Review for ‘Global atmospheric hydrogen chemistry and long-term source-sink budget simulation with the EMAC v2.55 model’ by Surawski et al.

This manuscript presents the implemention of a hydrogen flux scheme in the EMAC model. Model results are compared with H2 observations from the NOAA network. The EMAC model successfully captures global H2 mixing ratios, including the interhemispheric gradient and much of the seasonality observed at remote stations. The incorporation of a hydrogen flux scheme into EMAC represents a significant advancement, as it allows for a more comprehensive representation of CH4-H2-OH chemical feedbacks. These interactions are crucial for understanding the atmospheric and climatic implications of potential increases in hydrogen levels.

The paper is generally well-written and well-structured, and I would support publication after my comments below are addressed.

Specific comments.

Line 6: remove comma after scheme

Line 14: ‘by realistically simulating OH in the atmosphere’ – after reading the paper, the support offered for this statement is a comparison of the tropospheric chemical lifetime of methane in EMAC (8.9 years) with an ‘observational estimate’ of 9.1 years from Holmes et al. (2013). Could the authors confirm that these two values are directly comparable (i.e. represent the same loss mechanisms)?  The 9.1 yr value from Holmes et al. appears to come from Prather et al. 2012 – and is an estimate of the total atmospheric lifetime for methane (i.e. includes losses to the stratosphere and soil). The observational value for methane lifetime against OH based on methyl chloroform data is quoted as 11.2 years in Holmes et al. (2013) (and is also taken from Prather et al. 2012).

Line 49: ‘We find that correctly representing the oxidising capacity of the atmosphere is critical for predicting H2 mixing ratios and their spatio-temporal variability’. I’m not sure that this has been done – you have captured observations of H2 mixing ratios using the model’s OH and representations of the other sources/sinks, but you have not shown how sensitive H2 is to differences in OH? Spatially, and seasonally, H2 will likely be very sensitive to the soil sink – which is estimated to be significantly larger than the OH sink, as well as photochemical production of H2.

Line 64: Just a note that diurnal variability is seen in longer-lived gases at the surface due to diurnal variations in boundary layer height and the resulting changes to mixing (e.g. H2 measurements form Weybourne - Forster et al, Tellus B, 2012).

Line 66: I think there should probably be an acknowledgement here that in 2020, methane was (and still is) not in steady-state in the atmosphere. Therefore a simulation run to steady-state using repeating 2020 emissions is not fully representative of 2020 atmospheric conditions.

Line 71: ‘swamps or wetlands’: these 2 words are not interchangeable - swamps are a type of wetland. Maybe change to ‘wetlands other than bogs’ ?

Line 74: Change ‘swamps’ to ‘wetlands’ here (see comment above)?

Line 90: Could the authors clarify if the emissions for non-GHG species are transient or for a single year/climatology?

Line 86: Do the RETRO/GFED databases include estimates for H2 emissions? Usually, H2 emissions are obtained by using H2:CO emission factors to scale CO emission inventories – has the same been done here, and if so which emission factors are used?

Line 100, Section 2.2: It would be nice to see some analysis of the soil deposition velocities calculated within the model, including geographical variation etc.. Have the authors compared model results to any deposition velocity measurements?

Line 129: We are told the scaling factor ‘A’ is adjusted to obtain a global mean deposition velocity of 0.033 following Yashiro et al. 2011. What was the reason for choosing this value to scale to? The Yashiro study tuned their global soil uptake to optimise the model agreement with observations (by adjusting their inactive layer thickness, delta). Also, what value of ‘A’ was required for the adjustment – i.e. was a large or small adjustment required?

Line 146: Does the soil uptake calculated vary with time during the simulation, or is the ERA5 data averaged over a set period?

Figure 1: Much of the globe is a similar shade of green. You can see the IHG in the modelled data – but all observed data looks the same/very similar on this colour scale. Would it be possible to adjust the colour scale so that it is easier to discern differences in H2 between observational sites and see a bit more structure?

Figure 2: It would be helpful to have some further info on the station rather than just the station code in this figure, e.g. latitude/longitude. I think it would also help the reader if the plots were ordered by latitude going from north-south rather than alphabetical order. This would make it easier to discern latitudinal differences in seasonality and how the model is performing.

Line 225-230: As mentioned above, it’s not clear to me that the 8.9 and 9.1 year lifetimes quoted are comparable. The EMAC methane lifetime of 8.9 years is within the range of the other models referred to by Yang et al. 2024 that Yang argues underestimate the methane lifetime (8.3 to 9.5 years).

Line 247: ‘The small long-term trend in H2 captured by the model’ – I thought this was a steady-state simulation with methane and hydrogen emissions held constant (I’m not sure if non GHG emissions are transient)? We know CH4 (which is a source of H2) is increasing in the atmosphere, and this will not be captured in a steady-state simulation.

Line 254-5 (and elsewhere wherever bottom-up is mentioned): The authors refer to bottom-up and top-down estimates for the global soil sink (55-60 Tg/yr and 85-88 Tg/yr respectively). I think it is worth pointing out that many of the ‘bottom-up’ studies have scaled the global soil sink uniformly to capture H2 atmospheric observations (which makes them top-down global soil sink estimates from my perspective - although the geographical variability will be bottom-up). The only truly bottom-up global soil sink estimate I am aware of that did not scale the soil sink to match total sources is Sanderson et al. 2003.

The ‘top-down’ studies that are referenced are HD and inversion studies in which the larger soil sink was balanced by larger estimates of the photochemical production of H2 to close the H2 and HD budgets. The impact of including a geological H2 source in these studies is not clear without further information on the spatial/temporal variability and isotopic composition of the geological source.  The way this sentence is phrased – ‘the unaccounted for source almost bridges the gap between bottom-up and top-down estimates’ implies that the larger soil sink estimates are consistent with the existence of a geological source, which I don’t think can be assumed.

Line 280-1: ‘the CH4 chemical lifetime in excellent agreement with observational estimates’ – see my comments above about the CH4 lifetime.

Line 281: ‘We conclude that correctly simulating the oxidising capacity is a key requirement for high accuracy simulation of H2’ – I’m not sure why OH is emphasised here above other sources/sinks in the H2 budget.

Overall comment: This paper demonstrates the usefulness of a flux driven model for hydrogen and methane in simulating global hydrogen mixing ratios. The discussion is well written and clearly outlines the state of this model and its usefulness for future simulations. I support the publication of this paper, provided the comments below are considered.

Specific comments:

Title - ‘long-term source sink budget simulation’ is slightly misleading, given the input emissions for hydrogen are fixed to the year 2020 (but taken from the year 2000 in the RETRO dataset). I would suggest changing this title to reflect the actual simulation, or adding a comment discussing the trend in the deposition sink over the period.

Line 4: ‘Long-term global simulations were performed, with a horizontal resolution of 1.9 degrees. The results of this simulation are compared with’. Same comment here regarding ‘long-term’.

Line 6: Clarify that the soil sink is not the only sink present (as it currently reads), but that there is also a chemical sink for hydrogen in the model.

Line 10: Here, and later in the paper, discussion of ‘direct anthropogenic perturbation’ could be expanded. Terminology such as ‘unpolluted air masses’ - see Derwent et al. 2023 (doi: 10.1016/j.atmosenv.2023.120029) may read better. I think the paper could benefit from a discussion (or an additional figure of the emissions input such that sites near high emission regions can be clearly identified) of how it was determined which sites fit this criteria for being background/ undisturbed stations. This discussion regarding sites near high emission regions could also benefit from a statement on the long lifetime of hydrogen. 

Line 15: Remove ‘realistically’.

Line 38: State that all three species listed are radiatively active, not just stratospheric water vapour.

Line 39: Change ‘can’ to ‘may’. The impact of hydrogen on aerosols is highly uncertain currently.  In the next line ‘Arising from these observations’ should be changed to ‘Arising from these modelled results’ or similar.

Line 58: Link the sentences on spin-up to steady-state. In the intermediate sentence here, expand upon the issues which arise from prescribed boundary conditions. This is key to the benefits of this model simulation and should be highlighted.

Line 67: The COVID-19 pandemic in 2020 could first be mentioned here to clarify that emissions are estimates without lockdowns. It may also be useful to clarify here that although interannual variability for emissions is removed, there is still meteorological variability (and potentially other sources of variability?).

Line 70: Is this methane simulation published? If so, please cite this publication here. If not, a justification of this statement and further discussion on the methane representation is needed.

Line 82: Based on these slightly older emissions, a more detailed discussion on the comparison between this dataset and those used in more recent literature would be beneficial. There is mention later on of Paulot et al. (2021), but there is also the slightly updated values in Paulot et al. (2024) (https://doi.org/10.5194/acp-24-4217-2024) . This paper, alongside results presented in Sand et al. (2023), could also be added to Table 2.

Line 85: There have been changes in hydrogen emissions in the last few decades (see Paulot et al. 2021 and 2024). Following on from above, a more direct comparison between the dataset used in this paper and in the literature is needed.

Line 90: Include a sentence on the aerosol set-up used in the model.

Line 139: Rephrase the threshold moisture content to clarify that there is no uptake in the top, dry layer in the model. 

Figure 2: The line colours on this plot need to be more distinctive. A suggestion here is to split the stations into northern and southern hemisphere and to add lines to indicate January 1st of each cycle. This plot also demonstrates the changes in the observations in the period leading up to 2020. There has been an increase in background hydrogen concentrations in that decade, evident in the observations shown in sites such as SPO and PSA in Figure 2. The model does not capture this increase, due to emissions being fixed at one year. This is interesting, as it shows that this may not be related to any changes in the hydrogen soil sink over this period (I am assuming these interannual changes are simulated in this run, but this should be clarified).

Line 191: Or related to uncertainty in the soil sink? Broadly the soil sink is considered to be the most uncertain part of the hydrogen budget, however in Table 1, the uncertainty is very low. Comment on how this uncertainty was calculated and why it differs from other budgets.

Line 198: ‘from’ Zimmerman et al.

Line 218: Can a comparison be made to more up-to-date literature than Yashiro (2011)?

Line 227: Yang et al. (2025) is now published I believe as 10.1029/2024GL112445

Line 229: The 9.1 years estimate from Prather et al. (2012) states that “The atmospheric lifetime for a process is defined properly as the total atmospheric burden divided by total losses”. Therefore, comparing this estimate of the atmospheric lifetime to the tropospheric chemical one from this model is not accurate. Please clarify this difference and discuss how this model compares to the discussion on Yang et al. (2025) with the correct value. Yang also discusses the chemical lifetime, with their model giving this value to be 11.4 years, compared to an observed methane lifetime of 11.2 years (plus minus 1.3 years), based on Prather et al. (2012). To corroborate the statements in the paper regarding the accurate representation of hydroxyl in EMAC, a figure similar to Figure 1 in Yang et al. (2025) might be useful to compare the OH modelled output with measurements. 

Line 248: The trend in OH over the 2010’s would be influenced by methane emissions which have been held constant.

Line 255: In the previous paragraph, it was stated that this simulation agreed well with bottom-up estimates. If the additional source of natural hydrogen is present, a large shift elsewhere in the budget is needed, however the very small uncertainties presented in the hydrogen budget for this work do not leave room for any shifts.

Figure B2: WIS appears to have the same number of observations (167) as the sites included in Figure 2. Is there a reason this is not included in that figure?

A discussion of Figure B3 would be beneficial.