Summary

The manuscript describes a new configuration for UKESM1 to simulate flux boundary conditions for both H2 and CH4 at the same time, with the goal to more accurately model their interactions. A number of sensitivity simulations were conducted to isolate effects of switching from fixed lower boundary conditions (LBCs) to fluxes for either or both of the species. While the results of simulations with flux boundary conditions for the recent past broadly agree with measurements, the authors find a reduction in CH4 abundance associated with an increase in surface H2 mixing ratio, which is in contrast to all recent publications on effects of additional H2 in the atmosphere (e.g., Paulot et al., 2021, https://doi.org/10.1016/j.ijhydene.2021.01.088; Warwick et al., 2023, https://doi.org/10.5194/acp-23-13451-2023; Sand et al., 2023, https://doi.org/10.1038/s43247-023-00857-8).

To showcase applications of the model, a pre-industrial and a hydrogen pulse experiment were run and analyzed. A comparison of CH4 and H2 levels from the former to observation-derived data served as further evidence of the model's applicability, while the latter was used to determine a feedback factor for an atmospheric hydrogen increase.

General comments

The manuscript is generally well structured and written, the content clearly falls within the scope of GMD, and is certainly of sufficient scientific novelty. I strongly encourage its publication, but I think it requires some additional explanations.

After carefully re-reading it several times, I still struggle with the question whether or why a change from a fixed LBC for H2 to emission and deposition fluxes should change the response of the CH4 abundance to additional H2---or why a model with CH4 flux boundary conditions instead of a fixed LBC should react differently to additional H2. This should be addressed (more clearly) in my opinion before a study including applications of the new model configuration is published in ACP.

Especially, the changes induced by switching from fixed LBCs to fluxes should be disentangled from concurrent changes in the CH4 and H2 abundances. If resources permit, this could be achieved with the help of additional experiments with fewer changes, e.g., replacing fluxes by fixed LBCs derived from the corresponding flux-driven simulations, or repeating the PD timeslice simulation with different fixed LBCs, or tuning the H2 soil sink to match the H2 burden from the fixed LBC simulations. All budget terms could then be compared between the simulations, to illustrate and explain the interplay of the different processes.

It may also be possible to derive a more detailed understanding from the available data (e.g., analysis of OH and CH4 in the hydrogen pulse experiment, and comparison to the PD timeslice), but the currently presented analysis in Sect. 4.2 does not convince me. Rather, I agree with the authors' own conclusion at the end of Sect. 4.3 that "a more rigorous experiment should be conducted to confirm these results", as they have the potential to drastically change the view on all the recent studies on climate effects of hydrogen emissions. The main question seems to be whether the net effect of additional H2 on OH abundance, (-)dOH/dH2 in the notation of Warwick et al., 2023, https://doi.org/10.5194/acp-23-13451-2023, is an increase or a decrease, or whether there are different regimes, and which of them is prevalent under which conditions.

Specific comments

• Depending on final layout, consider reducing the number of figures to ease readability by bringing the figures closer to their discussion.
• l. 26: Please specify what you mean with "the methane feedback factor from the impact of hydrogen".
• l. 40: Please explain how the fixed LBCs are implemented. (Overwrite or "nudge"? Only lowest layer?)
• ll. 43f: Please explain and/or add a reference for the "very limited interannual variability" of hydrogen deposition. Since soil moisture plays a crucial role, I would expect some degree of variation, at least in the midlatitudes.
• l. 48: for how many years are the time slices run after the spin-up?
• ll. 61ff: Since you (probably) used the same datasets for anthropogenic and biomass burning as Paulot et al., 2021, https://doi.org/10.1016/j.ijhydene.2021.01.088 did, why did you derive emission ratios from their Table 1 values instead of simply applying the ratios (and emission factors, in case of BB) they supply in their supplement? Please make sure that you arrived at the same values. Furthermore, the oceanic and terrestrial emissions should be excluded from the parenthesis in l. 61, as they are not associated with CO emissions, if I am not mistaken.
• l. 88: What is "[t]his larger flux adjustment" here? From the next line, I would assume it refers to the difference between 135 Tg yr-1 and 190 Tg yr-1, but at the end of the paragraph, the text says that "the" flux adjustment from the PD time slice was increased by(?) 20% (although it suggested previously that you calculated a new flux adjustment). Furthermore, how do the 20% relate to the ~40% difference in the wetland emissions? Are there separate adjustments for the wetland and other emissions? I did not consult Folberth et al., 2022, https://doi.org/10.1029/2021MS002982, for answers to these questions, but I think the explanation here should be revised to not require reading that publication first. In my opinion, the whole description of the flux adjustment for the nudged simulations should be revised. Furthermore, please make sure the 124 Tg yr-1 in the caption of Fig. A1 are also related to this description.
• l. 97: Which other processes are considered in the top layer?
• l. 104f: What is the motivation for this discussion (and Figure 1)? My feeling is that neither is necessary.
• l. 123: If you describe the soil porosity as the likely inaccuracy causing too high SMC/porosity ratios, why do you adjust SMC and not porosity?
• Fig. 3: Depending on the values, showing the standard deviations from the simulation across the aggregation intervals may add further value to the comparison (should then be discussed in the text as well, of course).
• Fig. 3 caption and description in text: Please add information on data selection/aggregation for the figure (monthly means for the years of the measurements?).
• Fig. 3 discussion:
  
  
  • From the Figure, I would conclude that the Sanderson et al. parametrization results are no worse, if not better, than the new approach when it comes to the comparison with observations. Please comment on (or emphasize more) why you still chose to replace the Sanderson et al. scheme entirely, instead of maybe adapting it where it has its shortcomings.
  • Please comment on the differences between your comparison and the one by Paulot et al., 2021, https://doi.org/10.1016/j.ijhydene.2021.01.088, e.g., availability of summer data for Gif-sur-Yvette; differences in Sanderson parametrization results, especially for Mace Head; why your comparison does not include the other three stations that Paulot et al. considered; etc.
• l. 150: Please rephrase or explain what you mean with "averaged over one year" for the Sanderson simulation.
• ll. 170f: Please add justification for this hypothesis, e.g., actually evaluate the soil moisture that you simulate for Tasmania by comparison with satellite observations.
• Fig. 4 discussion:
  
  
  • While I agree that the (absent) trend in [H2] at CGO is captured well by the model from about 2003 onwards, I miss a comment on the disagreement during the period 1994--2003, which may also be reflected -- although to a lesser degree -- in the MHD comparison, where agreement is reached around 2002.
  • Why does the near-perfect agreement between simulated and observed [CH4] at CGO break after 1992? Can this be due to the way the flux correction is determined?
  • Similarly, how do you explain the large reduction in deviation between the simulated and observed [CH4] at MHD between 1992 and ~2002?
• Comparison to NOAA [H2]: Unless I miss an important detail, please exclude the year 2014 from the observations as well, as you only simulated until 2013.
• l. 203: Please elaborate on the effect of orography and how the Hayman et al., 2014, https://doi.org/10.5194/acp-14-13257-2014, publication helps explain this [H2] overestimation.
• ll. 205f: An underprediction of <0.4% can be explained by anything in my opinion. Thus, I recommend either to remove the association with deposition here (and also the last sentence of Sect. 3), or to report maybe the median deviation rather than the mean, which may be quite strongly biased by the large deviations over China.
• Sect. 4.1: Please add a comment on the very high simulated [H2] over central/tropical Africa as well, where the sink is actually quite strong as well, according to your Fig. 2.
• Fig. 6 discussion/image: changes mixed up between c_OH (opposite changes in troposphere and stratosphere in the figure) and [O3] (rather homogeneous difference in the figure)?
• l. 226f: While I agree that the trend until 1992 is captured well, the simulated [CH4] levels off much more quickly and stably than in the observations, and the increasing trend after 2007 is much steeper. Please explain these differences.
• l. 228: The difference in [CH4] between the simulations with fixed H2 LBC and H2 fluxes seems to grow over time. Considering the long methane lifetime, such behavior is of course expected, but I find it hard to judge from the figure whether it is not still increasing at the end of the three simulated decades. Please discuss this in the text.
• l. 247: How do you infer the causality here?
• Fig. 7: Please explain (or fix) the data gap in the surface [CH4] from the H2;CH4-flux simulation in 1986.
• Fig. 8 and its discussion: Please explain the relevance of differences of the order of 1e-4, if you consider even the 2% change in CH4 lifetime "minimal" (ll. 272f).
• Fig. 8: I think it is not good style to leave out data from a figure. Maybe the "noise" (I assume you mean large relative differences and their fluctuation) could also be reduced by plotting the inverses of the lifetimes (i.e., first-order destruction rate coefficients), and showing the absolute instead of the relative difference?
• Figs. 8 and A4: I would ask you to perform a statistical significance test on these differences, as the sharp changes in sign could indicate "noise" as well.
• Table 2 and its discussion: Given the very similar setup and the generally positive reviews, I suggest to also compare the budget terms to the results by Surawski et al., 2025, https://doi.org/10.5194/egusphere-2025-1559.
• Table 2 and 3, and/or discussion: Please provide a reason for averaging over 2003--2013 here instead of the previously used period from 2008--2013.
• l. 273f: Why would a lower CH4 abundance entail a CH4 lifetime reduction? Is this assuming that less CH4 means more OH?
• l. 307ff: This paragraph is very confusing. Please rework, considering the following points:
  • No need to speculate on the reason for lower emissions - please check your assumption based on the data you used
  • Different units for soil uptake and hydrogen production
  • Single numbers called ranges
  • Logic hard to follow, especially if/how southern hemisphere aspects should explain northern hemisphere differences
  • Please explain the change in sign of the interhemispheric difference between PI and PD and the reason for the seasonality in the southern hemisphere at PD which is absent in the PI simulation.
• Section 4.5 and Fig. 10: This section requires some extension in my opinion.
  1. Please explain why you chose to set a constant mixing ratio throughout the atmosphere instead of actually adding an emission pulse (or use a constant relative increase).
  2. Please explain at least briefly the math and assumptions behind the formulas you provide. Please also rewrite them so that you don't have to take logarithms of units. Furthermore, please comment on why you consider 6 years to be a long enough period for determination of the feedback factor, given the interaction with CH4 that has a perturbation lifetime of the order of 10 years.
  3. I suggest to refrain from citing the preprint by Skeie et al., 2024, https://doi.org/10.5194/egusphere-2024-3079, as the final revised version has already been available in ACP since May 2025: https://doi.org/10.5194/acp-25-4929-2025. Note also that they do no longer report their findings as feedback factors (see discussion during peer review).
  4. Please consider showing the temporal development of the hydrogen burdens instead of the surface mixing ratios in Fig. 10, as they would relate more directly to the feedback analysis.

Technical corrections

• Simulation naming: Please either add "simulation" where the abbreviations are used, or use a different naming scheme that identifies the simulation descriptors more easily, e.g., TR-/TS-... for the transient and time slice simulations, respectively. Capital letters would help in general. You might also consider avoiding the semicolon in the identifiers, as it interrupts the reading flow in some places, where it is not immediately clear that you refer to a simulation abbreviation.
• l. 37: Please add a couple of words on the terms "nudged" and "ERA5 data", and a reference for the ERA5 data.
• l. 39 (and throughout): I recommend to add the word "fixed" wherever the LBC is mentioned, as a flux is also a lower boundary condition.
• l. 39: which -> with [?]
• l. 41: four -> five [according to Table 1]
• ll. 41ff: This paragraph forces the reader to jump back and forth between text and Table. Please add essential information to the text, e.g., that a "Sanderson" simulation was run in addition to the 4 mentioned transients. It would also be good to mention explicitly that the time slice simulations have free running meteorology. Furthermore, I suggest to add some motivation for the individual simulations (e.g., Sanderson as standard UKESM hydrogen soil sink parametrization), to make the Section easier to follow.
• l. 51, and throughout: concentration -> mixing ratio (where appropriate); and why "number density" for OH, for which you actually do report concentrations?
• Table 1: I find the different wordings for the same things (if my understanding is correct) confusing.
  
  
  • "Nudged from 1982." for "Control" means the same as "Nudged from 1982 -- 2013" for the following ones!?
  • "CH4 biogenic, biomass burning and anthropogenic emissions + CH4 flux adjustment" for "CH4-flux" means the same as "all CH4 emissions" for "H2;CH4-flux"!?
• l. 58: are -> is
• l. 66: Please specify the version of the CEDS data you used.
• l. 85 (and throughout): I recommend to replace "modelled" by "simulated" where you refer to the output of the simulation, as I would consider "modeling" to refer to the method rather than the output of a model.
• ll. 91f: Something went wrong here during editing, I suppose (until "at" in "at 0.0358").
• l. 99: parametisation -> parameterisation
• l. 100: lead a -> lead to a
• Fig. 1 caption: hydrogen uptake -> deposition velocity of hydrogen uptake
• l. 102: Please add a note on the tuning of the soil sink here (cf. ll. 383ff).
• l. 103: Prior paragraph should mention that it describes the soil resistance in a resistor model.
• l. 104: hydrogen uptake -> deposition velocity of hydrogen uptake
• ll. 105f, and many places: deposition -> deposition velocity
• l. 109f: The two features should be mentioned in opposite order (or the text below rearranged). It is confusing that the 2nd feature is described first, and the first described in a separate paragraph below.
• l. 111: Either pull in equations and definitions here, or describe more abstractly (with reference(s) to the Appendix). The formulation as it is requires the reader to jump between this Section and the Appendix, which should be avoided.
• l. 115: Maybe replace "of high volumetric SMC" by "where SMC is of comparable magnitude to soil porosity", as you only refer to the relative value throughout the paragraph.
• l. 118: This -> The
• Fig. 2 caption:
  
  
  • from Paulot -> adapted from Paulot
  • remove redundant parenthesis "(H2-Flux)"
  • monthly mean hydrogen deposition -> monthly mean hydrogen deposition velocity
• l. 128: land use type -> land type (?)
• Fig. 3:
  •  Vertical axis label should be "H2 deposition velocity / cm s-1".
  • Suggest to add N and E (or W, without minus sign) to the coordinates.
• l. 136: solid -> dash-dotted
• l. 144: Gir -> Gif
• ll. 147f: hydrogen velocities -> hydrogen deposition velocities
• l. 149: deposition -> deposition velocities
• l. 152:
  
  
  • hydrogen values -> hydrogen deposition velocity values
  • Since Fig. 4 rather suggests an overestimation of mixing ratios at Mace Head during the period evaluated for Fig. 3, I assume "concentrations" to be a typo here. If so, the clause is redundant, as "underpredicted" already says that the simulated values are below the observed ones.
• l. 153: error -> standard deviation of the observations
• l. 175: 80? From the figure, I read more than 100 ppbv of deviation.
• l. 185: show the -> show that the
• ll. 187f: are able to capture ... -> indicate that ... is captured
• l. 188f: I can only find one "excluded" point, below the colorbar. Are there more? I suggest to move it/them below the Taylor diagram, and would ask you to move the explanation to the Figure caption.
• l. 195: observed deposition -> deposition comparison
• l. 200: between -> averaged from
• l. 201: the magnitude of the hydrogen concentrations -> observed hydrogen mixing ratios to within ... ppbv
• ll. 210ff: Although you mention sensitivity to chemical fluctuations, and find a 10% change in [H2], you expect minimal impact on O3 and OH!? Please consider rephrasing this paragraph.
• l. 212: H2-flux -> in the H2-flux
• Fig. 5 caption:
  
  
  • south -> southern hemisphere
  • north -> northern hemisphere
  • Label correspond is -> Labels correspond to
  • and are given -> as given
• Fig.s 6, 8, A3, A4: It would be nice to unify the simulation descriptions in the titles (column headers).
• Fig. 6 and ll. 244f (and analogously Figs. 8, A3, and A4): Please use blue for negative, and red for positive values, and plot "Flux - Control / Control" instead of its negative. The figure will then remain the same, but can be much more easily interpreted as the differences introduced by switching from fixed LBCs to fluxes. Furthermore, I suggest to leave out the middle column, as it does not provide any added value.
• Fig. 7: Vertical axes labels should be "Surface CH4" and "Surface H2".
• l. 241: fluxes -> loss rates
• l. 242f: You divide by species mixing ratios, and the reactions do not become independent of the species. Please use precise language. What you describe here might be called (aggregate) first-order rate coefficients, or you could directly refer to their inverses, namely the chemical lifetimes.
• Fig. 8 (3 times): H2 atm -> H2 chem
• l. 273: with -> which
• Table 3 caption: 10 years between 2003--2013 to 3sf -> 11 years from 2003--2013 (?)
• l. 291ff: Please delete the 10 ppb approximation, if the means are 765 ppb vs. 761 ppb, as you write two sentences later.
• Section A1: Please state explicitly here that you are reproducing the work by Ehhalt and Rohrer, 2013, https://doi.org/10.3402/tellusb.v65i0.19904
• l. 307: This -> There [?]
• Fig. 9 caption: This currently says that both the PI and the PD simulation provide data for 1850. For more precise language and easier reading, you could write "Five-year hemispherical averages of surface hydrogen (blue) and methane (red) mixing ratios for a) 1850 (H2;CH4-PI simulation) and b) 2020 (H2;CH4-PD simulation)."
• Fig. 10: I suggest to remove the "(2020)" from the title
• Fig. 10 caption: and -> over
• l. 348: simulation -> simulate
• l. 356: to -> of
• l. 357: THe -> The
• l. 360: (UM-UKCA).The -> (UM-UKCA). The
• l. 369: deposition -> deposition velocity
• l. 376: m3 air / m3 total pore space -> m3 air / m3 soil
• l. 376: m3 total pore space / m3 total volume -> m3 total pore space / m3 soil
• l. 378f: I suggest to use SI units here.
• l. 378ff: Please use either T or T_s throughout, when referring to soil temperature.
• l. 379: C° -> °C
• l. 380 (analogously l. 388, l. 393, and l. 394): f(\Theta_a) -> f(\Theta_w) [and \Theta_w needs to be defined]
• l. 386: Units are missing in the exponentials.
• l. 391f (analogously l. 395f): look like a mistake in the reproduction of the work by Ehhalt and Rohrer, 2013, https://doi.org/10.3402/tellusb.v65i0.19904, where limits of applicability are given for the equations in terms of allowed ranges of \Theta_w/\Theta_p ratios
• l. 392: \Theta_a -> f(\Theta_w)
• Fig. A2: Please clarify the "emission" label.
• Fig. A2 caption: Delete closing parenthesis.
• Fig. A3 caption: All scales are actually linear.
• Fig. A4:
  
  
  • LCB -> LBC (two instances)
  • It looks as if the values of the differences actually span a much narrower range than the colorbar - could be adjusted.
• l. 397ff: If NLA "provided the model runs for all simulations", what is meant with "MAJB ran the simulations"?
• l. 399: contirubted -> contributed
• l. 400: provivded -> provided
• l. 448: delete one instance of "https:doi.org/"
• l. 533: I suggest to cite the GRL article (https://doi.org/10.1029/2024GL112445) instead.

Review of “Development of Fully Interactive Hydrogen with Methane in UKESM1.0” by Brown et al for publication in GMD

The manuscript documents a more comprehensive configuration of UKESM1 that includes the simulation of hydrogen and methane driven by emissions rather than prescribed lower boundary conditions (LBCs) to capture the complex interactions and feedbacks between these species as well as impacts on atmospheric composition. The authors perform a number of sensitivity simulations to assess the effects of replacing LBCs with emissions of hydrogen and methane. The model configuration driven by emissions of both hydrogen and methane is generally able to capture the observations, though there are some peculiarities that need deeper assessment (more below). Specifically, the authors find a reduction in global mean surface methane concentration (and a drift) in this configuration characterized by higher global mean surface hydrogen concentration and the explanation given for this is not convincing. 

The authors apply the emissions driven configuration to simulate preindustrial concentrations of hydrogen and methane and estimate the hydrogen feedback factor to demonstrate the capability of this model configuration. 

The manuscript has some shortcomings which can be overcome with better organization of the material, and improved and additional analysis to support conclusions. The description of the model configuration falls within the scope of GMD and is novel enough to warrant publication.    I encourage the publication of this manuscript after my comments below have been addressed.  

Specific Comments: 

L17-18: While the main “chemical sink” of hydrogen is oxidation by OH, but it accounts for less than one third of the total H2 sink (Ehhalt and Rohrer, 2009; Paulot et al., 2021). It would be good to note that. 

L21-23: “Earth system models(ESMs) currently do not account for both hydrogen and methane fluxes at the surface,...” why? It would help to have an answer for this question as a justification of why this effort is undertaken here. 

L26: elaborate on “methane feedback factor”

L27: why is a deposition scheme important? This is where the soil sink of H2 comes into a picture. 

L34-40: an amip configuration is not the same as nudged. What is the motivation for choosing the option with Hydrogen time-invariant. And why are the LBCs uniform spatially?  

L43-44: “As hydrogen deposition has a very limited interannual variability,”- please provide supporting reference for this statement and elaborate how this compares with the findings of Paulot et al (2021) and Derwent et al. (2021).

L45: what meteorology is used to drive the timeslice simulations? Are these driven by climatological SSTs/sea-ice or are they nudged to repeated winds/temperature for a specific year? 

L47-50: Anthropogenic emissions of H2 are not available for CMIP6 historical and scenarios based on data holdings in input4MIPS https://aims2.llnl.gov/search?project=input4MIPs. Rather than a blanket statement, the authors should point the readers to the detailed description of emissions in section 2.2. Please elaborate on the reasoning behind a 30 year spin up. 

L50-53: a) these sentences can be combined, b) what does at all levels mean - all vertical levels? If so, why was this done throughout the vertical column and not at the surface only, c) was the hydrogen concentration set to 45.7ppb or 662.5ppbv? How long was the pulse (increased H2 concentration) implemented for - the full duration of the simulation or just one year? If it was implemented for the full duration of the simulation, then this is technically not a pulse simulation but a sustained perturbation.  

Table 1: The experiments need better naming. The H2;CH4-X construct is confusing. I would suggest something like H2_CH4-X, but I am sure the authors can be more creative. 

L55-78: The description of emissions of H2 used in the simulations can be improved. A few points to consider - 

1. i) the BB4CMIP (van marle et al) emissions provided H2 biomass burning emissions explicitly, and it sounds like oceanic and terrestrial H2 emissions are also used from available sources, so this statement  “The ratio of CO:H2 for each category (anthropogenic, biomass burning, oceanic and terrestrial) is derived from the period 1995−2014, where we have a known estimate of hydrogen emission” needs to be clarified. Further, “The resultant hydrogen emission for each source (anthropogenic, biomass burning, oceanic, and terrestrial) follows the spatial pattern of the equivalent CO source, but with values rescaled to give the global emission total appropriate for hydrogen” should also be clarified. 
2. ii) how do the emission totals compare with those from Paulot et al (2021)? This comparison should be noted in the text. 

iii) what are the anthro and bb total emissions for years 2020 and 1850? These are used in simulations, but not discussed/displayed anywhere in the manuscript. 

L81-82: How are biogenic emissions of methane implemented? Are wetland emissions prescribed or interactive? If prescribed, please elaborate on the source. I am sure all of this information is included by Folberth et al (2022), but I hope the authors agree that it would be cumbersome for the readers to go digging into that paper to understand the results here. 

L87: clarify what “Note that wetlands are excluded” means. I assume you mean that the flux adjustment is not applied to wetland emissions because they are calculated interactively.

L88-90: How can the authors tell that the underestimate in methane is due to an underestimate of wetland emissions or for that matter other source emissions or an overestimate of the methane sink (hydroxyl radical)? I think there is an assumption being made that emissions from all other sources are well-constrained and so is the modelled hydroxyl radical. If so, the authors should provide a basis for this assumption. 

L104: by “global hydrogen uptake”, do you mean the global mean hydrogen deposition velocity (especially since the units are cm s-1)? 

L106-107: Figure 1 shows deposition velocity. If you meant to show hydrogen uptake, please update the figure. Also, what year are these deposition velocities for? Do they vary between the transient and timeslice simulations? 

L132: It would be prudent to be precise in the text here and throughout the manuscript. Figure 2 shows the comparison of H2 deposition velocity calculated based on two two deposition schemes. 

L149: I am confused, did CMIP6 provide H2 deposition velocities? 

L162: “verify the integrity of the model” sounds strange. How about “evaluate the skill of the model?”

Figure 4 caption: I am assuming the years in the parentheses in “hydrogen (1994-2013) and b) methane (1985-2013).” indicate the years of observations and not the simulations. Please revise the caption to be precise. 

L164-165: What is the source of these observations? It would be appropriate to give credit to those who make these observations by providing a reference and/or doi for the data. I would also recommend adding a separate Observations subsection under the Methods section to describe them and their associated uncertainties, as well as the reasons for choosing specific sites (e.g., longer timeseries, remote station capturing background concentrations etc). 

L180-181: While the CMIP6 historical emissions ended in 2014, the timeseries could be  extended using an SSP scenario. The CMIP7 historical emissions are now available but of course the model simulations cannot be rerun with these emissions. 

Figure 4: please replace “model” in the labels with the title of the simulation being shown for better readability. 

L184-185: Do all sites provide data for the same time period? If not, I would suggest adding a column to Table A1 to indicate the years of data available for each site. 

L200: “averaged hydrogen concentration from all sites given as points“, this comes across as the average of data from all sites. Please change “all sites” to each site. 

L202-203: How does orography contribute to high simulated H2 concentrations over India and China? Are high values also simulated for CH4 over these regions because of orography?

L209: “Effect on Atmospheric Composition” of what? 

L210-212: Please point to the figure upon which this conclusion is based.  

L213-216: Since the discussion is focused on the effects of interactive (emission-driven) CH4 and H2 simulations on atmospheric composition, it would be more logical to subtract the control from the Flux to calculate the percent change [(Flux-control)/control].  

L218-219: I see the peak in 1991 in BB emissions in figure A2. 1992 is also the year of the Pinatubo eruption. Can there be any effects on H2 from that eruption? 

L220: “The addition of the methane flux” - this should technically be “replacement of the methane LBC to flux” since you are not adding a new emission flux to the simulation, rather replacing the CH4 LBC with emissions. The effect of methane is included in both the H2-flux and  H2; CH4-flux simulations. It is only how the effect of methane is included that is different. Please ensure this is corrected throughout the manuscript.  Further, because of the adjustment applied to the CH4-flux simulations, the expectation is that methane in both the emissions-driven and prescribed simulations will be similar with small differences (~30 ppb, as demonstrated in Fig 7b). Hence, the impact on hydrogen is simulated to be small going from the H2-flux to the H2; CH4-flux simulation. 

L223-224: Why is there a cross over in 1992 in CH4 concentrations simulated for the emission driven run versus prescribed CH4 in Figure 7? This was also evident from Fig 4b for Mace Head. Also, why is there a drift in the CH4 concentrations for the H2;CH4 Flux simulation? The difference between simulated methane concentrations for CH4 Flux and H2;CH4 Flux simulation increases progressively from 1983 (beginning of the simulation) to 2013 (end of simulation). Additionally, there is a gap in 1986 for  H2;CH4 Flux which needs to be addressed. 

L225: What is meant by good agreement? Is 30 ppb difference (noted in the previous sentence) between the CH4 emission driven runs and the control considered good agreement? 

L239-240: This is confusing -”Figure A3  shows the hydrogen and methane chemical loss; H2 chemical loss increases when H2 flux is implemented into the model, while the CH4 loss via OH decreases”, while the figure itself shows CH4-flux minus H2; CH4-flux. Please make it easier for the reader to understand by showing  H2; CH4-flux minus CH4-flux which would explicitly show the effect of implementing H2 flux and be consistent with what is written in the text. If CH4 loss via OH decreases when implementing H2 flux, then why does the methane lifetime stay the same between CH4-flux and  H2; CH4-flux simulations (Table 3 last two rows)? 

L242: What is meant by “the OH activity cannot be identified.” 

L2454-245: “Blue (red) indicates an increase (decrease) when H2 flux is included, relative to the simulation with H2 LBC” - this is not consistent with what is actually being shown in the figure. Please revise to show 100* (H2; CH4-flux minus CH4-flux)/ CH4-flux. 

Figure 8: Please include the full atmospheric column in the figures, particularly because you are using the full atmospheric burden and loss rates to calculate the lifetimes. Masking out just because of strong variability in the stratosphere is not appropriate. Further, please assess the significance of the differences being shown. Would you consider % differences of the order of 0.1% significant? 

Table 2: Please show the H2 budget terms for all the simulations conducted for completeness and ease of comparison. According to mass balance, the sum of all production (atm  prod + emissions) terms should be equal to the sum of all loss (soil + atmospheric) terms at equilibrium. This is not the case for any of the simulations being shown here (the imbalance ranges from 2.3 to 17.8 Tg). Can you please explain this, especially the mass imbalance for the PI simulation? 

Table 3: Budget terms for CH4 (prod, loss, deposition), should also be included which will help shed light on the effects of coupling of both emission-driven hydrogen and methane on methane lifetime.

Tables 2 and 3: please provide a motivation for averaging over 2003-2013 which is different from the averaging period for the figures. 

L267-268:Thus far the PI and PD simulations have not been discussed. I don't think these results should be included in the range of lifetime estimates in the text without providing a context. Rather the focus here should be on explaining the differences in budget terms related to the emissions-driven versus prescribed experimental setup. 

L279-280: Based on the results shown here I am not fully convinced that coupling of both interactive hydrogen and methane may cause a decrease in the methane lifetime. I agree with the next statement that further work is needed and perhaps the authors can do a better job at presenting the analysis here. The authors may want to consider running the CH4-flux simulation with H2 LBC increased by, say 10%, to roughly mimic the increased  H2 concentration in the H2; CH4-flux simulation. This could help isolate the impact of increased H2 on methane abundance. 

L283: Please remind the readers, the motivation for analyzing the PI and PD simulations.

L284: The hydrogen burden of 129.4Tg in PI simulation is inconsistent with that presented in Table 2 (136 Tg). 

L286-287: How is the conclusion derived? 

L291: replace south with the southern hemisphere. 

L288-294: Any thoughts on why the PI simulation is not able to capture the CH4 N-S gradient derived from ice cores?

L316-326: Is the methodology used here to assess the H2 feedback factor and the perturbation lifetime developed in this study or based on previous studies? No references are provided which gives the impression that this is original work. Please clarify. What is the reason for choosing the 6-year decay time? 

L339: “which has been tuned to literature values of the tropospheric hydrogen burden” did I miss something? Was there an adjustment applied to the H2 emissions or deposition? I may have lost track. 

L343: “little change in hydrogen concentration when CH4 flux was added” - please revise to “...when CH4 LBC was replaced with CH4 flux”. 

L348: replace simulation with simulate 

L347-349: But there are biases for PI methane. The statement comes across as overselling the model’s skills. Calling a spade a spade will ensure credibility! 

Figures: There is an inconsistency in the choice of color bases across the figures (e.g., Fig 8 top and bottom in columns 1 and 2 have different colorbars. why?). Please be consistent. 

Throughout the manuscript there is inconsistency in the labeling of simulations (e.g., CH4-Flux versus H2 LBC;CH4-Flux). Please ensure consistency in the labeling.