paulot).

However, there is a major scientific flaw in the current implementation of the soil sink. The authors model the soil sink based on bacterial activity as a function of moisture f(s) and temperature g(T). However, this approach confuses bacterial activity (the potential sink) with the actual soil sink, which is modulated by both biological activity and diffusion processes—the rate at which H₂ becomes available to bacteria. This fundamental distinction (and interplay) between diffusion (a physical process) and bacterial activity (a biotic process) has been known for decades (e.g., Yonemura et al., 2000, Tellus B; Smith-Downey et al., 2006, GRL; Yashiro et al., 2011, ACP; Ehhalt et al., 2011, 2013, Tellus B and more recently by Bertagni et al. 2021, GBC, which showed the critical role of diffusive limitations in humid regions). Although the authors reference some of these works, they have lost a non-negligible component of the processes involved.

By neglecting diffusion, the authors exclude a critical physical factor that substantially impacts soil sink representation. This omission introduces large biases in calculated soil uptake rates, particularly in humid temperate and tropical regions with more pronounced diffusion limitations. As a result, both the prototype scheme and the subsequent best-fit scheme are fundamentally flawed, rendering the conclusions unreliable. Addressing this issue requires incorporating diffusion into the soil sink parameterization and rerunning the entire modeling framework (prototype and best fit).

In addition to this central issue, the clarity and structure of the manuscript could be significantly improved. Just as examples: i) the results in terms of atmospheric concentrations are presented before introducing the underlying soil sink calculations, which disrupts the logical flow of the paper; ii) section 5 on the best-fit scheme includes mathematical equations that appear simultaneously overly simplistic and excessively detailed for inclusion in the main text (appendix?); iii) the abstract could be simplified to be less technical.

In conclusion, although the authors’ goal is valuable and the topic of significant scientific interest, the major flaw in the representation of the soil sink —the omission of diffusive processes— invalidates the study’s results. I recommend a comprehensive revision of the soil sink modeling framework to address this issue, along with a restructuring of the manuscript for clarity. At this stage, I cannot recommend publishing the paper in its current form. I am hence refraining from providing minor suggestions.

Citation: https://doi.org/10.5194/egusphere-2024-3247-RC2

CC1: 'Preliminary Reply on RC2', Alexander Tardito Chaudhri, 30 Jan 2025

Dear Reviewer,

This is a preliminary reply while I implement your valuable suggestion, and prepare revisions and detailed response.

Thank you for your insightful comment regarding diffusivity. I have attached an updated version of fig.4 where normalised soil diffusivity for different soils -- based on the Moldrup et al. (2013) version communicated in Bertagni et al. (2021) with soil parameters also communicated in the latter paper – is plotted. To maintain some simplicity (in the spirit of the paper – where we restrict ourselves based on the limits of available observations) this is plotted considering a constant diffusion in free air and neglecting the inclusion of diffusive barriers – which would particularly reduce high diffusivity at low soil moisture contents. The role of a diffusive barrier is carefully discussed in Bertagni et al. (2021).

Therefore, we consider soil diffusivity proportional to (porosity)^2 (1 – soil moisture content)^(2 + 3/b), where porosity and b are communicated for different soil textures is discussed in the aforementioned paper. Diffusivity is limited as soil moisture content increases. When we consider the three terms in the prototype scheme, uptake is prevented for very dry soils due to the low moisture limit on biological uptake. At higher moisture content restricted diffusivity and weaker biological uptake compound to reduce uptake – this slightly decreases the soil moisture content of peak uptake. Our original intention to neglect this term was based on the resulting uptake still having the form of: none below a low-moisture limit; then a sharp uptick in uptake with moisture; then a decline as moisture continues to increase. Of course, we scale our prototype deposition to achieve a global 57.2 Tg/yr avg.

When we include this in our zonally integrated prototype scheme, we see that – as you predicted – deposition is reduced in damp deep-tropical soils and this changes some of the distribution in the global uptake. Seasonality in the uptake is still dominated by f(soil moisture) in the tropics and h(soil temperature) in the extra tropics, this form of diffusivity contributes some changes in seasonality in the dampest soils (deep tropics, and some mid-latitudes). I will redo the integrations and produce a more detailed response.

Thank you again,

ATC

Citation: https://doi.org/10.5194/egusphere-2024-3247-CC1

EC1: 'Comment of reviewer #3 on egusphere-2024-3247', Jens-Uwe Grooß, 27 Feb 2025

AC1: 'Author Comments -- Final Response', Alexander Tardito Chaudhri, 24 Mar 2025

Dear the referees and the editor, Jens-Uwe Grooß, and for the interest of the community discussion,

Thank you all for your insightful and helpful comments and recommendations to improve our manuscript. In the revised manuscript we have included diffusivity in the prototype deposition scheme. This change required re-running each simulation in the paper and there have been changes to figures and text throughout to reflect this change. In general, as RC2 suggested, diffusivity has the strongest effect effect in moist soils – particularly in the tropics. Additionally, we have made many text and figure changes to improve readability and provide more clarity for our results and analysis.

Please find detailed responses to individual reviewer comments below.

Yours sincerely and with appreciation,

Alex Tardito Chaudhri

Responses to RC1:

1) Figure 1 shows the sites with different deposition rates, anomalous means, and late peaks. Can you please identify these stations so the reader can cross-compare with the NOAA dataset? This information can be provided in Supplementary Materials. There may be some local factors that can explain the statistically anomalous sites. For example, there may be local pollution sources, strong local soil sinks, variable sampling times, or potential sampling issues. Sites identified by your work might be tagged for further scrutiny. It would also be helpful to describe what is meant by ‘low’ vs ‘high’ deposition, and how this was assessed for each site.

Thank you for this request to help the reproducibility and broaden the application of this work. We have included an extensive table in the appendix section recording each of these values. The low versus high deposition was simply a way of coding the stations against the prototype scheme based on a local 0.2 g/m^2/yr deposition criterion. This is explained both in the caption and in the appendix table.

2) Line 43. The Meredith et al., 2017 paper, appears to be the appropriate reference here, in lieu of their 2014 paper.

Thank you for this recommendation, yes that is a more appropriate reference.

3) Line 101: “The seasonal H₂ signal does not depend significantly on zonal variations in local deposition”. Can you please clarify what is meant by this sentence? What does it mean for local deposition to vary across latitudes?

To make this clearer the sentence has been changed for more explanation:

(ln 154) The small spread of the phase of the seasonality of \chem{H_2} observations from the best-fit shows that the mid-filtered signal varies more with the latitude of sites than due to zonal variations in local deposition.

4) Line 153-154: In the model, the “long lifetime of H₂ compared with timescales of horizontal mixing in the atmosphere indicating that H₂ is reasonably well mixed across zonal bands”. Is this true for all latitudes, including the tropics which have a much larger circumference (and hence mixing time)? There can also be large variability within single latitudinal bands even without identified strong local deposition. (e.g., it appears there can be 30 ppb variation in the mean at specific latitudes, even those that have not been identified as anomalous).

Thank you for pointing out the problems with this assumption. We have added some explanation that at certain latitudes there is observed zonal variation c.5% of the annual mean:

(ln 189) Additionally, we note the long average lifetime of H_2 compared with timescales of horizontal mixing in the atmosphere (e.g. {pierrehumbert1993}) indicating that H_2 is reasonably well mixed across zonal bands. However, this assumption is challenged at latitudes with particularly strong sources and sinks. For example, there is a spread of c.5% in non-anomalous annual mean mixing ratios around 40N (Fig. 1b).

5) “Line 224-226: “In particular, the seasonality due to soil temperature captures the strong seasonality of BF1 in the NH mid-latitudes, which has been identified in microbial laboratory studies (Smith-Downey, 2006).” This sentence may need to be reworded. The microbial laboratory studies reveal the temperature sensitivity of H₂ deposition, but do not themselves identify the strong seasonality in NH mid-latitudes.

Hopefully this is more accurate in 2 sentences: one on capturing BF1; one on mid-latitude seasons and soil temperature sensitivity. Becomes:

(ln 262) The seasonality of the prototype scheme, (fgh)', reproduces some key features of BF1. In particular, the prototype scheme captures the strong seasonality of BF1 in the NH mid-latitudes. There, seasonality is driven by the sensitivity of microbial activity to variation in soil temperature, which has been identified in laboratory microbial studies {smith-downey2006}.

6) Line 311-313. “Without a seasonally varying soil uptake, zonal mean surface H₂ would peak with a similar amplitude during the late summer to early autumn in both the NH and SH extra-tropical regions”. Is this based primarily on estimated emissions, oxidation and mixing? What are the most important factors strongly influencing the modeled seasonality when soils are not included?

Rewritten to identify the inter-hemispheric symmetry in the atmospheric production and destruction:

(ln 368) Without a seasonally varying soil uptake, the seasonality of zonal mean surface H_2 would be dominated by the seasonality of atmospheric H_2 production and oxidation. H_2 concentrations would peak with a similar amplitude during the late-summer to early-autumn in both the NH and SH extra-tropical regions (Fig. 3); the seasonality of the deposition induces a stronger amplitude and earlier peak in the NH H_2 signal.

7) [optional] Lines 235-237. It would help the reader if the specific locations discussed are visually identified in figures 8a and 8b, such as with a circle, arrow or by indicating “areas of darker blue shading”.

Thank you for this helpful suggestion. Clear arrows (Fig. 8) have been added to show where the adjustments are that are discussed in the text. Also, with the updated prototype deposition scheme there are only 3 latitudes with peaks in seasonality – this makes the discussion somewhat clearer too (lns 268-290).

8) Lines 240-243 “In the NH, better agreement is achieved where this lag and the amplitude of the seasonality of the peaks are decreased with increasing latitude; the peak at 52N (D) agrees well with BF1 for a ~1 week lag and a 60% multiplier”. This statements suggests a steady decrease in the amplitude and lag time as you go towards the poles. Is this true, or does it refer to a specific high latitude band?

Thank you for pointing this out. Originally the discussion referred just to the peak amplitude latitudes. This has been extensively and carefully re-written to make sure the interpretation is clear:

In Fig. 8c the latitudes of peak amplitude of seasonality in the prototype scheme are isolated for optimised agreement with BF1 under adjustments to the seasonality multiplier and offset. In both deep tropical peaks (A,B), better agreement occurs for a lag of two to three months. Additionally, the strongest agreement occurs for a weaker seasonality in the SH tropical peak (A). In the NH mid-latitudes better agreement is achieved with a one week lag in the peak deposition at 52◦N (C).

Figure 8c shows that RBF is minimised for decreases in the amplitude of the seasonality at A, B, C. However, this arises as BF1 is unconstrained by the seasonality in the prototype scheme, instead assuming variations in deposition spread across latitudes. By integrating the deposition seasonality across wider latitude bands, Figs. 8d,e show a lag and increases in amplitude of seasonality between 30◦S and 30◦N; whereas Fig. 8f shows differences in the seasonal signal in the NH mid-latitudes, but with a similar amplitude (cf. Figs.7a,b).

9) Lines 264-265: “enhanced deposition with a maximum of around 0.2 Tg yr-1/ lat focused in the NH mid-latitudes, and peaking in both hemispheres between December and February (Fig 9b)”. A Dec-Feb peak in deposition is not obvious in Figure 9b.

Thank you for pointing out that that was not clear. This figure has changed slightly in the new version due to the new simulations. The figure has been replotted with different contour intervals that make these peaks clearer to see. The same intervals are now used in Figs. 5,7,9.

10) Lines 322-323. “In the SH the prototype scheme results in too-high surface mixing ratios in the annual mean, and differences in phase and a weak amplitude of the seasonality in the Southern tropics and subtropics”. Are your results consistent with a small but widespread additional sink in the Southern Hemisphere, such as a weak ocean sink? This may be too speculative for the manuscript, but it may be helpful to question the role of the oceans in the H₂ budget.

This has been changed to reference Paulot et al. 2024 who revise SH ocean emissions (included in their supplementary material).

(ln 380) Simulations in the toolbox model produce too-high H2 mixing ratios in the SH, where Paulot et al. (2024) have reduced SH net ocean emissions in the extra-tropics compared with emissions used in this study. However, we show how differences in phase and a too-weak amplitude of seasonality in the Southern tropics and subtropics may be resolved by the choice of the deposition scheme.

Responses to RC2:

I suggest the authors better articulate this work's distinctions and advancements compared to Paulot [Paulot et al. (2024, ACP)]

In the introduction we provide a clearer link for how this work builds on and complements that excellent study:

(ln 52) Our results and analysis also complement Paulot et al. (2024), who have revised H2 emissions and deposition estimates to better-reproduce the H2 distribution and seasonality of clustered observations. They identified major gaps in our understanding of soil removal of H2. We analyse the soil uptake arising from a model constrained to reproduce a latitude varying H2 seasonality, while relaxing assumptions on the estimated soil uptake.

In the analysis of observations, we highlight a key distinction:

(ln 156) We exploit a H_2 seasonality that continuously varies with latitude as a distinct constraint compared to Paulot et al. (2024). This constraint allows us to test assumptions in the prototype deposition scheme at higher meridional resolution (Sec. 5).

In the conclusion we also refer to their revised ocean emissions.

By neglecting diffusion, the authors exclude a critical physical factor that substantially impacts soil sink representation. This omission introduces large biases in calculated soil uptake rates, particularly in humid temperate and tropical regions with more pronounced diffusion limitations. As a result, both the prototype scheme and the subsequent best-fit scheme are fundamentally flawed, rendering the conclusions unreliable. Addressing this issue requires incorporating diffusion into the soil sink parameterization and rerunning the entire modeling framework (prototype and best fit).

Thank you for identifying this important point. Further to my (ATC) earlier reply in the community discussion, I have implemented a representation of diffusion limiting uptake into the prototype deposition scheme. This required a rewrite of former Sec. 3 (now Sec. 2 on the prototype scheme) that is too long to include here. As you suggested, the change to this new prototype scheme had an impact on uptake in moist soils (mostly tropical).

After re-running all simulations and analysis, the use of the new prototype scheme required changes to all figures (except the example decomposition at Mace Head). In Fig. 6, we show how strongly this inclusion of diffusion contributes to seasonality. Text changes reflect the changes. However, while BF1 and BF2 are changed a small amount, the new deposition scheme was still unable to produce the SH Feb-Apr and NH Aug-Oct peak uptake in the tropics in each hemisphere required to reproduce the best-fit observed seasonality.

Additionally, in the appendix we have included a comparison of soil moisture dependent uptake terms in the prototype scheme under 30-day rolling average and daily average inputs. This is mentioned in the text:

A comparison of f and g with soil moisture varying on 30-day and daily timescales is provided in Fig. A1. The use of monthly average ERA5 data can lead to slightly faster uptake rates in semi-arid regions (cf. Bertagni et al., 2021) but does not substantially affect the seasonality.

In addition to this central issue, the clarity and structure of the manuscript could be significantly improved. Just as examples: i) the results in terms of atmospheric concentrations are presented before introducing the underlying soil sink calculations, which disrupts the logical flow of the paper; ii) section 5 on the best-fit scheme includes mathematical equations that appear simultaneously overly simplistic and excessively detailed for inclusion in the main text (appendix?); iii) the abstract could be simplified to be less technical.

Thank you for these suggestions regarding clarity and structure. We have moved the equations showing the test for anomalous station time-series and ratio of RMS error in seasonality versus BF1 to the RMS BF1 seasonality to the appendix.

We have made text changes throughout to boost clarity and readability.

In the abstract we have identified specific months that we are comparing in order to make our fundings easier to understand.

Responses to RC3:

While the proposed observation-based methodology offers valuable insights into H₂ deposition, several critical concerns must be addressed to ensure the robustness of the findings. First, the sensitivity of the “best-fit” estimates to assumptions about the spatial and temporal distribution of the OH sink remains unclear. Given that OH chemistry is derived from a single model with prescribed H₂ and CH₄ concentrations, how can the deposition sink be effectively disentangled from the chemical sink? Could variations and uncertainties in OH fields also influence the zonal-mean seasonality? Despite H₂’s relatively long lifetime with respect to OH, the spatial and temporal heterogeneity of OH should be considered interactively. Second, beyond microbial uptake and soil diffusion, could other processes influence deposition? For instance, could atmospheric turbulence and its variability across latitudes contribute to seasonal variations? Third, how does the 2D model compare to seasonal patterns from 3D simulations? Would leveraging 3D model outputs (e.g., Sands et al., 2023) provide a more appropriate framework for optimizing deposition? Fourth, strengthening the manuscript’s impact would require presenting site-specific seasonality for all measurement sites, not just Mace Head. This would better highlight regional differences and their connection to zonal-mean anomalies. Finally, for the method to be reproducible, it would be best to elaborate on the rationale behind specific assumptions and thresholds, as well as describe the uncertainties on derived quantities of the filtering algorithm (e.g., phase and amplitude).

Thank you for these insightful and helpful questions, we have integrated many of these into the textual changes in the revised manuscript. We have attempted to answer these in the responses to individual comments (below) or in responses to R1 and R2 (above).

Line 55: “we assume that the general effect of these fluxes is well approximated when they are modelled in their zonal-mean monthly-mean”. How valid is this assumption? Can you please elaborate.

This is an important point, and we have extended the discussion of these assumptions in the model formulation section:

e.g. (ln 190) However, this assumption is challenged at latitudes with particularly strong sources and sinks. For example, there is a spread of c.5% in the non-anomalous observed annual mean mixing ratios around 40◦N (Fig. 2b).

Line 71: Can you please elaborate on the ‘spatial filtering’ used?

Thank you for this request, we have included more explanation:

(ln 174) The width of the filter was chosen to produce a smooth best-fit between observations that preserves the distinct patterns with latitude that vary over scales c.10◦N.

Figure 1 caption (also Line 95-97): What is the rationale behind choosing 20 ppb for the RMS error threshold for it to be an anomaly? Same for the Gaussian filter of 𝜎=5 degrees latitude.

Further to the previous reply, the criterion to reject anomalous sites isolated timeseries where 1^st and 2^nd harmonics could not easily be fitted. This was checked with inspection. Generally, these sites suffered inconsistencies in the data not seen in the other sites, but we do not attempt a deep discussion or speculation as to why this might be the case. In the appendix we have included an extended discussion of the equation used to identify these and shown the RMS error in a table for each site.

(ln 148) Anomalous results are categorised where this RMS error is greater than 20 ppb (Equation B1, sites indicated in Fig.2). By inspection, this criterion effectively excludes five sites where harmonics could not be identified (such as in Fig. 3).

Line 78-84: How sensitive are your findings to assumptions on timescales (<30 days and 1 year) for these filters? How robust is this method if other filtering methods are applied (e.g., singular spectrum analysis – SSA, Seasonal Trend decomposition using Loess – STL)?

This is a very interesting question and would be relevant for future research that could attempt to decode the seasonal signal at a finer resolution, or to infer regional fluxes by relating wind-direction to the sub-seasonal noise. However, the data are rather limited due to their sampling frequency, typically every one or two weeks (ln 120), and differences in sampling conditions at different sites, so analysis on shorter timescales is complicated. This being said, the data are generally strongly dominated by the change on the annual timescale, with strong consistency over the 2012-2018 time period (where these data existed), so this harmonic is particularly useful for this analysis.

Line 101: “The seasonal H₂ signal does not depend significantly on zonal variations in local deposition.” Why do you think this is?

We justify this as zonal mixing timescales are much shorter than the seasonal timescale, the bulk mass of H_2 divided by emission and production rates, and the average lifetime of H_2 in the atmosphere. However, please see reply above where we identify c.40N as having more variation because of stronger fluxes (more land surface and anthropogenic activity).

Line 106-108: “This supports the assumption that the deposition into soils is dominated by the larger land area of the NH, where this soil sink exceeds anthropogenic emissions and the net source of H₂ from atmospheric chemistry (Paulot et al., 2021).” Can this be attributed as well to variations in OH in NH, tropics, and SH?

Thank you for this question, we include a simulation where annual mean deposition velocities are used (Fig. 4 -dotted) to demonstrate the seasonality that would occur without seasonally varying uptake. In the revised manuscript, we have improved the clarity of the discussion on this:

The importance of deposition seasonality is indicated in Fig. 4: a simulation with the same annual deposition flux, but without deposition seasonality, (dotted line) fails to reproduce key features of the planetary H2 seasonality. In the simulation with H2 seasonality driven by emissions, deposition and atmospheric chemistry (solid line), in both hemispheres H2 peaks in late-summer to early-autumn – February-March in SH and August-September in NH – with similar zonal-mean peak amplitude 10-15 ppb to the observations in the mid-latitudes. Seasonally varying deposition is required for NH H2 to peak earlier in the year and to resolve the distinct latitude bands of peak seasonality. Alternately, prototype deposition seasonality has little impact in the SH, due to the relative lack of land. In the SH, the seasonality of H2 is mainly controlled by atmospheric chemistry.

Line 129-140: How large is the influence of diffusion into soil on deposition relative to microbial activity? Aren’t these processes coupled in reality?

Thank you for pointing this out. In the revised manuscript we have included a representation of diffusion into the prototype deposition scheme and explored the consequences of this in detail. In Figure 6, we now include the coefficient of variation of each of these terms and identify how diffusion (g) varies as fraction of its annual mean with latitude. It is most important in moist tropical soils.

Line 155-160: While the 2D model is justified, what would be the sensitivity to the best fit when 3D models are used?

This is a very relevant question. Currently, this is complicated by current poor constraints on deposition and emissions, so very few models have simulated H_2 with emissions and interactive deposition (an example would be Paulot et al., 2021) – but such models have tended to struggle or fail to capture the observed seasonality with high and low mixing ratios occurring too early in the year. Instead, models have tended to impose a surface boundary condition that can vary based on observations (such as the UKCA instance – that had been used in Sand et al. 2023 – from which we sourced chemistry fluxes).

Line 176-180: What is the physical rationale behind the choice of assuming that fluxes are independent to H₂ mixing ratio?

The attempt is to control fluxes except the deposition, where atmospheric production and destruction of H_2 are linked to a number of coupled reactions and feedbacks (e.g. Warwick et al., 2023) that would not be suitable to attempt to capture in this toolbox model. Additionally, in each of our experiments, H_2 mixing ratios did not deviate substantially (as a fraction of their absolute value) from the observations (related to BCs of input data). By assuming unchanged chemistry fluxes, we were then able to calculate BF1 and BF2 (where H_2 was constrained to follow observations) and compare these to the prototype experiment. We have made textual changes to clarify our methods and justifications for different assumptions.

Line 197-200: Interesting finding regarding the cross-term. Why do you think this is the case?

This is to do with seasons in tropics – similar temperatures and similar h(T) through the year but changing soil moisture with dry/rainy seasons; versus extra tropics – temperatures vary greatly.

Line 217: How sensitive would the best fit to assumptions/representations of P and rD, and M?

This is a very relevant point for future research – particularly as our understanding of H_2 production by atmospheric chemistry advances. As the soil uptake is generally considered to account for 70-80% of the H_2 uptake, and we find that seasonality is comparable with the annual mean, changes in the atmospheric loss would not have a strong influence on the conclusions of this work. We do provide a discussion of sensitivity to emissions (ln 310). We tune M based on reproducing observed SF_6 from an emissions inventory. However, beyond general arguments about changing meridional mixing rates, exploring the role of mixing in depth would require some representation at least of synoptic weather, or in the case of turbulence the role of diurnal variations in boundary layer thickness and mixing may be important to investigate deeply.

Citation: https://doi.org/10.5194/egusphere-2024-3247-AC1

AC2: 'Comment on egusphere-2024-3247', Alexander Tardito Chaudhri, 24 Mar 2025

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Soil Deposition of Atmospheric Hydrogen Constrained using Planetary Scale Observations

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